PLoS Medicine

doi: 10.1371/journal.pmed.1002391pmid: 28949963

In this week’s PLOS Medicine, Crowther and colleagues publish the results of the PROGRESS Study, which examined the effect of maternal vaginal progesterone on the risk of respiratory distress syndrome in the baby [1]. Women at high risk of preterm birth because of a previous spontaneous preterm birth were recruited to this study, which involved self-administering 100 mg progesterone or a placebo vaginally from 20 to 34 weeks of pregnancy. No differences were found in the rate of the primary outcome (incidence of respiratory distress syndrome and severity of respiratory disease) between the progesterone and the placebo groups (incidence of respiratory distress syndrome in 42/402 [10.5%] and 41/388 [10.6%], respectively [RR 0.98, 95% CI 0.64–1.49]), nor were there differences in any of the other secondary outcomes. The study, a double-masked randomised placebo-controlled trial, was well conducted. About 40% of women who were approached agreed to participate. The primary outcome was available for all participating women, and around 65% of women were still taking study treatment by 34 weeks gestation. Rates of preterm birth were 36% and 17% before 37 and 34 weeks, respectively; hence, the recruitment strategy effectively identified a group at high risk. Although the study was terminated earlier than planned (after recruitment of 787 women rather than the 984 initially intended), and the incidence of the primary outcome was lower than anticipated in the placebo group (10.6% rather than 15%), it is unlikely that these issues have materially affected the conclusions of the study. Although vaginal progesterone is not licensed for prevention of preterm birth, it has been widely adopted by clinicians around the world for this purpose. Progesterone for preterm birth prevention in high-risk women is endorsed by expert guideline groups [2], including the National Institute for Clinical Excellence (UK) [3] and the FIGO Working Group on Best Practice in Maternal-Fetal Medicine [4]. The PROGRESS Study is the third large randomized trial (the others being our own OPPTIMUM study [5] and the study of O’Brien et al. [6]) to show a lack of efficacy of vaginal progesterone. Specifically, the PROGRESS trial showed no difference between the 2 groups in gestation of delivery, preterm birth before 37 weeks, or preterm birth before 34 weeks. We believe it is now time for a comprehensive review of the data on progesterone to identify risks and benefits in women at risk of preterm birth for different reasons. Ostensibly, there is biological plausibility behind the administration of progesterone for prevention of preterm birth. Progesterone can inhibit contractions of the myometrium in vitro [7], and antiprogestogens are used as abortifacients. However, progesterone levels are high during pregnancy, far above receptor saturation. There is no evidence that women delivering preterm have lower progesterone levels and administration of progesterone vaginally does not increase circulating concentrations. Therefore, the mechanism by which a modest additional amount of progesterone could achieve a therapeutic effect is unclear. In evaluating progesterone to prevent preterm birth, the Cochrane analysis groups evidence by maternal risk factor for preterm birth rather than by route of administration or type of progesterone [8], even though vaginal natural progesterone and intramuscular 15 dihydroprogesterone caproate are very different therapies. The Cochrane analysis suggests that, in women with a previous preterm birth, progestogens reduce perinatal mortality and rates of preterm birth before 34 weeks, low birthweight, and neonatal death. Inclusion of women from OPPTIMUM and PROGRESS will double the existing sample size; a major impact on the treatment effect and confidence intervals is to be expected. In women at risk of preterm birth because of a short cervix, Cochrane suggests that progesterone reduces rates of preterm birth before 34 weeks but has no impact on perinatal mortality, low birthweight, or neonatal death [8]. A single randomized study and an individual patient data meta-analysis have shown that progesterone in women with a short cervix reduces a composite adverse neonatal outcome [9,10], although the individual study was insufficient to persuade the United States Food and Drug Administration (FDA) to license vaginal progesterone. Importantly, the FDA considered that a more robust statistical approach failed to result in a statistically significant effect of progesterone [11]. To address this complexity, the Patient-Centered Outcomes Research Initiative (PCORI) has initiated an individual patient data meta-analysis that will be conducted by an independent data centre. It is hoped that this will address the uncertainty about the efficacy of progesterone to prevent preterm birth in women with various risk factors. Even if progesterone is found to reduce preterm birth rates in women with either a previous preterm birth or a short cervix, it is increasingly evident that alternatives are needed because the impact on preterm birth rates overall are small. Modelling of the impact of progesterone to prevent preterm birth in women with a previous preterm birth (but without a short cervix), and assuming a 20% reduction in preterm birth before 37 weeks, suggests an absolute reduction of 0.01% in preterm birth rates [12]. It has been claimed that routine cervical length screening of the entire US pregnant population, and offering vaginal progesterone to all women with a cervical length of 10–20 mm, would be cost effective [13]. However, in this scenario preterm birth would be prevented in only 913 women. This represents an absolute risk reduction of 0.02%, given that in 2015 there were 382,786 preterm births in the US [14]. There has been huge renewed excitement amongst clinicians and the pharmaceutical industry for the use of progestogens to prevent preterm birth in the 21st century. A PubMed search shows 792 publications on this topic since 2000. The PROGRESS Study adds to a body of evidence suggesting that the role of progesterone may be more limited than previously thought. Preterm birth remains the single biggest cause of neonatal mortality and morbidity worldwide, and effective therapeutic interventions are desperately needed. It is time to start exploring alternatives, and to progress beyond progesterone for the prevention of preterm birth.

doi: 10.1371/journal.pmed.1002395pmid: 28961237

Background The household is a potentially important but understudied unit of analysis and intervention in chronic disease research. We sought to estimate the association between living with someone with a chronic condition and one’s own chronic condition status. Methods and findings We conducted a cross-sectional analysis of population-based household- and individual-level data collected in 4 socioculturally and geographically diverse settings across rural and urban India in 2013 and 2014. Of 10,703 adults ages 18 years and older with coresiding household members surveyed, data from 7,522 adults (mean age 39 years) in 2,574 households with complete covariate information were analyzed. The main outcome measures were diabetes (fasting plasma glucose ≥ 126 mg/dL or taking medication), common mental disorder (General Health Questionnaire score ≥ 12), hypertension (blood pressure ≥ 140/90 mmHg or taking medication), obesity (body mass index ≥ 30 kg/m2), and high cholesterol (total blood cholesterol ≥ 240 mg/dL or taking medication). Logistic regression with generalized estimating equations was used to model associations with adjustment for a participant’s age, sex, education, marital status, religion, and study site. Inverse probability weighting was applied to account for missing data. We found that 44% of adults had 1 or more of the chronic conditions examined. Irrespective of familial relationship, adults who resided with another adult with any chronic condition had 29% higher adjusted relative odds of having 1 or more chronic conditions themselves (adjusted odds ratio [aOR] = 1.29; 95% confidence interval [95% CI] 1.10–1.50). We also observed positive statistically significant associations of diabetes, common mental disorder, and hypertension with any chronic condition (aORs ranging from 1.19 to 1.61) in the analysis of all coresiding household members. Associations, however, were stronger for concordance of certain chronic conditions among coresiding household members. Specifically, we observed positive statistically significant associations between living with another adult with diabetes (aOR = 1.60; 95% CI 1.23–2.07), common mental disorder (aOR = 2.69; 95% CI 2.12–3.42), or obesity (aOR = 1.82; 95% CI 1.33–2.50) and having the same condition. Among separate analyses of dyads of parents and their adult children and dyads of spouses, the concordance between the chronic disease status was striking. The associations between common mental disorder, hypertension, obesity, and high cholesterol in parents and those same conditions in their adult children were aOR = 2.20 (95% CI 1.28–3.77), 1.58 (95% CI 1.15–2.16), 4.99 (95% CI 2.71–9.20), and 2.57 (95% CI 1.15–5.73), respectively. The associations between diabetes and common mental disorder in husbands and those same conditions in their wives were aORs = 2.28 (95% CI 1.52–3.42) and 3.01 (95% CI 2.01–4.52), respectively. Relative odds were raised even across different chronic condition phenotypes; specifically, we observed positive statistically significant associations between hypertension and obesity in the total sample of all coresiding adults (aOR = 1.24; 95% CI 1.02–1.52), high cholesterol and diabetes in the adult-parent sample (aOR = 2.02; 95% CI 1.08–3.78), and hypertension and diabetes in the spousal sample (aOR = 1.51; 95% CI 1.05–2.17). Of all associations examined, only the relationship between hypertension and diabetes in the adult-parent dyads was statistically significantly negative (aOR = 0.62; 95% CI 0.40–0.94). Relatively small samples in the dyadic analysis and site-specific analysis call for caution in interpreting qualitative differences between associations among different dyad types and geographical locations. Because of the cross-sectional nature of the analysis, the findings do not provide information on the etiology of incident chronic conditions among household members. Conclusions We observed strong concordance of chronic conditions within coresiding adults across diverse settings in India. These data provide early evidence that a household-based approach to chronic disease research may advance public health strategies to prevent and control chronic conditions. Trial registration Clinical Trials Registry India CTRI/2013/10/004049; http://ctri.nic.in/Clinicaltrials/login.php Why was this study done? Prior research, largely set in high-income country settings, demonstrates the concordance of physical health and mental health outcomes among spouses and between parents and their adult children. These prior studies have examined neither disease concordance among coresiding adults who are not parent-child pairs or spouses nor the correspondence of different chronic conditions (e.g., husband’s diabetes status and wife’s common mental disorder status). Few have examined physical and mental health outcomes simultaneously. Understanding associations of shared and differing chronic conditions among all coresiding adults in households may shed light on new approaches to identify and treat chronic illness in low- and middle-income countries such as India. What did the researchers do and find? We examined 5 chronic disease conditions—hypertension, diabetes, obesity, common mental disorder, and high total blood cholesterol—in 7,522 adults living in 2,574 households in 4 diverse settings in India. We demonstrate that there is substantial concordance in diabetes, common mental disorder, and obesity among Indian adults residing in the same household regardless of relationship type. Correspondence across different chronic conditions was weaker. What do these findings mean? Adults who live with someone with diabetes, common mental disorder, or obesity are more likely to have that same condition. Addressing the burgeoning chronic disease burden in India will benefit from understanding and intervening upon mechanisms responsible for disease concordance within households in this setting. Introduction Chronic conditions are now the biggest contributor to disability-adjusted life years across the globe [1], and morbidity due to these conditions has increased at a faster rate in South Asia as compared to the rest of the world over the past 20 years [2]. Alongside these major epidemiologic changes, the extended family system—in which relatives beyond the nuclear family reside with one another—remains salient in India: 50% of children reside in households with adults in addition to their parents [3], and 77% of the elderly reside with their married adult children [4]. Indians, therefore, from cradle to grave are likely to share a household environment and health-promoting resources with family members and also be exposed to one another’s lifestyle practices (e.g., tobacco use, diet). Genetically related household members—such as parents and children—may additionally share a similar hereditary predisposition to disease. Yet, most epidemiologic studies and public health interventions in India targeting chronic conditions currently focus on individuals or occasionally the community [5] and largely ignore the family unit despite its potential importance in understanding risk and designing sustainable interventions. Indeed, the literature suggests the promise of reorienting the focus of chronic disease research from the individual to the family. Prior systematic reviews drawing largely on populations residing in high-income countries (HICs) demonstrate the concordance of cardiovascular risk factors [6,7] and mental health and health behaviors [7] among spousal dyads. Concordance of cardiometabolic conditions among parent-child (e.g., [8,9]) and sibling dyads (e.g., [9]) has also been observed in studies conducted in HICs. A small but growing body of literature in Asian countries has examined and found concordance of cardiometabolic conditions among spousal [10–12], parent-child [11–13], and sibling [12,14] dyads and concordance of health behaviors among spousal dyads [15]. Genetic, environmental, and interpersonal mechanisms are 3 types of highly plausible drivers of familial concordance of disease implicitly or explicitly considered by prior studies. Understanding the extent of genetic predisposition to certain disease conditions has been the goal of many family-based studies [8,11], although genetic explanations of disease concordance largely apply to parent-child and sibling dyads. Environmental factors can include shared household socioeconomic resources important for health [7,16], a common household diet, and the extrahousehold shared community milieu (e.g., built environment and cultural norms around physical activity). Finally, interpersonal influences include modeling of lifestyle factors such as physical activity, diet, and smoking [7,17,18]; “affective contagion” in which the moods of those around us influence our own [7]; and the stress of living with and caring for someone with a chronic condition [19–22]. In addition to these 3 mechanisms, assortative mating (largely applicable to spousal pairs) or other self-selection processes into households/families may impact the concordance of chronic disease within families. We seek to build upon the existing literature to address 2 unresolved but important issues regarding chronic disease concordance in households. First, we are aware of no studies that have gone beyond the spousal, parent-child, and sibling pairs that comprise the nuclear family to investigate associations of chronic disease status among all household members. Most of the hypothesized pathways linking chronic conditions within families would also apply to individuals beyond the nuclear family who reside in the same household. Second, we are aware of no studies that have investigated the correspondence of different chronic conditions among household members (e.g., husband’s diabetes status and wife’s common mental disorder status). Because many chronic conditions have common behavioral and psychosocial risk factors, shared environmental or interpersonal factors that lead to the development of a specific chronic condition in 1 household member may lead to the development of another chronic condition in a coresiding household member. For example, diabetes, hypertension, obesity, and high cholesterol are cardiometabolic conditions that are impacted by physical activity and dietary intake [23], and much evidence links diabetes and depression [24]. Ignoring the correspondence between chronic conditions may underestimate the degree of household aggregation of disease. Understanding associations of shared and differing chronic conditions among all coresiding adults in households may shed light on new approaches to identify and treat chronic illness in India and other low- and middle-income countries (LMICs) where extended family households are prominent [25]. The extent to which the household as a unit may be effectively leveraged for mechanistic studies of prevention and interventions targeting chronic conditions in India will depend on whether there is indeed concordance of the same chronic conditions or correspondence of differing chronic conditions within household members. The overarching goal of this study was to test the hypothesis that living with any household member who has a chronic condition—diabetes, common mental disorder, hypertension, obesity, and/or high cholesterol—raises the risk of developing the same or another chronic condition. To explore this hypothesis, we conducted an analysis to examine whether living with someone with a chronic condition relates to one’s own chronic condition status in coresiding adults in households across 4 geographically and socioculturally diverse districts in India. In addition, we examined these associations among dyads of parents and their adult children and of spouses living in the same household. Methods Data source We conducted a cross-sectional observational analysis of the baseline survey and laboratory data from the Diet and Lifestyle Interventions for Hypertension Risk Reduction through Anganwadi Workers and Accredited Social Health Activists study (DISHA study) [26]. DISHA is a community-based cluster randomized trial designed to test the effectiveness of a community health worker-led lifestyle behavior change on hypertension reduction. The baseline study was conducted in 2013 and 2014 to measure risk factors in 4 regionally and socioeconomically diverse districts located in Madhya Pradesh, Gujarat, Tamil Nadu, and Himachal Pradesh that were selected for the initial phase of the intervention. Participants were selected using a multistage cluster sampling design stratified by district. Dhar District, Madhya Pradesh (central India), is home to a predominantly indigenous (Adivasi) population and has poor road connectivity. Junagadh District, Gujarat (western India), is a rural plains setting, while the Mashobra District, Himachal Pradesh (northern India), is a rural hilly setting consisting of sparsely populated villages. Finally, the Puducherry, a union territory bordering Tamil Nadu (southern India), is an urban and coastal setting with relatively better public health infrastructure. The primary sampling units were randomly selected villages within the districts (9–12 villages per site; a total of 45 villages in the study), from which 120–150 households were randomly selected. At the household level, all adults over the age of 18 years were invited to participate in the survey. We exploited this feature of the sampling design to identify adults residing in the same household. Of the 11,751 participants linkable to the household demographic roster, 10,703 participants had at least 1 coresiding household member enrolled in the study. Of participants with coresiding household members, 3,181 were excluded because of missing data on 1 or more outcomes. Thus, a total of 7,522 participants residing in 2,574 households with complete covariates and at least 2 sampled adults per household were analyzed in the primary analysis. We additionally examined associations of interest among adults with coresiding parents (1,660 dyads in 1,199 households) and spouses (1,598 dyads in 1,598 households). Dyads were identified through each participant’s relationship with the household head. The analysis of dyads was restricted to pairs of participants who were unambiguously identifiable as parent-adult child pairs or spouses through the participants’ relationship to the household head. The study obtained ethics approval from the Centre for Chronic Disease Control’s ethics committee (#IRB00006330), as well as ethics committees of participating sites. Participants provided written informed consent prior to being surveyed and assessed. This study is reported as per STROBE guidelines (S1 Text). Chronic conditions We analyzed 5 prevalent chronic conditions: diabetes (prior diagnosis by a physician, fasting plasma glucose ≥ 126 mg/dL, or taking medication [27]), common mental disorder (i.e., depressive and anxiety disorders, measured here using the General Health Questionnaire score ≥ 12 [28,29]), hypertension (prior diagnosis by a physician, blood pressure ≥ 140/90 mmHg, or taking medication [30]), obesity (body mass index ≥ 30 kg/m2 [31]), and high cholesterol (prior diagnosis by a physician, total blood cholesterol ≥ 240 mg/dL, or taking medication [32]). We also created a composite binary variable indicating the presence of at least 1 of the 5 chronic conditions. Data collection took place at the participant’s home. Height was measured using a stadiometer with accuracy of 2 mm (Seca), weight was measured using a digital weighing scale with accuracy of 100 gm (Seca), and systolic and diastolic blood pressure was measured using an electronic blood pressure monitor (OMRON 7080). A 5-ml fasting blood sample was collected from participants reporting at least 8 hours of fasting. The sample was centrifuged in the field, and the resulting serum and plasma samples were then transported to a central laboratory in New Delhi at the Indian Council of Medical Research for biochemical analysis and storage. Fasting plasma glucose was assessed using the Enzymatic Colorimetric Assay method. The General Health Questionnaire, previously validated for detecting common mental disorders in the Indian setting [28,29], was translated into the local language. Sociodemographic covariates Sociodemographic and behavioral data were collected through standard survey tools. For more details, please see the DISHA methods paper [26]. Individual age (continuously specified in years), sex (binary), education (years of schooling and college), marital status (married or unmarried), and family religion (Hindu or other) were included in the analysis as correlates of chronic conditions. Statistical analysis The development of the statistical analysis plan is described in S2 Text. We first constructed a set of indicator variables for each participant describing whether any other individual (excluding self) in the household had a given chronic condition. We next estimated 3 sets of logistic regression models that included differing groups of participants defined by the type of relationship among household members. Each set of logistic regression models estimated the relative odds of having any chronic condition for individuals living with a household member with any chronic condition relative to individuals who were not living with a household member with a chronic condition (i.e., the odds ratio of any chronic condition associated with living with someone who has any chronic condition). In addition, we estimated the relative odds of a given chronic condition associated with living with a household member with that same chronic condition (chronic condition concordance; e.g., the odds ratio of diabetes that is associated with living with someone who has diabetes) and living with a household member with a different chronic condition (chronic condition correspondence; e.g., the odds ratio of diabetes that is associated with living with someone who has a common mental disorder). The first set of models included data from all available household members aged 18 years and older and was agnostic to the type of relationship between the index participant and the coresiding household members. To examine whether associations were observed across all study sites, we also estimated a set of models with an interaction term between the exposure condition and the study site. We tested the statistical significance of the interaction term using generalized score tests for Type III contrasts. A second set of models examined associations among adult children with coresiding parents. For this analysis, the exposure was the presence of a given chronic condition in either parent for whom we had data. A third set of models examined associations among spousal dyads. In the spousal analysis, the wife’s chronic condition status was modeled as the outcome, and the husband’s chronic condition status was considered the exposure because it is culturally normative for women to move to their husband’s home after marriage and presumably adopt the household diet and lifestyle practices therein. Missing data for any single outcome ranged from 0.2%–3% for common mental disorder, obesity, and hypertension to 24%–26% for diabetes and high cholesterol. To maintain the same analytic sample for each exposure-outcome model, we were thus forced to exclude 30% of the available participants because of missing data. We applied inverse probability weighting (IPW) to address potential bias arising from the exclusion of participants with missing data. IPW weights each observation by the inverse of the probability of having complete data to create a weighted pseudopopulation that resembles the full sample with respect to observed data [33]. We constructed the missing data IPW weights using a logistic model to predict the probability of having complete covariate data. The IPW model predictors were study site, age, sex, and education. We further accounted for the uneven number of adults in a single household contributing to the analysis using an IPW approach by creating a household weight that was the inverse of the household size. All analyses were weighted by a final weight that was the product of the missing data weight and the household weight and normalized to sum to the number of individuals with complete covariate data (7,522 participants). S1 Table shows missing data by covariate and descriptive analysis of participant characteristics in the total sample, unweighted analytic sample, and weighted analytic sample. Adjusted models included the age, sex, education, marital status, religion, and study site of the index participant whose outcome was being modeled. Supplementary tables include results from unadjusted models. Data from Madhya Pradesh were excluded from the analysis of common mental disorder because less than 0.01% of respondents reported symptoms consistent with the common mental disorder definition. All analyses were model-based and accounted for data correlation arising from sampling multiple individuals in the same household and in the same cluster through generalized estimating equations [34]. Data management and recoding were performed using STATA 13 and 14 (College Station, Texas, United States), and statistical analyses were performed using SAS 9.4 (Cary, North Carolina, US) statistical software. Data source We conducted a cross-sectional observational analysis of the baseline survey and laboratory data from the Diet and Lifestyle Interventions for Hypertension Risk Reduction through Anganwadi Workers and Accredited Social Health Activists study (DISHA study) [26]. DISHA is a community-based cluster randomized trial designed to test the effectiveness of a community health worker-led lifestyle behavior change on hypertension reduction. The baseline study was conducted in 2013 and 2014 to measure risk factors in 4 regionally and socioeconomically diverse districts located in Madhya Pradesh, Gujarat, Tamil Nadu, and Himachal Pradesh that were selected for the initial phase of the intervention. Participants were selected using a multistage cluster sampling design stratified by district. Dhar District, Madhya Pradesh (central India), is home to a predominantly indigenous (Adivasi) population and has poor road connectivity. Junagadh District, Gujarat (western India), is a rural plains setting, while the Mashobra District, Himachal Pradesh (northern India), is a rural hilly setting consisting of sparsely populated villages. Finally, the Puducherry, a union territory bordering Tamil Nadu (southern India), is an urban and coastal setting with relatively better public health infrastructure. The primary sampling units were randomly selected villages within the districts (9–12 villages per site; a total of 45 villages in the study), from which 120–150 households were randomly selected. At the household level, all adults over the age of 18 years were invited to participate in the survey. We exploited this feature of the sampling design to identify adults residing in the same household. Of the 11,751 participants linkable to the household demographic roster, 10,703 participants had at least 1 coresiding household member enrolled in the study. Of participants with coresiding household members, 3,181 were excluded because of missing data on 1 or more outcomes. Thus, a total of 7,522 participants residing in 2,574 households with complete covariates and at least 2 sampled adults per household were analyzed in the primary analysis. We additionally examined associations of interest among adults with coresiding parents (1,660 dyads in 1,199 households) and spouses (1,598 dyads in 1,598 households). Dyads were identified through each participant’s relationship with the household head. The analysis of dyads was restricted to pairs of participants who were unambiguously identifiable as parent-adult child pairs or spouses through the participants’ relationship to the household head. The study obtained ethics approval from the Centre for Chronic Disease Control’s ethics committee (#IRB00006330), as well as ethics committees of participating sites. Participants provided written informed consent prior to being surveyed and assessed. This study is reported as per STROBE guidelines (S1 Text). Chronic conditions We analyzed 5 prevalent chronic conditions: diabetes (prior diagnosis by a physician, fasting plasma glucose ≥ 126 mg/dL, or taking medication [27]), common mental disorder (i.e., depressive and anxiety disorders, measured here using the General Health Questionnaire score ≥ 12 [28,29]), hypertension (prior diagnosis by a physician, blood pressure ≥ 140/90 mmHg, or taking medication [30]), obesity (body mass index ≥ 30 kg/m2 [31]), and high cholesterol (prior diagnosis by a physician, total blood cholesterol ≥ 240 mg/dL, or taking medication [32]). We also created a composite binary variable indicating the presence of at least 1 of the 5 chronic conditions. Data collection took place at the participant’s home. Height was measured using a stadiometer with accuracy of 2 mm (Seca), weight was measured using a digital weighing scale with accuracy of 100 gm (Seca), and systolic and diastolic blood pressure was measured using an electronic blood pressure monitor (OMRON 7080). A 5-ml fasting blood sample was collected from participants reporting at least 8 hours of fasting. The sample was centrifuged in the field, and the resulting serum and plasma samples were then transported to a central laboratory in New Delhi at the Indian Council of Medical Research for biochemical analysis and storage. Fasting plasma glucose was assessed using the Enzymatic Colorimetric Assay method. The General Health Questionnaire, previously validated for detecting common mental disorders in the Indian setting [28,29], was translated into the local language. Sociodemographic covariates Sociodemographic and behavioral data were collected through standard survey tools. For more details, please see the DISHA methods paper [26]. Individual age (continuously specified in years), sex (binary), education (years of schooling and college), marital status (married or unmarried), and family religion (Hindu or other) were included in the analysis as correlates of chronic conditions. Statistical analysis The development of the statistical analysis plan is described in S2 Text. We first constructed a set of indicator variables for each participant describing whether any other individual (excluding self) in the household had a given chronic condition. We next estimated 3 sets of logistic regression models that included differing groups of participants defined by the type of relationship among household members. Each set of logistic regression models estimated the relative odds of having any chronic condition for individuals living with a household member with any chronic condition relative to individuals who were not living with a household member with a chronic condition (i.e., the odds ratio of any chronic condition associated with living with someone who has any chronic condition). In addition, we estimated the relative odds of a given chronic condition associated with living with a household member with that same chronic condition (chronic condition concordance; e.g., the odds ratio of diabetes that is associated with living with someone who has diabetes) and living with a household member with a different chronic condition (chronic condition correspondence; e.g., the odds ratio of diabetes that is associated with living with someone who has a common mental disorder). The first set of models included data from all available household members aged 18 years and older and was agnostic to the type of relationship between the index participant and the coresiding household members. To examine whether associations were observed across all study sites, we also estimated a set of models with an interaction term between the exposure condition and the study site. We tested the statistical significance of the interaction term using generalized score tests for Type III contrasts. A second set of models examined associations among adult children with coresiding parents. For this analysis, the exposure was the presence of a given chronic condition in either parent for whom we had data. A third set of models examined associations among spousal dyads. In the spousal analysis, the wife’s chronic condition status was modeled as the outcome, and the husband’s chronic condition status was considered the exposure because it is culturally normative for women to move to their husband’s home after marriage and presumably adopt the household diet and lifestyle practices therein. Missing data for any single outcome ranged from 0.2%–3% for common mental disorder, obesity, and hypertension to 24%–26% for diabetes and high cholesterol. To maintain the same analytic sample for each exposure-outcome model, we were thus forced to exclude 30% of the available participants because of missing data. We applied inverse probability weighting (IPW) to address potential bias arising from the exclusion of participants with missing data. IPW weights each observation by the inverse of the probability of having complete data to create a weighted pseudopopulation that resembles the full sample with respect to observed data [33]. We constructed the missing data IPW weights using a logistic model to predict the probability of having complete covariate data. The IPW model predictors were study site, age, sex, and education. We further accounted for the uneven number of adults in a single household contributing to the analysis using an IPW approach by creating a household weight that was the inverse of the household size. All analyses were weighted by a final weight that was the product of the missing data weight and the household weight and normalized to sum to the number of individuals with complete covariate data (7,522 participants). S1 Table shows missing data by covariate and descriptive analysis of participant characteristics in the total sample, unweighted analytic sample, and weighted analytic sample. Adjusted models included the age, sex, education, marital status, religion, and study site of the index participant whose outcome was being modeled. Supplementary tables include results from unadjusted models. Data from Madhya Pradesh were excluded from the analysis of common mental disorder because less than 0.01% of respondents reported symptoms consistent with the common mental disorder definition. All analyses were model-based and accounted for data correlation arising from sampling multiple individuals in the same household and in the same cluster through generalized estimating equations [34]. Data management and recoding were performed using STATA 13 and 14 (College Station, Texas, United States), and statistical analyses were performed using SAS 9.4 (Cary, North Carolina, US) statistical software. Results Table 1 shows the household- and individual-level characteristics of the weighted analytic sample. A total of 2,574 households with 7,522 individuals were analyzed. On average, we observed 2.9 individuals per household (range: 2 to 11 individuals). The mean age of participants was 39 years (range: 18 to 96 years), 46% were men, and mean years of schooling of participants was 6 years. The majority of participants were married (78%) and Hindu (94%). While 43% of individuals had at least 1 chronic condition, this proportion varied from 37% in Mashobra to 50% in Gujarat. The least common chronic condition was high cholesterol (6%), and the most common condition was hypertension (23%). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Characteristics of the analytic sample. https://doi.org/10.1371/journal.pmed.1002395.t001 Data are from 7,522 adults in 2,574 households in the DISHA study. Chronic conditions were defined as follows: diabetes, fasting plasma glucose ≥ 126 mg/dL or taking medication; common mental disorder, General Health Questionnaire score ≥ 12; hypertension, blood pressure ≥ 140/90 mmHg or taking medication; obesity, body mass index ≥ 30 kg/m2; and high cholesterol, total blood cholesterol ≥ 240 mg/dL or taking medication. The sums of the weights in the analytic sample by site were 2,026 (Dhar), 2,039 (Junagadh), 1,957 (Pondicherry), and 1,500 (Mashobra). Table 2 summarizes the results from separate adjusted logistic regression models estimating the odds ratio for having a given chronic condition if living with an individual with that same condition (Table 2, diagonal cells) and living with an individual with a different chronic condition (Table 2, off-diagonal cells); see S2 Table for unadjusted associations. Those who resided with another individual with any chronic condition had 29% higher adjusted relative odds of having any chronic condition themselves (adjusted odds ratio [aOR] = 1.29; 95% confidence interval [95% CI] 1.10–1.50). In general, the strongest relationships were observed in the same-condition models; positive associations were observed for diabetes (aOR = 1.60; 95% CI 1.23–2.07), common mental disorder (aOR = 2.69; 95% CI 2.12–3.42), and obesity (aOR = 1.82; 95% CI 1.33–2.50). With respect to differing conditions, the only statistically significant relationship was that between living with someone with hypertension and obesity status (aOR = 1.24; 95% CI 1.02–1.53). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Adjusted association between living with someone with a given chronic condition and having that same or another chronic condition (n = 7,572). https://doi.org/10.1371/journal.pmed.1002395.t002 Fig 1 shows the adjusted association between living with someone with a given chronic condition and having that same chronic condition by study site in the full analytic sample. See S3 Table for point estimates, CIs, and interaction tests in table form. There were no statistically significant differences between sites, and point estimates of the odds ratios indicate positive associations for concordant conditions among coresiding household members at all sites. Point estimates of odds ratios for any chronic condition, depression, and hypertension were very comparable across sites. Although not statistically distinguishable, point estimates of odds ratios for diabetes, high cholesterol, and obesity were more variable than those observed for any chronic condition, depression, or hypertension. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Site-specific adjusted relative odds (95% confidence interval) of having a chronic condition if any other member of the household has that same chronic condition (reference: no other member of the household has that same condition) and test for interaction between sites. Site-specific associations were computed by including an interaction term between the site and the exposure condition. The P values shown are from generalized score tests for Type III contrasts for the site x exposure interaction term. The horizontal line marks the null value. Madhya Pradesh data were excluded from the common mental disorder analysis because of poor performance of the survey tool. Chronic conditions were defined as follows: diabetes (prior diagnosis, fasting plasma glucose ≥ 126 mg/dL, or taking medication); common mental disorder (General Health Questionnaire score ≥ 12); hypertension (prior diagnosis, blood pressure ≥ 140/90 mmHg, or taking medication); obesity (body mass index ≥ 30 kg/m2); and high cholesterol (prior diagnosis, total blood cholesterol ≥ 240 mg/dL, or taking medication). See S3 Table for these data in table form. https://doi.org/10.1371/journal.pmed.1002395.g001 Table 3 shows adjusted associations between the chronic condition status of parents and their adult children (sample restricted to parent-child dyads); see S4 Table for unadjusted associations. Adults coresiding with a parent who had a common mental disorder (aOR = 2.20; 95% CI 1.28–3.77), hypertension (aOR = 1.58; 95% CI 1.15–2.16), obesity (aOR = 4.99; 95% CI 2.71–9.20), or high cholesterol (aOR = 2.57; 95% CI 1.15–5.73) were more likely to have the same respective condition. We found no statistically significant association between parents and their adult children for any chronic condition or diabetes. The only statistically significant relationships between differing chronic conditions were those between parental high cholesterol and adult child diabetes (aOR = 2.02; 95% CI 1.08–3.78) and between parental diabetes and adult child hypertension (aOR = 1.97; 95% CI 1.28–3.02). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Adjusted association between living with a parent with a given chronic condition and having that same or another chronic condition (n = 1,660). https://doi.org/10.1371/journal.pmed.1002395.t003 Table 4 shows adjusted associations between chronic condition status of spousal dyads; see S5 Table for unadjusted associations. A woman had 44% higher adjusted relative odds of having a chronic condition if her husband had a chronic condition (aOR = 1.44; 95% CI 1.14–1.82). Similar to the analyses above, the strongest relationships were seen for the same condition. Concordant diabetes (aOR = 2.28; 95% CI 1.52–3.42) and common mental disorder (aOR = 3.01; 95% CI 2.01–4.52) status in husbands and wives were the only statistically significant associations among spouses. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 4. Adjusted association between living with a spouse with a given chronic condition and having that same or another chronic condition (n = 1,598). https://doi.org/10.1371/journal.pmed.1002395.t004 Discussion To our knowledge, this is the first study examining the relationship of 5 prevalent chronic conditions—hypertension, diabetes, obesity, common mental disorder, and high cholesterol—among coresiding adults in India. Irrespective of familial relationship, adults who resided with another adult with any chronic condition had 29% higher adjusted odds of having 1 or more chronic conditions themselves. For all of the 5 specific conditions examined, we consistently observed that adults tended to have the same chronic condition as a coresiding household member (e.g., living with someone who is obese was associated with 82% higher relative odds of obesity). Among all household members, parent-adult child dyads, and spousal dyads, common mental disorder was twice to thrice as high among individuals residing with someone with a common mental disorder. Other salient findings included the strong concordance of diabetes status among husbands and wives and concordance of obesity status among parents and their adult children. Across different disease phenotypes, we observed weaker and few statistically significant associations among household members. In India, the past 20 years of unprecedented economic growth [35] has coincided with an increase in healthy life expectancy in men and women by 6 and 9 years, respectively [36]. Chronic diseases, however, threaten continued progress in this arena. There is a great need to reorient the existing health system in India to address the rise of chronic conditions [5,37]. The bulk of familial concordance studies have been conducted to understand the genetic influences of parents on young or adolescent children or environmental influences on health among spouses [7]. In India [4] and other LMICs [25] where extended family households are still intact, it may be particularly relevant and effective to engage the full household—irrespective of genetic ties or marital connections—in the prevention and management of chronic conditions. At the most superficial level, family history of chronic disease can be used for risk stratification [38]. Our findings are largely consistent with prior literature examining the relationship of metabolic outcomes among spouses [10–12,39] and between parents and adolescent children [11–13] within nuclear families. Specifically, the concordance of chronic condition status among spouses in our study was remarkably similar to findings published in a systematic review, reporting odds ratios between 1.2 and 1.6 for hypertension, 1.1 to 1.8 for diabetes, and 1.3 to 1.7 for obesity [6]. Additionally, there is robust concordance in these metabolic outcomes as a package (i.e., metabolic syndrome) among spouses [10–12]. Regarding phenotypic similarities between parents and their adult children, our results tended to demonstrate more statistically robust relationships compared with prior studies [11,12], likely due to a larger sample size and our restriction to adult children (versus adolescents and younger children). Previous analyses of chronic disease-related traits—such as continuously measured blood pressure and body mass index (BMI)—have also found that these traits are related in parent-child dyads and cluster within the household [8,9,13,40,41]. Across these previous studies and ours, generally, the correlation of obesity/BMI among family members was stronger than the correlation of hypertension/blood pressure. Comparable to what we found for common mental disorder, a single study examining concordance of multiple diseases among married couples estimated an aOR of 2.1 for depression and also reported that depression was the most concordant condition of the many outcomes examined in the study [39]. Although we did not directly or quantitatively examine contributing pathways in this study, qualitative comparisons of coefficients across models may provide a preliminary understanding for future investigation. First, odds ratios for chronic condition concordance adjusted for sociodemographic information (such as educational level and site) were generally attenuated compared with unadjusted odds ratios; the greatest attenuation after adjustment was observed in the spousal concordance analysis (Table 4 versus S5 Table). To the extent that sociodemographic background proxies living conditions, this suggests that shared living conditions are relevant to determining spousal chronic condition concordance. Second, common mental disorder was the only condition that was highly and statistically significantly concordant in models including all household members, models restricted to dyads of parents and their adult children, and models restricted to dyads of spouses, implying a potential affective contagion that affects members of a household irrespective of familial relationship. Third, concordance in hypertension and high cholesterol were only observed in parent-adult child dyads, implying a potential genetic component for observed household concordance in those conditions. Fourth, household concordance in diabetes was not observed in parent-adult child dyads, and concordance in obesity was not statistically significant among spouses. Additionally, these findings run contrary to prior findings that metabolic syndrome is correlated in parents and their children [11,12] and that weight status is correlated among spouses [7,42]. The results raise the question of whether diabetes has a stronger environmental component and obesity has a stronger genetic component in this setting. Fifth, site-specific associations indicate a general tendency towards mild to moderate concordance of the 5 chronic conditions examined here, but diabetes, high cholesterol, and obesity odds ratios varied more than other conditions. Perhaps these conditions are more impacted by extrahousehold factors. Finally, correspondence across differing phenotypes was weaker than concordance of the same condition—even among spouses—possibly suggesting specificity of mechanisms contributing to each of the disease outcomes under study. Further data are needed to determine the robustness of each of these observations. The DISHA study provided a geographically and socioculturally diverse study population for our secondary data analysis of the relationships between chronic conditions among members of the same household, yielding a strong foundation for generalizing findings across India and possibly other LMICs where extended family households remain common [25]. A strength of this data source was our ability to objectively characterize 5 chronic conditions and subsequently examine associations among coresiding adults in a large sample of Indian households using very recent data. Not only did we report the concordance of the same chronic condition among household members, but we also reported the correspondence between different chronic conditions. Although this approach required making several comparisons, these comparisons addressed our predefined research question regarding potential heightened risk for chronic conditions across differing phenotypes, and thus, we do not adjust for multiple comparisons in the analysis [43]. Moreover, our comprehensive analysis of these relationships among all household members, parent-adult child dyads, and spousal dyads separately provides data on the concordance and correspondence between chronic conditions in genetically related and unrelated adults who share a common living environment. Site-specific analysis assures us that the findings were consistent across the heterogeneous districts. DISHA, however, was designed not to examine family-level associations in outcomes but rather to detect a 2 mmHg mean difference in systolic blood pressure between intervention and control villages. Thus, we had relatively small samples in the dyadic analysis, and we interpret tests of statistical significance and any qualitative differences between the associations observed for spousal versus parent-child dyads with caution. We also lacked sufficient sample size to examine associations in other potential familial relationships of interest (e.g., daughters-in-law and parents-in-law or disaggregated mother-child from father-child). In addition, 25% of the DISHA participants were missing fasting blood samples, which led to a high proportion of missing data. We addressed missing data using inverse probability weighting, which may negatively impact statistical precision. Finally, we were unable to investigate the development of new chronic conditions in household members—which could provide insight into the etiology of household clustering of disease—because of the cross-sectional nature of the analysis. Our results provide preliminary evidence that targeting households in which 1 adult has a chronic condition may be an effective way to identify other individuals with chronic conditions and potentially prevent emerging chronic conditions in India, as has been done among spouses elsewhere [44,45]. Moreover, studying the incidence of chronic disease within household members may provide new insight regarding mechanisms relevant to primordial prevention of chronic disease risk factors. It is thus critical to substantiate these early findings in ongoing prospective cohort studies to better understand the mechanisms through which coresiding household members develop chronic conditions over time. Elucidating such mechanisms can assist with designing novel interventions that cater to the needs of households across the socioeconomic spectrum in both urban and rural settings. The design and subsequent rigorous evaluation of such interventions will contribute to generate the evidence base needed to combat the rise of chronic conditions in India. Supporting information S1 Table. Missing data by covariate and participant characteristics in the total sample, unweighted analytic sample, and weighted analytic sample. https://doi.org/10.1371/journal.pmed.1002395.s001 (DOCX) S2 Table. Unadjusted association between living with someone with a given chronic condition and having that same or another chronic condition. https://doi.org/10.1371/journal.pmed.1002395.s002 (DOCX) S3 Table. Site-specific adjusted relative odds (95% confidence interval) of having a chronic condition if any other member of the household has that same chronic condition (reference: no other member of the household has that same condition) and tests for interaction by study site. https://doi.org/10.1371/journal.pmed.1002395.s003 (DOCX) S4 Table. Unadjusted association between living with a parent with a given chronic condition and having that same or another chronic condition. https://doi.org/10.1371/journal.pmed.1002395.s004 (DOCX) S5 Table. Unadjusted association between living with a spouse with a given chronic condition and having that same or another chronic condition. https://doi.org/10.1371/journal.pmed.1002395.s005 (DOCX) S1 Text. Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement—Checklist of items that should be included in reports of observational studies. https://doi.org/10.1371/journal.pmed.1002395.s006 (DOC) S2 Text. Development of the statistical analysis plan. https://doi.org/10.1371/journal.pmed.1002395.s007 (DOCX)

doi: 10.1371/journal.pmed.1002383pmid: 28898252

Background Glycated hemoglobin (HbA1c) is used to diagnose type 2 diabetes (T2D) and assess glycemic control in patients with diabetes. Previous genome-wide association studies (GWAS) have identified 18 HbA1c-associated genetic variants. These variants proved to be classifiable by their likely biological action as erythrocytic (also associated with erythrocyte traits) or glycemic (associated with other glucose-related traits). In this study, we tested the hypotheses that, in a very large scale GWAS, we would identify more genetic variants associated with HbA1c and that HbA1c variants implicated in erythrocytic biology would affect the diagnostic accuracy of HbA1c. We therefore expanded the number of HbA1c-associated loci and tested the effect of genetic risk-scores comprised of erythrocytic or glycemic variants on incident diabetes prediction and on prevalent diabetes screening performance. Throughout this multiancestry study, we kept a focus on interancestry differences in HbA1c genetics performance that might influence race-ancestry differences in health outcomes. Methods & findings Using genome-wide association meta-analyses in up to 159,940 individuals from 82 cohorts of European, African, East Asian, and South Asian ancestry, we identified 60 common genetic variants associated with HbA1c. We classified variants as implicated in glycemic, erythrocytic, or unclassified biology and tested whether additive genetic scores of erythrocytic variants (GS-E) or glycemic variants (GS-G) were associated with higher T2D incidence in multiethnic longitudinal cohorts (N = 33,241). Nineteen glycemic and 22 erythrocytic variants were associated with HbA1c at genome-wide significance. GS-G was associated with higher T2D risk (incidence OR = 1.05, 95% CI 1.04–1.06, per HbA1c-raising allele, p = 3 × 10−29); whereas GS-E was not (OR = 1.00, 95% CI 0.99–1.01, p = 0.60). In Europeans and Asians, erythrocytic variants in aggregate had only modest effects on the diagnostic accuracy of HbA1c. Yet, in African Americans, the X-linked G6PD G202A variant (T-allele frequency 11%) was associated with an absolute decrease in HbA1c of 0.81%-units (95% CI 0.66–0.96) per allele in hemizygous men, and 0.68%-units (95% CI 0.38–0.97) in homozygous women. The G6PD variant may cause approximately 2% (N = 0.65 million, 95% CI 0.55–0.74) of African American adults with T2D to remain undiagnosed when screened with HbA1c. Limitations include the smaller sample sizes for non-European ancestries and the inability to classify approximately one-third of the variants. Further studies in large multiethnic cohorts with HbA1c, glycemic, and erythrocytic traits are required to better determine the biological action of the unclassified variants. Conclusions As G6PD deficiency can be clinically silent until illness strikes, we recommend investigation of the possible benefits of screening for the G6PD genotype along with using HbA1c to diagnose T2D in populations of African ancestry or groups where G6PD deficiency is common. Screening with direct glucose measurements, or genetically-informed HbA1c diagnostic thresholds in people with G6PD deficiency, may be required to avoid missed or delayed diagnoses. Why was this study done? Blood glucose binds in an irreversible manner to circulating hemoglobin in red blood cells (RBCs), generating “glycated hemoglobin,” called HbA1c. HbA1c is used to diagnose and monitor diabetes. Previous large-scale human genetic studies have demonstrated that HbA1c is influenced by genetic variants. Some variants are thought to influence the function, structure, and lifespan of the red blood itself (“erythrocytic variants”), while others are thought to influence blood glucose control (“glycemic variants”). This study aimed to identify additional variants influencing HbA1c levels, and investigate the extent to which variants affecting this measurement independently of blood glucose concentration may lead to misdiagnosis, mistreatment, and human health disparities. What did the researchers do and find? We studied genetic variants and their association with HbA1c levels in almost 160,000 people from European, African, East Asian, and South Asian ancestry from 82 separate studies worldwide. We found 60 genetic variants influencing HbA1c, of which 42 variants were new. Of the 60 variants, we found 19 glycemic variants and 22 erythrocytic variants. In approximately 33,000 people from 5 ancestry groups followed carefully over time, we found that the more glycemic variants a person had, the higher their risk to get diabetes (OR = 1.05 per HbA1c-raising allele, p = 3 × 10−29). However, more erythrocytic variants did not lead to a higher risk of diabetes, meaning erythrocytic variants that lower HbA1c levels independently from glucose concentration could lead to missed diagnosis of diabetes. Next, we found that in everyone but those of African ancestry, those with more versus those with less of the 60 HbA1c genetic variants had a fairly small difference in HbA1c (about 0.2 units), while those of African ancestry had a larger difference (about 0.8 units, a fairly large number for this medical test). This difference in African ancestry was explained by one erythrocytic variant on the X chromosome. This variant mutates the protein made by the gene “glucose-6-phosphate dehydrogenase” (G6PD), which can shorten RBC lifespan, and thus lower HbA1c levels, no matter the blood glucose level. About 11% of people of African American ancestry carry at least one copy of this G6PD variant, while almost no one of any other ancestry does. We estimated that if we tested all Americans for diabetes using HbA1c, about 650,000 African Americans would be missed because of these genetically lowered HbA1c levels. What do these findings mean? We may want to investigate the benefits of screening for the G6PD genotype in specific communities or perform additional diagnostic tests to avoid health disparities between communities. It will also be important to follow up with additional studies to check whether new standardized thresholds for diagnoses should be recommended for those that have this G6PD variant. Introduction Type 2 diabetes (T2D) is a health scourge rising unabated worldwide, escaping all past and current control measures, in part because only half of prevalent T2D worldwide has been clinically diagnosed [1]. Glycated hemoglobin (HbA1c) is an accepted diagnostic test for T2D and a principal clinical measure of glycemic control in individuals with diabetes. T2D arises from the environment interacting with genetics. Studies investigating genetic contributions to HbA1c in individuals of European [2–4] and Asian ancestry [5–7] have identified 18 loci influencing HbA1c through glycemic and nonglycemic pathways, the latter primarily reflecting erythrocytic biology. Alterations in HbA1c that are due to genetic variation acting through nonglycemic pathways may not accurately reflect ambient glycemia or T2D risk and could affect the validity of HbA1c as a diagnostic test and measure of glycemic control in some individuals or populations. Some genetic variants (e.g., the sickle cell variant HbS) that vary in frequency across ancestries can interfere with the accuracy of certain assays [8]. Further, certain hematologic conditions associated with shortened erythrocyte lifespan (e.g., hemolytic anemias) lower HbA1c values irrespective of the assay performed. HbA1c values in such patients may no longer accurately reflect ambient glycemia [9]. Epidemiologic studies have reported ethnic differences in HbA1c, with African Americans having, on average, higher HbA1c than European ancestry Americans [10]. While these differences are largely due to demographic and metabolic factors [11,12], genetic factors associated with hematologic conditions that impact erythrocyte turnover may confound the relationship between HbA1c and glycemia, causing misclassification of T2D diagnosis [8,13]. This study had 3 aims, the first was to expand genetic discovery efforts to larger sample sizes, including populations of ancestries not previously studied, to uncover novel loci influencing HbA1c and that might capture a greater fraction of the variability in HbA1c. Second, as done in previous studies, we aimed to classify the variants as acting through glycemic or erythrocytic biology. Thirdly, as erythrocytic variants may influence HbA1c due to effects on the red blood cell (RBC), we wished to explore whether this might lead to HbA1c values that no longer reflected ambient glycemia. To do this, we specifically tested the hypothesis that HbA1c-associated genetic variants, particularly those that act through erythrocytic pathways, influence the performance of HbA1c for diabetes risk prediction and diabetes diagnoses (S1 Fig). Methods Analysis plans were followed and can be found in S1 Analysis Plans. Genetic discovery study participants In the genetic discovery analysis, we combined data from up to 159,940 participants (maximum number available for any variant) of European, African American, East Asian, and South Asian ancestry, including subsets from previous publications [4,5] (S1 Table, S2 Fig). All participants were free of diabetes defined by physician diagnosis, medication use, or fasting glucose (FG) ≥ 7 mmol/L. A small number of cohorts also removed individuals with 2hr glucose (2hrGlu) ≥ 11.1 mmol/L, or HbA1c ≥ 6.5%, where FG was not available (details of exclusions by individual cohorts, S1 Table). Analysis followed the details in S1 Analysis Plans (Hemoglobin A1c Genetic Discovery Analysis Plan). HbA1c measurement Where possible, studies reported HbA1c as a National Glycohemoglobin Standardization Program (NGSP) percent [14] (S1 Table). Genotyping and quality control Each cohort was genotyped on commercially available genome-wide arrays (for instance, the Affymetrix Genome-Wide Human SNP Assay 6.0 or the Illumina Human610-Quad BeadChip) or the Illumina CardioMetabochip (Metabochip) [15]. Variant and sample quality control (QC) was conducted within each cohort following a shared analysis plan (S1 Analysis Plans). Cohorts were advised to keep SNPs with hardy-weinberg-disequilibrium p-value ≥ 1 × 10−6, SNP genotyping call rate ≥ 95% and minor allele frequency (MAF) ≥ 1% (full details of SNP and sample QC can be found in S1 Table). Following QC, studies with genome-wide array data were imputed (primarily using the Phase 2 of the International HapMap Project reference panel [16], see S1 Table, row 40), and poorly imputed variants (variants which could not reliably be inferred from surrounding variants) were excluded based on standard imputation quality thresholds (R-sq < 0.3, INFO < 0.4). Approximately 2.5 million SNPs were available for analysis after imputation and QC (S1 Table). QC of the Metabochip data is described elsewhere, but included filtering out poorly genotyped individuals or low-quality SNPs [17]. Variant association testing in men and women combined was conducted under an additive model adjusting for study-specific covariates and was limited to variants with MAF of at least 1% in each cohort. Details of the study cohorts, genotyping platforms and QC criteria, imputation reference panel, covariates in the analysis, and software used are provided for each study in S1 Table. Our study followed STREGA guidelines (S1 Checklist). Genetic discovery using ancestry-specific and trans-ancestry meta-analyses Association data were combined within each ancestry group using a fixed-effects meta-analysis in METAL, which assumes the SNP effect is the same for each study within an ancestry [18]. Results for each cohort were corrected for any systematic biases, such as residual population structure using the genomic control inflation factor, λGC [17,19]. We excluded variants from further follow-up if they had an ancestry-specific sample size N < 20,000 in Europeans, N < 3,000 in African Americans, N < 7,000 in East Asians, and N < 3,000 in South Asians (minimum number of samples, where the threshold was chosen to minimize signals driven by a single cohort), or evidence of significant within-ancestry heterogeneity, suggesting effect size significantly differs between cohorts of the same ancestry (Cochran’s Q-test heterogeneity p-value < 0.0001). We retained the lead variant in the X-chromosome analysis of the African American ancestry data (rs1050828, G202A in G6PD) despite significant heterogeneity, as it was a strong biological candidate. Ancestry-specific meta-analysis results were conservatively corrected for a second round of genomic control by ancestry: European (λGC = 1.072); African American (λGC = 1.020); East Asian (λGC = 1.027); South Asian (λGC = 1.004); and combined using the Meta-Analysis of Transethnic Association (MANTRA) software that accounts for allelic heterogeneity across ancestry groups [20]. Identification of primary and secondary distinct HbA1c-associated signals Variants were considered to be significantly associated with HbA1c when they met standard genome-wide significant thresholds (based on p = 0.05 divided by the estimated number of independent tests across the genome), of p < 5 × 10−8 in the European and Asian, or p < 2.5 × 10−8 in African American [21] ancestry-specific meta-analyses, or a log10 Bayes Factor ≥6 in the transancestry meta-analysis. All significant variants within 500 kb of a lead (most significantly associated) variant were grouped into a single locus. Novel loci were by definition >500 kb from previously reported HbA1c-associated variants. We ran approximate conditional analyses using the Genome-wide Complex Trait Analysis (GCTA) software [22,23] (following analysis plans detailed in S1 Analysis Plans, Conditional analyses in GCTA) using the Women’s Genome Health Study (WGHS, Europeans), Jackson Heart Study (JHS, African Americans), Singapore Malay Eye Study (SiMES, East Asians), and the London Life Sciences Prospective Population Study (LOLIPOP, South Asians) as reference populations for linkage disequilibrium (LD) estimates, to confirm the lead variants on the autosomes (within 1 Mb) were distinct, and similarly used exact conditional regression for the African-American signals on the X-chromosome in JHS. To identify distinct signals at associated loci (that is, secondary signals), we performed approximate conditional analyses using GCTA, conditioning on lead variants identified in the transancestry MANTRA analysis. Where the lead variant was absent in a cohort, an exact proxy (r2 = 1) was used, unless the variant was very low frequency or monomorphic. Classification of variants as glycemic or erythrocytic We extracted summary association statistics from publicly available meta-analysis results for glycemic [17,24–26] and blood-cell [27] traits and asked a subset of the genome-wide discovery cohorts to repeat association analyses for each lead variant, conditioning on any one of FG, 2hrGlu, hemoglobin level (Hb), mean corpuscular volume (MCV), or mean corpuscular hemoglobin (MCH), where available (S3 Fig, S2 Table and S3 Table). Variants were classified as “glycemic” if they were associated (p < 0.0001) with any of the glycemic traits from publicly available results or had ≥25% attenuation of variant HbA1c effect size in association models conditioned on fasting or 2hrGlu. That is, evidence of being associated with any of the glycemic traits or a reduction in the effect of the variant on HbA1c after repeated association analysis in a model additionally adjusting for fasting/2hrGlu, suggested the observed association with HbA1c was being driven through an association with fasting/2hrGlu. Variants not classified as glycemic were classified as “erythrocytic” if they were associated (p < 0.0001) with Hb, MCH, MCV, PCV, RBC, or MCHC in the publicly available results or, as above, had ≥25% attenuation of effect size in Hb-, MCV-, or MCH-conditioned models (suggesting the observed association with HbA1c was being driven through an association with these blood cell traits). The 25% attenuation threshold was chosen as the optimal balance between specificity and sensitivity based on comparisons with the classification based only on association with any of the glycemic/erythrocytic traits. Two SNPs were classified based on evidence from the literature, rs12132919 (TMEM79) was classified as erythrocytic based on association with MCHC in Japanese individuals [28] and rs7616006 (SYN2) was classified as erythrocytic based on association with platelet count in Europeans [29]. Variants associated with HbA1c but not glycemic or erythrocytic traits remained “unclassified” (S3 Fig). A single variant (rs579459 near ABO) was classified as both glycemic and erythrocytic, but as we were primarily concerned about variants that might affect HbA1c without reflecting ambient glycemia and this variant also affected glycemia, we treated it as glycemic in all analyses. Effect of HbA1c genetic scores on reclassification of prevalent undiagnosed T2D for population screening using HbA1c Analyses on the reclassification of prevalent T2D around the HbA1c 6.5% threshold before and after accounting for the contribution of erythrocytic variants were conducted in up to 19,380 individuals and incident T2D prediction analyses in up to 33,241 individuals from European, African, and East Asian ancestry cohorts (derived in part from discovery cohorts; in S4 Table, and following the details in the S1 Analysis Plans, Net-reclassification analysis). We acknowledge that nonindependent GWAS discovery and application cohorts can lead to inflated effect estimates [30]; however, this was not evident in our study, and effect estimates across all cohorts were similar with low heterogeneity. We estimated reclassification of prevalent T2D status by HbA1c after accounting for the contribution of erythrocytic loci in 5 population-based cohorts with 3 ancestries partially overlapping with the discovery GWAS: the Framingham Heart Study (FHS), the Atherosclerosis Risk in Communities Study (ARIC), and the Multiethnic Study of Atherosclerosis (MESA) in individuals of European ancestry; ARIC and MESA in African Americans; and MESA, the Taiwan-Metabochip Study for Cardiovascular Disease (TAICHI), and the Singapore Prospective Study (SP2) in East Asians (N = 19,380). Variant-adjusted HbA1c was calculated as: where Yi was the measured HbA1c for individual, i, is the ancestry-specific, meta-analytic β coefficient for the kth erythrocytic SNP, gki is the dosage (estimated number of HbA1c-raising alleles), and E(gki) was two times the HbA1c-raising allele frequency. When the less frequent (minor) allele was associated with higher HbA1c, it was coded as the HbA1c-raising allele, when it was associated with lower HbA1c, the more frequent (major) allele was coded as the HbA1c-raising allele. As some HbA1c-raising alleles in one ancestry could be HbA1c-lowering in a different ancestry, we coded HbA1c-raising alleles by ancestry. Participants on antidiabetic therapy were excluded, and screen-detected T2D was defined as FG ≥ 7 mmol/L. For the reclassification analysis, we constructed 2-by-2 tables showing the proportion of participants reclassified around the HbA1c 6.5% diagnostic threshold, with and without adjusting measured HbA1c for the contribution of erythrocytic loci. Calculation of genetic risk scores. Genetic risk scores of erythrocytic variants and glycemic variants (GS-E and GS-G, respectively) were calculated as detailed in S1 Analysis Plans (Investigate the Effect of Glycemic and Erythrocytic Hemoglobin A1c (HbA1c) Genetic Variants on Diabetes Prediction), as standard in the field, by summing the number of ancestry-specific HbA1c-raising alleles at each variant (0, 1, 2, or expected number of alleles based on the probability of each genotype), multiplied by their ancestry-specific β coefficients for HbA1c from the genome-wide association study (GWAS) meta-analysis multiplied by the number of variants and divided by the sum of β coefficients [31]. This means the contribution of each associated variant to the trait, in a given individual, is influenced by the number of “risk alleles” (or in this case HbA1c-raising alleles) and the effect of the variant on the trait (increase in HbA1c estimated from the meta-analysis). Effect of HbA1c genetic scores on prediction of incident T2D We tested the hypothesis that glycemic and erythrocytic HbA1c loci predicted incident T2D differently in Europeans, East Asians, and African Americans from 5 cohorts (partially overlapping with the discovery GWAS) with prospective follow-up: FHS, the European Prospective Investigation into Cancer and Nutrition InterAct project (EPIC-InterAct), ARIC, MESA, and the Singapore Chinese Health Study (SCHS) (N = 33,241). Using age- and sex-adjusted regression models, we tested the association between the genetic scores GS-E or GS-G and incident T2D, defined by FG ≥ 7 mmol/L, 2hrGlu ≥ 11.1 mmol/L, antidiabetic medication use, or a physician diagnosis for T2D, accrued over a 10-to-15-year follow-up period. Clinical practice guidelines did not include HbA1c as a diagnostic test until 2010. As the majority of incident T2D cases were accrued before 2010, participants are very unlikely to have received a T2D diagnosis based only on HbA1c measurements. To test whether individuals with higher GS-E, compared to those with lower GS-E, had lower T2D risk for the same HbA1c, we adjusted models for baseline HbA1c. We meta-analyzed results using a fixed-effects meta-analysis and assessed heterogeneity using Higgin's I-squared. See S1 Analysis Plans (Investigate the Effect of Glycemic and Erythrocytic Hemoglobin A1c (HbA1c) Genetic Variants on Diabetes Prediction) for analysis plan. Ancestral differences in the genetic architecture of HbA1c In FHS, ARIC, MESA, and SCHS, we calculated the difference in HbA1c of individuals at the bottom and top 5% of the distribution of an ancestry-specific GS composed of all 60 variants (GS-Total) and an equivalent analysis using GS-E. We also pursued additional analyses at chromosome X rs1050828 because this single variant showed the largest effect on HbA1c in African Americans and was monomorphic in the other ancestries. The T allele is known to be associated with glucose-6-phosphate dehydrogenase (G6PD) deficiency, an enzymatic defect causing hemolytic anemia [32,33]. Imperfect correlation between HbA1c and glycemia may indicate the impact of reduced erythrocyte lifespan on HbA1c in individuals with the T allele. Fructosamine, a measure of serum protein glycation not influenced by erythrocyte-related factors, reflects average glycemia over the previous 2–3 weeks. Following the analysis plan detailed in S1 Analysis Plans (The Difference Between Fructosamine-inferred HbA1c and Measured HbA1c) we thus calculated the estimated residuals from a linear regression of HbA1c on fructosamine in ARIC African Americans (N = 1,676) to determine whether the T allele was associated with lower HbA1c than predicted by fructosamine, suggesting that the T allele artificially lowered HbA1c through a reduction in the average erythrocytic lifespan. We then reported the mean estimated residuals by genotype (women: CC, CT, TT; men: C, T). Estimated number of African Americans with T2D in the United States whose diagnosis would be missed due to the G6PD variant if screened with HbA1c. Using publicly-available data from the National Health and Nutrition Examination Survey (NHANES) 2013–2014 [34], a nationally representative sample of US residents, we calculated the proportion of African American adults (aged ≥ 18 years) with T2D who would be missed by not accounting for rs1050828 when using a single HbA1c diagnostic threshold of 6.5%, assuming the observed effect size of rs1050828, allele frequency of 11% and accounting for NHANES sampling design. The study sample was restricted to 1,133 adults, aged ≥ 18 years, who self-identified as non-Hispanic black with measured HbA1c in 2013–2014. We defined known T2D by self-reported physician diagnosis or medication use. Assuming Hardy-Weinberg Equilibrium and a T allele frequency of 11% for the G6PD variant in our sample, we lowered the diagnostic threshold from the widely accepted 6.5%-units cut-point to 5.7%-units in men with the T genotype, 5.8%-units in women with the TT genotype, and 6.2%-units in women with the CT genotype. We then calculated the proportion of African American individuals with missed T2D diagnosis if screened with HbA1c using the 6.5% diagnostic threshold. We applied procedures to account for sampling probabilities and complex sampling design to enable population-level inferences. Data analysis was performed using SAS (version 9.2 or 9.3; SAS Institute, Cary, NC). Genetic discovery study participants In the genetic discovery analysis, we combined data from up to 159,940 participants (maximum number available for any variant) of European, African American, East Asian, and South Asian ancestry, including subsets from previous publications [4,5] (S1 Table, S2 Fig). All participants were free of diabetes defined by physician diagnosis, medication use, or fasting glucose (FG) ≥ 7 mmol/L. A small number of cohorts also removed individuals with 2hr glucose (2hrGlu) ≥ 11.1 mmol/L, or HbA1c ≥ 6.5%, where FG was not available (details of exclusions by individual cohorts, S1 Table). Analysis followed the details in S1 Analysis Plans (Hemoglobin A1c Genetic Discovery Analysis Plan). HbA1c measurement Where possible, studies reported HbA1c as a National Glycohemoglobin Standardization Program (NGSP) percent [14] (S1 Table). Genotyping and quality control Each cohort was genotyped on commercially available genome-wide arrays (for instance, the Affymetrix Genome-Wide Human SNP Assay 6.0 or the Illumina Human610-Quad BeadChip) or the Illumina CardioMetabochip (Metabochip) [15]. Variant and sample quality control (QC) was conducted within each cohort following a shared analysis plan (S1 Analysis Plans). Cohorts were advised to keep SNPs with hardy-weinberg-disequilibrium p-value ≥ 1 × 10−6, SNP genotyping call rate ≥ 95% and minor allele frequency (MAF) ≥ 1% (full details of SNP and sample QC can be found in S1 Table). Following QC, studies with genome-wide array data were imputed (primarily using the Phase 2 of the International HapMap Project reference panel [16], see S1 Table, row 40), and poorly imputed variants (variants which could not reliably be inferred from surrounding variants) were excluded based on standard imputation quality thresholds (R-sq < 0.3, INFO < 0.4). Approximately 2.5 million SNPs were available for analysis after imputation and QC (S1 Table). QC of the Metabochip data is described elsewhere, but included filtering out poorly genotyped individuals or low-quality SNPs [17]. Variant association testing in men and women combined was conducted under an additive model adjusting for study-specific covariates and was limited to variants with MAF of at least 1% in each cohort. Details of the study cohorts, genotyping platforms and QC criteria, imputation reference panel, covariates in the analysis, and software used are provided for each study in S1 Table. Our study followed STREGA guidelines (S1 Checklist). Genetic discovery using ancestry-specific and trans-ancestry meta-analyses Association data were combined within each ancestry group using a fixed-effects meta-analysis in METAL, which assumes the SNP effect is the same for each study within an ancestry [18]. Results for each cohort were corrected for any systematic biases, such as residual population structure using the genomic control inflation factor, λGC [17,19]. We excluded variants from further follow-up if they had an ancestry-specific sample size N < 20,000 in Europeans, N < 3,000 in African Americans, N < 7,000 in East Asians, and N < 3,000 in South Asians (minimum number of samples, where the threshold was chosen to minimize signals driven by a single cohort), or evidence of significant within-ancestry heterogeneity, suggesting effect size significantly differs between cohorts of the same ancestry (Cochran’s Q-test heterogeneity p-value < 0.0001). We retained the lead variant in the X-chromosome analysis of the African American ancestry data (rs1050828, G202A in G6PD) despite significant heterogeneity, as it was a strong biological candidate. Ancestry-specific meta-analysis results were conservatively corrected for a second round of genomic control by ancestry: European (λGC = 1.072); African American (λGC = 1.020); East Asian (λGC = 1.027); South Asian (λGC = 1.004); and combined using the Meta-Analysis of Transethnic Association (MANTRA) software that accounts for allelic heterogeneity across ancestry groups [20]. Identification of primary and secondary distinct HbA1c-associated signals Variants were considered to be significantly associated with HbA1c when they met standard genome-wide significant thresholds (based on p = 0.05 divided by the estimated number of independent tests across the genome), of p < 5 × 10−8 in the European and Asian, or p < 2.5 × 10−8 in African American [21] ancestry-specific meta-analyses, or a log10 Bayes Factor ≥6 in the transancestry meta-analysis. All significant variants within 500 kb of a lead (most significantly associated) variant were grouped into a single locus. Novel loci were by definition >500 kb from previously reported HbA1c-associated variants. We ran approximate conditional analyses using the Genome-wide Complex Trait Analysis (GCTA) software [22,23] (following analysis plans detailed in S1 Analysis Plans, Conditional analyses in GCTA) using the Women’s Genome Health Study (WGHS, Europeans), Jackson Heart Study (JHS, African Americans), Singapore Malay Eye Study (SiMES, East Asians), and the London Life Sciences Prospective Population Study (LOLIPOP, South Asians) as reference populations for linkage disequilibrium (LD) estimates, to confirm the lead variants on the autosomes (within 1 Mb) were distinct, and similarly used exact conditional regression for the African-American signals on the X-chromosome in JHS. To identify distinct signals at associated loci (that is, secondary signals), we performed approximate conditional analyses using GCTA, conditioning on lead variants identified in the transancestry MANTRA analysis. Where the lead variant was absent in a cohort, an exact proxy (r2 = 1) was used, unless the variant was very low frequency or monomorphic. Classification of variants as glycemic or erythrocytic We extracted summary association statistics from publicly available meta-analysis results for glycemic [17,24–26] and blood-cell [27] traits and asked a subset of the genome-wide discovery cohorts to repeat association analyses for each lead variant, conditioning on any one of FG, 2hrGlu, hemoglobin level (Hb), mean corpuscular volume (MCV), or mean corpuscular hemoglobin (MCH), where available (S3 Fig, S2 Table and S3 Table). Variants were classified as “glycemic” if they were associated (p < 0.0001) with any of the glycemic traits from publicly available results or had ≥25% attenuation of variant HbA1c effect size in association models conditioned on fasting or 2hrGlu. That is, evidence of being associated with any of the glycemic traits or a reduction in the effect of the variant on HbA1c after repeated association analysis in a model additionally adjusting for fasting/2hrGlu, suggested the observed association with HbA1c was being driven through an association with fasting/2hrGlu. Variants not classified as glycemic were classified as “erythrocytic” if they were associated (p < 0.0001) with Hb, MCH, MCV, PCV, RBC, or MCHC in the publicly available results or, as above, had ≥25% attenuation of effect size in Hb-, MCV-, or MCH-conditioned models (suggesting the observed association with HbA1c was being driven through an association with these blood cell traits). The 25% attenuation threshold was chosen as the optimal balance between specificity and sensitivity based on comparisons with the classification based only on association with any of the glycemic/erythrocytic traits. Two SNPs were classified based on evidence from the literature, rs12132919 (TMEM79) was classified as erythrocytic based on association with MCHC in Japanese individuals [28] and rs7616006 (SYN2) was classified as erythrocytic based on association with platelet count in Europeans [29]. Variants associated with HbA1c but not glycemic or erythrocytic traits remained “unclassified” (S3 Fig). A single variant (rs579459 near ABO) was classified as both glycemic and erythrocytic, but as we were primarily concerned about variants that might affect HbA1c without reflecting ambient glycemia and this variant also affected glycemia, we treated it as glycemic in all analyses. Effect of HbA1c genetic scores on reclassification of prevalent undiagnosed T2D for population screening using HbA1c Analyses on the reclassification of prevalent T2D around the HbA1c 6.5% threshold before and after accounting for the contribution of erythrocytic variants were conducted in up to 19,380 individuals and incident T2D prediction analyses in up to 33,241 individuals from European, African, and East Asian ancestry cohorts (derived in part from discovery cohorts; in S4 Table, and following the details in the S1 Analysis Plans, Net-reclassification analysis). We acknowledge that nonindependent GWAS discovery and application cohorts can lead to inflated effect estimates [30]; however, this was not evident in our study, and effect estimates across all cohorts were similar with low heterogeneity. We estimated reclassification of prevalent T2D status by HbA1c after accounting for the contribution of erythrocytic loci in 5 population-based cohorts with 3 ancestries partially overlapping with the discovery GWAS: the Framingham Heart Study (FHS), the Atherosclerosis Risk in Communities Study (ARIC), and the Multiethnic Study of Atherosclerosis (MESA) in individuals of European ancestry; ARIC and MESA in African Americans; and MESA, the Taiwan-Metabochip Study for Cardiovascular Disease (TAICHI), and the Singapore Prospective Study (SP2) in East Asians (N = 19,380). Variant-adjusted HbA1c was calculated as: where Yi was the measured HbA1c for individual, i, is the ancestry-specific, meta-analytic β coefficient for the kth erythrocytic SNP, gki is the dosage (estimated number of HbA1c-raising alleles), and E(gki) was two times the HbA1c-raising allele frequency. When the less frequent (minor) allele was associated with higher HbA1c, it was coded as the HbA1c-raising allele, when it was associated with lower HbA1c, the more frequent (major) allele was coded as the HbA1c-raising allele. As some HbA1c-raising alleles in one ancestry could be HbA1c-lowering in a different ancestry, we coded HbA1c-raising alleles by ancestry. Participants on antidiabetic therapy were excluded, and screen-detected T2D was defined as FG ≥ 7 mmol/L. For the reclassification analysis, we constructed 2-by-2 tables showing the proportion of participants reclassified around the HbA1c 6.5% diagnostic threshold, with and without adjusting measured HbA1c for the contribution of erythrocytic loci. Calculation of genetic risk scores. Genetic risk scores of erythrocytic variants and glycemic variants (GS-E and GS-G, respectively) were calculated as detailed in S1 Analysis Plans (Investigate the Effect of Glycemic and Erythrocytic Hemoglobin A1c (HbA1c) Genetic Variants on Diabetes Prediction), as standard in the field, by summing the number of ancestry-specific HbA1c-raising alleles at each variant (0, 1, 2, or expected number of alleles based on the probability of each genotype), multiplied by their ancestry-specific β coefficients for HbA1c from the genome-wide association study (GWAS) meta-analysis multiplied by the number of variants and divided by the sum of β coefficients [31]. This means the contribution of each associated variant to the trait, in a given individual, is influenced by the number of “risk alleles” (or in this case HbA1c-raising alleles) and the effect of the variant on the trait (increase in HbA1c estimated from the meta-analysis). Calculation of genetic risk scores. Genetic risk scores of erythrocytic variants and glycemic variants (GS-E and GS-G, respectively) were calculated as detailed in S1 Analysis Plans (Investigate the Effect of Glycemic and Erythrocytic Hemoglobin A1c (HbA1c) Genetic Variants on Diabetes Prediction), as standard in the field, by summing the number of ancestry-specific HbA1c-raising alleles at each variant (0, 1, 2, or expected number of alleles based on the probability of each genotype), multiplied by their ancestry-specific β coefficients for HbA1c from the genome-wide association study (GWAS) meta-analysis multiplied by the number of variants and divided by the sum of β coefficients [31]. This means the contribution of each associated variant to the trait, in a given individual, is influenced by the number of “risk alleles” (or in this case HbA1c-raising alleles) and the effect of the variant on the trait (increase in HbA1c estimated from the meta-analysis). Effect of HbA1c genetic scores on prediction of incident T2D We tested the hypothesis that glycemic and erythrocytic HbA1c loci predicted incident T2D differently in Europeans, East Asians, and African Americans from 5 cohorts (partially overlapping with the discovery GWAS) with prospective follow-up: FHS, the European Prospective Investigation into Cancer and Nutrition InterAct project (EPIC-InterAct), ARIC, MESA, and the Singapore Chinese Health Study (SCHS) (N = 33,241). Using age- and sex-adjusted regression models, we tested the association between the genetic scores GS-E or GS-G and incident T2D, defined by FG ≥ 7 mmol/L, 2hrGlu ≥ 11.1 mmol/L, antidiabetic medication use, or a physician diagnosis for T2D, accrued over a 10-to-15-year follow-up period. Clinical practice guidelines did not include HbA1c as a diagnostic test until 2010. As the majority of incident T2D cases were accrued before 2010, participants are very unlikely to have received a T2D diagnosis based only on HbA1c measurements. To test whether individuals with higher GS-E, compared to those with lower GS-E, had lower T2D risk for the same HbA1c, we adjusted models for baseline HbA1c. We meta-analyzed results using a fixed-effects meta-analysis and assessed heterogeneity using Higgin's I-squared. See S1 Analysis Plans (Investigate the Effect of Glycemic and Erythrocytic Hemoglobin A1c (HbA1c) Genetic Variants on Diabetes Prediction) for analysis plan. Ancestral differences in the genetic architecture of HbA1c In FHS, ARIC, MESA, and SCHS, we calculated the difference in HbA1c of individuals at the bottom and top 5% of the distribution of an ancestry-specific GS composed of all 60 variants (GS-Total) and an equivalent analysis using GS-E. We also pursued additional analyses at chromosome X rs1050828 because this single variant showed the largest effect on HbA1c in African Americans and was monomorphic in the other ancestries. The T allele is known to be associated with glucose-6-phosphate dehydrogenase (G6PD) deficiency, an enzymatic defect causing hemolytic anemia [32,33]. Imperfect correlation between HbA1c and glycemia may indicate the impact of reduced erythrocyte lifespan on HbA1c in individuals with the T allele. Fructosamine, a measure of serum protein glycation not influenced by erythrocyte-related factors, reflects average glycemia over the previous 2–3 weeks. Following the analysis plan detailed in S1 Analysis Plans (The Difference Between Fructosamine-inferred HbA1c and Measured HbA1c) we thus calculated the estimated residuals from a linear regression of HbA1c on fructosamine in ARIC African Americans (N = 1,676) to determine whether the T allele was associated with lower HbA1c than predicted by fructosamine, suggesting that the T allele artificially lowered HbA1c through a reduction in the average erythrocytic lifespan. We then reported the mean estimated residuals by genotype (women: CC, CT, TT; men: C, T). Estimated number of African Americans with T2D in the United States whose diagnosis would be missed due to the G6PD variant if screened with HbA1c. Using publicly-available data from the National Health and Nutrition Examination Survey (NHANES) 2013–2014 [34], a nationally representative sample of US residents, we calculated the proportion of African American adults (aged ≥ 18 years) with T2D who would be missed by not accounting for rs1050828 when using a single HbA1c diagnostic threshold of 6.5%, assuming the observed effect size of rs1050828, allele frequency of 11% and accounting for NHANES sampling design. The study sample was restricted to 1,133 adults, aged ≥ 18 years, who self-identified as non-Hispanic black with measured HbA1c in 2013–2014. We defined known T2D by self-reported physician diagnosis or medication use. Assuming Hardy-Weinberg Equilibrium and a T allele frequency of 11% for the G6PD variant in our sample, we lowered the diagnostic threshold from the widely accepted 6.5%-units cut-point to 5.7%-units in men with the T genotype, 5.8%-units in women with the TT genotype, and 6.2%-units in women with the CT genotype. We then calculated the proportion of African American individuals with missed T2D diagnosis if screened with HbA1c using the 6.5% diagnostic threshold. We applied procedures to account for sampling probabilities and complex sampling design to enable population-level inferences. Data analysis was performed using SAS (version 9.2 or 9.3; SAS Institute, Cary, NC). Estimated number of African Americans with T2D in the United States whose diagnosis would be missed due to the G6PD variant if screened with HbA1c. Using publicly-available data from the National Health and Nutrition Examination Survey (NHANES) 2013–2014 [34], a nationally representative sample of US residents, we calculated the proportion of African American adults (aged ≥ 18 years) with T2D who would be missed by not accounting for rs1050828 when using a single HbA1c diagnostic threshold of 6.5%, assuming the observed effect size of rs1050828, allele frequency of 11% and accounting for NHANES sampling design. The study sample was restricted to 1,133 adults, aged ≥ 18 years, who self-identified as non-Hispanic black with measured HbA1c in 2013–2014. We defined known T2D by self-reported physician diagnosis or medication use. Assuming Hardy-Weinberg Equilibrium and a T allele frequency of 11% for the G6PD variant in our sample, we lowered the diagnostic threshold from the widely accepted 6.5%-units cut-point to 5.7%-units in men with the T genotype, 5.8%-units in women with the TT genotype, and 6.2%-units in women with the CT genotype. We then calculated the proportion of African American individuals with missed T2D diagnosis if screened with HbA1c using the 6.5% diagnostic threshold. We applied procedures to account for sampling probabilities and complex sampling design to enable population-level inferences. Data analysis was performed using SAS (version 9.2 or 9.3; SAS Institute, Cary, NC). Results HbA1c-associated genetic variants and classification into glycemic and nonglycemic pathways To discover new genetic loci influencing HbA1c in populations from 4 different ancestries (European, African American, East Asian, and South Asian), we performed within-ancestry fixed-effects genome-wide association meta-analyses and transancestry meta-analyses using a model that allowed for different effects between ancestry groups (Methods, S2 Fig). Using this approach in up to 159,940 participants without diabetes, we identified 60 variants associated with HbA1c at genome-wide significance (Fig 1, Table 1 and S5 Table). Of 60, 18 have been previously reported, and 42 were novel, including distinct secondary signals at 5 known loci. To classify the associated loci into groups reflecting their likely mode of action on HbA1c, we repeated association analyses conditioning on erythrocytic or glycemic traits and performed lookups in publicly-available association results summary statistics for additional glycemic and erythrocytic traits (Methods, S3 Fig, S2 Table and S3 Table). Based on the combined results from conditional and lookup results, we were able to classify 22 variants as erythrocytic and 19 as glycemic, with 19 remaining unclassified (Fig 1, Table 1 and S5 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Manhattan plot of HbA1c associated variants. Manhattan plot of the transethnic meta-analysis results in MANTRA. The dashed grey line indicates log10BF = 6. Grey and green points denote known/novel loci, respectively. The lead HbA1c-associated variants identified through the ancestry-specific/transethnic analyses are circled in purple (the G6PD variant was not included in the MANTRA analysis, but the locus on the X-chromosome is indicated in the figure). Lines joining the plot & SNP number denote known loci (black), novel loci (green), and loci with a secondary distinct signal (red). MANTRA, Meta-Analysis of Transethnic Association. https://doi.org/10.1371/journal.pmed.1002383.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Table of HbA1c associated variants. Table with results and classification of the 60 HbA1c-associated variants. SNP number corresponds to number in Fig 1. https://doi.org/10.1371/journal.pmed.1002383.t001 Effect of HbA1c genetic scores on reclassification of prevalent undiagnosed T2D in population screening using HbA1c Next, we tested whether erythrocytic variants influenced the ability of HbA1c to accurately classify individuals with diabetes when screening populations using a single HbA1c measurement. In 5 cohorts, among the 767 individuals with undiagnosed T2D by FG ≥ 7 mmol/L, 390 (50.8%) had measured HbA1c < 6.5% and would remain undiagnosed based on HbA1c. After accounting for the effect of erythrocytic variants, 5 (1.3%) of these individuals were correctly reclassified to having a HbA1c ≥ 6.5%. Among the 18,613 individuals without T2D by FG < 7 mmol/L, 266 (0.3%) had measured HbA1c ≥ 6.5% and would be incorrectly diagnosed with T2D by HbA1c. After accounting for the effect of erythrocytic variants, 50 (18.8%) of these individuals [13 of 80 (16.3%) European ancestry, 28 of 109 (25.7%) African ancestry, 9 of 77 (11.7%) Asian ancestry] were correctly reclassified to having a HbA1c<6.5% (Table 2, S6 Table). While adjusting for the effect of erythrocytic variants improved reclassification for individuals diagnosed with T2D by only HbA1c and not FG, it caused wrong reclassification for individuals diagnosed with T2D by both FG and HbA1c (S6 Table), suggesting that accounting for the contribution of erythrocytic variants may not be relevant for individuals who already meet diagnostic thresholds using both FG and HbA1c. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Reclassification of individuals with discordant T2D status based on prevailing diagnostic thresholds for FG and HbA1c before and after accounting for the effect of erythrocytic variants. https://doi.org/10.1371/journal.pmed.1002383.t002 Effect of HbA1c genetic scores on prediction of incident T2D Next, we tested whether erythrocytic variants influenced the ability of HbA1c to predict incident diabetes in initially nondiabetic populations. GS-G was associated with increased incidence of T2D (odds ratio [OR] per weighted allele 1.05, 95% CI 1.04–1.06 p = 2.5 × 10−29) overall, although not in African Americans (Fig 2, S7 Table). GS-E was not associated overall with incident T2D (OR 1.00 95% CI 0.99–1.01, p = 0.60) (Fig 3, S7 Table), but was negatively associated with incident T2D in Europeans and African Americans after adjusting for HbA1c (OR 0.95, 95% CI, 0.94–0.96, p = 3.3 × 10−16) (Fig 4, S4 Fig and S7 Table), meaning individuals with a higher GS-E will have a lower risk of developing T2D given the same HbA1c value, suggesting that despite having the same HbA1c value, this does not reflect the same level of glycemia. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. T2D prediction, glycemic genetic score. Forest plot of association between glycemic genetic score with incident T2D over a decade-long follow-up period, by ancestry. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 1.05, 95% CI 1.04–1.06, p = 2.5 × 10−29. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size; FHS, Framingham Heart Study; GWAS, genome-wide association study; G6PD, glucose-6-phosphate dehydrogenase; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, Multiethnic Study of Atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g002 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. T2D prediction, erythrocytic genetic score. Forest plot of association between erythrocytic genetic score with incident T2D over a decade-long follow-up period, by ancestry. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 1.00, 95% CI 0.99–1.01, p = 0.60. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size, FHS, Framingham Heart Study; GWAS, genome-wide association study; G6PD, glucose-6-phosphate dehydrogenase; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, Multiethnic Study of Atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g003 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. T2D prediction, erythrocytic genetic score adjusted for HbA1c as a binary variable. Forest plot of association between erythrocytic genetic score with incident T2D over a decade-long follow-up period adjusted for HbA1c as a binary variable (≥5.7% versus <5.7%), by ancestry. HbA1c at baseline was not available in SCHS and was excluded from the meta-analysis. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 0.95, 95% CI 0.94–0.96, p = 3.3 × 10−16. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size; GWAS, genome-wide association study; FHS, Framingham Heart Study; G6PD, glucose-6-phosphate dehydrogenase; HbA1c, glycated hemoglobin; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, multiethnic study of atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g004 Ancestral differences in the genetic architecture of HbA1c The population genetic history of African ancestry groups has undergone selective pressure due to the effects of malaria and other infectious diseases on erythrocytes, unlike in most European ancestry populations [35]. This led us to seek ancestral differences in the genetic determinants of HbA1c. The variance in HbA1c levels explained by all 60 genetic variants over a basic regression model including age and sex was 4.2%–5.8% in Europeans, 6.0%–14.3% in East Asians, and 8.9%–9.7% in African Americans (S8 Table). In addition, compared to Europeans and East Asians, African Americans had the largest difference in mean HbA1c between the bottom and top 5% of the GS-Total distribution (0.91%-units, 95% CI 0.78–1.05; Fig 5 and S9 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Mean HbA1c of individuals at the bottom 5% and top 5% of the distribution of ancestry-specific genetic scores and rs1050828 by genotype. The difference in measured HbA1c of individuals at the bottom 5% and top 5% of the distribution of an ancestry-specific additive GS composed of all 60 variants (GS-Total), and the equivalent calculation for an ancestry-specific GS composed of up to 20 erythrocytic variants (GS-E). Far right of the figure shows the mean HbA1c by genotype for chromosome X rs1050828. AA men, African American men; AA women, African American women; HbA1c, glycated hemoglobin; GS, genetic scores. https://doi.org/10.1371/journal.pmed.1002383.g005 Erythrocytic variants alone explained around one-fifth to three-quarters of the total explained genetic variance in HbA1c (S8 Table). The absolute differences in mean HbA1c from the bottom and top 5% of the GS-E distribution were similar to GS-Total, implying that genetically-induced differences in HbA1c may be largely driven by erythrocytic variants (S9 Table and S10 Table). In African Americans, this difference was largely driven by the C-to-T missense variant (G202A) in G6PD, rs1050828 on chromosome X. This variant alone explained 14.4% of variance in HbA1c (MESA; 9.6% in women; 19.9% in men). Men with the T allele had, on average, an absolute 0.81%-units (95% CI 0.66–0.96) lower HbA1c than those with the C allele. Homozygous TT women had, on average, an absolute 0.68%-units (95% CI 0.38–0.97) lower HbA1c compared to CC homozygous women. The effect size was similar after excluding those with anemia (Hb < 12 g/dL in women and < 13 g/dL in men, S11 Table). Fructosamine is another measure of serum protein glycation, which reflects glycemia over a 2–3 week window, but unlike HbA1c it is not influenced by RBC traits; therefore, we sought to explore the difference between fructosamine-inferred HbA1c and measured HbA1c (Methods, S1 Analysis Plans) to test the hypothesis that the G6PD variant might be influencing HbA1c levels independently of ambient glycemia. Among African Americans, the T allele at rs1050828 was associated with measured HbA1c that was lower than fructosamine-predicted HbA1c (0.31%-units, 95% CI 0.25–0.37, p = 6.4 × 10−19). Among men with the C allele, measured HbA1c was similar to fructosamine-predicted HbA1c (residuals, 0.04%-units, 95% CI −0.04 to 0.12, N = 351). This suggested that only the T allele was associated with markedly lower HbA1c than expected from glycemic measurements (S11 Table). Public health implications of the G6PD variant on T2D screening Given the large effects of the G6PD G202A variant on HbA1c levels, we sought to investigate the impact this variant would have on diabetes detection if using HbA1c as a screening tool. To do this, we used publicly-available data from NHANES 2013–2014 [34], a nationally representative sample of the US, to calculate the proportion of African Americans adults with T2D who would be missed by not accounting for rs1050828 when using a single HbA1c diagnostic threshold of 6.5%, assuming the observed effect size of rs1050828, allele frequency of 11%, and accounting for NHANES sampling design. In the NHANES sample of African Americans (N = 1,133), the mean age was 44.2 years (standard error 0.9), 55.2% were women, and mean HbA1c, excluding those with physician-diagnosed T2D, was 5.5%-units (standard error 0.02). 13.45% of African American adults aged ≥ 18 years had physician-diagnosed T2D with an additional 2.50% with undiagnosed T2D by HbA1c ≥ 6.5%. An additional estimated 2.17% (95% CI 1.88–2.46) with HbA1c < 6.5% may be considered to have T2D if the effect of rs1050828 was accounted for by using genotype-specific diagnostic thresholds of 5.7% for T in men, 5.8% for TT, and 6.2% for TC in women. According to the 2014 United States Census Bureau, approximately 29.9 million adults identified themselves as African American [36], suggesting that 0.65 (95% CI 0.55–0.74) million adults with T2D would remain undiagnosed when screened by a single HbA1c measurement if this genetic information were not taken into account (S12 Table). HbA1c-associated genetic variants and classification into glycemic and nonglycemic pathways To discover new genetic loci influencing HbA1c in populations from 4 different ancestries (European, African American, East Asian, and South Asian), we performed within-ancestry fixed-effects genome-wide association meta-analyses and transancestry meta-analyses using a model that allowed for different effects between ancestry groups (Methods, S2 Fig). Using this approach in up to 159,940 participants without diabetes, we identified 60 variants associated with HbA1c at genome-wide significance (Fig 1, Table 1 and S5 Table). Of 60, 18 have been previously reported, and 42 were novel, including distinct secondary signals at 5 known loci. To classify the associated loci into groups reflecting their likely mode of action on HbA1c, we repeated association analyses conditioning on erythrocytic or glycemic traits and performed lookups in publicly-available association results summary statistics for additional glycemic and erythrocytic traits (Methods, S3 Fig, S2 Table and S3 Table). Based on the combined results from conditional and lookup results, we were able to classify 22 variants as erythrocytic and 19 as glycemic, with 19 remaining unclassified (Fig 1, Table 1 and S5 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Manhattan plot of HbA1c associated variants. Manhattan plot of the transethnic meta-analysis results in MANTRA. The dashed grey line indicates log10BF = 6. Grey and green points denote known/novel loci, respectively. The lead HbA1c-associated variants identified through the ancestry-specific/transethnic analyses are circled in purple (the G6PD variant was not included in the MANTRA analysis, but the locus on the X-chromosome is indicated in the figure). Lines joining the plot & SNP number denote known loci (black), novel loci (green), and loci with a secondary distinct signal (red). MANTRA, Meta-Analysis of Transethnic Association. https://doi.org/10.1371/journal.pmed.1002383.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Table of HbA1c associated variants. Table with results and classification of the 60 HbA1c-associated variants. SNP number corresponds to number in Fig 1. https://doi.org/10.1371/journal.pmed.1002383.t001 Effect of HbA1c genetic scores on reclassification of prevalent undiagnosed T2D in population screening using HbA1c Next, we tested whether erythrocytic variants influenced the ability of HbA1c to accurately classify individuals with diabetes when screening populations using a single HbA1c measurement. In 5 cohorts, among the 767 individuals with undiagnosed T2D by FG ≥ 7 mmol/L, 390 (50.8%) had measured HbA1c < 6.5% and would remain undiagnosed based on HbA1c. After accounting for the effect of erythrocytic variants, 5 (1.3%) of these individuals were correctly reclassified to having a HbA1c ≥ 6.5%. Among the 18,613 individuals without T2D by FG < 7 mmol/L, 266 (0.3%) had measured HbA1c ≥ 6.5% and would be incorrectly diagnosed with T2D by HbA1c. After accounting for the effect of erythrocytic variants, 50 (18.8%) of these individuals [13 of 80 (16.3%) European ancestry, 28 of 109 (25.7%) African ancestry, 9 of 77 (11.7%) Asian ancestry] were correctly reclassified to having a HbA1c<6.5% (Table 2, S6 Table). While adjusting for the effect of erythrocytic variants improved reclassification for individuals diagnosed with T2D by only HbA1c and not FG, it caused wrong reclassification for individuals diagnosed with T2D by both FG and HbA1c (S6 Table), suggesting that accounting for the contribution of erythrocytic variants may not be relevant for individuals who already meet diagnostic thresholds using both FG and HbA1c. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Reclassification of individuals with discordant T2D status based on prevailing diagnostic thresholds for FG and HbA1c before and after accounting for the effect of erythrocytic variants. https://doi.org/10.1371/journal.pmed.1002383.t002 Effect of HbA1c genetic scores on prediction of incident T2D Next, we tested whether erythrocytic variants influenced the ability of HbA1c to predict incident diabetes in initially nondiabetic populations. GS-G was associated with increased incidence of T2D (odds ratio [OR] per weighted allele 1.05, 95% CI 1.04–1.06 p = 2.5 × 10−29) overall, although not in African Americans (Fig 2, S7 Table). GS-E was not associated overall with incident T2D (OR 1.00 95% CI 0.99–1.01, p = 0.60) (Fig 3, S7 Table), but was negatively associated with incident T2D in Europeans and African Americans after adjusting for HbA1c (OR 0.95, 95% CI, 0.94–0.96, p = 3.3 × 10−16) (Fig 4, S4 Fig and S7 Table), meaning individuals with a higher GS-E will have a lower risk of developing T2D given the same HbA1c value, suggesting that despite having the same HbA1c value, this does not reflect the same level of glycemia. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. T2D prediction, glycemic genetic score. Forest plot of association between glycemic genetic score with incident T2D over a decade-long follow-up period, by ancestry. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 1.05, 95% CI 1.04–1.06, p = 2.5 × 10−29. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size; FHS, Framingham Heart Study; GWAS, genome-wide association study; G6PD, glucose-6-phosphate dehydrogenase; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, Multiethnic Study of Atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g002 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. T2D prediction, erythrocytic genetic score. Forest plot of association between erythrocytic genetic score with incident T2D over a decade-long follow-up period, by ancestry. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 1.00, 95% CI 0.99–1.01, p = 0.60. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size, FHS, Framingham Heart Study; GWAS, genome-wide association study; G6PD, glucose-6-phosphate dehydrogenase; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, Multiethnic Study of Atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g003 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. T2D prediction, erythrocytic genetic score adjusted for HbA1c as a binary variable. Forest plot of association between erythrocytic genetic score with incident T2D over a decade-long follow-up period adjusted for HbA1c as a binary variable (≥5.7% versus <5.7%), by ancestry. HbA1c at baseline was not available in SCHS and was excluded from the meta-analysis. MESA (European and Asian ancestry) and the G6PD variant (rs1050828) in ARIC (European and African American) were not included in the discovery GWAS analysis. Effect estimates were combined in a fixed effects meta-analysis. Overall effect estimate: 0.95, 95% CI 0.94–0.96, p = 3.3 × 10−16. ARIC, Atherosclerosis Risk in Communities Study; ES, Effect Size; GWAS, genome-wide association study; FHS, Framingham Heart Study; G6PD, glucose-6-phosphate dehydrogenase; HbA1c, glycated hemoglobin; I-Squared, Higgin's I-squared statistic, a measure of heterogeneity; MESA, multiethnic study of atherosclerosis; SCHS, Singapore Chinese Health Study; T2D, type 2 diabetes. https://doi.org/10.1371/journal.pmed.1002383.g004 Ancestral differences in the genetic architecture of HbA1c The population genetic history of African ancestry groups has undergone selective pressure due to the effects of malaria and other infectious diseases on erythrocytes, unlike in most European ancestry populations [35]. This led us to seek ancestral differences in the genetic determinants of HbA1c. The variance in HbA1c levels explained by all 60 genetic variants over a basic regression model including age and sex was 4.2%–5.8% in Europeans, 6.0%–14.3% in East Asians, and 8.9%–9.7% in African Americans (S8 Table). In addition, compared to Europeans and East Asians, African Americans had the largest difference in mean HbA1c between the bottom and top 5% of the GS-Total distribution (0.91%-units, 95% CI 0.78–1.05; Fig 5 and S9 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Mean HbA1c of individuals at the bottom 5% and top 5% of the distribution of ancestry-specific genetic scores and rs1050828 by genotype. The difference in measured HbA1c of individuals at the bottom 5% and top 5% of the distribution of an ancestry-specific additive GS composed of all 60 variants (GS-Total), and the equivalent calculation for an ancestry-specific GS composed of up to 20 erythrocytic variants (GS-E). Far right of the figure shows the mean HbA1c by genotype for chromosome X rs1050828. AA men, African American men; AA women, African American women; HbA1c, glycated hemoglobin; GS, genetic scores. https://doi.org/10.1371/journal.pmed.1002383.g005 Erythrocytic variants alone explained around one-fifth to three-quarters of the total explained genetic variance in HbA1c (S8 Table). The absolute differences in mean HbA1c from the bottom and top 5% of the GS-E distribution were similar to GS-Total, implying that genetically-induced differences in HbA1c may be largely driven by erythrocytic variants (S9 Table and S10 Table). In African Americans, this difference was largely driven by the C-to-T missense variant (G202A) in G6PD, rs1050828 on chromosome X. This variant alone explained 14.4% of variance in HbA1c (MESA; 9.6% in women; 19.9% in men). Men with the T allele had, on average, an absolute 0.81%-units (95% CI 0.66–0.96) lower HbA1c than those with the C allele. Homozygous TT women had, on average, an absolute 0.68%-units (95% CI 0.38–0.97) lower HbA1c compared to CC homozygous women. The effect size was similar after excluding those with anemia (Hb < 12 g/dL in women and < 13 g/dL in men, S11 Table). Fructosamine is another measure of serum protein glycation, which reflects glycemia over a 2–3 week window, but unlike HbA1c it is not influenced by RBC traits; therefore, we sought to explore the difference between fructosamine-inferred HbA1c and measured HbA1c (Methods, S1 Analysis Plans) to test the hypothesis that the G6PD variant might be influencing HbA1c levels independently of ambient glycemia. Among African Americans, the T allele at rs1050828 was associated with measured HbA1c that was lower than fructosamine-predicted HbA1c (0.31%-units, 95% CI 0.25–0.37, p = 6.4 × 10−19). Among men with the C allele, measured HbA1c was similar to fructosamine-predicted HbA1c (residuals, 0.04%-units, 95% CI −0.04 to 0.12, N = 351). This suggested that only the T allele was associated with markedly lower HbA1c than expected from glycemic measurements (S11 Table). Public health implications of the G6PD variant on T2D screening Given the large effects of the G6PD G202A variant on HbA1c levels, we sought to investigate the impact this variant would have on diabetes detection if using HbA1c as a screening tool. To do this, we used publicly-available data from NHANES 2013–2014 [34], a nationally representative sample of the US, to calculate the proportion of African Americans adults with T2D who would be missed by not accounting for rs1050828 when using a single HbA1c diagnostic threshold of 6.5%, assuming the observed effect size of rs1050828, allele frequency of 11%, and accounting for NHANES sampling design. In the NHANES sample of African Americans (N = 1,133), the mean age was 44.2 years (standard error 0.9), 55.2% were women, and mean HbA1c, excluding those with physician-diagnosed T2D, was 5.5%-units (standard error 0.02). 13.45% of African American adults aged ≥ 18 years had physician-diagnosed T2D with an additional 2.50% with undiagnosed T2D by HbA1c ≥ 6.5%. An additional estimated 2.17% (95% CI 1.88–2.46) with HbA1c < 6.5% may be considered to have T2D if the effect of rs1050828 was accounted for by using genotype-specific diagnostic thresholds of 5.7% for T in men, 5.8% for TT, and 6.2% for TC in women. According to the 2014 United States Census Bureau, approximately 29.9 million adults identified themselves as African American [36], suggesting that 0.65 (95% CI 0.55–0.74) million adults with T2D would remain undiagnosed when screened by a single HbA1c measurement if this genetic information were not taken into account (S12 Table). Discussion In a very large transancestry GWAS of HbA1c, we identified 42 novel and 18 known genetic variants associated with HbA1c, explaining 4%–14% of the trait variance. Genetic variants influencing HbA1c through erythrocytic pathways did not predict future T2D, and adjusting for their contribution to HbA1c led to a moderate misclassification of T2D by adjusted HbA1c. Notably, we detected strong ancestral differences in the contribution of genetic variants to HbA1c that substantially altered the performance of HbA1c as a diagnostic test for T2D in African Americans compared with Europeans and East Asians. Our findings elucidate the contribution of common genetic variants to the genetic architecture of HbA1c and identify an important interface of modern human genetics with clinical and public health. In people of European and Asian ancestry, we found multiple genetic loci with small-to-modest effects, whereas, in African American ancestry, the genetic architecture was dominated by a single variant at G6PD (G202A). This variant was responsible for 0.81%-units HbA1c difference in men and 0.68%-units in homozygous TT women, corresponding to adjusted T2D diagnosis thresholds of 5.7 (95% CI 5.5–5.8) and 5.8 (95% CI 5.5–6.1), respectively. To meet the NGSP certification criteria, laboratory-reported HbA1c ought to be within 6% of the standard reference laboratory mean values (e.g., 6.5%-units ± 0.4%-units) for the majority of patient samples [14]. The limits of acceptable analytic variability were exceeded by this G6PD variant. This may also have important implications for the management of diabetes, with carriers of the HbA1c-lowering G6PD allele requiring adjusted (lower) HbA1c treatment targets. Previous epidemiologic studies have shown that a 1%-unit increase in HbA1c in individuals without T2D was associated with a more than 2-fold increase in risk of future T2D and a 20%–50% increased risk of cardiovascular disease (CVD) [37]. HbA1c ≥ 6.5% compared to those with HbA1c < 5.7% had a higher risk of kidney disease and retinopathy [38]. Only one other African-specific variant, rs11954649, located in the intron of SOX30, reached genome-wide significance in African Americans. However, this variant had a relatively small effect size (β = 0.12 per G allele) on HbA1c and was not classified as glycemic or erythrocytic. The variant was thus not included in the genetic scores and, unlike G6PD, the causal transcript and biological mechanism through which it influences HbA1c remains unclear. Future studies on larger sample sizes of ethnic minorities can focus on dissecting the genomic and biological implications of novel HbA1c-related variants. When considering all ethnicities, both glycemic and erythrocytic variants influence measured HbA1c; yet, only glycemic variants were associated with increased T2D risk (5% per allele) over a decade-long follow-up period. For an equivalent HbA1c, individuals carrying more erythrocytic HbA1c-raising alleles, or fewer HbA1c-lowering alleles, had lower incident T2D risk (−5% per allele), implying that for the same HbA1c level those individuals with the greater number of erythrocytic HbA1c- raising alleles have artificially higher HbA1c values that do not reflect ambient glycemia. Thus, the influence of erythrocytic HbA1c variants may partly explain why some individuals with the same HbA1c may have different risks of future T2D. We note that the estimates of variance explained by genetic variants underlying HbA1c were comparable with those for FG in Europeans (4.8%) [17]. Our results on the reclassification of prevalent T2D were consistent with previous reports indicating that a diagnostic cut-point at 6.5% for HbA1c classified fewer cases than FG ≥ 7 mmol/L [39,40]. Adjusting for the contribution of erythrocytic variants correctly reclassified approximately 1 in 5 individuals with FG < 7 mmol/L who were incorrectly diagnosed as having T2D (HbA1c ≥ 6.5%) to having HbA1c < 6.5%, suggesting that a subset of these individuals may have artificially elevated HbA1c due to the contribution of the erythrocytic variants. Though the specific G6PD variant we identified is monomorphic in Asian and European ancestry, other diverse G6PD variant alleles have reached polymorphic frequencies in malarial endemic regions around the world [35]. G6PD deficiency is unlikely to be identified through routine screening for anemia in healthy individuals, and universal screening for G6PD deficiency is not currently recommended worldwide [32,41]. Testing for G6PD deficiency is only performed on individuals before being prescribed specific drugs, such an antimalarial medications, or in patients with clinical presentation consistent with the disease; for instance, prolonged neonatal jaundice or hemolytic crisis following exposure to specific drugs, infections, or foods [32]. Thus, asymptomatic individuals often remain unaware of their G6PD genotype status and screening for the G6PD genotype before using HbA1c to diagnose T2D may be warranted in populations or ethnic groups where G6PD deficiency is common. Similarly, a recent study identified a significant hemolytic risk in women heterozygous for the G6PD Mahidol variant when treated with primaquine who were not detected by current screening methods [42]. Rarer hematologic conditions that reduce erythrocyte lifespan, e.g., hereditary hemolytic anemias, hereditary spherocytosis, and hemoglobinopathies have also been shown to lower HbA1c [9,43], and should also be considered before using HbA1c in these patients. We recommend additional testing using direct glucose measurements (e.g., FG or oral glucose tolerance testing) or other erythrocyte-independent methods to diagnose T2D. This supports the use of a combination of HbA1c and FG to confirm T2D diagnosis in routine screening [44]. Future studies could also explore G6PD effect modification by HbA1c assay type. Further studies in large cohorts with HbA1c, glycemic, and erythrocytic traits are required to better determine the biological action of genetic variants that have yet to be classified. Similarly, future analyses conditional on RBC distribution width or reticulocyte count will help to better understand the effects of erythrocytic HbA1c-associated variants, should such data become available. The relatively small sample size for Asian and African ancestry cohorts limited the discovery of ancestry-specific genetic variants, beyond the African-specific G6PD variant, and could explain why GS-G was associated with higher incident T2D in European, but not other, ancestries. This underscores the need to extend such studies to non-European populations, particularly those with a high prevalence of some hemoglobinopathies or iron deficiency anemias. Epidemiologic studies have reported higher mean HbA1c in African Americans compared to European ancestry individuals in the US [45,46]. While our genetic findings could not determine whether this difference was completely attributable to relative hyperglycemia, accounting for the effect of the G6PD variant that lowers HbA1c only in African Americans would further widen this disparity. In conclusion, HbA1c remains an appropriate diagnostic test for the majority of people of diverse genetic backgrounds, having lower intraindividual variability compared to FG with the ability to capture chronic hyperglycemia, and robust associations with T2D-related complications [37]. Nevertheless, nonglycemic lowering of measured HbA1c for 1 in 10 African American men who carry this G6PD variant, and 1 in a 100 African American women homozygous for this variant, could amount to 0.65 (95% CI 0.56–0.74) million African American adults in the US with a missed T2D diagnosis using HbA1c as a screening test. We therefore recommend investigation of the possible benefits of screening for the G6PD genotype along with using HbA1c to diagnose T2D in populations of African ancestry or groups where G6PD deficiency is common, and screening with direct glucose measurements, or genetically-informed HbA1c diagnostic thresholds in people with G6PD deficiency. This work supports a role for a precision medicine application to reduce race-ethnic health disparities using HbA1c genetics to improve T2D diagnosis and prediction and to inform screening strategies for T2D across the African continent where the prevalence of the G6PD variant can reach 20%. Supporting information S1 Checklist. STREGA checklist. https://doi.org/10.1371/journal.pmed.1002383.s001 (DOC) S1 Table. Cohort information, genotyping, quality control (QC), glycated hemoglobin (HbA1c), analysis and covariates. https://doi.org/10.1371/journal.pmed.1002383.s002 (XLSX) S2 Table. Association of lead glycated hemoglobin (HbA1c) variants with glycemic and erythrocytic traits from publicly available association results. https://doi.org/10.1371/journal.pmed.1002383.s003 (XLSX) S3 Table. Attenuation of glycated hemoglobin variant (HbA1c) effect size in association models conditioned on fasting glucose (FG), 2hr glucose (2hrGlu), hemoglobin level (Hb), mean corpuscular volume (MCV), and mean corpuscular hemoglobin (MCH) for the lead HbA1c-associated variants. https://doi.org/10.1371/journal.pmed.1002383.s004 (XLSX) S4 Table. Baseline characteristics among those who developed incident type 2 diabetes (T2D) during follow-up and among those who did not, by cohort and ethnicity. https://doi.org/10.1371/journal.pmed.1002383.s005 (XLSX) S5 Table. Genome-wide significant SNPs identified in the genetic discovery analysis. https://doi.org/10.1371/journal.pmed.1002383.s006 (XLSX) S6 Table. Net reclassification index of type 2 diabetes (T2D) status by measured glycated hemoglobin (HbA1c) ≥ 6.5% compared to fasting glucose (FG) ≥ 7 mmol/L with and without accounting for erythrocytic genetic variants by ancestry. https://doi.org/10.1371/journal.pmed.1002383.s007 (XLSX) S7 Table. Association of genetic score-glycemic (GS-G) and genetic score erythrocytic (GS-E) with incident type 2 diabetes (T2D) over a decade-long follow-up period by cohort and ancestry. https://doi.org/10.1371/journal.pmed.1002383.s008 (XLSX) S8 Table. Proportion of additional variance explained over age and sex in measured glycated hemoglobin (HbA1c) by erythryocytic genetic variants and by all genome-wide significant genetic variants by ethnicity. https://doi.org/10.1371/journal.pmed.1002383.s009 (XLSX) S9 Table. Mean difference in glycated hemoglobin (HbA1c) between the top and bottom 5 percentile of genetic score-total (GS-Total) by ancestry. https://doi.org/10.1371/journal.pmed.1002383.s010 (XLSX) S10 Table. Mean difference in glycated hemoglobin (HbA1c) between the top and bottom 5 percentile of genetic score-erythrocytic (GS-E) by ancestry. https://doi.org/10.1371/journal.pmed.1002383.s011 (XLSX) S11 Table. Additional analyses on the association of rs1050828, G6PD variant G202A, with glycated hemoglobin (HbA1c). https://doi.org/10.1371/journal.pmed.1002383.s012 (XLSX) S12 Table. Estimated number of African Americans with type 2 diabetes (T2D) in the US whose diagnosis would be missed due to the glycose-6-phosphate dehydrogenase (G6PD) variant if screened with glycated hemoglobin (HbA1c). https://doi.org/10.1371/journal.pmed.1002383.s013 (XLSX) S1 Fig. Diagram describing the flow of our study. https://doi.org/10.1371/journal.pmed.1002383.s014 (PDF) S2 Fig. Overview of participants included in the genetic discovery analysis. https://doi.org/10.1371/journal.pmed.1002383.s015 (PDF) S3 Fig. Overview of the classification of genetic variants as glycemic, erythrocytic, or unclassified. https://doi.org/10.1371/journal.pmed.1002383.s016 (PDF) S4 Fig. Forest plot of association between erythrocytic genetic score with incident type 2 diabetes (T2D) over a decade-long follow-up period adjusted for glycated hemoglobin (HbA1c) as a continuous variable by ancestry. https://doi.org/10.1371/journal.pmed.1002383.s017 (PDF) S1 Analysis Plans. Analysis plans. https://doi.org/10.1371/journal.pmed.1002383.s018 (DOCX) S1 Financial Disclosure. Authors’ funding information. https://doi.org/10.1371/journal.pmed.1002383.s019 (DOCX) Acknowledgments Published data on glycemic traits were contributed by MAGIC investigators and have been downloaded from www.magicinvestigators.org. The ARIC authors thank the staff and participants of the ARIC study for their important contributions. The CAGE authors thank the participants who made this work possible and who gave it value. The CAGE authors would like to thank Drs. Toshio Ogihara, Yukio Yamori, Akihiro Fujioka, Chikanori Makibayashi, Sekiharu Katsuya, Ken Sugimoto, Kei Kamide, and Ryuichi Morishita and the many physicians of the participating hospitals and medical institutions in Amagasaki Medical Association for their assistance in collecting the DNA samples and accompanying clinical information. The CROATIA authors would like to acknowledge the invaluable contributions of the Institute for Antropological Research, Zagreb, Croatia, the administrative team in Split, and the people of Vis and Korcula. The D.E.S.I.R. Study Group would like to acknowledge its members: B. Balkau, P. Ducimetière, E. Eschwège (INSERM U1018); F. Alhenc-Gelas (INSERM U367); A. Girault (CHU D’Angers); F. Fumeron, M. Marre, R Roussel (Bichat Hospital); F. Bonnet (CHU de Rennes); S. Cauchi, P. Froguel (CNRS UMR8090, Lille); Alençon, Angers, Blois, Caen, Chateauroux, Chartres, Cholet, Le Mans, Orléans, Tours (Centres d’Examens de Santé); J. Cogneau (Institute de Recherche Médecine Générale); General practitioners of the region; C. Born, E. Caces, M. Cailleau, O. Lantieri, J. G. Moreau, F. Rakotozafy, J. Tichet, and S. Vol. (Institute inter-Regional pour la Santé). Analyses contributed by FHS/MGH/BU reflect intellectual input and resource development from the FHS investigators participating in the SNP Health Association Resource (SHARe) project. The DIAGEN authors are grateful to all of the patients who cooperated in this study and to their referring physicians and diabetologists in Saxony. The InterAct authors thank all EPIC participants and staff for their contribution to the study. The InterAct authors also thank staff from the Technical, Field Epidemiology and Data Functional Group Teams of the MRC Epidemiology Unit in Cambridge, UK, for carrying out sample preparation, DNA provision and QC, genotyping and data-handling work. The JHS authors thank the JHS participants and staff for their contributions to this work. The KORA authors are grateful to all members of the Helmholtz Zentrum München, the field staff in Augsburg, and the Augsburg registry team who were involved in the planning, organization, and conduct of the KORA studies. In addition, the authors express their appreciation to all study participants. The Leipzig-adult authors thank all those who participated in the study. The Leipzig-kid authors are grateful to all the patients and families for contributing to the study. They also highly appreciate the support of the Obesity Team and Auxo Team of the Leipzig University Children’s Hospital for management of the patients and to the Pediatric Research Center Lab Team for support with DNA banking. The Lifelines authors thank Behrooz Alizadeh, Annemieke Boesjes, Marcel Bruinenberg, Noortje Festen, Pim van der Harst, Ilja Nolte, Lude Franke, Mitra Valimohammadi for their help in creating the GWAS database, and Rob Bieringa, Joost Keers, René Oostergo, Rosalie Visser, Judith Vonk for their work related to data collection and validation. The Lifelines authors are also grateful to the study participants, the staff from the Lifelines Cohort Study and the contributing research centers delivering data to Lifelines and the participating general practitioners and pharmacists. The LOLIPOP authors thank the participants and research staff who made the study possible. The LURIC authors extend their appreciation to the participants of the LURIC study and thank the LURIC study team who were either temporarily or permanently involved in patient recruitment as well as sample and data handling, in addition to the laboratory staff at the Ludwigshafen General Hospital and the Universities of Freiburg and Ulm, Germany. The MESA authors thank the investigators and participants of the MESA study for their significant and ongoing contributions. The NHAPC authors are grateful to all participants of the NHAPC and also thank their colleagues at the laboratory and local CDC staffs of Beijing and Shanghai for their assistance with data collection. The NSHD authors are very grateful to the members of NSHD birth cohort for their continuing interest and participation in the study. The NSHD authors would also like to acknowledge the Swallow group, UCL, who performed the DNA extractions (Rousseau, et al 2006). DOI: 10.1111/j.1469-1809.2006.00250. The ORCADES authors would like to acknowledge the invaluable contributions of Lorraine Anderson and the research nurses in Orkney, the administrative team in Edinburgh, and the people of Orkney. The SardiNIA authors are grateful to all the volunteers who generously participated in the study, as well as the Lanusei team for their continuous work. The SCHS-CHD (cases and controls) authors thank Siew-Hong Low of the National University of Singapore for supervising the field work of the SCHS and the Ministry of Health in Singapore for assistance with the identification of AMI cases via database linkages. They also acknowledge the founding, longstanding principal investigator of the SCHS, Mimi C. Yu. The SHIP authors are grateful to the contribution of Ravi Kumar Chilukoti, Florian Ernst, Anja Hoffmann, and Astrid Petersmann in generating the SNP data. The contributions of the SHIP staff and participants are gratefully acknowledged. The Sorbs authors thank all those who participated in the study. The Sorbs authors would also like to thank Knut Krohn (Microarray Core Facility, University of Leipzig, Institute of Pharmacology) for the genotyping support and Joachim Thiery (Institute of Laboratory Medicine, Clinical Chemistry and Molecular Diagnostics, University of Leipzig) for clinical chemistry services. The Sorbs authors thank Inga Prokopenko (Imperial College London, UK) and Anubha Mahajan (WTCHG, University of Oxford, UK) for statistical analyses. The TRAILS authors are grateful to all adolescents who participated in this research and to everyone who worked on this project and made it possible. The Twingene authors thank Tomas Axelsson, Ann-Christine Wiman, and Caisa Pöntinen at the SNP&SEQ Technology Platform in Uppsala (www.genotyping.se) for their excellent assistance with genotyping. The TWT2D authors thank the Taiwan Diabetes Consortium for phenotypes assessment and the National Center for Genome Medicine of the National Core Facility Program for Biotechnology, Ministry of Science and Technology for the technical/bioinformatics support. Disclaimer: The views expressed are those of the author(s) and not necessarily those of the NHS, the NIHR, the Department of Health or NHSBT. Members of the EPIC-CVD Consortium Adam Butterworth, John Danesh. Members of the EPIC-InterAct Consortium Claudia Langenberg, Robert A. Scott, Stephen J. Sharp, Nita G. Forouhi, Nicola D. Kerrison, Matt Sims, Debora ME. Lucarelli, Inês Barroso, Panos Deloukas, Mark I. McCarthy, Antonio Agudo, Beverley Balkau, Aurelio Barricarte, Heiner Boeing, Miren Dorronsoro, Paul W. Franks, Sara Grioni, Rudolf Kaaks, Timothy J. Key, Carmen Navarro, Peter M. Nilsson, Kim Overvad, Domenico Palli, Salvatore Panico, J. Ramón Quirós, Olov Rolandsson, Carlotta Sacerdote, María, José Sánchez, Nadia Slimani, Annemieke MW. Spijkerman, Anne Tjonneland, Rosario Tumino, Yvonne T. van der Schouw, Elio Riboli, Nicholas J. Wareham. Members of the Lifelines Cohort Study Behrooz Z Alizadeh, H Marike Boezen, Lude Franke, Pim van der Harst, Gerjan Navis, Marianne Rots, Harold Snieder, Morris Swertz, Bruce HR Wolffenbuttel, Cisca Wijmenga. Members of the EPIC-CVD Consortium Adam Butterworth, John Danesh. Members of the EPIC-InterAct Consortium Claudia Langenberg, Robert A. Scott, Stephen J. Sharp, Nita G. Forouhi, Nicola D. Kerrison, Matt Sims, Debora ME. Lucarelli, Inês Barroso, Panos Deloukas, Mark I. McCarthy, Antonio Agudo, Beverley Balkau, Aurelio Barricarte, Heiner Boeing, Miren Dorronsoro, Paul W. Franks, Sara Grioni, Rudolf Kaaks, Timothy J. Key, Carmen Navarro, Peter M. Nilsson, Kim Overvad, Domenico Palli, Salvatore Panico, J. Ramón Quirós, Olov Rolandsson, Carlotta Sacerdote, María, José Sánchez, Nadia Slimani, Annemieke MW. Spijkerman, Anne Tjonneland, Rosario Tumino, Yvonne T. van der Schouw, Elio Riboli, Nicholas J. Wareham. Members of the Lifelines Cohort Study Behrooz Z Alizadeh, H Marike Boezen, Lude Franke, Pim van der Harst, Gerjan Navis, Marianne Rots, Harold Snieder, Morris Swertz, Bruce HR Wolffenbuttel, Cisca Wijmenga.

doi: 10.1371/journal.pmed.1002393pmid: 28922419

Summary points The United Nations Sustainable Development Goals and the UN Convention on the Rights of the Child (CRC) envision an inclusive society in which health and education contribute to the well-being of all. To achieve this vision, children with developmental delays and behavioral, cognitive, mental, and neurological disabilities need greater access to health care, early childhood care and development services, and education. Improved population-level detection, alongside screening, assessment, and linkage to evidence-based, intersectoral services in the first years of life, can help maximize capabilities and increase the chances of social inclusion for children with developmental delays and disabilities. Educational programs for children with delays and disabilities whose service delivery structure supports the ability of parents to work should be encouraged so that parents can participate in achieving children’s educational goals while also meeting their financial needs. Parents and caregivers who receive training in psychosocial interventions and ongoing support can help children with delays and disabilities thrive in family contexts. Family mental health influences the developmental trajectory of children. Ensuring that parents and caregivers have access to affordable, quality mental health services helps to prevent poor outcomes for children. Rigorous evaluation, continuous quality improvement, and regular monitoring of the programmatic outcomes of services and policy approaches targeting children and caregivers would inform their implementation and serve to disseminate lessons learned from successful policy and program implementation. Background The UN Sustainable Development Goals (SDGs) were formulated based on the principle that people everywhere deserve “equitable and universal access to quality education at all levels, to health care and social protection, where physical, mental and social well-being are assured” [1]. This vision for inclusive healthy societies includes children with developmental delays and cognitive, mental, and neurological disabilities (henceforth developmental delays and disabilities). The UN Convention on the Rights of the Child (CRC) further stipulates that children with disabilities cannot be excluded from free and compulsory primary and secondary education based on their disability [2]. Yet, children with disabilities are more likely to grow up in poverty and to receive less healthcare, early childhood care and development services, and education [3,4]. Caregivers and parents play a central role in facilitating children’s access to early childhood development interventions, including healthcare and education, but must be adequately supported. Recent analyses highlight the importance of early child development and delineate the conditions that place children at risk for not achieving their developmental potential as well as the interventions and research needed to mitigate this [5–9]. With optimal implementation of existing prevention and care interventions, a subset of children will nevertheless be identified with developmental delays and disabilities of varying severity. Ideally, their caregivers, parents, community structures, and societies can be equipped to accommodate their needs to achieve maximum social inclusion and functioning. This paper identifies research and policy activities that, if implemented, could improve the identification of children with delays and disabilities and the ability of caregivers to help meet their developmental, health, and educational needs. We describe opportunities for research or policy shifts in 5 main areas: identifying children with delays and disabilities, ensuring access to early childhood programs and school programs for children, training and support of parents/caregivers to strengthen their ability to care for their children, supporting caregivers’ ability to work, and ensuring that the mental health needs of caregivers are met. Identify children with delays and disabilities The most recent Global Burden of Disease data estimate that in 2015, there were 3.6 million children aged 1–9 years living with autism and more than 15 million living with idiopathic developmental intellectual disability [10]. These are only 2 of many cognitive, emotional, mental, and neurological disabilities. Yet, neither incidence nor prevalence for the full range of childhood delays and disabilities is well established in global data. Rates of cognitive disabilities linked to infections (e.g., pneumonia, meningitis, encephalitis, and HIV), prematurity and stunting, neonatal encephalopathy, hyperbilirubinemia, prenatal iodine and other nutritional deficiencies, and neural tube defects linked to inadequate folic acid are likely higher in low- and middle-income countries (LMICs) than in high-income countries (HICs) given the numbers of children living in poverty and the distribution of these risk factors [11–14]. The accumulation of adversities, beginning before conception and continuing throughout prenatal and early life, can disrupt brain development, attachment, and early learning [5]. Developmental delays become evident in the first year, worsen during early childhood, and continue throughout life [6, 15]. Over the past decade, population-based studies have measured the prevalence of disabilities across several countries. Utilizing a disabilities module within the 2005–2007 Multiple Indicator Cluster Survey (MICS) [16], 1 study found that 20% of children across 16 LMICs screened positive for at least 1 impairment (range 3% to 45%), and 5%, 12.7%, 2.9%, and 6.2% of children screened positive for a cognitive, language, sensory, or motor impairment, respectively [17]. A more recent estimate derived from predictive modelling in 35 LMICs showed that 81 million 3-to-4-year-olds (33% prevalence) had low cognitive or socioemotional development in 2010 [18]. The proportion of under-5 children in LMICs at risk of not attaining their developmental potential because of extreme poverty and stunting remains high at 43% [5]. Accurate identification of a child’s impairment in the first years of life makes reversal or mitigation of adverse effects more likely [19]. Routine screening can be implemented in primary care with high fidelity, low cost, and acceptable levels of burden [20–23]. Provider training increases screening and identification of developmental delays [24, 25]. Proactive case finding using community informants is also a promising approach [26]. When linked with diagnostic assessment and evidence-based interventions, early detection helps to increase the proportion of children who achieve their developmental potential, fulfill their ability to work and contribute [27], are not raised in institutions, and do not need expensive services later in life [28–30]. Ethical care requires that screening be linked to intervention. Increase access to early childhood programs, schooling, and after-school and out-of-school programs The benefits of early intervention for children with developmental delays and disabilities, families, and communities have been well documented in HICs [28, 31, 32]. A recent review of studies from LMICs provides evidence of similar positive outcomes with early interventions for at-risk children, although research that examines outcomes for children with established disabilities is limited [33]. Scarce human resources for mental, neurological, or developmental pediatric care can limit access to services in LMICs. Task-sharing approaches that provide abbreviated training to less specialized providers for the delivery of evidence-based screening, care, and support interventions can help bridge the resource gap. Researchers in Pakistan screened a large rural community by distributing written descriptions of developmental disorders that included motivational messages and by administering the Ten Questions Screen for disability using an interactive voice response system [34]. Children who screened positive were eligible to work with a network of families equipped with “family champion volunteers” trained in evidence-based interventions outlined in the WHO Mental Health Gap Action Program’s (mhGAP) intervention guide. Significant results included reduced WHO Disability Assessment Schedule global disability scores, lower parent-reported socioemotional difficulties in children, and no diminution of caregiver well-being. Equally important, the family volunteers engaged in more advocacy for children’s education, healthcare, and community inclusion. In another study, nonspecialist health workers in India and Pakistan were trained to coach parents of children with autism to apply strategies for improving parent–child interactions, with an emphasis on communication [35]. Parents and children showed more synchronous communication, and children initiated more communication with the parent. Access to education remains a critical intervention for children with delays and disabilities, but disparities in educational opportunity, quality, and outcomes persist [36]. Poorer outcomes are related in part to nonenrolment in school, exclusion from participation in classroom activities, and greater likelihood of school dropout [36]. Yet, children with developmental delays and disabilities and their peers without these conditions benefit when early childhood, school, and out-of-school programs are fully inclusive. Education helps break cycles of poverty, potentially for the child with the delay or disability and for siblings who begin a “caregiver career” rather than attending school [3, 37]. The availability of educational programs year-round during the workday plays a key role in ensuring that children and youth with delays and disabilities have the fullest developmental and educational opportunities in settings far better than institutional care can provide. Such programs increase the likelihood that their parents are able to work, support their families, and lead full lives [3]. Integrated education also serves to educate peers on the needs of children with disabilities and provide pathways for interaction and understanding. Table 1 outlines population- and community-level interventions alongside healthcare interventions that can benefit children with delays and disabilities [38]. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Platforms for interventions for children with developmental delays and disabilities. https://doi.org/10.1371/journal.pmed.1002393.t001 Train and support parents Children with delays and disabilities can thrive in family contexts, particularly if parents and caregivers receive proper training and ongoing support. Directive parenting, combined with “sensitive, responsive, and reciprocal outcomes” and a stimulating home and community environment, led to favorable developmental outcomes for infants and children with Down syndrome in 1 study [39]. Conversely, a lack of knowledge about their child’s condition and needs, negative feelings, and lack of support adversely affected parent–child interactions, child behavior, and development. If provided with nurturing and supportive family care, children with delays and disabilities have a better chance of leading healthy and full lives, particularly when such care is provided from early in life. Nurturing care has recently been defined as a stable environment that is sensitive to children’s health and nutritional needs, with protection from threats, opportunities for early learning, and interactions that are responsive, emotionally supportive, and developmentally stimulating [40]. As an overarching concept, nurturing care is supported by an ecosystem of social contexts—from home to parental work, child care, schooling, the wider community, and policy influences [41]. Unfortunately, in many cases parents do not have access to specialized training and programs and/or flexibility in their work environment to care for their developmentally delayed or disabled child. In many countries, this results in high numbers of these children being institutionalized at an early age [42]. In Central and Eastern Europe and the Commonwealth of Independent States (CEE/CIS), a child with any type of disability is nearly 17 times more likely to be institutionalized than a child who does not have a disability [43]. When systemic measures to support children with disabilities and their families are encouraged and developed, institutionalization can often be prevented or reversed. With help from the civil sector, from 2009 to 2012, the Government of Moldova closed 18 institutions and reduced by 62% the number of children living in residential care [44]. Efforts like this http://www.openingdoors.eu/wp-content/uploads/2013/05/Facts-and-figures-Moldova-2015.pdf begin with and are sustained by empowering families and caregivers through making existing support programs more inclusive, developing specialized training programs on caring for atypically developing children, and ensuring that all parents of children with disabilities have access to this critical training. The need for services and support to parents to provide nurturing care and the need for training of health workers and nonspecialists have been identified as research priorities [7]. Support the ability of parents to work Worldwide, families caring for children with disabilities have lower incomes because of constraints on employment [45]. The income needs of families with children with developmental delays and disabilities are on average higher than those of families whose children do not have these conditions because of the costs of services and care [46], which are rarely fully covered by public funds. Studies from LMICs and HICs demonstrate that parental attention to children’s health and involvement in education leads to better outcomes for children [45]. To do this while sustaining financial stability requires access to paid leave; yet, globally, marked disparities in access to paid leave for both parents persist [45]. Parents and caregivers employed in informal work sectors likely have even fewer protections. In the absence of adequate leave, wage loss can be significant [47]. Families benefit if there are quality, affordable developmental and educational programs that are accessible year-round while parents work. Moreover, from a societal perspective, the full inclusion of parents of children with special needs in the workforce contributes markedly to broad social inclusion just as fully integrated classrooms for students do. Monitoring these policies at a country level would provide important groundwork for achieving progress (see Table 2). Families may also need additional support, and the evolving data on cash transfers and psychosocial support are an encouraging pathway [40]. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Policies to support children with developmental delays and disabilities and their caregivers. https://doi.org/10.1371/journal.pmed.1002393.t002 Treat caregivers with mental health problems In addition to psychosocial support, the mental health needs of caregivers must be met for them to nurture healthy developmental trajectories in their children. Disabling mental disorders like major depression are prevalent worldwide. The reported prevalence of maternal depression is higher in LMICs (15%–20%) compared to HICs (6%–13%), possibly because of the distribution of social risk factors for maternal depression and the limited healthcare infrastructure and resources for care [48, 49]. Depression limits a mother’s responsiveness to her infant and is associated with inconsistent behavior and less emotional sensitivity to the child [50]. Maternal depression may also lead to early cessation of breastfeeding and undernutrition in the first year of life, lower rates of immunization, higher rates of underweight and stunting [51], and higher rates of childhood illnesses like diarrhea [52]. As compared to children with healthy mothers, infants born to depressed mothers are at a higher risk of poorer long-term cognitive development and delayed motor development; have higher rates of antisocial behavior, hyperactivity, and attention difficulties; and have more frequent emotional problems [48]. There is a growing body of literature indicating that paternal mood also affects child development, and comprehensive provision needs to focus on both parents [53, 54]. Paternal depression is linked to an 8-fold increased likelihood of adverse child–child interactions, with the highest risk of problems with peers among children aged 4–6 years, possibly stemming from negative interactions of depressed fathers with their children [55]. Moreover, parenting children with developmental delays or disabilities can elevate caregivers’ stress, negatively impact quality of life [56, 57], and thus exacerbate the bidirectional adverse effects on both caregiver and child. Several studies have shown the effectiveness of psychological therapies such as cognitive behavioral therapy and interpersonal therapy in successfully treating and decreasing the symptoms of depression in adults in HICs and LMICs. Where mental health providers are scarce, task shifting is a promising solution to this human resource problem. A meta-analysis of 13 studies that used task shifting to provide psychological therapies aimed at improving parental depression and child health outcomes showed associations between maternal mood and infant health and development as well as positive bidirectional effects of interventions [48, 58]. Across several studies, psychotherapy-based treatments for depressed mothers generally led to improved mother–child bonding, as well as improved language acquisition and fewer externalizing behavior problems in children, but data here are limited [48]. Conclusion Managing the needs of children with developmental delays and disabilities and meeting their caregivers’ needs require collaboration across the health system as well as intersectoral cooperation (Table 1 [38]). Ideally, detection and screening would occur at all levels. Referrals for care typically involve educational and behavioral health specialists in HICs, but a small and growing evidence base from LMICs shows that families and nonspecialist providers can also be engaged. Crucially, medical providers must be sensitized to the needs of these children to ensure that they receive adequate preventive and curative healthcare alongside behavioral, social, and educational interventions. Care managers (employed in chronic care models) who can support families and facilitate communication among schools, social services, and healthcare personnel would prove valuable for coordinating care and support. Whether researchers address questions related to the extent of need or the efficacy of programmatic and policy approaches, they must also keep their focus on equity to achieve the SDGs. This requires careful assessment of whether all groups of children and caregivers are being equally well served. When researchers examine policies, programs, and services, it will be essential to map the extent to which different approaches to promoting equal participation and opportunities for children with disabilities and their families are being implemented and are closing equity gaps (Table 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Research gaps for the identification and care of children with developmental delays and disabilities. https://doi.org/10.1371/journal.pmed.1002393.t003 Progress will require regular monitoring and accountability to ensure that leaders who improve their approaches are rewarded, that countries and localities that lag are supported to improve, that toolkits growing out of the most effective solutions are readily available to all countries, and that approaches for accountability are widely disseminated to the public. Acknowledgments The authors were assisted by Kathryn Martin, Mirzayan Fellow, National Academies of Sciences, Engineering, and Medicine. Disclaimer: The findings and conclusions in this report are those of the authors and do not necessarily represent the official position of the National Academies of Sciences, Engineering, and Medicine; the United States National Institutes of Health; or the Open Society Foundations.

doi: 10.1371/journal.pmed.1002384pmid: 28898251

A common G6PD variant associated with HbA1c in African Americans without diabetes The implications of 1 specific finding reported by Wheeler et al. [3], cannot be so easily dismissed. They performed GWASs for HbA1c in people without diabetes (all forms) from multiple ethnic groups and identified a common missense variant, rs1050828 (G202A, p.Val68Met), which contributes with minor allele (T) at nearby rs1050829 to the A− haplotype of Glucose-6-phosphate dehydrogenase, G6PD [4], to be associated with lower HbA1c. rs1050828 has a minor allele frequency of 10%–15% in 7,564 African Americans without diabetes from 9 studies, but it is not polymorphic in European or Asian populations used for imputing genotypes. G6PD is on chromosome Xq28, thus, there are 5 possible genotypes at this SNP: African American males hemizygous for the minor allele at this variant (T) have HbA1c 0.79% (8.6 mmol/mol) lower than males without (C), heterozygous females (CT) have HbA1c 0.26% (2.8 mmol/mol) lower, and homozygous females (TT, 1%–2% of women) have HbA1c 0.67% (7.3 mmol/mol) lower than female common homozygotes (CC). Remarkably, in African Americans, the variance in HbA1c explained by the variant is 13%–20% in males and 2%–10% in females, indicating a large effect. The variant was first identified as a cause of G6PD deficiency in the late 1980’s: different variants have varying effects, and this variant results in moderate deficiency with 10%–60% residual enzyme activity [5]. Importantly, using data from GWASs of glucose in the same African Americans, Wheeler et al., showed that this variant was not associated with fasting glucose [3]. Unfortunately, for various technical reasons, GWASs have generally failed to include analysis of variants on the X chromosome [6]. Despite this, 2 previous GWASs of numerous red cell measures in African Americans fortunately did analyze variants on the X chromosome. They showed that the minor allele (T) at rs1050828 was associated with numerous red cell parameters: lower hematocrit, hemoglobin, red cell count, and Red cell Distribution Width (RDW); higher mean corpuscular volume and mean corpuscular hemoglobin concentration [7,8]; as well as principal component 2, formed by multivariate red cell measures [8]. The combined effect of the variant on multiple red cell parameters, along with its lack of association with fasting glucose, led the authors to conclude that its association with HbA1c is through erythrocytic mechanisms, likely through reducing red cell lifespan. However, red cell lifespan is difficult to measure in large cohorts. Likely related, a GWAS of serum bilirubin levels in Sardinians identified variants at G6PD to be associated [9]. Arguing for a causal role of G6PD, the genetic effect was attenuated when G6PD enzyme activity was included in the model. Although G6PD enzyme activity has been shown to be highly heritable [10] with, as expected, strong evidence for X-linked contribution, there has not yet been a GWAS. Unfortunately it appears that G6PD enzyme activity was not measured in any of the African American cohorts studied [3], nor were reticulocyte counts available. Shift from glucose to HbA1c to diagnose type 2 diabetes: rs1050828 results in approximately 650,000 cases of undiagnosed type 2 diabetes among African Americans Just like hypertension and blood pressure, the diagnosis of type 2 diabetes (T2D) is just a threshold on a quantitative trait: the threshold has changed over time as data regarding the risk for long-term complications at various levels of glucose/HbA1c has been more accurately determined using long-term longitudinal epidemiologic studies. The reason that this G6PD variant has potential clinical importance is that, in recent years, many countries have changed recommendations for the diagnosis of T2D to HbA1c from either fasting glucose or oral glucose tolerance tests for a combination of reasons [11,12]. The implication of the genetic association is that hemizygous T males at this variant would need to have an uncorrected HbA1c approximately 0.8% higher (i.e., ≥7.3% [56 mmol/mol] as opposed to ≥6.5% [48 mmol/mol]) than someone without the variant to meet criteria for diabetes diagnosis. If HbA1c were the only test used to diagnose T2D, then it would be diagnosed in such individuals longer after disease onset compared to those without the variant. This would expose them to a longer undiagnosed period while having higher glycemia: these 2 facts would be expected to place them at increased risk for long-term diabetes complications—major causes of morbidity and mortality for people with T2D. Such variants could contribute to the higher risk for long-term diabetes complications in African Americans than European Americans [13]. There would be similar implications for the identification of prediabetes. Compared to the conventional criteria for T2D of HbA1c ≥ 6.5% (48 mmol/mol), the authors argue that sex- and genotype-specific thresholds should be used to diagnose T2D: ≥5.7% (39 mmol/mol) for T males, ≥5.8% (40 mmol/mol) for TT females, and ≥6.2% (44 mmol/mol) for CT females. Wheeler et al., estimate that approximately 650,000 African Americans (2%, out of an estimated population of about 30 million) would have their T2D undiagnosed because of this single genetic variant (approximately 430,000 males and 180,000 females) if HbA1c were the only test used for T2D diagnosis. For the estimation, they assumed that the variant has an allele frequency of 11% and is in Hardy–Weinberg equilibrium (in females). Geographic heterogeneity in the proportion of African ancestry in African Americans [14,15] would be expected to vary the variant frequency across the United States and could therefore alter the number of individuals affected. Given that, worldwide, approximately 400 million people are G6PD deficient [16], approaching the global prevalence of T2D, then the global health impact of variants at G6PD on T2D diagnosis using HbA1c could be staggering. The vast majority of people with G6PD deficiency are undiagnosed, and screening is not routine [16]. Population genetics of rs1050828 Data from the 1000 Genomes Project provide allele and genotype frequencies for rs1050828 across a number of different populations. In the African populations, minor allele frequency is as follows: African Caribbeans in Barbados (ACB): 13%; Americans of African Ancestry in south-west USA (ASW): 17%; Esan in Nigeria (ESN): 16%; Mende in Sierra Leone (MSL): 7%; Gambian in Western Divisions in the Gambia (GWD): 4%; Luhya in Webuye, Kenya (LWK): 18%; Yoruba in Ibadan, Nigeria (YRI): 21% [17]—indicating that this variant is common in many African populations. In addition, allele frequency is 2% in both Colombian in Medellin, Columbia (CLM) and Puerto Ricans in Puerto Rico (PUR). Other G6PD alleles and other loci Partly because of the base reference panel that Wheeler used (HapMap phase 2 [18]), there were only 30 mother-father-adult child African trios (from the Yoruba in Ibadan, Nigeria), resulting in 90 X chromosomes. The number of rs1050828 variant alleles in the chromosomes was only 13. The number of other G6PD variants that are known to cause G6PD deficiency that were imputed in their study would be small, making imputation of these variants challenging. However, 2 major improvements have occurred since the analysis plan that Wheeler used was implemented [3]: the 1000 Genomes Project [17] and the Haplotype Reference Consortium [19]. Both consortia have provided genetic data from genotyping and/or sequencing of larger numbers of individuals from more diverse ethnic origins. The use of these as references will likely increase the number of independent variants associated with HbA1c, not only at G6PD but also at other loci. For example, the sickle cell trait (rs334) has recently been associated with lower HbA1c in African Americans based on an expanded number of subjects from 2 of the cohorts included in the Wheeler paper [20,21]. Future challenges at G6PD locus will involve describing the sex- and genotype-specific effects of each variant on HbA1c, since we cannot assume that other G6PD alleles have the same magnitude of effect—some may be larger or smaller, requiring genotype-dependent adjustment of HbA1c thresholds. At G6PD in females, such data will enable the analysis of multiple loci within the locus. For example, some women may be compound heterozygotes for 2 different variants that cause G6PD deficiency, 1 each on their maternal and paternal X chromosomes. Depending on which X chromosome is inactive in red cell precursors, this could have an important influence on HbA1c. X chromosome inactivation Larger variance in HbA1c in heterozygous (CT) than in homozygotes females is an interesting observation from this study (CC, Fig 3 [3]). It could be a result of smaller heterozygote sample size but could also indicate unidentified interacting factor(s). Such factors could include X-inactivation and other ungenotyped and/or poorly imputed variants on the other parental haplotype. G6PD is subject to X-inactivation, but X-inactivation status was not determined in heterozygous females in any of the studies included [3]. Skewed X-inactivation typically increases with age, so the genetic effect on HbA1c could become larger with age in heterozygous females. Depending on which X chromosome is inactive in red cell precursors of heterozygous females, this could have an important clinical application since the effect on HbA1c could either be minimal or similar to that seen in female T/T homozygotes. Ethnic differences in HbA1c Since HbA1c was introduced for T2D diagnosis, heated discussion has ensued regarding whether ethnic differences in HbA1c have implications for both T2D diagnosis as well as glycemic control in people with diabetes [22,23]. Genetic variants such as rs10508282 could play a role but, by itself, cannot explain the higher HbA1c in African Americans than in European Americans, since the effect of the variant allele (which is mostly absent in Europeans) is to lower rather than raise HbA1c. Alternatives for T2D diagnosis have considered other glycated proteins including glycated serum albumin or fructosamine, either alone or in combination with HbA1c. However, as has been commented recently, no clinical trials have used alternative glycated proteins to link them to risk of long-term diabetes complications, and standardization of these assays has not yet been achieved [24]. Implications for glycemic control in people with diabetes Although it was not the focus of Wheeler and colleagues [3], there are also potential implications for people with diabetes. HbA1c is the most common laboratory test performed in people with diabetes, used to measure recent glycemia, and has been the target of many diabetes interventions. Discrepancies between self-monitored glucose and HbA1c are often seen in people with diabetes. Treatment decisions, including escalation of medical therapy in people with T2D are determined, in part, based on HbA1c. Although it has not been directly shown, it is reasonable to assume that the variant has a similar effect on HbA1c in people with diabetes. Previously, it has been shown that males with type 1 diabetes (T1D) and Mediterranean G6PD deficiency have approximately 1% lower HbA1c compared to those without G6PD deficiency [25,26]. Importantly, retinopathy was present only in those males with T1D with G6PD deficiency but not in those without G6PD deficiency, despite similar diabetes duration [26]. Similar results have been observed in other populations [27]. (NB: likely these HbA1c were not standardized). In parallel, more recent data from clinical studies that used repeated glucose measures from Continuous Glucose Measurements along with frequent contemporaneous HbA1c from the same individuals with diabetes showed that there is between-individual heterogeneity in the relationship between these 2 measures [28]. Genetic differences are prime candidates to explain much of this variation. Finally, genetic factors may also contribute to heterogeneous benefits and harms of intensive therapy in people with T2D, as has been observed in some clinical trials [29]. Take home message and future directions The G6PD variant rs1050828 is common in people of African and African American origin: it has a large effect on HbA1c, which, if ignored, can result in people failing to meet criteria for T2D using HbA1c while being classified as having T2D using glucose tests. National clinical practice guidelines need to be revisited. Individuals with this variant should either be screened for T2D using glucose, or sex-and genotype-adjusted thresholds for HbA1c should be used. There are also likely implications for the measurement of glycemic control using HbA1c in people with diabetes. Subjects of European ancestry have been the disproportionate focus of GWASs; as the costs for genotyping have dropped recently, larger sample sizes of much more diverse individuals of non-European ancestry are needed to identify other loci that have clinical relevance.

doi: 10.1371/journal.pmed.1002381pmid: 28873087

Background Understanding the past-year prevalence of male-perpetrated intimate partner violence (IPV) and risk factors is essential for building evidence-based prevention and monitoring progress to Sustainable Development Goal (SDG) 5.2, but so far, population-based research on this remains very limited. The objective of this study is to compare the population prevalence rates of past-year male-perpetrated IPV and nonpartner rape from women’s and men’s reports across 4 countries in Asia and the Pacific. A further objective is to describe the risk factors associated with women’s experience of past-year physical or sexual IPV from women’s reports and factors driving women’s past-year experience of partner violence. Methods and findings This paper presents findings from the United Nations Multi-country Study on Men and Violence in Asia and the Pacific. In the course of this study, in population-based cross-sectional surveys, 5,206 men and 3,106 women aged 18–49 years were interviewed from 4 countries: Cambodia, China, Papua New Guinea (PNG), and Sri Lanka. To measure risk factors, we use logistic regression and structural equation modelling to show pathways and mediators. The analysis was not based on a written plan, and following a reviewer’s comments, some material was moved to supplementary files and the regression was performed without variable elimination. Men reported more lifetime perpetration of IPV (physical or sexual IPV range 32.5%–80%) than women did experience (physical or sexual IPV range 27.5%–67.4%), but women’s reports of past-year experience (physical or sexual IPV range 8.2%–32.1%) were not very clearly different from men’s (physical or sexual IPV range 10.1%–34.0%). Women reported much more emotional/economic abuse (past-year ranges 1.4%–5.7% for men and 4.1%–27.7% for women). Reports of nonpartner rape were similar for men (range 0.8%–1.9% in the past year) and women (range 0.4%–2.3% in past year), except in Bougainville, where they were higher for men (11.7% versus 5.7%). The risk factor modelling shows 4 groups of variables to be important in experience of past-year sexual and/or physical IPV: (1) poverty, (2) all childhood trauma, (3) quarrelling and women’s limited control in relationships, and (4) partner factors (substance abuse, unemployment, and infidelity). The population attributable fraction (PAF) was largest for quarrelling often, but the second greatest PAF was for the group related to exposure to violence in childhood. The relationship control variable group had the third highest PAF, followed by other partner factors. Currently married women were also more at risk. In the structural model, a resilience pathway showed less poverty, higher education, and more gender-equitable ideas were connected and conveyed protection from IPV. These are all amenable risk factors. This research was cross-sectional, so we cannot be sure of the temporal sequence of exposure, but the outcome being a past-year measure to some extent mitigates this problem. Conclusions Past-year IPV indicators based on women’s reported experience that were developed to track SDG 5 are probably reasonably reliable but will not always give the same prevalence as may be reported by men. Report validity requires further research. Interviews with men to track past-year nonpartner rape perpetration are feasible and important. The findings suggest a range of factors are associated with past-year physical and/or sexual IPV exposure; of particular interest is the resilience pathway suggested by the structural model, which is highly amenable to intervention and explains why combining economic empowerment of women and gender empowerment/relationship skills training has been successful. This study provides additional rationale for scaling up violence prevention interventions that combine economic and gender empowerment/relationship skills building of women, as well as the value of investing in girls’ education with a view to long-term violence reduction. Why was the study done? Understanding the past-year prevalence of physical and or sexual intimate partner violence (IPV) and risk factors is essential for building evidence-based prevention. Previous studies have not compared men’s and women’s past-year prevalence reports and have been limited by a predominant focus on risk factors for lifetime exposure to IPV. Monitoring SDG 5.2 and building evidence-based prevention require a relative understanding of the measures of past-year prevalence and the drivers of this violence. What did the authors do and find? We use data from 4 countries of the UN Multi-country Study on Men and Violence in Asia and the Pacific to compare the population prevalence rates of past-year IPV and nonpartner rape from women’s and men’s reports and present an analysis of drivers of women’s experience of past-year physical or sexual IPV. Women’s reports of past-year male-perpetrated IPV were similar to those from men. Four groups of variables are important drivers of IPV: poverty, all childhood trauma, quarrelling and women’s limited control in the relationship, and partner factors (substance abuse, unemployment, and infidelity). What do these findings mean? Past-year IPV indicators based on women’s reported experience that were developed to track SDG 5 are probably reasonably reliable. Women appear to gain resilience to violence through combined economic power and understanding gender empowerment/relationship skills, as well as education; this is an important foundation for intervention. Further research is needed on the validity of men’s and women’s reports of IPV, which could not be determined from these data. Introduction In 2015, eliminating all forms of violence against women and girls (VAWG) was adopted as a target for the Sustainable Development Goal (SDG) 5 on gender equality and empowerment of women. To achieve this, we must develop and roll out effective measures to prevent male-perpetrated violence and show their effect. The indicators of progress towards this target are not finalized but will be a measure of women’s experience of intimate partner violence (IPV) and of nonpartner sexual violence in the past 12 months. According to most recent estimates, 30% of women aged 15 years and over have experienced male-perpetrated physical and/or sexual IPV, and 7% nonpartner sexual violence, in their lifetime [1,2]. In low- and middle-income countries, the World Health Organization instrument that was developed for its Multi-country Study on Women’s Health and Domestic Violence against Women is generally seen as the gold standard measure for women. Parallel research with men has developed a methodology for measuring perpetration, but the 2 measures of violence in heterosexual relationships have not been compared. Given that widely used indicators will most likely focus on reports of just 1 gender for reasons of resource constraints, it is important that there be an understanding of the comparability of men’s and women’s reports. Without this, we have uncertainty about the validity of women’s reports of experiences of IPV and nonpartner sexual violence. There is particular concern that sexual violence may be under-reported by women because rape is highly stigmatized, which may result in minimization of events, but it is also possible men might under-report perpetration of violence so as not to incriminate themselves [3,4]. Prevention of VAWG needs to be built on evidence of drivers among women currently at risk (as well as those of perpetration). There is a reasonably large amount of literature on risk factors for experience of IPV (for example, summarized in the World Health Organization’s 2010 review [5]), but major limitations include a focus on lifetime exposure (rather than past year) and overadjustment of models for (nonamenable) at-risk groups rather than focusing on risk factors. In the case of the former, this means that the outcome modelled is not exactly the ‘problem’ for which interventions are required (which is current, or future, violence). In the case of the latter, the analyses focus largely on who is at risk rather than understanding factors driving risk. The literature is also mostly focused on a single country and is cross-sectional [6], and given the variability in the variables measured and the modelling approaches used, this often constrains the ability to compare across countries and global regions. Prevention science is better informed by looking at risk factors amenable to intervention and linked to past-year experience of IPV, which are likely to differ from factors associated with lifetime experience of IPV. The UN Multi-country Study on Men and Violence was designed to address many of the gaps in previous data sources [7]. It has a large multicountry dataset with women’s reports of IPV, collected using gold standard exposure measures, and also includes standard measures of the most important currently recognised drivers of violence as well as some hypothesised ones. We present the population prevalence of women’s experiences of past-year IPV and nonpartner rape and compare it to men’s reported perpetration across 4 countries in Asia and the Pacific, and we present risk factors associated with women’s experience of past-year physical or sexual IPV (risk factors for men’s perpetration in this dataset have been presented previously [8,9]). We present structural models to show pathways and mediators. Methods Ethical approval was provided by the Medical Research Council of South Africa; the College of Humanities, Beijing Forestry University; National Ethics Committee for Health Research of Cambodia; and the Faculty of Medicine at the University of Colombo, Sri Lanka. The survey was developed by Partners for Prevention in collaboration with the Medical Research Council of South Africa and the country research teams. Research was conducted in 2011–2012. Of the 6 country surveys, only 4 had male and female interviews: China, Cambodia, Bougainville in Papua New Guinea, and Sri Lanka. The present study is intended to contrast women's reported experience of IPV and nonpartner rape with men's reported perpetration of IPV and nonpartner rape; therefore, our analysis focuses on these 4 surveys. The sample from Cambodia and the sample from Papua New Guinea were representative, respectively, of Cambodia and the island of Bougainville. The Chinese site was a county with a town and rural area, and in Sri Lanka, Colombo and 3 contrasting districts were surveyed. Further details of the research can be found elsewhere [7,10]. In each setting, we selected census enumeration areas, with a probability proportionate to size, and systematically selected households within these areas. In households, we invited a man or woman (depending on the cluster) aged 18–49 years (where necessary, randomly selected) for interview, with a trained sex-matched interviewer. Most interviews were face to face, but for men, answers to most sensitive questions were self-completed on audio-enhanced personal digital assistants (APDAs). In China, a household list of individuals in each cluster by age and sex was available and used for sampling within selected clusters, and the entire questionnaire was self-completed. Full details of the methods, sampling, and response rates are presented elsewhere [10]. We conducted surveys with women on their health and experiences of violence in 4 sites (Cambodia, China, Bougainville, and Sri Lanka). We sampled men and women in separate clusters. We conducted interviews with 3,106 women (between 477–1,103 per country) and 5,206 men (between 849–1,777 per country across the 4 analysed here). The proportion of enumerated and eligible women interviewed per site was between 92.7% (in Cambodia) and 73.9% (in Sri Lanka). For men, it ranged between 97.3% (in Cambodia) and 58.7% (in Sri Lanka; for details [7]). Measures used in the questionnaire are presented in Table 1. We followed ethical and safety guidelines for research on violence against women [11,12]. The interviewees received an information sheet and provided written consent. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Measures. https://doi.org/10.1371/journal.pmed.1002381.t001 Data analysis The data analysis was largely planned at the point of commencement of the work on the paper. Authors EF and RJ were involved in the research from its inception and had planned the questionnaire so that it would be possible to undertake an analysis of prevalence of violence and risk factors. They ensured as much as possible that the main variables previously described in the literature [5] were included in the dataset. We planned the analysis to test the relationships between the independent variables and the outcomes. This study is reported as per the STROBE guidelines (S1 STROBE Checklist). We combined the datasets and analysed the data using Stata, version 13. All procedures took into account the multistage structure of the dataset, with stratification by site within a country and enumeration areas as clusters. The sample was self-weighting. Women’s experiences of violence and male partner violence perpetration, as well as the independent variables, were summarized as percentages (or means), with 95% confidence limits calculated using standard methods (Taylor linearization). We categorised the type of violence exposure according to the most severe type experienced, where greatest severity was considered as exposure to physical and/or sexual IPV, as this is the category that has been the basis of most health consequences research [1] and is consistent with the paper on male risk factors for IPV published from the same dataset [10]. It is currently common practice in the field not to model a combined variable with sexual and physical IPV and economic and emotional abuse, although this has been sometimes done [13]. This is because the field’s understanding of the latter is at a much earlier stage, with limited agreement on how to measure it, how to prevent it, and the implications (of emotional abuse alone) for health and development outcomes. It is important for the field that the issue is not ignored, hence its inclusion here, but we do not feel that the field is quite ready for it to be meaningfully pooled with sexual and physical violence for risk factor modelling and interventions. This approach has been followed by other authors, for example, Mahenge et al. [14]. The multiple emotional/economic abuse category consisted of women who had experienced more than 1 act of economic or emotional abuse but never experienced sexual or physical abuse. All ever-partnered women and men were classified into 5 violence exposure categories: none, emotional/economic without sexual or physical (henceforth referred to as ‘emotional/economic’), sexual without physical and with or without emotional/economic (henceforth referred to as ‘sexual’), physical without sexual and with or without emotional/economic (henceforth referred to as ‘physical’), or sexual and physical with or without emotional/economic (henceforth referred to as ‘physical/sexual’). We also evaluated the relationship between the outcome (IPV) and nonresponse (missing data) in putative risk factors. No association was found between a woman’s IPV status and her nonresponse to any of the possible risk factors. However, to increase the sample of women with responses to scale measurements (e.g., gender attitudes and relationship control), women with partial responses to scale items were also included. Three methods for imputing for missing data were initially compared. These involved imputing for missing scale items using either (1) a woman’s responses to other items in the scale (individual respondent mean) or (2) the average for each item adjusted for IPV status, or (3) the average of the overall score adjusted for IPV status. There were no significant differences in the 3 methods for both gender attitudes and relationship control scores. We used ‘the average of the overall score (adjusted for IPV status)’ to impute for missing scores. The exercise of testing variables and building model drew on current theories about risk factors and drivers of violence against women. The selection of variables as putative risk factors was informed by the state of knowledge in the field. Drawing on a life-course modified ecological model of violence risk [15], we conceptualized possible risk factors as (1) structural, (2) those pertaining to the women (including stemming from her childhood), (3) those pertaining to her partner, and (4) those pertaining to their relationship. We further were informed in our thinking by research on masculinities that views a range of male behaviours as indicator variables for hegemonic masculinity [16]. The connections between hegemonic masculinity and violence against women have been extensively theorized. In building the structural equation model, we drew on our extensive knowledge base on gender-based violence. It is well recognized that IPV is strongly associated with poverty and that poverty increases the likelihood of experience of adversity in childhood and influences access to education [9,17–19]. Research with men has shown that childhood trauma exposure influences ideas about gender equity, which is why we hypothesized this direction of effect for women [19]. Further research has shown that women’s ideas about gender influence partner selection, as does exposure to childhood trauma [20]. To show associations between independent variables that were putative risk factors, we first conducted a bivariable analysis with a (by type) lifetime IPV exposure measure and a multinomial regression with no physical, sexual, or severe economic/financial violence as the comparison group. A maximum likelihood multinomial logit model, which adjusted for the survey design, was used to compare factors associated with different types of IPV experienced with the no-violence reference category. We initially fitted bivariable models and then included all factors that were significantly associated with IPV experience in the bivariate models into an overall model, which was adjusted for the country and age group of the woman. We examined factors associated with past-year experience of IPV considering the same independent variables, but with a past-year exposure to any physical and/or sexual IPV as the outcome, due to sample size considerations, we did not perform multinomial modelling. We sought to model 19 covariates in the logistic regression model, which, according to generally accepted rules of thumb [21], would require a total of 190 events. Because the category ‘physical and sexual IPV’ contained only 124 events, having this as an outcome in a multinomial model could have resulted in overfitting. We therefore decided to fit a regression model specifying the combined outcome of ‘any exposure to physical and/or sexual IPV’. Since this combined outcome contained 2,765 x 16.7% = 461 events, this decision allowed us to proceed with less concern about overfitting. Multivariable logistic regression was used to determine risk factors associated with past-year physical and/or sexual IPV experience in women, with those not experiencing this as the reference group. To enable the use of a variable on frequency of quarrelling, which was not measured in Cambodia, a dummy level for Cambodia was created for the quarrelling variable for use in the logistic regression model. All variables were included in the multivariate analysis. We focus the discussion on variables with P < or = 0.05 in the model, which is adjusted for country/site and age-group of the woman. The population attributable fractions (PAFs) for each category of IPV were calculated using the formula PAF = ((RRR − 1) / RRR) * Pe, where RRR is the adjusted relative risk ratio from the adjusted model and Pe is the proportion of women who had experienced that particular IPV type and who had the exposure. Structural equation modelling (SEM) was conducted using Stata 13.0 to assess the interrelationship between variables associated with physical and/or sexual IPV in the multinomial regression model. The model outcome was a past-year IPV variable that had 4 levels drawn from the physical and sexual IPV questions: no exposure, sexual IPV, physical IPV, and physical or sexual IPV. The correlation between each hypothesized variable and the IPV variable was then tested by building variable pairs. All associations were tested by running a full-information maximum likelihood method to deal with missing values. This method was chosen over multiple imputations because it has been shown to yield superior results in structural equation modelling [22]. As a next stage, a measurement model was fitted with the variables allowed to freely correlate. To assess model fit of the observed data, we used the comparative fit index (CFI) (>0.95); Tucker-Lewis Index (TLI) (>0.9) for acceptable fit and (>0.95) as indicative of good fit [23]; and root mean square error of approximation (RMSEA) (of 0.05 or less) [24,25]. We fitted a path model using full information maximum likelihood (FIML) estimation to model all available data. The final model was built based on theory and statistically meaningful modifications using backwards elimination to exclude endogenous variables that did not mediate any path (with significance set at the P < 0.05 level) from the exogenous variables to IPV in order to ensure model parsimony. Before adjusting standard errors for clustering of participants in countries, model fit was very good (p(χ2) = 0.519, RMSEA < 0.001, CFI = 1.000, and TLI = 1.001). After adjusting for clustering, the coefficient of determination (CD) was 0.215. The model did not include any error covariances. Data analysis The data analysis was largely planned at the point of commencement of the work on the paper. Authors EF and RJ were involved in the research from its inception and had planned the questionnaire so that it would be possible to undertake an analysis of prevalence of violence and risk factors. They ensured as much as possible that the main variables previously described in the literature [5] were included in the dataset. We planned the analysis to test the relationships between the independent variables and the outcomes. This study is reported as per the STROBE guidelines (S1 STROBE Checklist). We combined the datasets and analysed the data using Stata, version 13. All procedures took into account the multistage structure of the dataset, with stratification by site within a country and enumeration areas as clusters. The sample was self-weighting. Women’s experiences of violence and male partner violence perpetration, as well as the independent variables, were summarized as percentages (or means), with 95% confidence limits calculated using standard methods (Taylor linearization). We categorised the type of violence exposure according to the most severe type experienced, where greatest severity was considered as exposure to physical and/or sexual IPV, as this is the category that has been the basis of most health consequences research [1] and is consistent with the paper on male risk factors for IPV published from the same dataset [10]. It is currently common practice in the field not to model a combined variable with sexual and physical IPV and economic and emotional abuse, although this has been sometimes done [13]. This is because the field’s understanding of the latter is at a much earlier stage, with limited agreement on how to measure it, how to prevent it, and the implications (of emotional abuse alone) for health and development outcomes. It is important for the field that the issue is not ignored, hence its inclusion here, but we do not feel that the field is quite ready for it to be meaningfully pooled with sexual and physical violence for risk factor modelling and interventions. This approach has been followed by other authors, for example, Mahenge et al. [14]. The multiple emotional/economic abuse category consisted of women who had experienced more than 1 act of economic or emotional abuse but never experienced sexual or physical abuse. All ever-partnered women and men were classified into 5 violence exposure categories: none, emotional/economic without sexual or physical (henceforth referred to as ‘emotional/economic’), sexual without physical and with or without emotional/economic (henceforth referred to as ‘sexual’), physical without sexual and with or without emotional/economic (henceforth referred to as ‘physical’), or sexual and physical with or without emotional/economic (henceforth referred to as ‘physical/sexual’). We also evaluated the relationship between the outcome (IPV) and nonresponse (missing data) in putative risk factors. No association was found between a woman’s IPV status and her nonresponse to any of the possible risk factors. However, to increase the sample of women with responses to scale measurements (e.g., gender attitudes and relationship control), women with partial responses to scale items were also included. Three methods for imputing for missing data were initially compared. These involved imputing for missing scale items using either (1) a woman’s responses to other items in the scale (individual respondent mean) or (2) the average for each item adjusted for IPV status, or (3) the average of the overall score adjusted for IPV status. There were no significant differences in the 3 methods for both gender attitudes and relationship control scores. We used ‘the average of the overall score (adjusted for IPV status)’ to impute for missing scores. The exercise of testing variables and building model drew on current theories about risk factors and drivers of violence against women. The selection of variables as putative risk factors was informed by the state of knowledge in the field. Drawing on a life-course modified ecological model of violence risk [15], we conceptualized possible risk factors as (1) structural, (2) those pertaining to the women (including stemming from her childhood), (3) those pertaining to her partner, and (4) those pertaining to their relationship. We further were informed in our thinking by research on masculinities that views a range of male behaviours as indicator variables for hegemonic masculinity [16]. The connections between hegemonic masculinity and violence against women have been extensively theorized. In building the structural equation model, we drew on our extensive knowledge base on gender-based violence. It is well recognized that IPV is strongly associated with poverty and that poverty increases the likelihood of experience of adversity in childhood and influences access to education [9,17–19]. Research with men has shown that childhood trauma exposure influences ideas about gender equity, which is why we hypothesized this direction of effect for women [19]. Further research has shown that women’s ideas about gender influence partner selection, as does exposure to childhood trauma [20]. To show associations between independent variables that were putative risk factors, we first conducted a bivariable analysis with a (by type) lifetime IPV exposure measure and a multinomial regression with no physical, sexual, or severe economic/financial violence as the comparison group. A maximum likelihood multinomial logit model, which adjusted for the survey design, was used to compare factors associated with different types of IPV experienced with the no-violence reference category. We initially fitted bivariable models and then included all factors that were significantly associated with IPV experience in the bivariate models into an overall model, which was adjusted for the country and age group of the woman. We examined factors associated with past-year experience of IPV considering the same independent variables, but with a past-year exposure to any physical and/or sexual IPV as the outcome, due to sample size considerations, we did not perform multinomial modelling. We sought to model 19 covariates in the logistic regression model, which, according to generally accepted rules of thumb [21], would require a total of 190 events. Because the category ‘physical and sexual IPV’ contained only 124 events, having this as an outcome in a multinomial model could have resulted in overfitting. We therefore decided to fit a regression model specifying the combined outcome of ‘any exposure to physical and/or sexual IPV’. Since this combined outcome contained 2,765 x 16.7% = 461 events, this decision allowed us to proceed with less concern about overfitting. Multivariable logistic regression was used to determine risk factors associated with past-year physical and/or sexual IPV experience in women, with those not experiencing this as the reference group. To enable the use of a variable on frequency of quarrelling, which was not measured in Cambodia, a dummy level for Cambodia was created for the quarrelling variable for use in the logistic regression model. All variables were included in the multivariate analysis. We focus the discussion on variables with P < or = 0.05 in the model, which is adjusted for country/site and age-group of the woman. The population attributable fractions (PAFs) for each category of IPV were calculated using the formula PAF = ((RRR − 1) / RRR) * Pe, where RRR is the adjusted relative risk ratio from the adjusted model and Pe is the proportion of women who had experienced that particular IPV type and who had the exposure. Structural equation modelling (SEM) was conducted using Stata 13.0 to assess the interrelationship between variables associated with physical and/or sexual IPV in the multinomial regression model. The model outcome was a past-year IPV variable that had 4 levels drawn from the physical and sexual IPV questions: no exposure, sexual IPV, physical IPV, and physical or sexual IPV. The correlation between each hypothesized variable and the IPV variable was then tested by building variable pairs. All associations were tested by running a full-information maximum likelihood method to deal with missing values. This method was chosen over multiple imputations because it has been shown to yield superior results in structural equation modelling [22]. As a next stage, a measurement model was fitted with the variables allowed to freely correlate. To assess model fit of the observed data, we used the comparative fit index (CFI) (>0.95); Tucker-Lewis Index (TLI) (>0.9) for acceptable fit and (>0.95) as indicative of good fit [23]; and root mean square error of approximation (RMSEA) (of 0.05 or less) [24,25]. We fitted a path model using full information maximum likelihood (FIML) estimation to model all available data. The final model was built based on theory and statistically meaningful modifications using backwards elimination to exclude endogenous variables that did not mediate any path (with significance set at the P < 0.05 level) from the exogenous variables to IPV in order to ensure model parsimony. Before adjusting standard errors for clustering of participants in countries, model fit was very good (p(χ2) = 0.519, RMSEA < 0.001, CFI = 1.000, and TLI = 1.001). After adjusting for clustering, the coefficient of determination (CD) was 0.215. The model did not include any error covariances. Results In total, 3,106 women aged between 18 and 49 years were interviewed in the 4 countries, among whom 2,855 (91.9%) were ever-partnered. Of the ever-partnered women, 90 (3.3%) did not respond to any of the questions related to IPV experience and were thus excluded from analysis. In total, 5,206 men were interviewed in the 4 countries, and 4,360 (83.8%) had ever been partnered. Four thousand and fifteen men completed the IPV questions, and 5,062 completed the non-partner rape questions. Comparison of prevalence Comparing lifetime reports of women’s experiences and men’s reports of IPV by type from the 4 countries (Table 2) reveals that sexual IPV was quite similarly reported by men and women, except women less often disclosed lifetime sexual IPV in Cambodia (9.1% versus 21%) and China (8.3% versus 19.4%) and men reported less past-year sexual IPV in Sri Lanka. Men reported less lifetime and past-year physical IPV than women in Cambodia, but much more in China. Men reported more lifetime physical IPV than women in Bougainville, but past-year reports were similar. In Sri Lanka, the overall level of violence reported by men and women and the rates for each type were similar. In every country, women reported much more past-year emotional and financial IPV than men. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Among partnered women and men, past 12-month prevalence of women’s and men’s experience of different types of violence perpetrated by their intimate partners, by country. https://doi.org/10.1371/journal.pmed.1002381.t002 In Cambodia, 0.4% (95% CI 0.1%–1.73%) of women had experienced nonpartner rape in the past year, and 1.9% (95% CI 1.12%–2.70%) of men disclosed perpetration. In China, 2.3% (95% CI 1.49%–3.43%) of women had experienced nonpartner rape in the past year, and 1.7% (95% CI 0.94%–2.52%) of men disclosed perpetration. In Bougainville, 5.7% (95% CI 4.21%–7.75%) of women had experienced nonpartner rape in the past year, and 11.7% (95% CI 9.02%–14.30%) of men disclosed perpetration. In Sri Lanka, 0.5% (95% CI 0.15%–1.40%) of women had experienced nonpartner rape in the past year, and 0.8% (95% CI 0.22%–1.43%) of men disclosed perpetration. The prevalence of past-year physical and/or sexual IPV experience increased with age (Table 3). Poverty, indicated by present food insecurity and problems finding money for an emergency, was associated with a greater risk of IPV, as was the women being the main breadwinner. Families in which the wife provided most of the money for the home were twice as likely to have food insecurity (P < 0.001) as those in which the husband provided, another provided, or both the husband and wife shared equally in providing. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Prevalence and distribution of factors associated with women’s past-year experience of sexual or physical intimate partner violence (N = 2,765). https://doi.org/10.1371/journal.pmed.1002381.t003 Risk factor analysis All 3 forms of childhood abuse (sexual, physical, and emotional) and witnessing abuse of mother were more common among women with past-year physical or sexual IPV experience. Women whose partners earned more than them had a lower past-year IPV prevalence than those earning the same as their partners or women who earned more. Partner characteristics associated with women’s past-year IPV experience were the male partner’s regular alcohol use, ever or past-year drug use, lack of fidelity, and unemployment. Women who were highly controlled by their partner were more likely to have experienced past-year IPV, as were those who quarrelled more often and those holding less gender-inequitable views. S1 Table shows the prevalence of women’s social characteristics, victimisation history, partner characteristics, and gender attitudes and relationship factors by lifetime IPV exposure category for the combined dataset (all 4 countries), with the unadjusted associations and the adjusted associations shown in S2 Table. These tables show very similar patterns of associated factors as was seen in the past-year physical or sexual IPV exposure analysis. Table 3 shows the logistic regression models of factors associated with past-year IPV. In the past 12 months, 461/ 2,765 (16.7%) women had experienced sexual or physical (or both forms of) IPV. The risk factors shown are experiencing more poverty; having experienced abuse in childhood (sexual, physical, or emotional); having a partner who drinks alcohol, uses drugs, may be unfaithful, is unemployed, or is highly controlling; and having more frequent quarrelling in the relationship. The PAF was the largest for quarrelling often, but the second greatest PAF was for the group related to exposure to violence in childhood, followed by the PAF for the group related to the woman being controlled by her partner. The partner characteristics (substance abuse, unemployment, and infidelity) had the next highest PAFs. In the backwards/forwards elimination model, currently married women were at much higher risk. Structural model Results for the structural equation model are presented in Fig 1 and Table 4 and follow recommended guidelines outlined by Mueller and Hancock [26]. The paths between socioeconomic status and IPV were mediated by childhood trauma exposure (i.e., poorer women had a higher trauma exposure) and increased IPV risk or by women’s educational attainment (i.e., wealthier women had been in school for longer) and having more equitable gender attitudes, which conveyed IPV protection, unless associated with more quarrelling. Childhood trauma was linked to IPV through 4 pathways. One was direct, such that childhood trauma increased the risk of IPV. One was mediated by partner alcohol use and frequency of quarrelling, such that childhood trauma reduced the chance of having a low-alcohol-using partner and thus lower quarrelling. One path was mediated by (more inequitable) attitudes to gender equity. The fourth path was mediated by partner fidelity such that risk was associated with greater confidence in him being faithful. Witnessing abuse of the woman’s mother was more common in women exposed to trauma in childhood and was included to improve model fit but did not mediate a pathway. A figure with all significant and nonsignificant paths and standard errors is presented in S1 Fig. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Final structural model of final factors influencing women’s experience of intimate partner violence (IPV) (standardized path coefficients [only statistically significant paths shown]). https://doi.org/10.1371/journal.pmed.1002381.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 4. Women's path model: Direct effects, disturbance variances, and equation-level goodness of fit. https://doi.org/10.1371/journal.pmed.1002381.t004 Comparison of prevalence Comparing lifetime reports of women’s experiences and men’s reports of IPV by type from the 4 countries (Table 2) reveals that sexual IPV was quite similarly reported by men and women, except women less often disclosed lifetime sexual IPV in Cambodia (9.1% versus 21%) and China (8.3% versus 19.4%) and men reported less past-year sexual IPV in Sri Lanka. Men reported less lifetime and past-year physical IPV than women in Cambodia, but much more in China. Men reported more lifetime physical IPV than women in Bougainville, but past-year reports were similar. In Sri Lanka, the overall level of violence reported by men and women and the rates for each type were similar. In every country, women reported much more past-year emotional and financial IPV than men. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Among partnered women and men, past 12-month prevalence of women’s and men’s experience of different types of violence perpetrated by their intimate partners, by country. https://doi.org/10.1371/journal.pmed.1002381.t002 In Cambodia, 0.4% (95% CI 0.1%–1.73%) of women had experienced nonpartner rape in the past year, and 1.9% (95% CI 1.12%–2.70%) of men disclosed perpetration. In China, 2.3% (95% CI 1.49%–3.43%) of women had experienced nonpartner rape in the past year, and 1.7% (95% CI 0.94%–2.52%) of men disclosed perpetration. In Bougainville, 5.7% (95% CI 4.21%–7.75%) of women had experienced nonpartner rape in the past year, and 11.7% (95% CI 9.02%–14.30%) of men disclosed perpetration. In Sri Lanka, 0.5% (95% CI 0.15%–1.40%) of women had experienced nonpartner rape in the past year, and 0.8% (95% CI 0.22%–1.43%) of men disclosed perpetration. The prevalence of past-year physical and/or sexual IPV experience increased with age (Table 3). Poverty, indicated by present food insecurity and problems finding money for an emergency, was associated with a greater risk of IPV, as was the women being the main breadwinner. Families in which the wife provided most of the money for the home were twice as likely to have food insecurity (P < 0.001) as those in which the husband provided, another provided, or both the husband and wife shared equally in providing. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Prevalence and distribution of factors associated with women’s past-year experience of sexual or physical intimate partner violence (N = 2,765). https://doi.org/10.1371/journal.pmed.1002381.t003 Risk factor analysis All 3 forms of childhood abuse (sexual, physical, and emotional) and witnessing abuse of mother were more common among women with past-year physical or sexual IPV experience. Women whose partners earned more than them had a lower past-year IPV prevalence than those earning the same as their partners or women who earned more. Partner characteristics associated with women’s past-year IPV experience were the male partner’s regular alcohol use, ever or past-year drug use, lack of fidelity, and unemployment. Women who were highly controlled by their partner were more likely to have experienced past-year IPV, as were those who quarrelled more often and those holding less gender-inequitable views. S1 Table shows the prevalence of women’s social characteristics, victimisation history, partner characteristics, and gender attitudes and relationship factors by lifetime IPV exposure category for the combined dataset (all 4 countries), with the unadjusted associations and the adjusted associations shown in S2 Table. These tables show very similar patterns of associated factors as was seen in the past-year physical or sexual IPV exposure analysis. Table 3 shows the logistic regression models of factors associated with past-year IPV. In the past 12 months, 461/ 2,765 (16.7%) women had experienced sexual or physical (or both forms of) IPV. The risk factors shown are experiencing more poverty; having experienced abuse in childhood (sexual, physical, or emotional); having a partner who drinks alcohol, uses drugs, may be unfaithful, is unemployed, or is highly controlling; and having more frequent quarrelling in the relationship. The PAF was the largest for quarrelling often, but the second greatest PAF was for the group related to exposure to violence in childhood, followed by the PAF for the group related to the woman being controlled by her partner. The partner characteristics (substance abuse, unemployment, and infidelity) had the next highest PAFs. In the backwards/forwards elimination model, currently married women were at much higher risk. Structural model Results for the structural equation model are presented in Fig 1 and Table 4 and follow recommended guidelines outlined by Mueller and Hancock [26]. The paths between socioeconomic status and IPV were mediated by childhood trauma exposure (i.e., poorer women had a higher trauma exposure) and increased IPV risk or by women’s educational attainment (i.e., wealthier women had been in school for longer) and having more equitable gender attitudes, which conveyed IPV protection, unless associated with more quarrelling. Childhood trauma was linked to IPV through 4 pathways. One was direct, such that childhood trauma increased the risk of IPV. One was mediated by partner alcohol use and frequency of quarrelling, such that childhood trauma reduced the chance of having a low-alcohol-using partner and thus lower quarrelling. One path was mediated by (more inequitable) attitudes to gender equity. The fourth path was mediated by partner fidelity such that risk was associated with greater confidence in him being faithful. Witnessing abuse of the woman’s mother was more common in women exposed to trauma in childhood and was included to improve model fit but did not mediate a pathway. A figure with all significant and nonsignificant paths and standard errors is presented in S1 Fig. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Final structural model of final factors influencing women’s experience of intimate partner violence (IPV) (standardized path coefficients [only statistically significant paths shown]). https://doi.org/10.1371/journal.pmed.1002381.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 4. Women's path model: Direct effects, disturbance variances, and equation-level goodness of fit. https://doi.org/10.1371/journal.pmed.1002381.t004 Discussion Comparing reports Between a quarter and two-thirds of women in the 4 countries studied had experienced IPV, and 1.7% and 15.9% had experienced nonpartner rape. There was very great diversity in the prevalence of IPV between countries, as previously reported in Asia and the Pacific [1]. Reports by men and women show much similarity, but overall, women’s reported prevalence of lifetime physical and sexual violence experience was lower than men’s reports of perpetration, notably in sexual violence reporting. Men’s reporting of past-year nonpartner rape was much higher than women’s in Bougainville. A different pattern was seen in past-year reports that were not clearly patterned with respect to those of men, except in the area of emotional/financial abuse, for which in all countries women reported much more. We would not necessarily expect men’s and women’s reports of nonpartner sexual violence to concur, and some women are at much higher risk than others in the population and may experience multiple rapes [27]. Although we did not have couples’ reports on partner violence, we do expect the acts/experiences of violence of men and women to be similar at a population level for past-year violence, as 75% of men had had only 1 sexual partner in the last year, and most women were married (77.7%) or cohabiting (2.9%). It is possible that women tended to minimise or forget some lifetime experiences of partner violence, but it may also be the case that higher levels of reports by men are explained by men using violence on some types of female partners more often than on their wives. Given the differences in men’s and women’s lifetime reports, we must conclude that the current global lifetime prevalence rates that are based on women’s reported experiences may underestimate the lifetime perpetration of IPV and nonpartner rape by men. Risk factors and drivers We saw 4 important groups of risk factors for IPV experience. First, our results confirm that past-year IPV victimisation is more common in a context of poverty [6]. Secondly, exposure to physical, sexual, and/or emotional childhood trauma was very strongly associated with experience of all forms of IPV (past year or lifetime). This advances current research that has focused on sexual violence or on witnessing maternal abuse [5,6]. In the structural model, childhood trauma had a direct pathway to IPV experience, and it mediated several indirect paths. This helps explain why childhood trauma exposure is such an important risk factor (as shown by the PAF). The analysis of factors associated with IPV perpetration by men has also shown the importance of all forms of childhood trauma [10]. We observed also that childhood trauma exposure was associated with a more conservative position towards gender equity. It is possible that this is easier for women to adopt if they have lower self-esteem and more insecurity after trauma, as it generally is socially rewarded and normative. Witnessing abuse of one’s mother has been found to be associated with both experience of and perpetration of IPV in many studies [17,28–35]. We confirmed this, but in the structural model, it was not as important as childhood trauma. Since previous research has often focused on witnessing abuse rather than more thoroughly measuring childhood trauma, it is possible that assumptions that there is a direct intergenerational learning process normalising IPV victimisation among women and girls are overemphasising this 1 traumatic experience, and witnessing abuse may be better interpreted as an indicator of exposure to wider childhood experiences of emotional and other trauma, all of which elevate IPV risk. The latter explanation fits better with the knowledge that witnessing abuse of one’s mother is traumatic and repulsive, which has long been an observation that fits uncomfortably with a direct learning explanation. The third variable group consists of partner characteristics: his drinking, past-year drug use, controlling behaviour, unemployment, and fidelity. Generally, these are previously well-established risk factors, although research with men has not confirmed associations with drug use in Asia and the Pacific, except in relation to perpetration of multiple perpetrator rape [8,10]. Alcohol abuse combines a direct impact on behaviour, financial tensions, and gender-inequitable masculinity; the fidelity measure reflects the male sexual entitlement dimension of the latter [6,8,36,37]. Highly controlling behaviour is an abusive practice that is closely related to the use of physical and sexual violence [38] and is viewed by some authors as part of the concept of emotional abuse. In the structural model, male partner alcohol consumption and infidelity both mediated pathways between childhood trauma and IPV experience—in the former case, mediated by frequency of quarrelling. These partner variables may highlight the potential for enhanced prevention intervention impact if men and women are both involved in interventions to reduce violence [39]. Partner unemployment was significant on 1 of the models and would generally be interpreted as contributing to poverty in the relationship, with associated tensions, but it may also impact on self-perceived manliness, and violence may be used as a response to this [39]. The frequency of quarrelling was very strongly associated with IPV, as it was in the models of men’s perpetration in the 4 countries [10]. Although quarrelling is linked to men’s and women’s ideas about gender equity, intervention research shows that it can be reduced within relationships by training in communication skills, and this can reduce partner violence [40]. One of the most important findings of the structural model was a pathway that can be interpreted as indicating variables that build women’s resilience to violence. This linked higher wealth, higher educational attainment, and having more gender-equitable attitudes. This is very important because all of these factors are amenable to intervention, and it highlights the role of poverty reduction and interventions to enhance girls’ schooling, which may be supported for many reasons related to development and the general upliftment of women, in IPV prevention. In this study, the Gender Equitable Men (GEM) scale was used to measure women’s gender attitudes. This is a broad measure that includes attitudes towards the use of violence against women. The latter alone have been shown to be very strongly associated with risk of violence [41,42]; however, we found strong correlations with IPV in a version of the scale without the question about attitudes towards violence. Economic empowerment has been shown to be a fruitful area of intervention with women [43], but more consistently so when combined with a gender empowerment intervention [44]. Our analysis suggests that interventions with adult women would do better to include a focus on gender empowerment and relationship dynamics in order to ensure that empowerment alone does not result in greater quarrelling and violence. Our structural model provides some indication of why interventions that impact on several variables in the resilience pathway for women (economic status and gender attitudes/relationship skills) may be much better than single-component interventions. Reducing childhood trauma exposure is ultimately critical to reducing women’s experience of violence and is strongly related to poverty. Whilst there is much work on early interventions in childhood to reduce the experience of trauma and IPV in the next generation, it is possible that poverty reduction will have the greatest impact. Limitations The study findings reflect the sampled sites; generalizability beyond this is unclear, and the combined dataset analysed here does not reflect the whole region. Since the research was cross-sectional, temporality may be questioned, but since this was recent violence, this is not likely to be a great problem. All the prevalence estimates for violence were compared with estimates weighted for the number of eligible men and women per household. The latter were not significantly different in any site, and thus, we have used unweighted estimates. The main analysis was on past-year IPV exposure, and because this is less common than lifetime exposure, the power of the analysis was inevitably impacted. However, the focus has strengthened the interpretability of the results for programming, as it is the goal of IPV prevention to reduce exposure of women at risk in the future and recent abuse is the best measure of this. A study limitation is that we do not have a comparison of men’s and women's reports from the same relationship. In accordance with WHO ethics and safety guidelines, we did not interview men and women in the same location, much less in couples. The motivation is to avoid the (to our knowledge small) possibility of retaliatory violence associated with partners learning of the interview content. This risk is not justified in cross-sectional research but prevents comparison of couples’ reports. Comparing reports Between a quarter and two-thirds of women in the 4 countries studied had experienced IPV, and 1.7% and 15.9% had experienced nonpartner rape. There was very great diversity in the prevalence of IPV between countries, as previously reported in Asia and the Pacific [1]. Reports by men and women show much similarity, but overall, women’s reported prevalence of lifetime physical and sexual violence experience was lower than men’s reports of perpetration, notably in sexual violence reporting. Men’s reporting of past-year nonpartner rape was much higher than women’s in Bougainville. A different pattern was seen in past-year reports that were not clearly patterned with respect to those of men, except in the area of emotional/financial abuse, for which in all countries women reported much more. We would not necessarily expect men’s and women’s reports of nonpartner sexual violence to concur, and some women are at much higher risk than others in the population and may experience multiple rapes [27]. Although we did not have couples’ reports on partner violence, we do expect the acts/experiences of violence of men and women to be similar at a population level for past-year violence, as 75% of men had had only 1 sexual partner in the last year, and most women were married (77.7%) or cohabiting (2.9%). It is possible that women tended to minimise or forget some lifetime experiences of partner violence, but it may also be the case that higher levels of reports by men are explained by men using violence on some types of female partners more often than on their wives. Given the differences in men’s and women’s lifetime reports, we must conclude that the current global lifetime prevalence rates that are based on women’s reported experiences may underestimate the lifetime perpetration of IPV and nonpartner rape by men. Risk factors and drivers We saw 4 important groups of risk factors for IPV experience. First, our results confirm that past-year IPV victimisation is more common in a context of poverty [6]. Secondly, exposure to physical, sexual, and/or emotional childhood trauma was very strongly associated with experience of all forms of IPV (past year or lifetime). This advances current research that has focused on sexual violence or on witnessing maternal abuse [5,6]. In the structural model, childhood trauma had a direct pathway to IPV experience, and it mediated several indirect paths. This helps explain why childhood trauma exposure is such an important risk factor (as shown by the PAF). The analysis of factors associated with IPV perpetration by men has also shown the importance of all forms of childhood trauma [10]. We observed also that childhood trauma exposure was associated with a more conservative position towards gender equity. It is possible that this is easier for women to adopt if they have lower self-esteem and more insecurity after trauma, as it generally is socially rewarded and normative. Witnessing abuse of one’s mother has been found to be associated with both experience of and perpetration of IPV in many studies [17,28–35]. We confirmed this, but in the structural model, it was not as important as childhood trauma. Since previous research has often focused on witnessing abuse rather than more thoroughly measuring childhood trauma, it is possible that assumptions that there is a direct intergenerational learning process normalising IPV victimisation among women and girls are overemphasising this 1 traumatic experience, and witnessing abuse may be better interpreted as an indicator of exposure to wider childhood experiences of emotional and other trauma, all of which elevate IPV risk. The latter explanation fits better with the knowledge that witnessing abuse of one’s mother is traumatic and repulsive, which has long been an observation that fits uncomfortably with a direct learning explanation. The third variable group consists of partner characteristics: his drinking, past-year drug use, controlling behaviour, unemployment, and fidelity. Generally, these are previously well-established risk factors, although research with men has not confirmed associations with drug use in Asia and the Pacific, except in relation to perpetration of multiple perpetrator rape [8,10]. Alcohol abuse combines a direct impact on behaviour, financial tensions, and gender-inequitable masculinity; the fidelity measure reflects the male sexual entitlement dimension of the latter [6,8,36,37]. Highly controlling behaviour is an abusive practice that is closely related to the use of physical and sexual violence [38] and is viewed by some authors as part of the concept of emotional abuse. In the structural model, male partner alcohol consumption and infidelity both mediated pathways between childhood trauma and IPV experience—in the former case, mediated by frequency of quarrelling. These partner variables may highlight the potential for enhanced prevention intervention impact if men and women are both involved in interventions to reduce violence [39]. Partner unemployment was significant on 1 of the models and would generally be interpreted as contributing to poverty in the relationship, with associated tensions, but it may also impact on self-perceived manliness, and violence may be used as a response to this [39]. The frequency of quarrelling was very strongly associated with IPV, as it was in the models of men’s perpetration in the 4 countries [10]. Although quarrelling is linked to men’s and women’s ideas about gender equity, intervention research shows that it can be reduced within relationships by training in communication skills, and this can reduce partner violence [40]. One of the most important findings of the structural model was a pathway that can be interpreted as indicating variables that build women’s resilience to violence. This linked higher wealth, higher educational attainment, and having more gender-equitable attitudes. This is very important because all of these factors are amenable to intervention, and it highlights the role of poverty reduction and interventions to enhance girls’ schooling, which may be supported for many reasons related to development and the general upliftment of women, in IPV prevention. In this study, the Gender Equitable Men (GEM) scale was used to measure women’s gender attitudes. This is a broad measure that includes attitudes towards the use of violence against women. The latter alone have been shown to be very strongly associated with risk of violence [41,42]; however, we found strong correlations with IPV in a version of the scale without the question about attitudes towards violence. Economic empowerment has been shown to be a fruitful area of intervention with women [43], but more consistently so when combined with a gender empowerment intervention [44]. Our analysis suggests that interventions with adult women would do better to include a focus on gender empowerment and relationship dynamics in order to ensure that empowerment alone does not result in greater quarrelling and violence. Our structural model provides some indication of why interventions that impact on several variables in the resilience pathway for women (economic status and gender attitudes/relationship skills) may be much better than single-component interventions. Reducing childhood trauma exposure is ultimately critical to reducing women’s experience of violence and is strongly related to poverty. Whilst there is much work on early interventions in childhood to reduce the experience of trauma and IPV in the next generation, it is possible that poverty reduction will have the greatest impact. Limitations The study findings reflect the sampled sites; generalizability beyond this is unclear, and the combined dataset analysed here does not reflect the whole region. Since the research was cross-sectional, temporality may be questioned, but since this was recent violence, this is not likely to be a great problem. All the prevalence estimates for violence were compared with estimates weighted for the number of eligible men and women per household. The latter were not significantly different in any site, and thus, we have used unweighted estimates. The main analysis was on past-year IPV exposure, and because this is less common than lifetime exposure, the power of the analysis was inevitably impacted. However, the focus has strengthened the interpretability of the results for programming, as it is the goal of IPV prevention to reduce exposure of women at risk in the future and recent abuse is the best measure of this. A study limitation is that we do not have a comparison of men’s and women's reports from the same relationship. In accordance with WHO ethics and safety guidelines, we did not interview men and women in the same location, much less in couples. The motivation is to avoid the (to our knowledge small) possibility of retaliatory violence associated with partners learning of the interview content. This risk is not justified in cross-sectional research but prevents comparison of couples’ reports. Conclusions Our findings suggest that newly emphasised past-year IPV indicators that were developed to track SDG 5 would be reasonably reliable if based on women’s interviews. Interviews with men to track past-year nonpartner rape perpetration are important. We have shown an important IPV resilience pathway. This helps us to understand why interventions that combine women’s economic empowerment and building gender-equitable attitudes (and communication skills), such as Pronyk and colleagues’ Image [43], may be more effective than those with a single-component focus. This is a very important advance in understanding as these are imminently amenable risk factors through work with populations of adult women. However, integrated approaches that reach women and men with a comprehensive set of interventions to address different risk factors would almost certainly bring the most benefit. Supporting information S1 Fig. Modelling showing all standardized path coefficients and standard errors (statistically significant paths shown in bold). https://doi.org/10.1371/journal.pmed.1002381.s001 (TIF) S1 STROBE Checklist. Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement. Checklist of items that should be included in reports of cross-sectional studies. https://doi.org/10.1371/journal.pmed.1002381.s002 (DOC) S1 Table. Prevalence of factors associated with lifetime women’s experience of intimate partner violence (IPV), by type of violence. https://doi.org/10.1371/journal.pmed.1002381.s003 (DOCX) S2 Table. Crude relative risk ratios (RRRs) and adjusted relative risk ratios (aRRRs) of factors associated with lifetime women’s experience of intimate partner violence (IPV), by type of violence. https://doi.org/10.1371/journal.pmed.1002381.s004 (DOCX) Acknowledgments The UN Multi-country Study on Men and Violence was a collaborative effort and only made possible by the commitment, dedication, and hard work of all of the organizations and individuals involved, both internationally and in each of the study countries. First and foremost, we would like to acknowledge and give gratitude to the women and men who gave their time to participate in our study and generously shared their life experiences with us. We wish to express our profound thanks to our partner institutions and organizations in each of the study countries, as well as all of the interviewers and supervisors who worked tirelessly, and often under difficult circumstances, to collect the data for this study. We would like to thank the studies’ technical advisors, members of the steering committee, and members of the national working groups. We would like to thank all the members of the Partner for Prevention Technical Advisory Group and Regional Steering Committee who guided the overall study. UN Multi-country Study on Men and Violence Study Team: Core research team: Emma Fulu (P4P) (Study Coordinator), Rachel Jewkes (Medical Research Council, South Africa), Xian Warner (P4P), Stephanie Miedema (P4P), Tim Roselli (P4P), and James Lang (P4P). Country study teams—China: Dr Wang Xiangxian (PI) (Tianjin University, China); Fang Gang (Beijing Forestry University); Li Hongtao (Chinese Women’s College and Anti-Domestic Violence Network); Zeljka Mudrovcic, Wen Hua, Arie Hoekman, Elina Nikulainen, Bernard Coquelin, and Mariam Khan (UNFPA China); Cambodia: Wenny Kusuma, Clara Magariño Manero, and Freya Larsen (UN Women Cambodia); Emma Fulu (PI) and Xian Warner (P4P); and Saba Moussavi (independent consultant); Sri Lanka: Neloufer de Mel (PI) (University of Colombo); Pradeep Peiris (Social Scientists’ Association); Shyamala Gomez (independent consultant); Social Indicator Team; and Kamani Jinadasa (CARE Sri Lanka); Papua New Guinea (Bougainville): Rachel Jewkes (PI), Yandisa Sikweyiya, and Nwabisa Shai (Medical Research Council, South Africa); Francesca Drapuluvik-Tinabar (National Statistics Office, PNG); Peterson Magoola and Anthony Agyenta (UNDP PNG); Thomas Shanahan and Tracy Vienings (UNDP Regional Pacific Centre). Steering committee—Rachel Jewkes (MRC, South Africa), Claudia Garcia-Moreno (WHO), Ruchira Tabassum Naved (ICDDR,B), Kamani Jinadasa (CARE Sri Lanka), Tracy Vienings (UNDP Regional Pacific Centre) and Wenny Kusuma (UN Women Cambodia). Technical advisory group—Rachel Jewkes (MRC, South Africa), Raewyn Connell (University of Sydney, Australia), Gary Barker (Instituto Promundo, USA & Brazil), Alan Greig (Independent consultant, USA), Rahul Roy (AAKAR, India), Ravi Verma (ICRW), Kalyani Menon Sen (Independent consultant). PDA programmer: Scott Johnson (University of Kentucky) Disclaimer: The authors alone are responsible for the views expressed in this article, and they do not necessarily represent the views, decisions, or policies of the World Health Organization.

doi: 10.1371/journal.pmed.1002389pmid: 28926573

Background Self-monitoring of blood pressure (BP) appears to reduce BP in hypertension but important questions remain regarding effective implementation and which groups may benefit most. This individual patient data (IPD) meta-analysis was performed to better understand the effectiveness of BP self-monitoring to lower BP and control hypertension. Methods and findings Medline, Embase, and the Cochrane Library were searched for randomised trials comparing self-monitoring to no self-monitoring in hypertensive patients (June 2016). Two reviewers independently assessed articles for eligibility and the authors of eligible trials were approached requesting IPD. Of 2,846 articles in the initial search, 36 were eligible. IPD were provided from 25 trials, including 1 unpublished study. Data for the primary outcomes—change in mean clinic or ambulatory BP and proportion controlled below target at 12 months—were available from 15/19 possible studies (7,138/8,292 [86%] of randomised participants). Overall, self-monitoring was associated with reduced clinic systolic blood pressure (sBP) compared to usual care at 12 months (−3.2 mmHg, [95% CI −4.9, −1.6 mmHg]). However, this effect was strongly influenced by the intensity of co-intervention ranging from no effect with self-monitoring alone (−1.0 mmHg [−3.3, 1.2]), to a 6.1 mmHg (−9.0, −3.2) reduction when monitoring was combined with intensive support. Self-monitoring was most effective in those with fewer antihypertensive medications and higher baseline sBP up to 170 mmHg. No differences in efficacy were seen by sex or by most comorbidities. Ambulatory BP data at 12 months were available from 4 trials (1,478 patients), which assessed self-monitoring with little or no co-intervention. There was no association between self-monitoring and either lower clinic or ambulatory sBP in this group (clinic −0.2 mmHg [−2.2, 1.8]; ambulatory 1.1 mmHg [−0.3, 2.5]). Results for diastolic blood pressure (dBP) were similar. The main limitation of this work was that significant heterogeneity remained. This was at least in part due to different inclusion criteria, self-monitoring regimes, and target BPs in included studies. Conclusions Self-monitoring alone is not associated with lower BP or better control, but in conjunction with co-interventions (including systematic medication titration by doctors, pharmacists, or patients; education; or lifestyle counselling) leads to clinically significant BP reduction which persists for at least 12 months. The implementation of self-monitoring in hypertension should be accompanied by such co-interventions. Background Self-monitoring of BP appears to lower BP in people with hypertension, over and above usual care. Implementation of self-monitoring has been inconsistent, perhaps because important evidence gaps remain regarding how best to use it and for which patient groups. Why was this study done? To better understand the effect of self-monitoring on BP lowering and BP control. Specifically, to examine the effect of self-monitoring in combination with various co-interventions, and in different groups of patients. What did the researchers do and find? We undertook a systematic literature search to identify all studies that included self-monitoring of BP in people with high BP. For studies published since the year 2000 with at least 6 months of follow-up data and at least 100 patients, we contacted authors to gain access to the original data collected for each individual patient (15/19 studies with the primary outcome provided data: 7,138/8,292 randomised participants). We then used these data to perform IPD meta-analysis to evaluate the effect of self-monitoring on BP levels and in the control of hypertension using 1 year of follow-up as our primary end point. We predefined levels of intensity of co-intervention and subgroups of patients for further analysis. Self-monitoring worked best when combined with more intensive interventions such as self-management, systematic medication titration, or lifestyle counselling, but had little or no effect on its own. Self-monitoring was most effective in those with fewer antihypertensive medications and higher baseline sBP up to 170 mmHg. No differences in efficacy were seen by sex or by most comorbidities. What do these findings mean? Self-monitoring can be recommended to lower BP when combined with co-interventions involving individually tailored support. Self-monitoring alone does not seem to lower BP but may be useful for other reasons including engaging with patients or reducing clinician workload. Introduction Treatment of hypertension results in significant reductions in risk of subsequent cardiovascular disease [1,2]. Despite strong evidence for such treatment, international epidemiological studies suggest that many people remain suboptimally controlled [3]. Self-monitoring of blood pressure (BP), where individuals measure their own blood pressure, usually in a home environment, can improve BP control and is an increasingly common part of hypertension management. Such monitoring can be accompanied by additional support such as from a nurse or pharmacist [4]. Self-monitoring is well tolerated by patients and has been shown to be a better predictor of end organ damage than clinic measurement [5–8]. This is despite potential issues with quality control of self-measurement such as poor technique or withholding of results [9,10]. The latter can be reduced to an extent by the use of telemonitoring [11]. Previous meta-analyses have shown that self-monitoring reduces clinic BP by a small but significant amount compared to conventional care (around 4/1.5 mmHg) [4,12–14]. Analysis by Bray and colleagues suggested that when self-monitoring was accompanied by a co-intervention, participants were more likely to meet target BP, but it remains unclear which interventions are most effective and what specific populations (if any) should be targeted [14]. The aim of this work was therefore to use individual patient data (IPD) from relevant trials to assess the effectiveness of BP self-monitoring on BP reduction and hypertension control, evaluating how best to utilise self-monitoring of BP and to determine which subpopulation is most likely to benefit. Materials and methods This study systematically reviewed the existing literature to identify randomised trials examining the efficacy of self-monitoring of BP compared to control. Authors of all eligible trials were approached for access to IPD. A protocol with detailed methods has been published previously [15]. The methods used are summarised below. Data sources and searches Medline, Embase, and the Cochrane Library were searched for trials using BP self-monitoring in hypertensive patients (S2 Fig; search date June 2016). Study selection Two reviewers (RM and KT) independently assessed the articles for eligibility and inclusion; disagreements were resolved by discussion. Randomised trials were eligible that recruited patients with hypertension being managed as outpatients using an intervention that included self-measurement of BP. Self-monitoring had to be without medical professional input (i.e., by patient with or without carer support) and using a validated monitor, with or without other co-interventions, and where a comparator group had no organised self-measurement of BP. Included studies were required to have involved at least 100 patients, followed up for at least 24 weeks, and to have been published since 2000. This was to ensure that self-monitoring equipment was likely to be relevant to contemporary medical management (i.e., automated oscillometric monitors). Relevant outcomes were systolic blood pressure (sBP) and/or diastolic blood pressure (dBP) measured in clinic, by researcher or by ambulatory measurement, and achievement of BP control. Data extraction and quality assessment Authors whose trials met the inclusion criteria were approached for provision of IPD including demographic details, comorbidities, antihypertensive medications, lifestyle factors, and BP end points (clinic and/or ambulatory). Study-level data were extracted where available from published articles and checked by the original authors. In particular, any co-interventions were carefully documented and prospectively allocated to 1 of 4 levels of interventional support based on a previous classification [4] (S1 Table). Study quality was assessed in terms of potential bias from randomisation, blinding, outcome assessment, and method of analysis using an adaptation of the Cochrane tool [16]. Original data were kept on a secure server and assembled in a consistent format for all trials. Three researchers (KT, RM, and JS) cross-checked trial details, summary measures, major outcomes, and definitions against published articles. Any apparent inconsistencies were checked with the original trial authors. Overall ethical approval was not required as this study does not include identifiable data; collaborating groups gained individual approval where required for data sharing. Data synthesis and analysis A 2-stage IPD meta-analysis was conducted using linear regression for continuous outcomes and logistic regression for proportions, aggregated across studies by random-effects inverse variance methods. Intention-to-treat comparisons of outcomes between the self-monitoring and comparator arms were summarised with forest plots using the I-squared (I2) statistic for heterogeneity. Regression models were adjusted for age, sex, baseline clinic BP, and diabetic status (the latter due to the lower BP target generally used in a diabetic population). The primary outcomes were change in sBP and dBP at 12 months and likelihood of uncontrolled BP below target at 12 months (control as defined by each trial). Analyses are reported in subgroups, by pre-specified level of self-monitoring intervention as described in Table 1 and in the published protocol [15]. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Characteristics of the included studies. https://doi.org/10.1371/journal.pmed.1002389.t001 Subgroup analyses examined the effect of self-monitoring on BP mean and control by age, sex, baseline sBP, the presence and number of antihypertensive medications prescribed, and comorbidities (myocardial infarction [MI], stroke, diabetes mellitus [DM], chronic kidney disease [CKD], and obesity [defined as a body mass index (BMI) ≥ 30 kg/m2]). All subgroup analyses were adjusted for age, sex, baseline clinic BP, level of intervention, and individual study (contributing to each analysis). Sensitivity analyses included incorporation of aggregate data from studies that did not contribute IPD [17–23], exclusion of individual patients for whom a lower home BP target was not used (due to study design or the presence of comorbidities such as diabetes) [24–27], influence of BP inclusion criteria (clinic or ambulatory) from ambulatory outcome studies, different assumptions regarding BP of patients lost to follow-up (controlled or uncontrolled), and influence of adjusting for medication changes (in those studies which recorded changes in medication). Finally, the influence of each study on the overall results was assessed using an influence analysis. Egger’s test for funnel plot asymmetry was applied to consider possible publication bias (S21 Fig) [28]. There were no deviations from the protocol [15]. Five post-hoc analyses were undertaken: firstly, an additional subgroup analysis was carried out (resistant hypertension [defined as BP > 140/90 mmHg and 3 medications at baseline or any BP level and 4 or more medications at baseline]); secondly, the distribution of baseline antihypertensive medications was compared in patients with and without a history of stroke using Pearson’s chi-squared; thirdly, the effectiveness of self-monitoring in stroke was assessed controlling for the number of baseline medications; fourthly, the influence of blinding was assessed; and finally, sBP was plotted against medication changes. Statistical software and presentation All analyses were conducted using STATA version 13.1 (MP parallel edition, StataCorp, College Station, Texas, USA), using the ipdmetan package [29]. Data are presented as proportions of the total study population, means with standard deviation or relative risk (RR) with 95% confidence intervals unless otherwise stated. Data sources and searches Medline, Embase, and the Cochrane Library were searched for trials using BP self-monitoring in hypertensive patients (S2 Fig; search date June 2016). Study selection Two reviewers (RM and KT) independently assessed the articles for eligibility and inclusion; disagreements were resolved by discussion. Randomised trials were eligible that recruited patients with hypertension being managed as outpatients using an intervention that included self-measurement of BP. Self-monitoring had to be without medical professional input (i.e., by patient with or without carer support) and using a validated monitor, with or without other co-interventions, and where a comparator group had no organised self-measurement of BP. Included studies were required to have involved at least 100 patients, followed up for at least 24 weeks, and to have been published since 2000. This was to ensure that self-monitoring equipment was likely to be relevant to contemporary medical management (i.e., automated oscillometric monitors). Relevant outcomes were systolic blood pressure (sBP) and/or diastolic blood pressure (dBP) measured in clinic, by researcher or by ambulatory measurement, and achievement of BP control. Data extraction and quality assessment Authors whose trials met the inclusion criteria were approached for provision of IPD including demographic details, comorbidities, antihypertensive medications, lifestyle factors, and BP end points (clinic and/or ambulatory). Study-level data were extracted where available from published articles and checked by the original authors. In particular, any co-interventions were carefully documented and prospectively allocated to 1 of 4 levels of interventional support based on a previous classification [4] (S1 Table). Study quality was assessed in terms of potential bias from randomisation, blinding, outcome assessment, and method of analysis using an adaptation of the Cochrane tool [16]. Original data were kept on a secure server and assembled in a consistent format for all trials. Three researchers (KT, RM, and JS) cross-checked trial details, summary measures, major outcomes, and definitions against published articles. Any apparent inconsistencies were checked with the original trial authors. Overall ethical approval was not required as this study does not include identifiable data; collaborating groups gained individual approval where required for data sharing. Data synthesis and analysis A 2-stage IPD meta-analysis was conducted using linear regression for continuous outcomes and logistic regression for proportions, aggregated across studies by random-effects inverse variance methods. Intention-to-treat comparisons of outcomes between the self-monitoring and comparator arms were summarised with forest plots using the I-squared (I2) statistic for heterogeneity. Regression models were adjusted for age, sex, baseline clinic BP, and diabetic status (the latter due to the lower BP target generally used in a diabetic population). The primary outcomes were change in sBP and dBP at 12 months and likelihood of uncontrolled BP below target at 12 months (control as defined by each trial). Analyses are reported in subgroups, by pre-specified level of self-monitoring intervention as described in Table 1 and in the published protocol [15]. Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Characteristics of the included studies. https://doi.org/10.1371/journal.pmed.1002389.t001 Subgroup analyses examined the effect of self-monitoring on BP mean and control by age, sex, baseline sBP, the presence and number of antihypertensive medications prescribed, and comorbidities (myocardial infarction [MI], stroke, diabetes mellitus [DM], chronic kidney disease [CKD], and obesity [defined as a body mass index (BMI) ≥ 30 kg/m2]). All subgroup analyses were adjusted for age, sex, baseline clinic BP, level of intervention, and individual study (contributing to each analysis). Sensitivity analyses included incorporation of aggregate data from studies that did not contribute IPD [17–23], exclusion of individual patients for whom a lower home BP target was not used (due to study design or the presence of comorbidities such as diabetes) [24–27], influence of BP inclusion criteria (clinic or ambulatory) from ambulatory outcome studies, different assumptions regarding BP of patients lost to follow-up (controlled or uncontrolled), and influence of adjusting for medication changes (in those studies which recorded changes in medication). Finally, the influence of each study on the overall results was assessed using an influence analysis. Egger’s test for funnel plot asymmetry was applied to consider possible publication bias (S21 Fig) [28]. There were no deviations from the protocol [15]. Five post-hoc analyses were undertaken: firstly, an additional subgroup analysis was carried out (resistant hypertension [defined as BP > 140/90 mmHg and 3 medications at baseline or any BP level and 4 or more medications at baseline]); secondly, the distribution of baseline antihypertensive medications was compared in patients with and without a history of stroke using Pearson’s chi-squared; thirdly, the effectiveness of self-monitoring in stroke was assessed controlling for the number of baseline medications; fourthly, the influence of blinding was assessed; and finally, sBP was plotted against medication changes. Statistical software and presentation All analyses were conducted using STATA version 13.1 (MP parallel edition, StataCorp, College Station, Texas, USA), using the ipdmetan package [29]. Data are presented as proportions of the total study population, means with standard deviation or relative risk (RR) with 95% confidence intervals unless otherwise stated. Results Of 2,846 unique studies from the combined searches, 132 were assessed in full and 36 studies were deemed potentially eligible (S1 Fig). One study which would otherwise have been eligible was excluded because the comparator group used ambulatory monitoring to guide treatment, a control intervention that had not been anticipated in the protocol but which was not comparable to any other included studies [30]. Of the 36 potentially eligible studies, 19 had published data at 12 months, the primary outcome. Authors from 24 of the potentially eligible studies provided IPD, with 1 group submitting additional data from an unpublished study. These 25 studies were published from 2005–2014, were conducted in North America and Europe (11 United States; 6 United Kingdom; 3 Italy; 1 each from the Netherlands, Australia, Spain, Finland, and Canada), and included a wide range of self-monitoring protocols, co-interventions, and populations (Table 1) [23–27,31–48]. Authors from the remaining 12 studies were either unable to provide IPD (2 studies) or did not respond to the request for data (10 studies). Four studies which followed up patients for 12 months did not provide IPD, so that data for the primary outcome were available from 15/19 studies (7,138/8,292 [86%], of potential participants) (S2 Table) [17,18,22,49]. A total of 838 patients (12%) were lost to follow-up across all included studies, and a further 227 patients from the potentially available studies were lost to follow-up, leaving 6,300/7,227 patients (87%) for inclusion in the final analysis of the primary outcome (12 months follow-up). Overall, the information from the included trials was judged to be at low risk of bias: most studies used computerised generation of randomisation sequences (23/25, 92%), appropriate allocation concealment (24/25, 96%), and all used an intention-to-treat approach with either multiple imputation for missing data or analysis of complete cases. Most studies (19/25, 76%) followed up more than 80% of participants, but only 12/25 (48%) used blinded assessment of outcome (S3 Table). An influence analysis assessed the impact of each individual study on the overall results. Included studies were predominantly publically funded (S4 Table). Clinic BP Overall, self-monitoring was associated with reduced clinic sBP between baseline and 12-months follow-up compared to usual care (systolic −3.2 mmHg, 95% CI −4.9 to −1.6 mmHg) (Fig 1). Significant heterogeneity was present between studies: I2 = 76%, P < 0.001. Self-monitoring was also associated with reduced dBP at 12-months follow-up (diastolic −1.5 mmHg, 95% CI −2.2 to −0.8 mmHg) and significant heterogeneity remained (I2 = 62%, P < 0.001) (Fig 2). Similar reductions in BP were seen after 6-months follow-up, but the point estimates after 18-months follow-up were smaller, albeit from only 5 studies (S3, S4, S6 and S7 Figs). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Impact of self-monitoring of BP on clinic sBP according to level of co-intervention support at 12 months (15 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. Effect of self-monitoring on clinic sBP at 6 and 18 months are shown in S3 and S6 Figs, respectively. Wakefield’s study participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Impact of self-monitoring of BP on clinic dBP according to level of co-intervention support at 12 months (15 studies). Change in dBP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. Effect of self-monitoring on clinic dBP at 6 and 18 months are shown in S4 and S7 Figs, respectively. Wakefield’s participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g002 Clinic BP control Clinic BP control was improved at 12-months follow-up (RR of uncontrolled BP 0.7 [95% CI 0.56 to 0.86]) again with significant heterogeneity between groups (Fig 3). Similar results were seen at 6 and 18 months (S5 and S8 Figs, respectively). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months according to level of co-intervention support (15 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. The effect of self-monitoring on the RR of BP at 6 and 18 months are displayed in S5 and S8 Figs, respectively. Wakefield study participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.g003 Intensity of co-intervention The reductions in clinic sBP varied with different levels of intervention: level 1 (with no co-intervention) −1.0 mmHg, [95% CI −3.3 to 1.2 mmHg]; level 4 (personal support throughout the trial) −6.1 mmHg, [95% CI −9.0 to −3.2 mmHg] (Fig 1) (heterogeneity in outcome between different levels of intervention P < 0.001). Within predefined categories of intensity of co-intervention, significant heterogeneity remained, apart from within level 2. A similar pattern of reductions was seen in dBP: level 1 (with no co-intervention) −1.1 mmHg, [95% CI −2.4 to 0.2 mmHg]; level 4 (personal support throughout the trial) −2.3 mmHg, [95% CI −4.0 to −0.6 mmHg] (Fig 2) (heterogeneity in outcome between different levels of intervention P < 0.001). Within predefined categories of intensity of co-intervention, significant heterogeneity remained in levels 1 and 4. BP control (defined according to individual study targets, Table 1) at 12 months also differed by level of intensity. The RR of having uncontrolled BP with a self-monitoring intervention at 12 months varied from level 1 (RR 1.0, 95% CI 0.7 to 1.4) to level 4 (RR 0.4, 95% CI 0.3 to 0.6) (Fig 3) (heterogeneity between levels of intervention P < 0.001). Heterogeneity within levels of intervention in this analysis was low for levels 2 and 4 of co-intervention, although the I2 remained above 50% for level 1. Similar results were seen at 6-months follow-up (21 studies) and at 18-months follow-up (5 studies) (S5 and S8 Figs, respectively). Ambulatory BP Four studies had data at 12 months using ambulatory BP as the outcome (1,478 participants); these were studies with no co-intervention (level 1; n = 3) or automated feedback only (level 2; n = 1). No change was seen in ambulatory sBP associated with self-monitoring (1.1 mmHg [−0.3, 2.5]) (Fig 4) or ambulatory dBP (0.8 mmHg [−0.2, 1.9]), and there was no significant heterogeneity between studies in either case (Fig 5). At 6 months, data were available for 5 studies with no difference seen in ambulatory sBP (−1.0 mmHg [−2.8, 0.9]) or dBP (−0.4 mmHg [−1.6, 0.8]) (S9 and S10 Figs, respectively). The additional study, which used a level 3–intensity intervention, increased heterogeneity as it had a significant outcome. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Impact of self-monitoring of BP on clinic and ambulatory sBP at 12 months (4 studies). These 4 studies used both clinic and ambulatory BP as endpoints and so are presented in addition to the overall results in Fig 1, which are for clinic BP alone (including these studies). Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Effect of self-monitoring on systolic clinic and ambulatory BP at 6 months is in S9 Fig. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g004 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Impact of self-monitoring of BP on clinic and ambulatory dBP at 12 months (4 studies). These 4 studies used both clinic and ambulatory BP as endpoints and so are presented in addition to the overall results in Fig 1, which are for clinic BP alone (including these studies). Change in dBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Effect of self-monitoring on diastolic clinic and ambulatory BP at 6 months is in S10 Fig. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g005 No ambulatory data were available at 18 months. Subgroup analysis Subgroup analyses using data from 12-months follow-up showed little difference in either reduction of systolic or diastolic clinic BP or likelihood of uncontrolled BP depending on history of MI or presence of CKD or diabetes (Figs 6, 7 and 8) (I2 ≤ 20% for all subgroups). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 6. Impact of self-monitoring of BP on clinic sBP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. Change in sBP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; MI, myocardial infarction; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g006 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 7. Impact of self-monitoring of BP on clinic dBP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. Change in dBP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; dBP, diastolic blood pressure; MI, myocardial infarction. https://doi.org/10.1371/journal.pmed.1002389.g007 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 8. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. RR of uncontrolled BP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; MI, myocardial infarction; RR, risk ratio; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g008 However, a history of stroke was associated with a reduced effectiveness of self-monitoring in terms of clinic sBP lowering (I2 = 77%, P = 0.04), though this difference was not observed for dBP or maintained in the likelihood of control analysis (RR I2 = 42%, P = 0.19). Post-hoc analyses showed that the distribution of number of medications between stroke and non-stroke patients was similar (S5 Table), and adjusting for baseline medication use did not explain the lack of effectiveness in patients with stroke. There was moderate heterogeneity between age groups for the effect of self-monitoring on systolic and diastolic clinic BP (I2 = 31%, P = 0.20 and I2 = 33, P = 0.19, respectively) but not in the likelihood of uncontrolled BP (I2 = 0.0%, P = 0.60). Considering the effect of obesity, there was no difference in the effect on systolic clinic BP reduction (I2 = 0, P = 0.72) but there was some evidence of heterogeneity of effect for dBP (I2 = 63, P = 0.10) and the risk of uncontrolled BP (I2 = 61%, P = 0.11). Fewer baseline antihypertensive medications were associated with larger reductions of BP and better control (Figs 6–8). Post-hoc analyses, comparing those with resistant hypertension to those without, suggested that self-monitoring was less effective at achieving BP control in the former (RR of uncontrolled BP = 0.62, 95% CI 0.54–0.71 [non-resistant hypertension] versus RR of uncontrolled BP = 0.94, 95% CI 0.65–1.36 [resistant hypertension], I2 = 76%, P = 0.04). Similarly, the post-hoc analysis plotting change in sBP against medication changes was consistent with the hypothesis that self-monitoring interventions resulted in BP decreases via increases in prescribed medication (S22 Fig). Sensitivity analysis Inclusion of aggregate data for clinic BP at 12 months from the 4 eligible studies that did not contribute IPD (S2 Table) and exclusion of studies that did not use a lower home BP threshold did not materially change the results (S11 and S12 Figs). The exclusion of studies that randomised on the basis of ambulatory BP monitoring (ABPM) or studies that randomised on clinic BP did not change the impact of clinic or ambulatory measurement of sBP at 12 months (S13 and S14 Figs). Assuming patients lost to follow-up had uncontrolled BP attenuated the results, whereas assuming that they had controlled BP accentuated them (S15 and S16 Figs, respectively). Exclusion of patients with controlled BP at baseline also accentuated the results (S17 Fig). A post-hoc comparison of studies with blinded outcome (2,829 patients) versus unblinded (3,257 patients) showed that blinding was associated with a reduced point estimate for the change in sBP at 12 months in those studies examining higher-level interventions, albeit with overlapping confidence intervals (level 1 & 2 intervention studies: −1.51, 95% CI −4.06 to 1.04 [blinded] versus −0.83, 95% CI −2.38 to 0.73 [unblinded]; level 3 & 4 intervention studies: −4.67, 95% CI −7.51 to −1.84 [blinded] versus −6.16, 95% CI −9.36 to −2.95 [unblinded]). Where studies had measured changes in antihypertensive medication over time, there was evidence of attenuation of the change in sBP when the analysis was adjusted for change in medication (S18 and S19 Figs). The influence analysis did not suggest that any one study was materially influencing the results (S20 Fig and Egger’s test found no evidence of asymmetry in the funnel plot (P = 0.9, S21 Fig). Clinic BP Overall, self-monitoring was associated with reduced clinic sBP between baseline and 12-months follow-up compared to usual care (systolic −3.2 mmHg, 95% CI −4.9 to −1.6 mmHg) (Fig 1). Significant heterogeneity was present between studies: I2 = 76%, P < 0.001. Self-monitoring was also associated with reduced dBP at 12-months follow-up (diastolic −1.5 mmHg, 95% CI −2.2 to −0.8 mmHg) and significant heterogeneity remained (I2 = 62%, P < 0.001) (Fig 2). Similar reductions in BP were seen after 6-months follow-up, but the point estimates after 18-months follow-up were smaller, albeit from only 5 studies (S3, S4, S6 and S7 Figs). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Impact of self-monitoring of BP on clinic sBP according to level of co-intervention support at 12 months (15 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. Effect of self-monitoring on clinic sBP at 6 and 18 months are shown in S3 and S6 Figs, respectively. Wakefield’s study participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Impact of self-monitoring of BP on clinic dBP according to level of co-intervention support at 12 months (15 studies). Change in dBP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. Effect of self-monitoring on clinic dBP at 6 and 18 months are shown in S4 and S7 Figs, respectively. Wakefield’s participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g002 Clinic BP control Clinic BP control was improved at 12-months follow-up (RR of uncontrolled BP 0.7 [95% CI 0.56 to 0.86]) again with significant heterogeneity between groups (Fig 3). Similar results were seen at 6 and 18 months (S5 and S8 Figs, respectively). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months according to level of co-intervention support (15 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. The trials are grouped into the 4 levels of intervention, and I2 and P values are shown for each level of intervention and for the overall analysis. The effect of self-monitoring on the RR of BP at 6 and 18 months are displayed in S5 and S8 Figs, respectively. Wakefield study participants self-monitored for 6 months; follow-up continued to 12 months. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.g003 Intensity of co-intervention The reductions in clinic sBP varied with different levels of intervention: level 1 (with no co-intervention) −1.0 mmHg, [95% CI −3.3 to 1.2 mmHg]; level 4 (personal support throughout the trial) −6.1 mmHg, [95% CI −9.0 to −3.2 mmHg] (Fig 1) (heterogeneity in outcome between different levels of intervention P < 0.001). Within predefined categories of intensity of co-intervention, significant heterogeneity remained, apart from within level 2. A similar pattern of reductions was seen in dBP: level 1 (with no co-intervention) −1.1 mmHg, [95% CI −2.4 to 0.2 mmHg]; level 4 (personal support throughout the trial) −2.3 mmHg, [95% CI −4.0 to −0.6 mmHg] (Fig 2) (heterogeneity in outcome between different levels of intervention P < 0.001). Within predefined categories of intensity of co-intervention, significant heterogeneity remained in levels 1 and 4. BP control (defined according to individual study targets, Table 1) at 12 months also differed by level of intensity. The RR of having uncontrolled BP with a self-monitoring intervention at 12 months varied from level 1 (RR 1.0, 95% CI 0.7 to 1.4) to level 4 (RR 0.4, 95% CI 0.3 to 0.6) (Fig 3) (heterogeneity between levels of intervention P < 0.001). Heterogeneity within levels of intervention in this analysis was low for levels 2 and 4 of co-intervention, although the I2 remained above 50% for level 1. Similar results were seen at 6-months follow-up (21 studies) and at 18-months follow-up (5 studies) (S5 and S8 Figs, respectively). Ambulatory BP Four studies had data at 12 months using ambulatory BP as the outcome (1,478 participants); these were studies with no co-intervention (level 1; n = 3) or automated feedback only (level 2; n = 1). No change was seen in ambulatory sBP associated with self-monitoring (1.1 mmHg [−0.3, 2.5]) (Fig 4) or ambulatory dBP (0.8 mmHg [−0.2, 1.9]), and there was no significant heterogeneity between studies in either case (Fig 5). At 6 months, data were available for 5 studies with no difference seen in ambulatory sBP (−1.0 mmHg [−2.8, 0.9]) or dBP (−0.4 mmHg [−1.6, 0.8]) (S9 and S10 Figs, respectively). The additional study, which used a level 3–intensity intervention, increased heterogeneity as it had a significant outcome. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Impact of self-monitoring of BP on clinic and ambulatory sBP at 12 months (4 studies). These 4 studies used both clinic and ambulatory BP as endpoints and so are presented in addition to the overall results in Fig 1, which are for clinic BP alone (including these studies). Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Effect of self-monitoring on systolic clinic and ambulatory BP at 6 months is in S9 Fig. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g004 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Impact of self-monitoring of BP on clinic and ambulatory dBP at 12 months (4 studies). These 4 studies used both clinic and ambulatory BP as endpoints and so are presented in addition to the overall results in Fig 1, which are for clinic BP alone (including these studies). Change in dBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Effect of self-monitoring on diastolic clinic and ambulatory BP at 6 months is in S10 Fig. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g005 No ambulatory data were available at 18 months. Subgroup analysis Subgroup analyses using data from 12-months follow-up showed little difference in either reduction of systolic or diastolic clinic BP or likelihood of uncontrolled BP depending on history of MI or presence of CKD or diabetes (Figs 6, 7 and 8) (I2 ≤ 20% for all subgroups). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 6. Impact of self-monitoring of BP on clinic sBP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. Change in sBP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; MI, myocardial infarction; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g006 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 7. Impact of self-monitoring of BP on clinic dBP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. Change in dBP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; dBP, diastolic blood pressure; MI, myocardial infarction. https://doi.org/10.1371/journal.pmed.1002389.g007 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 8. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months according to prespecified subgroups (15 studies). Obesity defined as BMI ≥ 30 kg/m2. RR of uncontrolled BP at 12 months adjusted for age, sex, baseline clinic BP, level of intervention, and studies contributing patient data. Abbreviations: BMI, body mass index; BP, blood pressure; CKD, chronic kidney disease; MI, myocardial infarction; RR, risk ratio; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.g008 However, a history of stroke was associated with a reduced effectiveness of self-monitoring in terms of clinic sBP lowering (I2 = 77%, P = 0.04), though this difference was not observed for dBP or maintained in the likelihood of control analysis (RR I2 = 42%, P = 0.19). Post-hoc analyses showed that the distribution of number of medications between stroke and non-stroke patients was similar (S5 Table), and adjusting for baseline medication use did not explain the lack of effectiveness in patients with stroke. There was moderate heterogeneity between age groups for the effect of self-monitoring on systolic and diastolic clinic BP (I2 = 31%, P = 0.20 and I2 = 33, P = 0.19, respectively) but not in the likelihood of uncontrolled BP (I2 = 0.0%, P = 0.60). Considering the effect of obesity, there was no difference in the effect on systolic clinic BP reduction (I2 = 0, P = 0.72) but there was some evidence of heterogeneity of effect for dBP (I2 = 63, P = 0.10) and the risk of uncontrolled BP (I2 = 61%, P = 0.11). Fewer baseline antihypertensive medications were associated with larger reductions of BP and better control (Figs 6–8). Post-hoc analyses, comparing those with resistant hypertension to those without, suggested that self-monitoring was less effective at achieving BP control in the former (RR of uncontrolled BP = 0.62, 95% CI 0.54–0.71 [non-resistant hypertension] versus RR of uncontrolled BP = 0.94, 95% CI 0.65–1.36 [resistant hypertension], I2 = 76%, P = 0.04). Similarly, the post-hoc analysis plotting change in sBP against medication changes was consistent with the hypothesis that self-monitoring interventions resulted in BP decreases via increases in prescribed medication (S22 Fig). Sensitivity analysis Inclusion of aggregate data for clinic BP at 12 months from the 4 eligible studies that did not contribute IPD (S2 Table) and exclusion of studies that did not use a lower home BP threshold did not materially change the results (S11 and S12 Figs). The exclusion of studies that randomised on the basis of ambulatory BP monitoring (ABPM) or studies that randomised on clinic BP did not change the impact of clinic or ambulatory measurement of sBP at 12 months (S13 and S14 Figs). Assuming patients lost to follow-up had uncontrolled BP attenuated the results, whereas assuming that they had controlled BP accentuated them (S15 and S16 Figs, respectively). Exclusion of patients with controlled BP at baseline also accentuated the results (S17 Fig). A post-hoc comparison of studies with blinded outcome (2,829 patients) versus unblinded (3,257 patients) showed that blinding was associated with a reduced point estimate for the change in sBP at 12 months in those studies examining higher-level interventions, albeit with overlapping confidence intervals (level 1 & 2 intervention studies: −1.51, 95% CI −4.06 to 1.04 [blinded] versus −0.83, 95% CI −2.38 to 0.73 [unblinded]; level 3 & 4 intervention studies: −4.67, 95% CI −7.51 to −1.84 [blinded] versus −6.16, 95% CI −9.36 to −2.95 [unblinded]). Where studies had measured changes in antihypertensive medication over time, there was evidence of attenuation of the change in sBP when the analysis was adjusted for change in medication (S18 and S19 Figs). The influence analysis did not suggest that any one study was materially influencing the results (S20 Fig and Egger’s test found no evidence of asymmetry in the funnel plot (P = 0.9, S21 Fig). Discussion Main findings Using IPD from 25 studies totalling 10,487 patients, this meta-analysis provides strong evidence that the degree of BP lowering is related to the intensity of the co-intervention (i.e., additional support) combined with self-monitoring, with little or no effect from self-monitoring alone. These results held whether systolic or diastolic clinic BP or clinic BP control were assessed and were consistent at both 6 and 12 months. No data were available from studies with intensive co-interventions which used ambulatory BP monitoring to measure outcomes at 12 months or longer, and those with little or no co-intervention showed similar effects to the clinic BP data (no effect in either case). There was a suspicion of attenuation of the effect of self-monitoring in the few studies to date that have followed up patients for longer than 1 year but data were sparse. Future research might be directed towards longer studies with ambulatory BP measurement (or other measurements to reduce the white coat effect) for outcomes. Self-monitoring appeared most effective at lowering BP in people on fewer BP medications at baseline, and there was a suggestion of a greater effect with higher BP—provided BP was not 170 mmHg or above. Analyses considering those with apparent resistant hypertension at baseline suggested that self-monitoring works less well in this group, but this analysis was not prespecified, could not take into account dose of antihypertensive medication, and should be interpreted with caution. In terms of comorbidities, the effects of self-monitoring were similar whether or not an individual had a history of MI, diabetes, or CKD. In people with previous stroke, there may be a reduced effect of self-monitoring but this did not reflect more intensive treatment prior to randomisation. Strengths and weaknesses To our knowledge, this is the first analysis of self-monitoring of BP to use IPD from a wide range of self-monitoring trials from North America, Australia, and Europe and including both specialist and primary care settings. IPD allowed for standardised adjustment of outcomes and sufficient power to detect differences between subgroups. An important issue in IPD analysis is selection of studies. The BP—SMART collaboration has gained access to a large number of datasets; nevertheless, some studies were not available due to unavailability of data or lack of response. Despite this, only 4 studies eligible for the primary outcome (14% of available patient data) were unable to provide data, and sensitivity analyses suggested no material change in the results when the published aggregate data from these studies were included. Quality of included studies was adequate in terms of randomisation sequences, appropriate allocation concealment, and analyses. Follow-up was high for most studies but only half used blinded assessment of outcome. However, a post-hoc sensitivity analysis showed no difference in results from blinding, perhaps because in most studies BP was assessed using automated monitors reducing the chance of bias. Despite the use of IPD and the division of studies into subgroups, significant heterogeneity remained, which limited the ability to do meta-analysis. However, this does not negate the conclusion that the evidence for both BP reduction and control is stronger for higher-intensity interventions and weak for self-monitoring alone. The hypothesis that effect would vary with level of intervention was prespecified and the categorisation of studies into 4 levels of intervention was agreed to by all study investigators before results were available. Whilst all included studies compared self-monitoring of BP to control groups without self-monitoring, inevitably different investigators used different protocols and therefore studies differed in inclusion criteria, self-monitoring regime, and target BPs. These issues could at least in part explain the remaining heterogeneity between studies. The exclusion of studies which did not use lower BP targets for self-monitored BP did not change the results, but even IPD analysis is unable to take differences between studies entirely into account and this may be reflected in the heterogeneity which remained. Significance tests should be interpreted with caution when, as in Figs 6 and 7, multiple coequal exposures are under test; however, the 3 P values ≤ 5% for heterogeneity across these 18 tests are unlikely to be all due to chance alone and the tests were prespecified. Most outcome data were based on clinic measurement of BP, which is what was used by the majority of trials of outcome of hypertension treatment [1]. Ambulatory monitoring might reduce any attenuation to the white coat effect from repeated habituation to measurement but, whilst 6 studies used ambulatory BP as an outcome [25,32,33,43,45] (including 1 unpublished study), all but 1 of these used less intensive or no co-interventions. The single intensive study with an ambulatory outcome had data to 6 months and a positive result, whereas the remaining 4 studies showed no impact on ambulatory BP in common with the pooled results for clinic BP. Other studies have used multiple automated BP measurements in the clinic to assess habituation and have found no evidence that the BP differences are removed when the white coat effect is reduced, though further studies examining the effects of self-monitoring with intensive co-interventions on outcomes which reduce white coat effects are arguably needed [36] [35]. Even with IPD, issues such as loss to follow-up may be important. Included studies had rates of follow-up between 58% and 98% at 12 months with most studies following-up around 90%. In the main analysis, formal methods for handling missing data were not used since methods for imputation in IPD meta-analysis are in their infancy; however, the impact of each individual study on the overall results as assessed by the influence analysis suggests that factors such as differential follow-up between studies were unlikely to have affected the results [52]. The outcomes included in this review are all related to BP. Whilst BP is directly related to stroke and coronary heart disease risk, it is nevertheless an intermediate outcome. Ideally, such hard outcomes would be directly measured in trials. However, because of relatively short follow-up and small numbers of participants, few included individual trials did so. Comparison with the previous literature There have been previous systematic reviews of trials of self-monitoring [4,13,14,53], including those focussing on specific outcomes such as adherence [54] or processes such as telemonitoring [55], but all previous analyses have relied on summary statistics rather than IPD. Compared to the most recent and comprehensive summary data review, the current study has provided pooled estimates of the effect of self-monitoring with different levels of co-intervention, suggests that self-monitoring alone has little impact on BP, and provides new evidence that the level of BP reduction is related to the intensity of the co-intervention [4]. Self-monitoring in the absence of such a co-intervention had little effect on BP. This is not to say that self-monitoring alone should be discouraged, for it brings other advantages both theoretical (better estimation of the underlying BP, increased self-efficacy for the patient) [6] and practical (increased adherence, reduced need for monitoring within the clinic, and identification of white coat and masked hypertension) [24,54]. These advantages are despite any potential inaccuracy caused by individuals not conforming to the recommended self-monitoring regime [9,10]. Obese patients had similar BP reductions to non-obese individuals but greater chance of BP control, which does not reflect differences in mean BP. The findings concerning patients with previous stroke and resistant hypertension require some caution, particularly the latter which was a post-hoc analysis, but have not been previously described. In the case of stroke, the results do not appear to be due to baseline intensity of antihypertensive treatment and warrant further study as more data become available. Meaning of the study Combining self-monitoring with increased collaboration between patient and either a nurse, physician, or pharmacist can result in important decreases in BP (6 mmHg systolic on average for the more intensive co-interventions) and improved control. The mechanisms for these reductions in BP could include lifestyle changes (no data available); increased adherence to medication (no data available) [54]; or increased prescription of medications, i.e., overcoming clinical inertia (data available from 11 studies). In order to assess the impact of enhanced medication prescription, number of medication changes was plotted against changes in BP and showed that increased numbers of medication changes were weakly correlated with reduced BP (S22 Fig). Whatever the mechanism, the literature suggests that a 6 mmHg reduction in sBP, as observed in higher-intensity interventions, would reduce subsequent stroke by more than 20% [56]. Considering the content of such interventions is an important part of decision-making in the implementation of self-monitoring. Table 1 and S1 Table describe the key characteristics of effective interventions which depend on actively intervening in terms of medication titration and/or health behaviours. Much of the effect appears to be associated with one-to-one intervention combined with medication intensification. Self-monitoring can therefore facilitate significant improvements in BP level and control but should not necessarily be seen as reducing clinical input because clinical input within the co-interventions is often required for effective BP lowering. The recent SPRINT trial results suggest that more intensive BP interventions are likely to be important in terms of morbidity and mortality [57]. Increasing the level or intensity of intervention also increases the cost of an intervention, both directly to the health provider and also in terms of patients’ time. Understanding the relative cost-effectiveness of the different co-interventions is likely to be important in deciding policy in this area and will require further work. The effects appear to be independent of age, sex, and a range of comorbidities (such as MI, CKD, diabetes, and obesity), but there was a suggestion that people receiving less intensive antihypertensive treatment, and those with the highest BPs (up to 170 mmHg systolic), may have the most to gain, presumably because they are not already receiving sufficient doses of medication. Conversely, with resistant hypertension there appeared to be little effect from self-monitoring. Similar results for stroke should be interpreted cautiously and warrant further study. The data presented appear to indicate a potential attenuation of the beneficial effects of self-monitoring over time (see S6, S7 and S8 Figs). We believe that the key issue is a need for longer studies (at least 2 years, and preferably 5 years or more) that are accompanied by investigation of how best to administer a self-monitoring—based intervention in the long term, including whether it should be perhaps “topped up” with additional training over time. Finally, we know from the individual trials that only a proportion of those with hypertension will be suitable for self-monitoring. Despite this, the numbers of people with hypertension and access to their own BP monitor are likely to be well into the tens of millions internationally and represent an important population to engage with [58,59]. Future research Several unanswered questions remain. Ultimately, trials including cardiovascular endpoints would provide the strongest evidence for self-monitoring in the management of hypertension but may not be appropriate given the strong evidence linking BP to outcome. Further consideration of self-monitoring in the presence of comorbidities seems warranted, particularly for stroke. Furthermore, this review has not included economic outcomes (available from 6 of the included studies) or quality of life measures (available in 8 of the included studies), and these outcomes form part of the next series of investigations for this collaboration. Conclusions Self-monitoring of BP combined with co-interventions involving individually tailored support lowers clinic BP but has little effect on its own. Self-monitoring supported by such co-interventions should be recommended as part of routine clinical practice in international guidelines and further research should determine the most cost-effective means of supporting implementation. Main findings Using IPD from 25 studies totalling 10,487 patients, this meta-analysis provides strong evidence that the degree of BP lowering is related to the intensity of the co-intervention (i.e., additional support) combined with self-monitoring, with little or no effect from self-monitoring alone. These results held whether systolic or diastolic clinic BP or clinic BP control were assessed and were consistent at both 6 and 12 months. No data were available from studies with intensive co-interventions which used ambulatory BP monitoring to measure outcomes at 12 months or longer, and those with little or no co-intervention showed similar effects to the clinic BP data (no effect in either case). There was a suspicion of attenuation of the effect of self-monitoring in the few studies to date that have followed up patients for longer than 1 year but data were sparse. Future research might be directed towards longer studies with ambulatory BP measurement (or other measurements to reduce the white coat effect) for outcomes. Self-monitoring appeared most effective at lowering BP in people on fewer BP medications at baseline, and there was a suggestion of a greater effect with higher BP—provided BP was not 170 mmHg or above. Analyses considering those with apparent resistant hypertension at baseline suggested that self-monitoring works less well in this group, but this analysis was not prespecified, could not take into account dose of antihypertensive medication, and should be interpreted with caution. In terms of comorbidities, the effects of self-monitoring were similar whether or not an individual had a history of MI, diabetes, or CKD. In people with previous stroke, there may be a reduced effect of self-monitoring but this did not reflect more intensive treatment prior to randomisation. Strengths and weaknesses To our knowledge, this is the first analysis of self-monitoring of BP to use IPD from a wide range of self-monitoring trials from North America, Australia, and Europe and including both specialist and primary care settings. IPD allowed for standardised adjustment of outcomes and sufficient power to detect differences between subgroups. An important issue in IPD analysis is selection of studies. The BP—SMART collaboration has gained access to a large number of datasets; nevertheless, some studies were not available due to unavailability of data or lack of response. Despite this, only 4 studies eligible for the primary outcome (14% of available patient data) were unable to provide data, and sensitivity analyses suggested no material change in the results when the published aggregate data from these studies were included. Quality of included studies was adequate in terms of randomisation sequences, appropriate allocation concealment, and analyses. Follow-up was high for most studies but only half used blinded assessment of outcome. However, a post-hoc sensitivity analysis showed no difference in results from blinding, perhaps because in most studies BP was assessed using automated monitors reducing the chance of bias. Despite the use of IPD and the division of studies into subgroups, significant heterogeneity remained, which limited the ability to do meta-analysis. However, this does not negate the conclusion that the evidence for both BP reduction and control is stronger for higher-intensity interventions and weak for self-monitoring alone. The hypothesis that effect would vary with level of intervention was prespecified and the categorisation of studies into 4 levels of intervention was agreed to by all study investigators before results were available. Whilst all included studies compared self-monitoring of BP to control groups without self-monitoring, inevitably different investigators used different protocols and therefore studies differed in inclusion criteria, self-monitoring regime, and target BPs. These issues could at least in part explain the remaining heterogeneity between studies. The exclusion of studies which did not use lower BP targets for self-monitored BP did not change the results, but even IPD analysis is unable to take differences between studies entirely into account and this may be reflected in the heterogeneity which remained. Significance tests should be interpreted with caution when, as in Figs 6 and 7, multiple coequal exposures are under test; however, the 3 P values ≤ 5% for heterogeneity across these 18 tests are unlikely to be all due to chance alone and the tests were prespecified. Most outcome data were based on clinic measurement of BP, which is what was used by the majority of trials of outcome of hypertension treatment [1]. Ambulatory monitoring might reduce any attenuation to the white coat effect from repeated habituation to measurement but, whilst 6 studies used ambulatory BP as an outcome [25,32,33,43,45] (including 1 unpublished study), all but 1 of these used less intensive or no co-interventions. The single intensive study with an ambulatory outcome had data to 6 months and a positive result, whereas the remaining 4 studies showed no impact on ambulatory BP in common with the pooled results for clinic BP. Other studies have used multiple automated BP measurements in the clinic to assess habituation and have found no evidence that the BP differences are removed when the white coat effect is reduced, though further studies examining the effects of self-monitoring with intensive co-interventions on outcomes which reduce white coat effects are arguably needed [36] [35]. Even with IPD, issues such as loss to follow-up may be important. Included studies had rates of follow-up between 58% and 98% at 12 months with most studies following-up around 90%. In the main analysis, formal methods for handling missing data were not used since methods for imputation in IPD meta-analysis are in their infancy; however, the impact of each individual study on the overall results as assessed by the influence analysis suggests that factors such as differential follow-up between studies were unlikely to have affected the results [52]. The outcomes included in this review are all related to BP. Whilst BP is directly related to stroke and coronary heart disease risk, it is nevertheless an intermediate outcome. Ideally, such hard outcomes would be directly measured in trials. However, because of relatively short follow-up and small numbers of participants, few included individual trials did so. Comparison with the previous literature There have been previous systematic reviews of trials of self-monitoring [4,13,14,53], including those focussing on specific outcomes such as adherence [54] or processes such as telemonitoring [55], but all previous analyses have relied on summary statistics rather than IPD. Compared to the most recent and comprehensive summary data review, the current study has provided pooled estimates of the effect of self-monitoring with different levels of co-intervention, suggests that self-monitoring alone has little impact on BP, and provides new evidence that the level of BP reduction is related to the intensity of the co-intervention [4]. Self-monitoring in the absence of such a co-intervention had little effect on BP. This is not to say that self-monitoring alone should be discouraged, for it brings other advantages both theoretical (better estimation of the underlying BP, increased self-efficacy for the patient) [6] and practical (increased adherence, reduced need for monitoring within the clinic, and identification of white coat and masked hypertension) [24,54]. These advantages are despite any potential inaccuracy caused by individuals not conforming to the recommended self-monitoring regime [9,10]. Obese patients had similar BP reductions to non-obese individuals but greater chance of BP control, which does not reflect differences in mean BP. The findings concerning patients with previous stroke and resistant hypertension require some caution, particularly the latter which was a post-hoc analysis, but have not been previously described. In the case of stroke, the results do not appear to be due to baseline intensity of antihypertensive treatment and warrant further study as more data become available. Meaning of the study Combining self-monitoring with increased collaboration between patient and either a nurse, physician, or pharmacist can result in important decreases in BP (6 mmHg systolic on average for the more intensive co-interventions) and improved control. The mechanisms for these reductions in BP could include lifestyle changes (no data available); increased adherence to medication (no data available) [54]; or increased prescription of medications, i.e., overcoming clinical inertia (data available from 11 studies). In order to assess the impact of enhanced medication prescription, number of medication changes was plotted against changes in BP and showed that increased numbers of medication changes were weakly correlated with reduced BP (S22 Fig). Whatever the mechanism, the literature suggests that a 6 mmHg reduction in sBP, as observed in higher-intensity interventions, would reduce subsequent stroke by more than 20% [56]. Considering the content of such interventions is an important part of decision-making in the implementation of self-monitoring. Table 1 and S1 Table describe the key characteristics of effective interventions which depend on actively intervening in terms of medication titration and/or health behaviours. Much of the effect appears to be associated with one-to-one intervention combined with medication intensification. Self-monitoring can therefore facilitate significant improvements in BP level and control but should not necessarily be seen as reducing clinical input because clinical input within the co-interventions is often required for effective BP lowering. The recent SPRINT trial results suggest that more intensive BP interventions are likely to be important in terms of morbidity and mortality [57]. Increasing the level or intensity of intervention also increases the cost of an intervention, both directly to the health provider and also in terms of patients’ time. Understanding the relative cost-effectiveness of the different co-interventions is likely to be important in deciding policy in this area and will require further work. The effects appear to be independent of age, sex, and a range of comorbidities (such as MI, CKD, diabetes, and obesity), but there was a suggestion that people receiving less intensive antihypertensive treatment, and those with the highest BPs (up to 170 mmHg systolic), may have the most to gain, presumably because they are not already receiving sufficient doses of medication. Conversely, with resistant hypertension there appeared to be little effect from self-monitoring. Similar results for stroke should be interpreted cautiously and warrant further study. The data presented appear to indicate a potential attenuation of the beneficial effects of self-monitoring over time (see S6, S7 and S8 Figs). We believe that the key issue is a need for longer studies (at least 2 years, and preferably 5 years or more) that are accompanied by investigation of how best to administer a self-monitoring—based intervention in the long term, including whether it should be perhaps “topped up” with additional training over time. Finally, we know from the individual trials that only a proportion of those with hypertension will be suitable for self-monitoring. Despite this, the numbers of people with hypertension and access to their own BP monitor are likely to be well into the tens of millions internationally and represent an important population to engage with [58,59]. Future research Several unanswered questions remain. Ultimately, trials including cardiovascular endpoints would provide the strongest evidence for self-monitoring in the management of hypertension but may not be appropriate given the strong evidence linking BP to outcome. Further consideration of self-monitoring in the presence of comorbidities seems warranted, particularly for stroke. Furthermore, this review has not included economic outcomes (available from 6 of the included studies) or quality of life measures (available in 8 of the included studies), and these outcomes form part of the next series of investigations for this collaboration. Conclusions Self-monitoring of BP combined with co-interventions involving individually tailored support lowers clinic BP but has little effect on its own. Self-monitoring supported by such co-interventions should be recommended as part of routine clinical practice in international guidelines and further research should determine the most cost-effective means of supporting implementation. Supporting information S1 PRISMA Checklist. PRISMA checklist. https://doi.org/10.1371/journal.pmed.1002389.s001 (DOC) S1 Text. The protocol paper published by the BMJ Open (available at http://bmjopen.bmj.com/content/bmjopen/5/9/e008532.full.pdf). https://doi.org/10.1371/journal.pmed.1002389.s002 (PDF) S1 Table. Levels of self-monitoring intervention. Levels used to describe the included self-monitoring interventions. * 1:1 contact or support in this context refers to contact over and above that in usual care. Abbreviation: BP, blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s003 (DOCX) S2 Table. Studies not included in the IPD analysis. *Data were available from trials including 7,138/8,292 (86%) of patients randomised. +Data at 6 months follow-up were available from 8,563/12,822 (67%) of patients randomised. Abbreviation: IPD, individual patient data. https://doi.org/10.1371/journal.pmed.1002389.s004 (DOCX) S3 Table. Assessment of bias. *Due to the nature of the intervention, the participants in all studies were aware that they were in the self-monitoring group. https://doi.org/10.1371/journal.pmed.1002389.s005 (DOCX) S4 Table. Funding provided to the included studies. Table showing the funding of the included studies. https://doi.org/10.1371/journal.pmed.1002389.s006 (DOCX) S5 Table. Distribution of baseline medications by history of stroke. https://doi.org/10.1371/journal.pmed.1002389.s007 (DOCX) S1 Fig. Flow diagram of the systematic search and selection of relevant studies. Flow diagram of the systematic review and selection of studies for the IPD. https://doi.org/10.1371/journal.pmed.1002389.s008 (DOCX) S2 Fig. Example search strategy. An example search from Medline. https://doi.org/10.1371/journal.pmed.1002389.s009 (DOCX) S3 Fig. Impact of self-monitoring of BP on clinic sBP according to level of co-intervention support at 6 months (21 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s010 (TIF) S4 Fig. Impact of self-monitoring of BP on clinic dBP according to level of co-intervention support at 6 months (21 studies). Change in dBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s011 (TIF) S5 Fig. Impact of self-monitoring of BP on the RR of uncontrolled BP at 6 months according to level of co-intervention support (21 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.s012 (TIF) S6 Fig. Impact of self-monitoring of BP on clinic sBP according to level of co-intervention support at 18 months (5 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s013 (TIF) S7 Fig. Impact of self-monitoring of BP on clinic dBP according to level of co-intervention support at 18 months (5 studies). Change in dBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s014 (TIF) S8 Fig. Impact of self-monitoring of BP on the RR of uncontrolled BP at 18 months according to level of co-intervention support (5 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.s015 (TIF) S9 Fig. Impact of self-monitoring of BP on clinic and ambulatory sBP at 6 months. Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s016 (TIF) S10 Fig. Impact of self-monitoring of BP on clinic and ambulatory dBP at 6 months. Change in dBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Abbreviations: BP, blood pressure; dBP, diastolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s017 (TIF) S11 Fig. Change in sBP at 12 months including aggregate data from studies which did not contribute IPD for the primary analysis (19 studies). *Four studies containing aggregate data only: Varis et al. [17], Rinfret et al. [22], Artinian et al. [18], and Kim et al. [49]. Change in sBP from studies contributing IPD adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: IPD, individual patient data; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s018 (TIF) S12 Fig. Primary analyses excluding all studies* which did not use a home BP threshold which was lower than clinic BP. Change in sBP at 12 months. *Patients from TASMINH1 (Verberk et al. [25] and McManus et al. [24]) and diabetics from HINTS (Bosworth et al. [26]) and TCYB (Bosworth et al. [27]) all excluded. Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s019 (TIF) S13 Fig. Primary analyses (ABPM) excluding all studies which randomised patients on the basis of ABPM. Change in sBP at 12 months. Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Abbreviations: ABPM, ambulatory blood pressure monitoring; BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s020 (TIFF) S14 Fig. Primary analyses (ABPM) excluding all studies which randomised patients on the basis of clinic BP. Change in sBP at 12 months. Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and level of intervention. Abbreviations: ABPM, ambulatory blood pressure monitoring; BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s021 (TIFF) S15 Fig. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months, with patients lost to follow-up assumed to have controlled BP (15 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.s022 (TIF) S16 Fig. Impact of self-monitoring of BP on the RR of uncontrolled BP at 12 months, with patients lost to follow-up assumed to have uncontrolled BP (15 studies). RR of uncontrolled BP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; RR, relative risk. https://doi.org/10.1371/journal.pmed.1002389.s023 (TIF) S17 Fig. Impact of self-monitoring of BP on clinic sBP at 12 months, with patients who had controlled BP at baseline excluded (15 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s024 (TIF) S18 Fig. Studies which measured change in medication at follow-up. sBP change at 12 months analysed without adjusting for medication changes at follow-up (11 studies). Change in sBP adjusted for age, sex, baseline clinic BP, and history of diabetes. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s025 (TIF) S19 Fig. Studies which measured change in medication at follow-up. sBP change at 12 months analysed adjusting for medication changes at follow-up (11 studies). Change in sBP adjusted for age, sex, baseline clinic BP, history of diabetes, and medication changes at 12 months follow-up. Abbreviations: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s026 (TIF) S20 Fig. Influence analysis presenting the pooled estimate of mean change in sBP at 12 months with each individual study omitted from the meta-analysis in turn. Each line indicates pooled meta-analysis results with that study omitted from the results. Abbreviation: sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s027 (TIFF) S21 Fig. Funnel plot showing mean change in sBP at 12 months. The standard error is plotted against the mean change in sBP at 12 months. An Egger’s test of zero (P = 1.00) would indicate little influence of publication bias. Abbreviation: sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s028 (TIFF) S22 Fig. sBP change plotted against medication changes at 12 months follow-up, by level of intervention (11 studies). *Test for trend using a fixed-effects linear regression model adjusted for study. †The HOMERUS and TCYB trials, and studies by Godwin et al. [43] and Leiva et al. [46], were excluded due to missing data on medication changes at follow-up. Results where a negative change in BP is associated with a positive change in number of medications suggest medication intensification may be related to improved BP at 12 months. Abbreviation: BP, blood pressure; sBP, systolic blood pressure. https://doi.org/10.1371/journal.pmed.1002389.s029 (TIFF) S23 Fig. The STATA code used for the meta-analysis. The STATA code used to perform the meta-analysis and figures. https://doi.org/10.1371/journal.pmed.1002389.s030 (DOCX) Acknowledgments The authors would like to thank Felicia McCant, MSSW (Durham, NC VA Medical Center, Durham, USA); Steve Asche, MA (HealthPartners Institute for Education and Research, Minneapolis, USA); Leah Tuzzio, MPH (Group Health Research Institute, Seattle, USA); Mark Butler, MA (Center for Healthful Behavior Change, New York, USA); Melissa L. Anderson, MS (Group Health Research Institute, Seattle, USA); Nichole Wagner, MPH (Institute for Health Research, Colorado, USA); and Shadi Chamany (New York City Department of Health & Mental Hygiene, New York, USA) for helping with data formatting and data queries. The views expressed are those of the author(s) and not necessarily those of the NIHR, the NHS, or the Department of Health.

doi: 10.1371/journal.pmed.1002390pmid: 28949973

Background Neonatal respiratory distress syndrome, as a consequence of preterm birth, is a major cause of early mortality and morbidity. The withdrawal of progesterone, either actual or functional, is thought to be an antecedent to the onset of labour. There remains limited information on clinically relevant health outcomes as to whether vaginal progesterone may be of benefit for pregnant women with a history of a previous preterm birth, who are at high risk of a recurrence. Our primary aim was to assess whether the use of vaginal progesterone pessaries in women with a history of previous spontaneous preterm birth reduced the risk and severity of respiratory distress syndrome in their infants, with secondary aims of examining the effects on other neonatal morbidities and maternal health and assessing the adverse effects of treatment. Methods Women with a live singleton or twin pregnancy between 18 to <24 weeks’ gestation and a history of prior preterm birth at less than 37 weeks’ gestation in the preceding pregnancy, where labour occurred spontaneously or in association with cervical incompetence or following preterm prelabour rupture of the membranes, were eligible. Women were recruited from 39 Australian, New Zealand, and Canadian maternity hospitals and assigned by randomisation to vaginal progesterone pessaries (equivalent to 100 mg vaginal progesterone) (n = 398) or placebo (n = 389). Participants and investigators were masked to the treatment allocation. The primary outcome was respiratory distress syndrome and severity. Secondary outcomes were other respiratory morbidities; other adverse neonatal outcomes; adverse outcomes for the woman, especially related to preterm birth; and side effects of progesterone treatment. Data were analysed for all the 787 women (100%) randomised and their 799 infants. Findings Most women used their allocated study treatment (740 women, 94.0%), with median use similar for both study groups (51.0 days, interquartile range [IQR] 28.0–69.0, in the progesterone group versus 52.0 days, IQR 27.0–76.0, in the placebo group). The incidence of respiratory distress syndrome was similar in both study groups—10.5% (42/402) in the progesterone group and 10.6% (41/388) in the placebo group (adjusted relative risk [RR] 0.98, 95% confidence interval [CI] 0.64–1.49, p = 0.912)—as was the severity of any neonatal respiratory disease (adjusted treatment effect 1.02, 95% CI 0.69–1.53, p = 0.905). No differences were seen between study groups for other respiratory morbidities and adverse infant outcomes, including serious infant composite outcome (155/406 [38.2%] in the progesterone group and 152/393 [38.7%] in the placebo group, adjusted RR 0.98, 95% CI 0.82–1.17, p = 0.798). The proportion of infants born before 37 weeks’ gestation was similar in both study groups (148/406 [36.5%] in the progesterone group and 146/393 [37.2%] in the placebo group, adjusted RR 0.97, 95% CI 0.81–1.17, p = 0.765). A similar proportion of women in both study groups had maternal morbidities, especially those related to preterm birth, or experienced side effects of treatment. In 9.9% (39/394) of the women in the progesterone group and 7.3% (28/382) of the women in the placebo group, treatment was stopped because of side effects (adjusted RR 1.35, 95% CI 0.85–2.15, p = 0.204). The main limitation of the study was that almost 9% of the women did not start the medication or forgot to use it 3 or more times a week. Conclusions Our results do not support the use of vaginal progesterone pessaries in women with a history of a previous spontaneous preterm birth to reduce the risk of neonatal respiratory distress syndrome or other neonatal and maternal morbidities related to preterm birth. Individual participant data meta-analysis of the relevant trials may identify specific women for whom vaginal progesterone might be of benefit. Trial registration Current Clinical Trials ISRCTN20269066. Why was the study done? Prevention of preterm birth remains a global challenge. Vaginal progesterone has been suggested to reduce the incidence of preterm birth in women at risk, but there has been limited assessment of the effects on relevant neonatal morbidity. The aim of our trial was to assess whether vaginal progesterone pessaries in pregnant women with a history of previous spontaneous preterm birth reduced the risk and severity of respiratory distress syndrome, other neonatal morbidities, and maternal health outcomes and if there were any side effects of treatment. What did the researchers do and find? Seven hundred and eighty-seven women were randomly allocated to receive vaginal progesterone or placebo from between 20 to 24 weeks’ to 34 weeks’ gestation. The rate of respiratory distress syndrome amongst infants in both treatment groups was similar, as were the outcomes for other respiratory measures and adverse outcomes. Maternal health outcomes and side effects of treatment were also similar between treatment groups. What do these findings mean? Vaginal progesterone pessaries did not reduce the risk of respiratory distress syndrome compared to placebo vaginal pessaries. Vaginal progesterone pessaries cannot be recommended in women with a history of previous preterm birth to reduce infant or maternal morbidity associated with any recurrence. These results provide robust evidence for health practitioners and consumers to make informed clinical decisions. Introduction The prevention of preterm birth remains a global challenge [1]. Women who have had a previous preterm birth have over twice the risk of giving birth preterm in a subsequent pregnancy [2,3,4]. Babies born preterm are at increased risk of respiratory distress syndrome as a result of immature lung development, and this is a major cause of their early neonatal mortality and morbidity [5] as well as long-term morbidity [6,7]. Progesterone has an important role in uterine quiescence [8,9] and is essential for the maintenance of pregnancy through multiple and complex mechanisms [10,11,12]. An initial systematic review of studies from the 1960s showed that use of progesterone may prevent preterm birth [13]. Over the last decade, there has been renewed interest in the use of vaginal progesterone in pregnancy to prevent recurrence of preterm birth, with several published trials included in the Cochrane systematic review [14]. Some trials suggest that use of vaginal progesterone reduces the risk of preterm birth [15], whilst others do not [16]. This has led to considerable debate and differences in clinical practice recommendations [17,18,19,20]. At the time of planning our trial, there were 2 published clinical trials with relatively small sample sizes that included women with a previous history of preterm birth, and these studies had shown a reduction in preterm birth with the use of both natural vaginal progesterone [15] and intramuscular injection of 17 OH progesterone, a synthetic progestogen [21]. However, intramuscular 17 alpha-hydroxyprogesterone caproate is not available for use in some countries, including Australia and New Zealand. Whilst a reduction in preterm birth may seem beneficial, prolongation of gestation may not lead to health benefits, so it also is important to know the effects on neonatal morbidities, such as respiratory distress syndrome and its sequelae, and on maternal health outcomes. The primary aim of the PROGRESS randomised, placebo-controlled trial was therefore to assess whether the use of vaginal progesterone pessaries in pregnant women with a history of previous spontaneous preterm birth reduced the risk and severity of respiratory distress syndrome, thus improving the infant’s health. The secondary aims were to examine the effects on other respiratory outcomes; other neonatal morbidities; and maternal health outcomes, especially those related to preterm birth; and to assess any side effects of treatment. Methods Design and participants We conducted a multicentre, placebo-blinded, randomised controlled trial at 39 Australian, New Zealand, and Canadian maternity hospitals. This study is reported as per CONSORT guidelines (S1 Text). The study was approved by the Children’s Youth and Women’s Health Services Human Research Ethics Committee at the Women’s and Children’s Hospital, Adelaide, Australia (approval record number HREC 2006015), and by the ethics committee at each of the 39 collaborating centres (32 in Australia, 5 in New Zealand, and 2 in Canada). Women were eligible if they had a live singleton or twin pregnancy between 18 and <24 weeks’ gestation and a history of prior preterm birth (either vaginal birth or caesarean birth) at greater than 20 weeks’ gestation and less than 37 weeks’ gestation in their preceding pregnancy where the onset of labour occurred spontaneously or in association with cervical incompetence or following preterm prelabour rupture of membranes. If the women had received progesterone therapy prior to 16 weeks’ gestation, they remained eligible. The protocol for this study has been published [22] (S2 Text). Women were ineligible if their preceding preterm birth at less than 37 weeks’ gestation was associated with placental abruption or placenta praevia, if it was a multiple pregnancy, or if there had been an iatrogenic decision for early birth, for example, related to fetal distress or preeclampsia. Women were ineligible if their current pregnancy, at consideration for trial entry, was associated with active vaginal bleeding requiring hospital admission at 18 weeks’ gestation or more, preterm prelabour rupture of membranes, active labour (defined as the presence of uterine activity and cervical dilatation greater than 3 cm), known lethal fetal anomaly or fetal demise, progesterone treatment after 16 weeks’ gestation, or any contraindication to continuation of the pregnancy, such as chorioamnionitis requiring delivery, or contraindication to progesterone therapy (known active liver disease, active or hormone-related thrombophlebitis or thromboembolic disorder, or breast or genital malignancy). The PROGRESS Study protocol did not include the need for cervical length measurement at trial entry or during the pregnancy. The clinician responsible for care of the participant decided whether cervical length screening was undertaken. The study was approved by the Children’s Youth and Women’s Health Services Human Research Ethics Committee at the Women’s and Children’s Hospital, Adelaide, Australia, and by the ethics committee at each of the 39 collaborating centres (33 in Australia, 4 in New Zealand and 2 in Canada). Eligible women were provided with written information about the study in the antenatal clinic, counselled by 1 member of the research team, and asked if they would participate. Recruitment started in February 2006 and was completed in September 2012. Randomisation Women who gave written informed consent were randomly assigned to either ‘progesterone’ or 'placebo’ using a central telephone randomisation service. The randomisation schedule, prepared by an investigator not involved with clinical care, used balanced variable blocks with stratification by plurality of the pregnancy (singleton versus twin versus triplet) and collaborating centre. Participants, staff, and investigators were masked to study group allocation, and treatment packs appeared identical. The baseline information collected included maternal age, parity, ethnicity, body mass index, plurality, gestational age at trial entry, gestational age, and reason for the previous preterm birth. Intervention and outcomes Progesterone group and placebo group. Women randomised to the progesterone and placebo groups were allocated a study number that corresponded to a treatment pack containing the allocated study treatment. Depending on the study treatment allocation, the treatment packs contained either a 14-week supply of progesterone pessaries (equivalent to 100 mg vaginal progesterone as active substance in hard fat) or similar-appearing placebo pessaries (in hard fat) bought for the study from Orion Laboratories, Western Australia. The manufacturer of the pessaries had no other involvement in the study. Women were asked to self-administer a vaginal pessary each evening from 20 weeks’ gestation, or from randomisation if this occurred after 20 weeks’ gestation, until birth or 34 weeks’ gestation, whichever occurred first. The maximum number of days treatment could be used for was 98 days. Women were reviewed in the antenatal clinic by the practitioner responsible for their care. Women who presented with preterm prelabour rupture of the membranes after trial entry were advised to discontinue using the vaginal pessaries to reduce the risk of introducing infection. In the event of the development of serious depression or a medical condition that may have been aggravated by fluid retention (asthma, epilepsy, migraine, known cardiac dysfunction, or known renal dysfunction), the clinician was to advise the woman to cease using the trial medication if he or she felt it would be in the woman’s best interests to do so. At 34 weeks’ gestation, women were asked to complete a questionnaire that assessed health-related quality of life [23], anxiety [24], and depression [25] and asked about any side effects they may have experienced and their compliance with the treatment protocol. After birth, information relating to birth, maternal and infant health, and care was collected from the woman's and infant's case notes by trained research assistants. Study outcomes Primary outcome. The primary outcome was the incidence of neonatal respiratory distress syndrome (defined as increasing respiratory distress or oxygen requirement or the need for respiratory support from the first 6 hours of life) and severity of neonatal respiratory disease (defined as mild = mean airway pressure [MAP] < 7 cm H2O and/or fractional inspired oxygen [FiO2] < 0.4; moderate = MAP 7–9.9 cm H2O and/or FiO2 0.40–0.79; severe = MAP ≥ 10 cm H2O, and/or FiO2 ≥ 0.80 with need for ventilation). Secondary outcomes for the child. The secondary outcomes for the child were as follows: other respiratory measures, which included the need for and duration of oxygen therapy (including highest FiO2 [%] within 12 hours of birth), need for and duration of mechanical ventilation (including maximum peak pressure [cm H2O] within 12 hours of birth), need for surfactant therapy, nitric oxide for respiratory support, air leak syndrome, and chronic lung disease (defined as the need for any respiratory support, supplemental oxygen, or intermittent positive pressure ventilation or continuous positive airways pressure for a chronic pulmonary disorder on the day the baby reached 36 weeks’ postmenstrual age for infants born before 32 weeks’ gestation, or continued oxygen requirement at 28 days of age for infants born after 36 weeks’ gestation) and a composite adverse outcome for the infant that included 1 or more of the following: preterm birth (defined as birth at less than 37 weeks’ gestation), perinatal mortality (defined as either a stillbirth [intrauterine fetal death after trial entry and prior to birth] or infant death [death of a live-born infant prior to hospital discharge] and excluding lethal congenital anomalies), severe respiratory disease, chronic lung disease, Apgar score < 4 at 5 minutes of age, birth weight less than the third centile for gestational age at birth and infant sex, intraventricular haemorrhage on early cranial ultrasound, periventricular leucomalacia on later cranial ultrasound, inotropic support for the treatment of patent ductus arteriosus, proven necrotising enterocolitis, proven systemic infection within 48 hours of birth treated with antibiotics, and retinopathy of prematurity. Secondary study outcomes for the mother. The secondary study outcomes for the mother were as follows: significant health outcomes, particularly related to preterm birth, such as use of tocolytic therapy or antenatal corticosteroid therapy, defined by 1 or more of the following: maternal death, antepartum haemorrhage, pre-eclampsia, preterm prelabour rupture of membranes, prelabour ruptured membranes at or near term (defined as prelabour rupture of membranes after 36 weeks’ gestation), chorioamnionitis requiring antibiotic use during labour, postpartum haemorrhage, or antibiotic use after birth; length of any antenatal hospital stay or postnatal stay and psychological health (assessed by quality of life [23], anxiety [24], and depression [25]); and side effects of progesterone supplementation (including headache, nausea, pain and discomfort, breast tenderness, and coughing) and if any of them were sufficient to stop treatment. Statistical methods Primary analyses were performed on an intention-to-treat basis, according to the study group allocated at randomisation. As prespecified, unadjusted analyses were performed and then adjusted for the potential confounders of gestational age at randomisation, gestational age of the previous preterm birth, and reason for the previous preterm birth. Binary outcomes were analysed using log binomial regression, with treatment effects expressed as relative risk (RR) with 95% confidence interval (CI), or Fisher’s exact tests with no adjustment for covariates in the case of rare outcomes. Outcomes measured on a continuous scale were analysed using linear regression, with treatment effects expressed as differences in means. Count outcomes were analysed using Poisson regression or negative binomial regression where overdispersion was present, with treatment effects expressed as ratios of means. Ordinal outcomes were analysed using proportional odds models, with treatment effects expressed as odds ratios of higher severity. For infant outcomes, clustering due to multiple births was taken into account using generalised estimating equations. Statistical significance was assessed at the 2-sided p < 0.05 level, and no adjustment was made for multiple comparisons. No adjustments were made for the 2 primary outcomes, as they were considered strongly related and expected to provide complementary information [26]. All analyses followed a prespecified statistical analysis plan and were performed using SAS software version 9.3 (SAS Institute, Cary, North Carolina, United States). Sample size. We originally estimated that a sample size of 984 women would be able to show a 40% reduction in neonatal respiratory distress syndrome from 15% to 9% with progesterone supplementation (5% level of significance, 2-tailed alpha, 80% power, 4% loss to follow-up) based upon data from a randomised trial with similar eligibility profile when this trial commenced [21]. In 2009, because of slower than anticipated accrual, we applied for additional funding to complete the study. At this time, the Trial Steering Group asked the following questions of an independent review: (1) ‘Should recruitment stop (because of a significant result or futility)?’ (2) ‘Should we continue recruiting to reach our previous sample size?’ and (3) ‘Does the sample size need refining based on the interim assessment?’ The Trial Steering Group did not see the interim data or the analyses. The independent review undertaken, masked to treatment group, made the following recommendations to the Trial Steering Group: to continue recruitment and to reduce the sample size to 784 women. Design and participants We conducted a multicentre, placebo-blinded, randomised controlled trial at 39 Australian, New Zealand, and Canadian maternity hospitals. This study is reported as per CONSORT guidelines (S1 Text). The study was approved by the Children’s Youth and Women’s Health Services Human Research Ethics Committee at the Women’s and Children’s Hospital, Adelaide, Australia (approval record number HREC 2006015), and by the ethics committee at each of the 39 collaborating centres (32 in Australia, 5 in New Zealand, and 2 in Canada). Women were eligible if they had a live singleton or twin pregnancy between 18 and <24 weeks’ gestation and a history of prior preterm birth (either vaginal birth or caesarean birth) at greater than 20 weeks’ gestation and less than 37 weeks’ gestation in their preceding pregnancy where the onset of labour occurred spontaneously or in association with cervical incompetence or following preterm prelabour rupture of membranes. If the women had received progesterone therapy prior to 16 weeks’ gestation, they remained eligible. The protocol for this study has been published [22] (S2 Text). Women were ineligible if their preceding preterm birth at less than 37 weeks’ gestation was associated with placental abruption or placenta praevia, if it was a multiple pregnancy, or if there had been an iatrogenic decision for early birth, for example, related to fetal distress or preeclampsia. Women were ineligible if their current pregnancy, at consideration for trial entry, was associated with active vaginal bleeding requiring hospital admission at 18 weeks’ gestation or more, preterm prelabour rupture of membranes, active labour (defined as the presence of uterine activity and cervical dilatation greater than 3 cm), known lethal fetal anomaly or fetal demise, progesterone treatment after 16 weeks’ gestation, or any contraindication to continuation of the pregnancy, such as chorioamnionitis requiring delivery, or contraindication to progesterone therapy (known active liver disease, active or hormone-related thrombophlebitis or thromboembolic disorder, or breast or genital malignancy). The PROGRESS Study protocol did not include the need for cervical length measurement at trial entry or during the pregnancy. The clinician responsible for care of the participant decided whether cervical length screening was undertaken. The study was approved by the Children’s Youth and Women’s Health Services Human Research Ethics Committee at the Women’s and Children’s Hospital, Adelaide, Australia, and by the ethics committee at each of the 39 collaborating centres (33 in Australia, 4 in New Zealand and 2 in Canada). Eligible women were provided with written information about the study in the antenatal clinic, counselled by 1 member of the research team, and asked if they would participate. Recruitment started in February 2006 and was completed in September 2012. Randomisation Women who gave written informed consent were randomly assigned to either ‘progesterone’ or 'placebo’ using a central telephone randomisation service. The randomisation schedule, prepared by an investigator not involved with clinical care, used balanced variable blocks with stratification by plurality of the pregnancy (singleton versus twin versus triplet) and collaborating centre. Participants, staff, and investigators were masked to study group allocation, and treatment packs appeared identical. The baseline information collected included maternal age, parity, ethnicity, body mass index, plurality, gestational age at trial entry, gestational age, and reason for the previous preterm birth. Intervention and outcomes Progesterone group and placebo group. Women randomised to the progesterone and placebo groups were allocated a study number that corresponded to a treatment pack containing the allocated study treatment. Depending on the study treatment allocation, the treatment packs contained either a 14-week supply of progesterone pessaries (equivalent to 100 mg vaginal progesterone as active substance in hard fat) or similar-appearing placebo pessaries (in hard fat) bought for the study from Orion Laboratories, Western Australia. The manufacturer of the pessaries had no other involvement in the study. Women were asked to self-administer a vaginal pessary each evening from 20 weeks’ gestation, or from randomisation if this occurred after 20 weeks’ gestation, until birth or 34 weeks’ gestation, whichever occurred first. The maximum number of days treatment could be used for was 98 days. Women were reviewed in the antenatal clinic by the practitioner responsible for their care. Women who presented with preterm prelabour rupture of the membranes after trial entry were advised to discontinue using the vaginal pessaries to reduce the risk of introducing infection. In the event of the development of serious depression or a medical condition that may have been aggravated by fluid retention (asthma, epilepsy, migraine, known cardiac dysfunction, or known renal dysfunction), the clinician was to advise the woman to cease using the trial medication if he or she felt it would be in the woman’s best interests to do so. At 34 weeks’ gestation, women were asked to complete a questionnaire that assessed health-related quality of life [23], anxiety [24], and depression [25] and asked about any side effects they may have experienced and their compliance with the treatment protocol. After birth, information relating to birth, maternal and infant health, and care was collected from the woman's and infant's case notes by trained research assistants. Progesterone group and placebo group. Women randomised to the progesterone and placebo groups were allocated a study number that corresponded to a treatment pack containing the allocated study treatment. Depending on the study treatment allocation, the treatment packs contained either a 14-week supply of progesterone pessaries (equivalent to 100 mg vaginal progesterone as active substance in hard fat) or similar-appearing placebo pessaries (in hard fat) bought for the study from Orion Laboratories, Western Australia. The manufacturer of the pessaries had no other involvement in the study. Women were asked to self-administer a vaginal pessary each evening from 20 weeks’ gestation, or from randomisation if this occurred after 20 weeks’ gestation, until birth or 34 weeks’ gestation, whichever occurred first. The maximum number of days treatment could be used for was 98 days. Women were reviewed in the antenatal clinic by the practitioner responsible for their care. Women who presented with preterm prelabour rupture of the membranes after trial entry were advised to discontinue using the vaginal pessaries to reduce the risk of introducing infection. In the event of the development of serious depression or a medical condition that may have been aggravated by fluid retention (asthma, epilepsy, migraine, known cardiac dysfunction, or known renal dysfunction), the clinician was to advise the woman to cease using the trial medication if he or she felt it would be in the woman’s best interests to do so. At 34 weeks’ gestation, women were asked to complete a questionnaire that assessed health-related quality of life [23], anxiety [24], and depression [25] and asked about any side effects they may have experienced and their compliance with the treatment protocol. After birth, information relating to birth, maternal and infant health, and care was collected from the woman's and infant's case notes by trained research assistants. Study outcomes Primary outcome. The primary outcome was the incidence of neonatal respiratory distress syndrome (defined as increasing respiratory distress or oxygen requirement or the need for respiratory support from the first 6 hours of life) and severity of neonatal respiratory disease (defined as mild = mean airway pressure [MAP] < 7 cm H2O and/or fractional inspired oxygen [FiO2] < 0.4; moderate = MAP 7–9.9 cm H2O and/or FiO2 0.40–0.79; severe = MAP ≥ 10 cm H2O, and/or FiO2 ≥ 0.80 with need for ventilation). Secondary outcomes for the child. The secondary outcomes for the child were as follows: other respiratory measures, which included the need for and duration of oxygen therapy (including highest FiO2 [%] within 12 hours of birth), need for and duration of mechanical ventilation (including maximum peak pressure [cm H2O] within 12 hours of birth), need for surfactant therapy, nitric oxide for respiratory support, air leak syndrome, and chronic lung disease (defined as the need for any respiratory support, supplemental oxygen, or intermittent positive pressure ventilation or continuous positive airways pressure for a chronic pulmonary disorder on the day the baby reached 36 weeks’ postmenstrual age for infants born before 32 weeks’ gestation, or continued oxygen requirement at 28 days of age for infants born after 36 weeks’ gestation) and a composite adverse outcome for the infant that included 1 or more of the following: preterm birth (defined as birth at less than 37 weeks’ gestation), perinatal mortality (defined as either a stillbirth [intrauterine fetal death after trial entry and prior to birth] or infant death [death of a live-born infant prior to hospital discharge] and excluding lethal congenital anomalies), severe respiratory disease, chronic lung disease, Apgar score < 4 at 5 minutes of age, birth weight less than the third centile for gestational age at birth and infant sex, intraventricular haemorrhage on early cranial ultrasound, periventricular leucomalacia on later cranial ultrasound, inotropic support for the treatment of patent ductus arteriosus, proven necrotising enterocolitis, proven systemic infection within 48 hours of birth treated with antibiotics, and retinopathy of prematurity. Secondary study outcomes for the mother. The secondary study outcomes for the mother were as follows: significant health outcomes, particularly related to preterm birth, such as use of tocolytic therapy or antenatal corticosteroid therapy, defined by 1 or more of the following: maternal death, antepartum haemorrhage, pre-eclampsia, preterm prelabour rupture of membranes, prelabour ruptured membranes at or near term (defined as prelabour rupture of membranes after 36 weeks’ gestation), chorioamnionitis requiring antibiotic use during labour, postpartum haemorrhage, or antibiotic use after birth; length of any antenatal hospital stay or postnatal stay and psychological health (assessed by quality of life [23], anxiety [24], and depression [25]); and side effects of progesterone supplementation (including headache, nausea, pain and discomfort, breast tenderness, and coughing) and if any of them were sufficient to stop treatment. Primary outcome. The primary outcome was the incidence of neonatal respiratory distress syndrome (defined as increasing respiratory distress or oxygen requirement or the need for respiratory support from the first 6 hours of life) and severity of neonatal respiratory disease (defined as mild = mean airway pressure [MAP] < 7 cm H2O and/or fractional inspired oxygen [FiO2] < 0.4; moderate = MAP 7–9.9 cm H2O and/or FiO2 0.40–0.79; severe = MAP ≥ 10 cm H2O, and/or FiO2 ≥ 0.80 with need for ventilation). Secondary outcomes for the child. The secondary outcomes for the child were as follows: other respiratory measures, which included the need for and duration of oxygen therapy (including highest FiO2 [%] within 12 hours of birth), need for and duration of mechanical ventilation (including maximum peak pressure [cm H2O] within 12 hours of birth), need for surfactant therapy, nitric oxide for respiratory support, air leak syndrome, and chronic lung disease (defined as the need for any respiratory support, supplemental oxygen, or intermittent positive pressure ventilation or continuous positive airways pressure for a chronic pulmonary disorder on the day the baby reached 36 weeks’ postmenstrual age for infants born before 32 weeks’ gestation, or continued oxygen requirement at 28 days of age for infants born after 36 weeks’ gestation) and a composite adverse outcome for the infant that included 1 or more of the following: preterm birth (defined as birth at less than 37 weeks’ gestation), perinatal mortality (defined as either a stillbirth [intrauterine fetal death after trial entry and prior to birth] or infant death [death of a live-born infant prior to hospital discharge] and excluding lethal congenital anomalies), severe respiratory disease, chronic lung disease, Apgar score < 4 at 5 minutes of age, birth weight less than the third centile for gestational age at birth and infant sex, intraventricular haemorrhage on early cranial ultrasound, periventricular leucomalacia on later cranial ultrasound, inotropic support for the treatment of patent ductus arteriosus, proven necrotising enterocolitis, proven systemic infection within 48 hours of birth treated with antibiotics, and retinopathy of prematurity. Secondary study outcomes for the mother. The secondary study outcomes for the mother were as follows: significant health outcomes, particularly related to preterm birth, such as use of tocolytic therapy or antenatal corticosteroid therapy, defined by 1 or more of the following: maternal death, antepartum haemorrhage, pre-eclampsia, preterm prelabour rupture of membranes, prelabour ruptured membranes at or near term (defined as prelabour rupture of membranes after 36 weeks’ gestation), chorioamnionitis requiring antibiotic use during labour, postpartum haemorrhage, or antibiotic use after birth; length of any antenatal hospital stay or postnatal stay and psychological health (assessed by quality of life [23], anxiety [24], and depression [25]); and side effects of progesterone supplementation (including headache, nausea, pain and discomfort, breast tenderness, and coughing) and if any of them were sufficient to stop treatment. Statistical methods Primary analyses were performed on an intention-to-treat basis, according to the study group allocated at randomisation. As prespecified, unadjusted analyses were performed and then adjusted for the potential confounders of gestational age at randomisation, gestational age of the previous preterm birth, and reason for the previous preterm birth. Binary outcomes were analysed using log binomial regression, with treatment effects expressed as relative risk (RR) with 95% confidence interval (CI), or Fisher’s exact tests with no adjustment for covariates in the case of rare outcomes. Outcomes measured on a continuous scale were analysed using linear regression, with treatment effects expressed as differences in means. Count outcomes were analysed using Poisson regression or negative binomial regression where overdispersion was present, with treatment effects expressed as ratios of means. Ordinal outcomes were analysed using proportional odds models, with treatment effects expressed as odds ratios of higher severity. For infant outcomes, clustering due to multiple births was taken into account using generalised estimating equations. Statistical significance was assessed at the 2-sided p < 0.05 level, and no adjustment was made for multiple comparisons. No adjustments were made for the 2 primary outcomes, as they were considered strongly related and expected to provide complementary information [26]. All analyses followed a prespecified statistical analysis plan and were performed using SAS software version 9.3 (SAS Institute, Cary, North Carolina, United States). Sample size. We originally estimated that a sample size of 984 women would be able to show a 40% reduction in neonatal respiratory distress syndrome from 15% to 9% with progesterone supplementation (5% level of significance, 2-tailed alpha, 80% power, 4% loss to follow-up) based upon data from a randomised trial with similar eligibility profile when this trial commenced [21]. In 2009, because of slower than anticipated accrual, we applied for additional funding to complete the study. At this time, the Trial Steering Group asked the following questions of an independent review: (1) ‘Should recruitment stop (because of a significant result or futility)?’ (2) ‘Should we continue recruiting to reach our previous sample size?’ and (3) ‘Does the sample size need refining based on the interim assessment?’ The Trial Steering Group did not see the interim data or the analyses. The independent review undertaken, masked to treatment group, made the following recommendations to the Trial Steering Group: to continue recruitment and to reduce the sample size to 784 women. Sample size. We originally estimated that a sample size of 984 women would be able to show a 40% reduction in neonatal respiratory distress syndrome from 15% to 9% with progesterone supplementation (5% level of significance, 2-tailed alpha, 80% power, 4% loss to follow-up) based upon data from a randomised trial with similar eligibility profile when this trial commenced [21]. In 2009, because of slower than anticipated accrual, we applied for additional funding to complete the study. At this time, the Trial Steering Group asked the following questions of an independent review: (1) ‘Should recruitment stop (because of a significant result or futility)?’ (2) ‘Should we continue recruiting to reach our previous sample size?’ and (3) ‘Does the sample size need refining based on the interim assessment?’ The Trial Steering Group did not see the interim data or the analyses. The independent review undertaken, masked to treatment group, made the following recommendations to the Trial Steering Group: to continue recruitment and to reduce the sample size to 784 women. Results Baseline information Of an estimated 1,919 eligible women able to be approached by the research team between February 2006 and September 2012, a total of 787 (41%) women consented to be enrolled in the study. Reasons for eligible women declining to participate included ‘not interested in research’ (25%), ‘concerned about side effects and risks of use of drugs in pregnancy’ (15%), ‘no reason given’ (13%), ‘did not like the need to use vaginal pessaries’ (9%), ‘too busy’ (8%), ‘did not consider themselves to be at risk of preterm birth’ (6%), ‘partner declined to let them participate’ (5), and ‘other’ (19%). Of the 787 women recruited, 398 (50.6%) were randomised to the progesterone group, and 389 (49.4%) to the placebo group. There were no losses to follow-up, with clinical outcomes to primary hospital discharge after birth available for all 787 (100%) women and their 799 infants (Fig 1). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Consolidated Standards of Reporting Trials (CONSORT) flow diagram of participants in the study. https://doi.org/10.1371/journal.pmed.1002390.g001 The 2 study groups were similar at the time of study entry for maternal demographics and key variables including gestational age, the reason for the preterm birth in the preceding pregnancy, and the gestational age at which that birth occurred (Table 1). The majority of participants had a singleton pregnancy, with less than 2% having a twin pregnancy (Table 1). Almost all women recruited in both study groups used their allocated study treatment (381 [95.7%] in the progesterone group and 359 [92.3%] in the placebo group), with similar median days of use in both study groups (51.0 days [interquartile range (IQR) 28.0–69.0] in the progesterone group versus 52.0 days [IQR 27.0–76.0] in the placebo group) (Table 1). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Comparability of randomised study groups at trial entry and use of study treatment. https://doi.org/10.1371/journal.pmed.1002390.t001 Primary infant outcomes Risk of respiratory distress syndrome and severity of respiratory disease. The risk of respiratory distress syndrome was similar in both study groups, 10.5% (42/402) in the progesterone group and 10.6% (41/388) in the placebo group (adjusted RR 0.98, 95% CI 0.64–1.49, p = 0.912), as was the severity of any neonatal respiratory disease (adjusted treatment effect 1.02 [95% CI 0.69–1.53, p = 0.905]) (Table 2). Unadjusted analyses showed similar findings to the analyses adjusted for gestational age at randomisation, gestation of previous preterm birth, and reason for previous preterm birth (Table 2). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Primary and secondary neonatal outcomes by study group. https://doi.org/10.1371/journal.pmed.1002390.t002 Secondary outcomes for the infant Other respiratory measures. In keeping with these findings, there were no differences between the study groups for any of the secondary respiratory outcomes that included need for and duration of oxygen therapy, maximum appropriate FIO2 values within 12 hours of birth, use and duration of mechanical ventilation, use of surfactant, use of nitric oxide, air leak syndrome, and chronic lung disease (Table 2). Adverse infant outcomes. Overall, the risk of any serious adverse outcome for the infant was similar between the study groups (155/406 [38.2%] in the progesterone group and 152/393 [38.7%] in the placebo group, adjusted RR 0.98, 95% CI 0.82–1.17, p = 0.798) (Table 2). There were 12 (1.5%) infant deaths before hospital discharge: 4 stillbirths and 1 death of a live-born infant in the progesterone group and 5 stillbirths and 2 deaths of live-born infants in the placebo group—not a significant difference (Table 2). The proportion of infants born before 37 weeks’ gestation was similar in both study groups (148/406 [36.5%] in the progesterone group and 146/393 [37.2%] in the placebo group, adjusted RR 0.97, 95% CI 0.81–1.17, p = 0.765). A similar proportion of infants were born by caesarean section in both study groups. No differences were evident between the study groups for any of the other individual adverse infant outcomes that included low Apgar score, small for gestational age at birth, intraventricular haemorrhage, periventricular leucomalacia, patent ductus arteriosus requiring treatment, necrotising enterocolitis, proven early neonatal sepsis, retinopathy of prematurity, and need for admission to the neonatal intensive care unit and duration of the infant’s postnatal stay (Table 2). Secondary outcomes for the women Significant health outcomes. There were no differences between study groups in the proportion of women experiencing 1 or more significant health outcomes overall (180/398 [45.2%] in the progesterone group and 174/389 [44.7%] in the placebo group, adjusted RR 1.00, 95% CI 0.86–1.17, p = 0.994) or in the individual health outcomes, particularly those related to preterm birth, including use of tocolytic therapy and antenatal corticosteroids prior to the birth, antepartum haemorrhage, preeclampsia, risk of rupture of the membranes preterm or at or near term, chorioamnionitis requiring antibiotics, and postpartum haemorrhage (Table 3). There were no maternal deaths. Antibiotic use after birth was similar between the study groups, as was the need for antenatal admission and the length of any antenatal or postnatal hospital stay (Table 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Secondary maternal outcomes by study group, including those related to preterm birth, psychological health, side effects of study treatment, and compliance. https://doi.org/10.1371/journal.pmed.1002390.t003 Psychological health. All measures on the 36-Item Short Form Health Survey (SF-36), including the overall physical and mental components, were similar in both study groups. No differences were seen in the proportion of women with a score on the Edinburgh Postnatal Depression Scale (EPDS) that was suggestive of depression (9.4% in the progesterone group and 9.0% in the placebo group), and the level of anxiety was similar in the 2 study groups (Table 3). Side effects of study treatment and compliance. The proportion of women reporting any side effects of the treatment at 34 weeks’ gestation was similar between the study groups (134/394 [34.0%] in the progesterone group versus 118/382 [30.9%] in the placebo group), as was the proportion of women who stopped therapy because of side effects (39/394 [9.9%] in the progesterone group versus 28/382 [7.3%] in the placebo group) (Table 3). A similar proportion of women in both study groups either did not start the medication or forgot to use it 3 or more times a week, our measure of compliance (33/394 [8.4%] in the progesterone group and 35/380 [9.2%] in the placebo group) (Table 3). A similar proportion of women in both study groups used the study treatment up to 34 weeks’ gestation and remained undelivered (250/381 [65.6%] in the progesterone group versus 247/360 [68.6%] in the placebo group). Baseline information Of an estimated 1,919 eligible women able to be approached by the research team between February 2006 and September 2012, a total of 787 (41%) women consented to be enrolled in the study. Reasons for eligible women declining to participate included ‘not interested in research’ (25%), ‘concerned about side effects and risks of use of drugs in pregnancy’ (15%), ‘no reason given’ (13%), ‘did not like the need to use vaginal pessaries’ (9%), ‘too busy’ (8%), ‘did not consider themselves to be at risk of preterm birth’ (6%), ‘partner declined to let them participate’ (5), and ‘other’ (19%). Of the 787 women recruited, 398 (50.6%) were randomised to the progesterone group, and 389 (49.4%) to the placebo group. There were no losses to follow-up, with clinical outcomes to primary hospital discharge after birth available for all 787 (100%) women and their 799 infants (Fig 1). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Consolidated Standards of Reporting Trials (CONSORT) flow diagram of participants in the study. https://doi.org/10.1371/journal.pmed.1002390.g001 The 2 study groups were similar at the time of study entry for maternal demographics and key variables including gestational age, the reason for the preterm birth in the preceding pregnancy, and the gestational age at which that birth occurred (Table 1). The majority of participants had a singleton pregnancy, with less than 2% having a twin pregnancy (Table 1). Almost all women recruited in both study groups used their allocated study treatment (381 [95.7%] in the progesterone group and 359 [92.3%] in the placebo group), with similar median days of use in both study groups (51.0 days [interquartile range (IQR) 28.0–69.0] in the progesterone group versus 52.0 days [IQR 27.0–76.0] in the placebo group) (Table 1). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Comparability of randomised study groups at trial entry and use of study treatment. https://doi.org/10.1371/journal.pmed.1002390.t001 Primary infant outcomes Risk of respiratory distress syndrome and severity of respiratory disease. The risk of respiratory distress syndrome was similar in both study groups, 10.5% (42/402) in the progesterone group and 10.6% (41/388) in the placebo group (adjusted RR 0.98, 95% CI 0.64–1.49, p = 0.912), as was the severity of any neonatal respiratory disease (adjusted treatment effect 1.02 [95% CI 0.69–1.53, p = 0.905]) (Table 2). Unadjusted analyses showed similar findings to the analyses adjusted for gestational age at randomisation, gestation of previous preterm birth, and reason for previous preterm birth (Table 2). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Primary and secondary neonatal outcomes by study group. https://doi.org/10.1371/journal.pmed.1002390.t002 Risk of respiratory distress syndrome and severity of respiratory disease. The risk of respiratory distress syndrome was similar in both study groups, 10.5% (42/402) in the progesterone group and 10.6% (41/388) in the placebo group (adjusted RR 0.98, 95% CI 0.64–1.49, p = 0.912), as was the severity of any neonatal respiratory disease (adjusted treatment effect 1.02 [95% CI 0.69–1.53, p = 0.905]) (Table 2). Unadjusted analyses showed similar findings to the analyses adjusted for gestational age at randomisation, gestation of previous preterm birth, and reason for previous preterm birth (Table 2). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Primary and secondary neonatal outcomes by study group. https://doi.org/10.1371/journal.pmed.1002390.t002 Secondary outcomes for the infant Other respiratory measures. In keeping with these findings, there were no differences between the study groups for any of the secondary respiratory outcomes that included need for and duration of oxygen therapy, maximum appropriate FIO2 values within 12 hours of birth, use and duration of mechanical ventilation, use of surfactant, use of nitric oxide, air leak syndrome, and chronic lung disease (Table 2). Adverse infant outcomes. Overall, the risk of any serious adverse outcome for the infant was similar between the study groups (155/406 [38.2%] in the progesterone group and 152/393 [38.7%] in the placebo group, adjusted RR 0.98, 95% CI 0.82–1.17, p = 0.798) (Table 2). There were 12 (1.5%) infant deaths before hospital discharge: 4 stillbirths and 1 death of a live-born infant in the progesterone group and 5 stillbirths and 2 deaths of live-born infants in the placebo group—not a significant difference (Table 2). The proportion of infants born before 37 weeks’ gestation was similar in both study groups (148/406 [36.5%] in the progesterone group and 146/393 [37.2%] in the placebo group, adjusted RR 0.97, 95% CI 0.81–1.17, p = 0.765). A similar proportion of infants were born by caesarean section in both study groups. No differences were evident between the study groups for any of the other individual adverse infant outcomes that included low Apgar score, small for gestational age at birth, intraventricular haemorrhage, periventricular leucomalacia, patent ductus arteriosus requiring treatment, necrotising enterocolitis, proven early neonatal sepsis, retinopathy of prematurity, and need for admission to the neonatal intensive care unit and duration of the infant’s postnatal stay (Table 2). Other respiratory measures. In keeping with these findings, there were no differences between the study groups for any of the secondary respiratory outcomes that included need for and duration of oxygen therapy, maximum appropriate FIO2 values within 12 hours of birth, use and duration of mechanical ventilation, use of surfactant, use of nitric oxide, air leak syndrome, and chronic lung disease (Table 2). Adverse infant outcomes. Overall, the risk of any serious adverse outcome for the infant was similar between the study groups (155/406 [38.2%] in the progesterone group and 152/393 [38.7%] in the placebo group, adjusted RR 0.98, 95% CI 0.82–1.17, p = 0.798) (Table 2). There were 12 (1.5%) infant deaths before hospital discharge: 4 stillbirths and 1 death of a live-born infant in the progesterone group and 5 stillbirths and 2 deaths of live-born infants in the placebo group—not a significant difference (Table 2). The proportion of infants born before 37 weeks’ gestation was similar in both study groups (148/406 [36.5%] in the progesterone group and 146/393 [37.2%] in the placebo group, adjusted RR 0.97, 95% CI 0.81–1.17, p = 0.765). A similar proportion of infants were born by caesarean section in both study groups. No differences were evident between the study groups for any of the other individual adverse infant outcomes that included low Apgar score, small for gestational age at birth, intraventricular haemorrhage, periventricular leucomalacia, patent ductus arteriosus requiring treatment, necrotising enterocolitis, proven early neonatal sepsis, retinopathy of prematurity, and need for admission to the neonatal intensive care unit and duration of the infant’s postnatal stay (Table 2). Secondary outcomes for the women Significant health outcomes. There were no differences between study groups in the proportion of women experiencing 1 or more significant health outcomes overall (180/398 [45.2%] in the progesterone group and 174/389 [44.7%] in the placebo group, adjusted RR 1.00, 95% CI 0.86–1.17, p = 0.994) or in the individual health outcomes, particularly those related to preterm birth, including use of tocolytic therapy and antenatal corticosteroids prior to the birth, antepartum haemorrhage, preeclampsia, risk of rupture of the membranes preterm or at or near term, chorioamnionitis requiring antibiotics, and postpartum haemorrhage (Table 3). There were no maternal deaths. Antibiotic use after birth was similar between the study groups, as was the need for antenatal admission and the length of any antenatal or postnatal hospital stay (Table 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Secondary maternal outcomes by study group, including those related to preterm birth, psychological health, side effects of study treatment, and compliance. https://doi.org/10.1371/journal.pmed.1002390.t003 Psychological health. All measures on the 36-Item Short Form Health Survey (SF-36), including the overall physical and mental components, were similar in both study groups. No differences were seen in the proportion of women with a score on the Edinburgh Postnatal Depression Scale (EPDS) that was suggestive of depression (9.4% in the progesterone group and 9.0% in the placebo group), and the level of anxiety was similar in the 2 study groups (Table 3). Side effects of study treatment and compliance. The proportion of women reporting any side effects of the treatment at 34 weeks’ gestation was similar between the study groups (134/394 [34.0%] in the progesterone group versus 118/382 [30.9%] in the placebo group), as was the proportion of women who stopped therapy because of side effects (39/394 [9.9%] in the progesterone group versus 28/382 [7.3%] in the placebo group) (Table 3). A similar proportion of women in both study groups either did not start the medication or forgot to use it 3 or more times a week, our measure of compliance (33/394 [8.4%] in the progesterone group and 35/380 [9.2%] in the placebo group) (Table 3). A similar proportion of women in both study groups used the study treatment up to 34 weeks’ gestation and remained undelivered (250/381 [65.6%] in the progesterone group versus 247/360 [68.6%] in the placebo group). Significant health outcomes. There were no differences between study groups in the proportion of women experiencing 1 or more significant health outcomes overall (180/398 [45.2%] in the progesterone group and 174/389 [44.7%] in the placebo group, adjusted RR 1.00, 95% CI 0.86–1.17, p = 0.994) or in the individual health outcomes, particularly those related to preterm birth, including use of tocolytic therapy and antenatal corticosteroids prior to the birth, antepartum haemorrhage, preeclampsia, risk of rupture of the membranes preterm or at or near term, chorioamnionitis requiring antibiotics, and postpartum haemorrhage (Table 3). There were no maternal deaths. Antibiotic use after birth was similar between the study groups, as was the need for antenatal admission and the length of any antenatal or postnatal hospital stay (Table 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Secondary maternal outcomes by study group, including those related to preterm birth, psychological health, side effects of study treatment, and compliance. https://doi.org/10.1371/journal.pmed.1002390.t003 Psychological health. All measures on the 36-Item Short Form Health Survey (SF-36), including the overall physical and mental components, were similar in both study groups. No differences were seen in the proportion of women with a score on the Edinburgh Postnatal Depression Scale (EPDS) that was suggestive of depression (9.4% in the progesterone group and 9.0% in the placebo group), and the level of anxiety was similar in the 2 study groups (Table 3). Side effects of study treatment and compliance. The proportion of women reporting any side effects of the treatment at 34 weeks’ gestation was similar between the study groups (134/394 [34.0%] in the progesterone group versus 118/382 [30.9%] in the placebo group), as was the proportion of women who stopped therapy because of side effects (39/394 [9.9%] in the progesterone group versus 28/382 [7.3%] in the placebo group) (Table 3). A similar proportion of women in both study groups either did not start the medication or forgot to use it 3 or more times a week, our measure of compliance (33/394 [8.4%] in the progesterone group and 35/380 [9.2%] in the placebo group) (Table 3). A similar proportion of women in both study groups used the study treatment up to 34 weeks’ gestation and remained undelivered (250/381 [65.6%] in the progesterone group versus 247/360 [68.6%] in the placebo group). Discussion Main findings The PROGRESS Trial showed that in women with a history of previous spontaneous preterm birth, the use of 100-mg vaginal progesterone pessaries daily from 20 weeks’ gestation until 34 weeks’ gestation had no effect on the risk of the baby developing respiratory distress syndrome or on reducing the severity of any neonatal respiratory disease compared with placebo pessaries. In keeping with these findings, no benefits were seen relating to other respiratory outcomes or other neonatal morbidities. For women, the risk of having a preterm birth was not reduced with the use of progesterone, and the need for interventions related to preterm birth such as tocolysis and antenatal corticosteroids; the need for antenatal hospital admission; and, if admitted, the length of hospital stay were also not reduced. Over 36% of the women in both study groups in the PROGRESS Trial were given antenatal corticosteroids, appropriate for the 36% rate of preterm birth seen in our high-risk population. Although progesterone can suppress proinflammatory cytokines [27], there was no evidence that progesterone exerted an anti-inflammatory effect on infective outcomes for the mother or the baby such as chorioamnionitis requiring the use of antibiotics, need for antibiotic use after birth, or the infant having proven early sepsis. Maternal psychological health status was similar in both study groups, including vulnerability to depression. This is reassuring given the concern that progesterone could aggravate depression. Generalisability and comparison with other studies We found no effect of vaginal progesterone on the risk of preterm birth for women with a previous preterm birth, similar to the findings from the O’Brien Trial [16] and the recently published OPPTIMUM Trial [28] but in contrast to other published reports [15, 29, 30, 31,32]. Strengths of the PROGRESS Trial The clear entry criteria for the PROGRESS Trial were specifically set to easily identify women at high risk of a recurrence of preterm birth based on their previous history and to assess the effects of vaginal progesterone on this population. Inclusion criteria for our study were based on a previous history of preterm birth—a strong predictor for subsequent preterm birth—and not dependent on assessment of cervical length. Women identified and recruited with a history of preterm birth in their preceding pregnancy were at high risk of recurrence, with 36% giving birth before 37 weeks’ gestation, although there was no difference in gestational age at birth or in the proportion born preterm between the study groups. The trial was masked for participants and investigators with a placebo, and the primary outcome of respiratory distress syndrome was reported for all babies. Potential limitations of current trial It is possible that the dose of 100 mg progesterone used may have been too low. However, the Da Fonseca Trial [15] used the same 100-mg dose of vaginal progesterone and included women at high risk for preterm birth, defined by at least 1 previous spontaneous preterm birth, prophylactic cervical cerclage, or uterine malformation, but reported a lower rate of preterm birth compared with placebo (13.8% versus 28.5%), as have other trials [29,31]. Of note, a larger daily dose of 200 mg as used in the OPPTIMUM Trial was not found to reduce the risk of preterm birth or improve neonatal or child health at 2 years of age [28]. Our pretrial sample size estimate, based on the reported effect of treatment with progesterone compared with placebo on neonatal respiratory distress syndrome [21], would provide 80% to detect a difference at the 5% significance level. Whilst the reduction in sample size recommended at the masked interim review of data may have reduced power to detect differences, the final trial results do provide reliable study estimates with CIs. To show differences between treatment groups based on these study estimates at the 5% significance level and with 80% power would require a sample size of over 2,966,780 women. Of eligible women invited to participate in the PROGRESS Trial, only 41% chose to do so, not too dissimilar to the 52% consent rate in the OPPTIMUM Trial [28]. Whether greater involvement of consumers in research proposals and promotion of trials open for recruitment within the community can increase participation in preterm birth research in priority areas, already identified by consumers of care and healthcare practitioners, needs to be established [1,33]. In any intervention study, compliance is crucial to ascertain true effect. Few other studies to date have reported on measures of compliance. In our study, most women started the allocated study treatment, and the median days of use was around 51 days. Nevertheless, a proportion of women in both study groups, almost 9%, either did not start the medication or forgot to use it 3 or more times a week, which was our measure of compliance. Within the OPPTIMUM Trial, compliance—defined slightly differently as 80% or more use of study treatment—was 69% [28]. This is similar to the proportion of women in the PROGRESS Trial who were still taking their study treatment and remained undelivered up to 34 weeks’ gestation (65.2% for women in the progesterone group and 68.6% in the placebo group). Almost a third of the women reported side effects of treatment with the vaginal pessaries, the most frequent reasons given being headache, nausea, and pain or discomfort, although there were no differences in the proportion of women reporting side effects or the side effects reported by study group. For over 8% of women, these side effects were sufficient for them to stop their study treatment. Cessation of therapy because of side effects has not been well reported in earlier studies. Clinical relevance There are ongoing differences in clinical practice recommendations as to whether to recommend use of progesterone or not [17,18,19,20]. The critical issues are whether there are particular subgroups of women who may benefit from use of vaginal progesterone by virtue of their previous obstetric history (such as a history of preterm birth or factors in their current pregnancy, such as shortening of the cervix) and what is the optimal dose and treatment regimen to use (including the gestational age to start treatment, the length of time to use treatment, and the optimal mode of administration: vaginal or intramuscular preparation). There have been calls for an individual participant data meta-analysis (IPD-MA) of the trials already conducted [28, 34] that we strongly endorse. An IPD-MA can assess different participant- and treatment-level characteristics, which is not possible using an aggregate meta-analysis, and thus provide cumulated evidence on these critical issues identified that can be used by women and their families, clinicians, and policy makers as well as identify future research priorities. Conclusions Recommendations for clinical practice. Our results do not support the use of vaginal progesterone pessaries in women with a history of a previous spontaneous preterm birth to reduce the risk of respiratory distress syndrome or other neonatal or maternal morbidity. IPD-MA of the relevant trials may identify specific women for whom vaginal progesterone may be of benefit. The search for alternative strategies for the prevention of preterm birth and its sequelae must continue. Main findings The PROGRESS Trial showed that in women with a history of previous spontaneous preterm birth, the use of 100-mg vaginal progesterone pessaries daily from 20 weeks’ gestation until 34 weeks’ gestation had no effect on the risk of the baby developing respiratory distress syndrome or on reducing the severity of any neonatal respiratory disease compared with placebo pessaries. In keeping with these findings, no benefits were seen relating to other respiratory outcomes or other neonatal morbidities. For women, the risk of having a preterm birth was not reduced with the use of progesterone, and the need for interventions related to preterm birth such as tocolysis and antenatal corticosteroids; the need for antenatal hospital admission; and, if admitted, the length of hospital stay were also not reduced. Over 36% of the women in both study groups in the PROGRESS Trial were given antenatal corticosteroids, appropriate for the 36% rate of preterm birth seen in our high-risk population. Although progesterone can suppress proinflammatory cytokines [27], there was no evidence that progesterone exerted an anti-inflammatory effect on infective outcomes for the mother or the baby such as chorioamnionitis requiring the use of antibiotics, need for antibiotic use after birth, or the infant having proven early sepsis. Maternal psychological health status was similar in both study groups, including vulnerability to depression. This is reassuring given the concern that progesterone could aggravate depression. Generalisability and comparison with other studies We found no effect of vaginal progesterone on the risk of preterm birth for women with a previous preterm birth, similar to the findings from the O’Brien Trial [16] and the recently published OPPTIMUM Trial [28] but in contrast to other published reports [15, 29, 30, 31,32]. Strengths of the PROGRESS Trial The clear entry criteria for the PROGRESS Trial were specifically set to easily identify women at high risk of a recurrence of preterm birth based on their previous history and to assess the effects of vaginal progesterone on this population. Inclusion criteria for our study were based on a previous history of preterm birth—a strong predictor for subsequent preterm birth—and not dependent on assessment of cervical length. Women identified and recruited with a history of preterm birth in their preceding pregnancy were at high risk of recurrence, with 36% giving birth before 37 weeks’ gestation, although there was no difference in gestational age at birth or in the proportion born preterm between the study groups. The trial was masked for participants and investigators with a placebo, and the primary outcome of respiratory distress syndrome was reported for all babies. Potential limitations of current trial It is possible that the dose of 100 mg progesterone used may have been too low. However, the Da Fonseca Trial [15] used the same 100-mg dose of vaginal progesterone and included women at high risk for preterm birth, defined by at least 1 previous spontaneous preterm birth, prophylactic cervical cerclage, or uterine malformation, but reported a lower rate of preterm birth compared with placebo (13.8% versus 28.5%), as have other trials [29,31]. Of note, a larger daily dose of 200 mg as used in the OPPTIMUM Trial was not found to reduce the risk of preterm birth or improve neonatal or child health at 2 years of age [28]. Our pretrial sample size estimate, based on the reported effect of treatment with progesterone compared with placebo on neonatal respiratory distress syndrome [21], would provide 80% to detect a difference at the 5% significance level. Whilst the reduction in sample size recommended at the masked interim review of data may have reduced power to detect differences, the final trial results do provide reliable study estimates with CIs. To show differences between treatment groups based on these study estimates at the 5% significance level and with 80% power would require a sample size of over 2,966,780 women. Of eligible women invited to participate in the PROGRESS Trial, only 41% chose to do so, not too dissimilar to the 52% consent rate in the OPPTIMUM Trial [28]. Whether greater involvement of consumers in research proposals and promotion of trials open for recruitment within the community can increase participation in preterm birth research in priority areas, already identified by consumers of care and healthcare practitioners, needs to be established [1,33]. In any intervention study, compliance is crucial to ascertain true effect. Few other studies to date have reported on measures of compliance. In our study, most women started the allocated study treatment, and the median days of use was around 51 days. Nevertheless, a proportion of women in both study groups, almost 9%, either did not start the medication or forgot to use it 3 or more times a week, which was our measure of compliance. Within the OPPTIMUM Trial, compliance—defined slightly differently as 80% or more use of study treatment—was 69% [28]. This is similar to the proportion of women in the PROGRESS Trial who were still taking their study treatment and remained undelivered up to 34 weeks’ gestation (65.2% for women in the progesterone group and 68.6% in the placebo group). Almost a third of the women reported side effects of treatment with the vaginal pessaries, the most frequent reasons given being headache, nausea, and pain or discomfort, although there were no differences in the proportion of women reporting side effects or the side effects reported by study group. For over 8% of women, these side effects were sufficient for them to stop their study treatment. Cessation of therapy because of side effects has not been well reported in earlier studies. Clinical relevance There are ongoing differences in clinical practice recommendations as to whether to recommend use of progesterone or not [17,18,19,20]. The critical issues are whether there are particular subgroups of women who may benefit from use of vaginal progesterone by virtue of their previous obstetric history (such as a history of preterm birth or factors in their current pregnancy, such as shortening of the cervix) and what is the optimal dose and treatment regimen to use (including the gestational age to start treatment, the length of time to use treatment, and the optimal mode of administration: vaginal or intramuscular preparation). There have been calls for an individual participant data meta-analysis (IPD-MA) of the trials already conducted [28, 34] that we strongly endorse. An IPD-MA can assess different participant- and treatment-level characteristics, which is not possible using an aggregate meta-analysis, and thus provide cumulated evidence on these critical issues identified that can be used by women and their families, clinicians, and policy makers as well as identify future research priorities. Conclusions Recommendations for clinical practice. Our results do not support the use of vaginal progesterone pessaries in women with a history of a previous spontaneous preterm birth to reduce the risk of respiratory distress syndrome or other neonatal or maternal morbidity. IPD-MA of the relevant trials may identify specific women for whom vaginal progesterone may be of benefit. The search for alternative strategies for the prevention of preterm birth and its sequelae must continue. Recommendations for clinical practice. Our results do not support the use of vaginal progesterone pessaries in women with a history of a previous spontaneous preterm birth to reduce the risk of respiratory distress syndrome or other neonatal or maternal morbidity. IPD-MA of the relevant trials may identify specific women for whom vaginal progesterone may be of benefit. The search for alternative strategies for the prevention of preterm birth and its sequelae must continue. Supporting information S1 Text. Consolidated Standards of Reporting Trials (CONSORT) statement. https://doi.org/10.1371/journal.pmed.1002390.s001 (DOCX) S2 Text. Trial protocol for the PROGRESS study. https://doi.org/10.1371/journal.pmed.1002390.s002 (DOCX) Acknowledgments Contributions to the PROGRESS study group The following persons and institutions participated in The PROGRESS Study Group: The PROGRESS Trial Steering Group: C. A. Crowther, A. J. McPhee, V. Flenady, J. M. Dodd, J. S. Robinson. Data Safety Monitoring Committee: J. Lumley, J. Hiller, C. Andersen, T. Y. Khong. C. A. Crowther had full access to all the data in the study and had final responsibility for the decision to submit for publication. Collaboration by hospital (total number of women recruited from each site in parentheses): Caboolture Hospital (23), S. Bradford, L. Cochrane, K. Millard, M. Ratnapala, S. Rehman, L. Tanda; Campbelltown Hospital (2), R. Dalal, J. Song; Christchurch Women’s Hospital (49), P. Kyle, D. Leishman, B. Puller, R. Reid; Dunedin Hospital (2), C. Devenish; Flinders Medical Centre (3), J. MacGavigan; Goulburn Valley Health (3), G. Teale; Gawler Health Service (2), S. Angus, F. Chenia; Ipswich Hospital (102), A. Drew, A. Green, K. Mahomed; John Hunter Hospital (2), F. Patel; Launceston General Hospital (23), J. Bates, A. Dennis, M. Parr; Liverpool Hospital (1), J. Smoleneic; Lyell McEwin Hospital (Adelaide) (2), C. Pawley; Logan Hospital (10), M. Haran, L. Sharma, H. Teng; Mater Hospital Mackay (3), L. Herron; Mercy Hospital for Women, Melbourne (1), S. Walker; Monash Medical Centre (24), J. Mockler, E. Wallace; The Women’s Hospital Melbourne (26), C. East, R. Palma-Dias, P. Sheehan, S. Veljanovski; Mt Sinai Hospital Toronto (77), M.-J. Clarke, K. Leliever, T. Rocco, W. Whittle, R. Windrim; Nepean Hospital (50), T. Codner, S. Downward, C. Dunn, D. Hansen, E. Masson, M. Peek, S. Sellar; Auckland City Hospital (46), M. Cropper, H. Hauch, L. McCowan, E. Parry; Redcliffe Hospital (6), A. Kothari, J. Owens, M. Shallcross; Royal Darwin Hospital (5), M. Finn, S. Thomas; Royal Hobart Hospital (1), K. Butterley; S. Raymond; Royal North Shore Hospital (30), J. Milligan, J. Morris, K. Rickard, J. Sedgley, K. White-Mathews; Rockhampton Hospital (8), F. Ashrafi, T. Gordon; Royal Prince Alfred Hospital (3), H. Phipps, A. Welsh; Sydney Adventist Hospital (1), G. Campbell; St George Hospital Sydney (14), G. Davis, L. Roberts; Royal Hospital for Women, Sydney (1), R. Reid, A. Welsh; The Canberra Hospital (5), D. Ellwood, A. Shand; The Townsville Hospital (29), C. Boniface, C. Davies, M. Edmondson, A. Lawrence, R. Lok, C. Mitchell, P. Stone, D. Watson; The Mater Hospital, Brisbane (90), J. Chaplin, V. Flenady, S. Jenkins-Marsh, D. Karamujic, S. Peterson; The Queen Elizabeth Hospital Adelaide (3), A. Singla; Toowoomba Hospital (3), D. Gibson; University of British Columbia Hospital (2), M.-F. Delisle, A. Skoll; Waikato Hospital Hamilton (9), F. Herman, D. Rohlandt; Women’s and Children’s Hospital (94), P. Ashwood, V. Ball, C. Crowther, A. Deussen, J. Dodd, D. Gagliardi, C. Holst, R. Grivell, M. Jarrett, E. Lyrtzis, D. McCormack, A. McPhee, P. Muller, B. Peat, J. Robinson, K. Robinson, T. Tran, S. Trenowden, L. Yelland, S. Zhang. Westmead Hospital (23), I. Alahakoon, D. Fleming; Wellington Women’s Hospital (9), M. Sangali, K. Groom. Contributions to the PROGRESS study group The following persons and institutions participated in The PROGRESS Study Group: The PROGRESS Trial Steering Group: C. A. Crowther, A. J. McPhee, V. Flenady, J. M. Dodd, J. S. Robinson. Data Safety Monitoring Committee: J. Lumley, J. Hiller, C. Andersen, T. Y. Khong. C. A. Crowther had full access to all the data in the study and had final responsibility for the decision to submit for publication. Collaboration by hospital (total number of women recruited from each site in parentheses): Caboolture Hospital (23), S. Bradford, L. Cochrane, K. Millard, M. Ratnapala, S. Rehman, L. Tanda; Campbelltown Hospital (2), R. Dalal, J. Song; Christchurch Women’s Hospital (49), P. Kyle, D. Leishman, B. Puller, R. Reid; Dunedin Hospital (2), C. Devenish; Flinders Medical Centre (3), J. MacGavigan; Goulburn Valley Health (3), G. Teale; Gawler Health Service (2), S. Angus, F. Chenia; Ipswich Hospital (102), A. Drew, A. Green, K. Mahomed; John Hunter Hospital (2), F. Patel; Launceston General Hospital (23), J. Bates, A. Dennis, M. Parr; Liverpool Hospital (1), J. Smoleneic; Lyell McEwin Hospital (Adelaide) (2), C. Pawley; Logan Hospital (10), M. Haran, L. Sharma, H. Teng; Mater Hospital Mackay (3), L. Herron; Mercy Hospital for Women, Melbourne (1), S. Walker; Monash Medical Centre (24), J. Mockler, E. Wallace; The Women’s Hospital Melbourne (26), C. East, R. Palma-Dias, P. Sheehan, S. Veljanovski; Mt Sinai Hospital Toronto (77), M.-J. Clarke, K. Leliever, T. Rocco, W. Whittle, R. Windrim; Nepean Hospital (50), T. Codner, S. Downward, C. Dunn, D. Hansen, E. Masson, M. Peek, S. Sellar; Auckland City Hospital (46), M. Cropper, H. Hauch, L. McCowan, E. Parry; Redcliffe Hospital (6), A. Kothari, J. Owens, M. Shallcross; Royal Darwin Hospital (5), M. Finn, S. Thomas; Royal Hobart Hospital (1), K. Butterley; S. Raymond; Royal North Shore Hospital (30), J. Milligan, J. Morris, K. Rickard, J. Sedgley, K. White-Mathews; Rockhampton Hospital (8), F. Ashrafi, T. Gordon; Royal Prince Alfred Hospital (3), H. Phipps, A. Welsh; Sydney Adventist Hospital (1), G. Campbell; St George Hospital Sydney (14), G. Davis, L. Roberts; Royal Hospital for Women, Sydney (1), R. Reid, A. Welsh; The Canberra Hospital (5), D. Ellwood, A. Shand; The Townsville Hospital (29), C. Boniface, C. Davies, M. Edmondson, A. Lawrence, R. Lok, C. Mitchell, P. Stone, D. Watson; The Mater Hospital, Brisbane (90), J. Chaplin, V. Flenady, S. Jenkins-Marsh, D. Karamujic, S. Peterson; The Queen Elizabeth Hospital Adelaide (3), A. Singla; Toowoomba Hospital (3), D. Gibson; University of British Columbia Hospital (2), M.-F. Delisle, A. Skoll; Waikato Hospital Hamilton (9), F. Herman, D. Rohlandt; Women’s and Children’s Hospital (94), P. Ashwood, V. Ball, C. Crowther, A. Deussen, J. Dodd, D. Gagliardi, C. Holst, R. Grivell, M. Jarrett, E. Lyrtzis, D. McCormack, A. McPhee, P. Muller, B. Peat, J. Robinson, K. Robinson, T. Tran, S. Trenowden, L. Yelland, S. Zhang. Westmead Hospital (23), I. Alahakoon, D. Fleming; Wellington Women’s Hospital (9), M. Sangali, K. Groom.

doi: 10.1371/journal.pmed.1002386pmid: 28898239

Background Counselling for Alcohol Problems (CAP), a brief intervention delivered by lay counsellors, enhanced remission and abstinence over 3 months among male primary care attendees with harmful drinking in a setting in India. We evaluated the sustainability of the effects after treatment termination, the cost-effectiveness of CAP over 12 months, and the effects of the hypothesized mediator ‘readiness to change’ on clinical outcomes. Methods and findings Male primary care attendees aged 18–65 years screening with harmful drinking on the Alcohol Use Disorders Identification Test (AUDIT) were randomised to either CAP plus enhanced usual care (EUC) (n = 188) or EUC alone (n = 189), of whom 89% completed assessments at 3 months, and 84% at 12 months. Primary outcomes were remission and mean standard ethanol consumed in the past 14 days, and the proposed mediating variable was readiness to change at 3 months. CAP participants maintained the gains they showed at the end of treatment through the 12-month follow-up, with the proportion with remission (AUDIT score < 8: 54.3% versus 31.9%; adjusted prevalence ratio [aPR] 1.71 [95% CI 1.32, 2.22]; p < 0.001) and abstinence in the past 14 days (45.1% versus 26.4%; adjusted odds ratio 1.92 [95% CI 1.19, 3.10]; p = 0.008) being significantly higher in the CAP plus EUC arm than in the EUC alone arm. CAP participants also fared better on secondary outcomes including recovery (AUDIT score < 8 at 3 and 12 months: 27.4% versus 15.1%; aPR 1.90 [95% CI 1.21, 3.00]; p = 0.006) and percent of days abstinent (mean percent [SD] 71.0% [38.2] versus 55.0% [39.8]; adjusted mean difference 16.1 [95% CI 7.1, 25.0]; p = 0.001). The intervention effect for remission was higher at 12 months than at 3 months (aPR 1.50 [95% CI 1.09, 2.07]). There was no evidence of an intervention effect on Patient Health Questionnaire 9 score, suicidal behaviour, percentage of days of heavy drinking, Short Inventory of Problems score, WHO Disability Assessment Schedule 2.0 score, days unable to work, or perpetration of intimate partner violence. Economic analyses indicated that CAP plus EUC was dominant over EUC alone, with lower costs and better outcomes; uncertainty analysis showed a 99% chance of CAP being cost-effective per remission achieved from a health system perspective, using a willingness to pay threshold equivalent to 1 month’s wages for an unskilled manual worker in Goa. Readiness to change level at 3 months mediated the effect of CAP on mean standard ethanol consumption at 12 months (indirect effect −6.014 [95% CI −13.99, −0.046]). Serious adverse events were infrequent, and prevalence was similar by arm. The methodological limitations of this trial are the susceptibility of self-reported drinking to social desirability bias, the modest participation rates of eligible patients, and the examination of mediation effects of only 1 mediator and in only half of our sample. Conclusions CAP’s superiority over EUC at the end of treatment was largely stable over time and was mediated by readiness to change. CAP provides better outcomes at lower costs from a societal perspective. Trial registration ISRCTN registry ISRCTN76465238 Why was this study done? Alcohol use disorders (AUDs), including harmful drinking, are one of the leading mental health contributors to the global burden of disease. Access to effective treatments is low globally, but especially so in low- and middle-income countries (LMICs) like India, where a recent national survey reported a treatment gap of 86% for AUDs. Counselling for Alcohol Problems (CAP) is a brief psychological treatment based on the principles of motivational interviewing and delivered by non-specialist providers; we have earlier reported the effectiveness of this intervention in increasing abstinence and promoting remission at the end of treatment. The goal of the present study was to evaluate the sustained effectiveness and the cost-effectiveness of CAP over 12 months. What did the researchers do and find? We implemented a randomised controlled trial in which 377 adult male primary healthcare attendees with harmful drinking were assigned to either the CAP treatment plus enhanced usual care (EUC) (n = 188) or EUC alone (n = 189); those assigned to CAP received treatment over 2 months. CAP participants maintained the gains they showed at the end of treatment through the 12-month period, with higher remission and abstinence rates than among individuals who received EUC alone. Cost analyses indicated that CAP was likely to be cost-effective, and could even save money if productivity costs were taken into account. What do these findings mean? CAP is associated with sustained effects on drinking outcomes over a 12-month period and represents good value for money. CAP is ideally suited for scaling up to reduce the treatment gap for harmful drinking. Introduction Alcohol use disorders (AUDs) [1] contribute substantially to the disability and premature mortality attributable to mental and substance use disorders [2]. In low- and middle-income countries (LMICs), alcohol use is a leading risk factor for disease and injuries [3]. Harmful drinking is also associated with socioeconomic consequences for the drinker (e.g., loss of earnings), harm to others (e.g., domestic violence), and harm to society at large (e.g., loss of productive years of life to death and disability) [1]. Economic growth in India has made it a key target for trans-national producers of alcoholic beverages, resulting in increased alcohol availability, alcohol consumption, and alcohol-related problems [4,5]. Although the less severe forms of AUDs (hazardous or harmful drinking) affect a larger proportion of the population than the more severe AUD (dependent drinking), the policy response in India remains focused predominantly on the latter [4]. There is substantial evidence for the effectiveness of brief psychological treatments for AUDs [6], and, with larger effect sizes in studies that have excluded dependent drinkers [7], such interventions are recommended for scaling up in primary care [8]. However, the vast majority of people in LMICs, including India, lack access to such interventions; for example, the recent National Mental Health Survey of India reported that 86% of persons with AUDs had not received any treatment in the previous 12 months [9]. The PRogram for Effective Mental health Interventions in Under-resourced health systeMs (PREMIUM) used a systematic framework to develop and evaluate the Healthy Activity Programme (HAP) for depression and Counselling for Alcohol Problems (CAP) for harmful drinking, both potentially scalable psychological treatments that are culturally appropriate, affordable, and feasible for delivery by the same pool of non-specialist health workers (whom we refer to as lay counsellors) [10–13], as they would be delivered in actual clinical practice. We have previously reported the findings of the impact of the CAP treatment on the primary (drinking) and secondary (consequences of alcohol use and costs of illness) outcomes at the primary endpoint of 3 months [14]. At 3 months, there was an intervention effect on remission on the Alcohol Use Disorders Identification Test (AUDIT) (36.0% in the CAP plus enhanced usual care [EUC] arm versus 25.6% in the EUC alone arm; aPR 1.50 [95% CI 1.09, 2.07]), the proportion abstinent in the past 14 days (41.5% versus 18.0%; adjusted odds ratio [aOR] 3.00 [95% CI 1.76, 5.13]), and percent of days abstinent in past 14 days (mean 69.4% versus 54.4%; adjusted mean difference [AMD] 16.0%; p < 0.001), but no effect on other drinking and related outcomes. Having reported the favourable results of the effectiveness of CAP in reducing harmful drinking and increasing abstinence at the primary end-of-treatment endpoint of 3 months post-enrolment, the question now becomes whether these effects were sustained following the end of treatment in a disorder that is highly prone to relapse, especially given the delivery of CAP by non-specialised workers (brief treatments for AUDs in high-income countries are typically delivered by highly trained professionals). In addition, a meaningful sustained effect should be accompanied by evidence of the mediating factor targeted by the intervention accounting for its effects. In this paper we address 4 new questions: the effects of the intervention on drinking and other outcomes 12 months post-enrolment, the cost-effectiveness of the intervention over this period, for whom and under what circumstances (moderators) the intervention works, and the mediation of these outcomes by patient ‘readiness to change’ assessed at 3 months. Methods The methods are described in detail in the protocol (S1 Text) [15] and the 3-month outcome paper [14], and a summary is presented below. The trial was conducted in alignment with the protocol (ISRCTN76465238) (S1 Text) [15], which was approved by the trial steering committee (TSC). Approval for the conduct of the trial was obtained from the institutional review boards of the London School of Hygiene & Tropical Medicine, Sangath (the implementing institution in India), and the Indian Council of Medical Research. Written (or witnessed, if the participant was illiterate) informed consent was mandatory for enrolment. This study is reported as per CONSORT guidelines (S1 CONSORT Checklist). Study design and participants This was a parallel-arm, single-blind, individually randomised controlled trial conducted in 10 primary health centres (PHCs) in Goa, a state on the west coast of India. The Directorate of Health Services in Goa gave permission for PREMIUM to operate in 10 of the 14 PHCs in the north district of Goa. We started screening in 8 PHCs, but during the trial, 2 of these PHCs were replaced: 1 had low attendance and 1 had a large proportion of migrant labourers. So, while the trial was conducted in a total of 10 PHCs, at any given time point in the trial, screening was happening in only 8 of these facilities. Participants were consenting males aged 18–65 years who met the a priori eligibility criteria (residing within the PHC catchment area, planning to stay at the same address for at least 12 months, able to speak English or the local vernacular, and not having been screened for harmful drinking in the past 3 months) [14,15] and were harmful drinkers, defined as scoring 12–19 on AUDIT [16], a 10-item screening questionnaire developed by the World Health Organization for the detection of AUDs and validated in India [17]. Consenting participants were randomised in a 1:1 allocation scheme to either of 2 intervention arms (EUC or CAP plus EUC) after completion of the baseline assessments, using sequentially numbered opaque sealed envelopes [18]. Baseline assessments included data on socio-demographic factors and potential moderators of treatment outcome: illness severity (baseline AUDIT score), readiness to change, and expectations from treatment. Enrolment was conducted between 28 October 2013 and 29 July 2015, 3-month assessment was completed on 30 November 2015, and the final 12-month assessment was completed on 30 August 2016. Physicians providing EUC were masked to allocation status, as were the independent assessors who did the outcome assessments, and these people had no contact with the PHCs or other team members. All authors, apart from the data manager (BB), were masked until the trial results were unmasked. Outcomes The following outcomes were examined at 12 months post-enrolment. The 2 primary outcomes were remission, defined as an AUDIT score < 8, and mean standard ethanol (in grams) consumed in the past 14 days immediately preceding the 12-month outcome evaluation. A range of secondary outcomes (S1 Table) included recovery (AUDIT score < 8 at both 3 and 12 months), percent of days abstinent in past 14 days, percent of days of heavy drinking in past 14 days, the Short Inventory of Problems (SIP) mean score, Patient Health Questionnaire 9 (PHQ-9) mean score, disability (WHO Disability Assessment Schedule 2.0 [WHODAS 2.0] score), total days unable to work in past 30 days, suicidal behaviour (suicidal thoughts in past 14 days and/or suicidal attempts in past 3 months), perpetration of intimate partner violence in past 3 months, and resource use and costs of illness estimated from the Client Service Receipt Inventory (CSRI) [19]. Percentage of days abstinent and percentage of days of heavy drinking generated from the Alcohol Timeline Followback were not pre-specified but were added prior to commencing analysis to bring the trial in line with recommendations of the US National Institute on Alcohol Abuse and Alcoholism. Similarly, our proposed mediator of patient-reported readiness to change at 3 months was added to the trial protocol midway through the trial, and thus data were available for only a subset of participants. Patient-reported readiness to change at 3 months was pre-selected as a potential mediator of the intervention for the mean standard ethanol consumption outcome, rather than the remission outcome as measured by the AUDIT score, for 2 reasons: the former is the most widely used outcome in alcohol trials, and it represents a continuous score, which is recommended over binary variables in mediation analyses to capture adequate variance [20]. Description of all the outcome tools and their contextual validity is provided in the published trial protocol (S1 Text) [15]. Sample size estimations Based on the assumptions that participants would be randomised within each of the clinics, with 1 counsellor per PHC at any one time, an intra-cluster correlation of 0.04, a loss to follow-up of 15% over 3 months, and a 1:1 allocation ratio, a trial size of 400 enrolled participants with harmful drinking had 90% power to detect the hypothesized effects (effect size of 0.45 for mean standard ethanol consumed; remission rate of 68% for CAP plus EUC versus 40% for EUC alone) for the primary outcomes, with a 5% type I error. No multiple testing adjustment was made for multiple primary outcomes. Interventions EUC comprised consultation with the PHC physician enhanced by providing the AUDIT screening results to the patient and physician, and a contextualised version of the WHO Mental Health Gap Action Programme (mhGAP) guidelines [21] for harmful drinking to the physician, which included information on when and where to refer for psychiatric care. CAP is a manualised psychological treatment (S2 Text) delivered in 3 phases over a maximum of 4 sessions (each lasting approximately 30–45 minutes) at weekly to fortnightly intervals. The psychosocial strategies used include detailed assessment followed by personalised feedback, cognitive and behavioural skills, and relapse prevention. The stance adopted by the counsellor is that of motivational interviewing [22]. A participant was classified as a ‘planned discharge’ if at least 1 of the following criteria were met: participant’s exit from treatment was decided in collaboration with the counsellor, treatment goals were achieved, or the maximum of 4 sessions were completed. The 11 counsellors were adults who had no prior professional training and/or qualification in the field of mental health, had completed at least high school education, were fluent in the vernacular languages used in the study settings, and were trained and supervised in delivering CAP through a rigorous process. Further details of the intervention [12] and of the selection, training, and supervision of the counsellors are provided elsewhere [23]. The full intervention can be accessed online (http://cap.nextgenu.org). Process and fidelity assessments were based on treatment completion rates from the counsellors’ clinical records, CAP therapy quality scores from peer and expert supervisor ratings of audio-recordings of sessions during weekly group supervision, and therapy quality ratings of a random selection of 10% of all sessions by an expert involved in the development of CAP. The same counsellors also delivered HAP to adults who met criteria for moderate to severe depression. Counsellors maintained separate clinical registers for the 2 groups of patients and reviewed individual patient records before each session. In order to ensure that their treatment-specific counselling skills were maintained throughout the trial, weekly peer-led group supervision sessions were structured in ways that involved holding separate sessions for each of the 2 treatments. This arrangement allowed the expert supervisors for each of the 2 treatments to provide more focused feedback to the counsellors. Statistical analyses Analyses were intention-to-treat, with multiple imputation (20 iterations) for missing outcome data, assuming data were missing at random, and assuming predictive mean matching for positively skewed outcomes. The following variables were used in the imputation model: age, marital status, and baseline AUDIT score. Zero-inflated negative binomial (ZINB) regression [24] was used to estimate the intervention effect for positively skewed over-dispersed outcomes with an excess of zeros. Continuous outcomes with normally distributed residuals were analysed using linear regression, and binary outcomes were analysed using binary logistic regression. All models were adjusted for baseline AUDIT score and for PHC as a fixed effect to allow for within-PHC clustering. For ZINB regression, the intervention effect was estimated for all participants in 1 model as an adjusted prevalence ratio (aPR) with a 95% CI for proportion with zero (i.e., no reported drinking), and with an adjusted count ratio among those with non-zero responses. For other continuous outcomes, the intervention effect was reported as the AMD and 95% CI; for binary outcomes, the intervention effect was reported as aPR estimated using the marginal standardisation technique, with 95% CIs for the prevalence ratios estimated using the delta method [25] following logistic regression. Moderation of treatment effect was assessed for a priori defined moderators. Sensitivity analyses for linear and logistic regression models included adjustment for counsellor as a random effect, and complete case analysis. In addition, repeated measures analysis was conducted, including analysis of change over time between the 3- and 12-month endpoints. The repeated measures analysis included a treatment-by-time interaction term to allow for a different intervention effect at 3 versus 12 months. The Monte Carlo method for assessing mediation (MCMAM) [26] was used for assessing the mediating effects of readiness to change assessed at 3 months on the 12-month primary outcome of mean standard ethanol consumption over the previous 14 days for the sub-sample of participants for whom the mediating variable data had been collected. In the current study, 95% CI was computed with 20,000 repetitions. Economic evaluation was performed from the healthcare system perspective and from a broader societal perspective, which also took account of productivity impacts on patients and families. Costs, including the intervention costs for CAP, per additional remission, additional individual in recovery and quality-adjusted life year (QALY) gained were calculated. Information on the use of health services, including contacts with PHCs, hospital doctor contacts and inpatient stays (including detoxification), medication use, and diagnostic tests, was collected from service users using a tailored version of the CSRI at 3 and 12 months. Unit costs for doctor contacts and inpatient stays were inflated to 2015 prices using published unit costs previously used in an economic evaluation of a brief psychological intervention in Goa [27]. Detailed information on medications and lab tests used were extracted from medical records, including costs to the public purse. Mean health system costs were then extrapolated to cover the full 12 months. Detailed information was also recorded on the time taken to deliver each CAP session and whether it was delivered at a PHC, over the telephone, or at a patient’s home. Travel time and transportation costs (mainly petrol costs) were also recorded for home visits, including ‘no show’ home visits. Per minute unit costs for counsellors, taking account of their training, supervision, costs related to home delivery, and other overheads, were then attached to time to estimate the total costs of intervention delivery. The number of days completely out of normal role (i.e., days unable to work) over the previous 30 days was based on responses to the WHODAS 2.0. WHODAS 2.0 data on days of activity cutback over this period were also included, with the assumption that each day of cutback would have half the value of a complete day out of role. The value of time that patients reported attending health services was estimated; when patients reported being accompanied by someone, it was assumed that 1 family member also incurred the same level of productivity loss. We assumed that the mean of patient and family time costs at 3 months and 12 months would also apply to the rest of the year. Costs due to cutback and complete days out of role were adjusted to avoid double counting time that patients spent attending health services. All patient and family time was valued using different daily wage rates recommended in 2015 by the Indian Office of the Labour Commissioner. The rate used was dependent on whether the patient/family member was classified as an unskilled, skilled, or clerical/professional worker. We assumed the value of days out of role for those classified as unemployed was the same as that for unskilled workers. Further information on data collection methods is provided elsewhere [14,15]. Differences in mean costs were compared using standard parametric tests. QALYs were derived through transformation of WHODAS 2.0 12-item scores [27]. Five imputations were run to deal with missing values for QALYs and cost data. Statistical uncertainty was explored through bootstrapping and the generation of cost-effectiveness acceptability curves showing the likelihood that CAP would be cost-effective at different willingness to pay thresholds. All costs are presented in 2015 international dollars. Statistical analyses were conducted using Excel 2016 and SPSS 21 for the cost-effectiveness analyses, SAS and R-Studio for the mediation analyses, and STATA 13/14 for all other analyses. The PREMIUM statistical analysis plan (version 2, 17 December 2015) was originally drafted to address both 3- and 12-month outcomes. However, following the analyses of the 3-month outcomes, modifications to the plan for the 12-month outcome analyses were proposed, principally by making it a stand-alone plan specifically for the 12-month outcomes. The key differences from the registered protocol included changing SIP to a secondary outcome to reduce multiplicity of the primary outcomes and adding 2 secondary outcomes (percentage of days abstinent and percentage of days of heavy drinking generated from the Alcohol Timeline Followback) to bring the trial in line with recommendations of the US National Institute on Alcohol Abuse and Alcoholism. The draft revised analysis plan was then circulated to the TSC (independent chairperson) and data safety monitoring committee (DSMC) (independent members) for review and discussion through teleconference. The final analysis was started (1 October 2016) only after the analysis plan was approved and locked by the TSC/DSMC members (4 September 2016) (S3 Text). Study design and participants This was a parallel-arm, single-blind, individually randomised controlled trial conducted in 10 primary health centres (PHCs) in Goa, a state on the west coast of India. The Directorate of Health Services in Goa gave permission for PREMIUM to operate in 10 of the 14 PHCs in the north district of Goa. We started screening in 8 PHCs, but during the trial, 2 of these PHCs were replaced: 1 had low attendance and 1 had a large proportion of migrant labourers. So, while the trial was conducted in a total of 10 PHCs, at any given time point in the trial, screening was happening in only 8 of these facilities. Participants were consenting males aged 18–65 years who met the a priori eligibility criteria (residing within the PHC catchment area, planning to stay at the same address for at least 12 months, able to speak English or the local vernacular, and not having been screened for harmful drinking in the past 3 months) [14,15] and were harmful drinkers, defined as scoring 12–19 on AUDIT [16], a 10-item screening questionnaire developed by the World Health Organization for the detection of AUDs and validated in India [17]. Consenting participants were randomised in a 1:1 allocation scheme to either of 2 intervention arms (EUC or CAP plus EUC) after completion of the baseline assessments, using sequentially numbered opaque sealed envelopes [18]. Baseline assessments included data on socio-demographic factors and potential moderators of treatment outcome: illness severity (baseline AUDIT score), readiness to change, and expectations from treatment. Enrolment was conducted between 28 October 2013 and 29 July 2015, 3-month assessment was completed on 30 November 2015, and the final 12-month assessment was completed on 30 August 2016. Physicians providing EUC were masked to allocation status, as were the independent assessors who did the outcome assessments, and these people had no contact with the PHCs or other team members. All authors, apart from the data manager (BB), were masked until the trial results were unmasked. Outcomes The following outcomes were examined at 12 months post-enrolment. The 2 primary outcomes were remission, defined as an AUDIT score < 8, and mean standard ethanol (in grams) consumed in the past 14 days immediately preceding the 12-month outcome evaluation. A range of secondary outcomes (S1 Table) included recovery (AUDIT score < 8 at both 3 and 12 months), percent of days abstinent in past 14 days, percent of days of heavy drinking in past 14 days, the Short Inventory of Problems (SIP) mean score, Patient Health Questionnaire 9 (PHQ-9) mean score, disability (WHO Disability Assessment Schedule 2.0 [WHODAS 2.0] score), total days unable to work in past 30 days, suicidal behaviour (suicidal thoughts in past 14 days and/or suicidal attempts in past 3 months), perpetration of intimate partner violence in past 3 months, and resource use and costs of illness estimated from the Client Service Receipt Inventory (CSRI) [19]. Percentage of days abstinent and percentage of days of heavy drinking generated from the Alcohol Timeline Followback were not pre-specified but were added prior to commencing analysis to bring the trial in line with recommendations of the US National Institute on Alcohol Abuse and Alcoholism. Similarly, our proposed mediator of patient-reported readiness to change at 3 months was added to the trial protocol midway through the trial, and thus data were available for only a subset of participants. Patient-reported readiness to change at 3 months was pre-selected as a potential mediator of the intervention for the mean standard ethanol consumption outcome, rather than the remission outcome as measured by the AUDIT score, for 2 reasons: the former is the most widely used outcome in alcohol trials, and it represents a continuous score, which is recommended over binary variables in mediation analyses to capture adequate variance [20]. Description of all the outcome tools and their contextual validity is provided in the published trial protocol (S1 Text) [15]. Sample size estimations Based on the assumptions that participants would be randomised within each of the clinics, with 1 counsellor per PHC at any one time, an intra-cluster correlation of 0.04, a loss to follow-up of 15% over 3 months, and a 1:1 allocation ratio, a trial size of 400 enrolled participants with harmful drinking had 90% power to detect the hypothesized effects (effect size of 0.45 for mean standard ethanol consumed; remission rate of 68% for CAP plus EUC versus 40% for EUC alone) for the primary outcomes, with a 5% type I error. No multiple testing adjustment was made for multiple primary outcomes. Interventions EUC comprised consultation with the PHC physician enhanced by providing the AUDIT screening results to the patient and physician, and a contextualised version of the WHO Mental Health Gap Action Programme (mhGAP) guidelines [21] for harmful drinking to the physician, which included information on when and where to refer for psychiatric care. CAP is a manualised psychological treatment (S2 Text) delivered in 3 phases over a maximum of 4 sessions (each lasting approximately 30–45 minutes) at weekly to fortnightly intervals. The psychosocial strategies used include detailed assessment followed by personalised feedback, cognitive and behavioural skills, and relapse prevention. The stance adopted by the counsellor is that of motivational interviewing [22]. A participant was classified as a ‘planned discharge’ if at least 1 of the following criteria were met: participant’s exit from treatment was decided in collaboration with the counsellor, treatment goals were achieved, or the maximum of 4 sessions were completed. The 11 counsellors were adults who had no prior professional training and/or qualification in the field of mental health, had completed at least high school education, were fluent in the vernacular languages used in the study settings, and were trained and supervised in delivering CAP through a rigorous process. Further details of the intervention [12] and of the selection, training, and supervision of the counsellors are provided elsewhere [23]. The full intervention can be accessed online (http://cap.nextgenu.org). Process and fidelity assessments were based on treatment completion rates from the counsellors’ clinical records, CAP therapy quality scores from peer and expert supervisor ratings of audio-recordings of sessions during weekly group supervision, and therapy quality ratings of a random selection of 10% of all sessions by an expert involved in the development of CAP. The same counsellors also delivered HAP to adults who met criteria for moderate to severe depression. Counsellors maintained separate clinical registers for the 2 groups of patients and reviewed individual patient records before each session. In order to ensure that their treatment-specific counselling skills were maintained throughout the trial, weekly peer-led group supervision sessions were structured in ways that involved holding separate sessions for each of the 2 treatments. This arrangement allowed the expert supervisors for each of the 2 treatments to provide more focused feedback to the counsellors. Statistical analyses Analyses were intention-to-treat, with multiple imputation (20 iterations) for missing outcome data, assuming data were missing at random, and assuming predictive mean matching for positively skewed outcomes. The following variables were used in the imputation model: age, marital status, and baseline AUDIT score. Zero-inflated negative binomial (ZINB) regression [24] was used to estimate the intervention effect for positively skewed over-dispersed outcomes with an excess of zeros. Continuous outcomes with normally distributed residuals were analysed using linear regression, and binary outcomes were analysed using binary logistic regression. All models were adjusted for baseline AUDIT score and for PHC as a fixed effect to allow for within-PHC clustering. For ZINB regression, the intervention effect was estimated for all participants in 1 model as an adjusted prevalence ratio (aPR) with a 95% CI for proportion with zero (i.e., no reported drinking), and with an adjusted count ratio among those with non-zero responses. For other continuous outcomes, the intervention effect was reported as the AMD and 95% CI; for binary outcomes, the intervention effect was reported as aPR estimated using the marginal standardisation technique, with 95% CIs for the prevalence ratios estimated using the delta method [25] following logistic regression. Moderation of treatment effect was assessed for a priori defined moderators. Sensitivity analyses for linear and logistic regression models included adjustment for counsellor as a random effect, and complete case analysis. In addition, repeated measures analysis was conducted, including analysis of change over time between the 3- and 12-month endpoints. The repeated measures analysis included a treatment-by-time interaction term to allow for a different intervention effect at 3 versus 12 months. The Monte Carlo method for assessing mediation (MCMAM) [26] was used for assessing the mediating effects of readiness to change assessed at 3 months on the 12-month primary outcome of mean standard ethanol consumption over the previous 14 days for the sub-sample of participants for whom the mediating variable data had been collected. In the current study, 95% CI was computed with 20,000 repetitions. Economic evaluation was performed from the healthcare system perspective and from a broader societal perspective, which also took account of productivity impacts on patients and families. Costs, including the intervention costs for CAP, per additional remission, additional individual in recovery and quality-adjusted life year (QALY) gained were calculated. Information on the use of health services, including contacts with PHCs, hospital doctor contacts and inpatient stays (including detoxification), medication use, and diagnostic tests, was collected from service users using a tailored version of the CSRI at 3 and 12 months. Unit costs for doctor contacts and inpatient stays were inflated to 2015 prices using published unit costs previously used in an economic evaluation of a brief psychological intervention in Goa [27]. Detailed information on medications and lab tests used were extracted from medical records, including costs to the public purse. Mean health system costs were then extrapolated to cover the full 12 months. Detailed information was also recorded on the time taken to deliver each CAP session and whether it was delivered at a PHC, over the telephone, or at a patient’s home. Travel time and transportation costs (mainly petrol costs) were also recorded for home visits, including ‘no show’ home visits. Per minute unit costs for counsellors, taking account of their training, supervision, costs related to home delivery, and other overheads, were then attached to time to estimate the total costs of intervention delivery. The number of days completely out of normal role (i.e., days unable to work) over the previous 30 days was based on responses to the WHODAS 2.0. WHODAS 2.0 data on days of activity cutback over this period were also included, with the assumption that each day of cutback would have half the value of a complete day out of role. The value of time that patients reported attending health services was estimated; when patients reported being accompanied by someone, it was assumed that 1 family member also incurred the same level of productivity loss. We assumed that the mean of patient and family time costs at 3 months and 12 months would also apply to the rest of the year. Costs due to cutback and complete days out of role were adjusted to avoid double counting time that patients spent attending health services. All patient and family time was valued using different daily wage rates recommended in 2015 by the Indian Office of the Labour Commissioner. The rate used was dependent on whether the patient/family member was classified as an unskilled, skilled, or clerical/professional worker. We assumed the value of days out of role for those classified as unemployed was the same as that for unskilled workers. Further information on data collection methods is provided elsewhere [14,15]. Differences in mean costs were compared using standard parametric tests. QALYs were derived through transformation of WHODAS 2.0 12-item scores [27]. Five imputations were run to deal with missing values for QALYs and cost data. Statistical uncertainty was explored through bootstrapping and the generation of cost-effectiveness acceptability curves showing the likelihood that CAP would be cost-effective at different willingness to pay thresholds. All costs are presented in 2015 international dollars. Statistical analyses were conducted using Excel 2016 and SPSS 21 for the cost-effectiveness analyses, SAS and R-Studio for the mediation analyses, and STATA 13/14 for all other analyses. The PREMIUM statistical analysis plan (version 2, 17 December 2015) was originally drafted to address both 3- and 12-month outcomes. However, following the analyses of the 3-month outcomes, modifications to the plan for the 12-month outcome analyses were proposed, principally by making it a stand-alone plan specifically for the 12-month outcomes. The key differences from the registered protocol included changing SIP to a secondary outcome to reduce multiplicity of the primary outcomes and adding 2 secondary outcomes (percentage of days abstinent and percentage of days of heavy drinking generated from the Alcohol Timeline Followback) to bring the trial in line with recommendations of the US National Institute on Alcohol Abuse and Alcoholism. The draft revised analysis plan was then circulated to the TSC (independent chairperson) and data safety monitoring committee (DSMC) (independent members) for review and discussion through teleconference. The final analysis was started (1 October 2016) only after the analysis plan was approved and locked by the TSC/DSMC members (4 September 2016) (S3 Text). Results Trial conduct A detailed description of the conduct of the trial is provided in the primary trial paper [14]. Between 28 October 2013 and 29 July 2015, 16,007 (21.7%) of the 73,887 adult male PHC attendees assessed met inclusion/exclusion criteria. Of these, 14,773 were screened for harmful drinking using AUDIT, of whom 679 (4.6%) were eligible (AUDIT score 12–19) for inclusion in the trial, and 378 (55.7%) consented to participate and were enrolled. A total of 190 participants were randomised to EUC alone, and 188 to CAP plus EUC. Of the former, 1 was subsequently excluded (erroneously enrolled in this trial as well as the one for depression), leaving a total of 189 participants in the EUC arm (Fig 1). The leading reasons for ineligibility for screening included age younger than 18 years or older than 65 years, already having been screened within the last 3 months, not planning to be resident in the study area for the duration of the study, and being resident outside of the study catchment areas. The common reasons for refusal to participate included ‘no interest’ in the trial (45.2%), ‘no time’ to participate (30.5%), and the patient’s belief that he did not have a problem (17.6%). There was no statistically significant difference in socio-demographic profile and baseline mean AUDIT score between those who consented and those who refused participation. Baseline characteristics were similar by arm. In all, 337 participants (89.4%) completed the primary outcomes at the 3-month post-enrolment endpoint, and 316 participants (83.8%) at the 12-month follow-up; rates were similar between arms. At the 12-month outcome evaluation, 315 participants completed PHQ-9, 312 completed the WHODAS 2.0, and 311 completed the CSRI. A total of 305 (81%) participants had primary outcome data for both follow-up time points. In all, only 30 (8%) participants did not have any follow-up data. Those lost to follow-up at 12 months were significantly younger (mean age [SD] 38.8 [11.8] versus 42.6 [11.2]; p = 0.02) (S2 Table), and this was consistent with the 3-month post-enrolment endpoint. Reasons for loss to follow-up were inability to track down the participant (29 [47.5%] of 61), refusal (20 [32.8%]), and death (12 [19.7%]). In all, 258 (81.1%) participants were seen within the 4-week window period for the 12-month assessment, and there were no statistically significant differences on baseline predictors of delayed 12-month outcome evaluation, i.e., outcome data collected outside the 4-week window period. In the CAP plus EUC arm, 131 (70%) of the participants had a planned discharge. The mean number of sessions for those who had a planned discharge was 2.8 (95% CI 2.7, 3.0), and for those who had an unplanned discharge it was 1.1 (95% CI 1.0, 1.3). Mean therapy quality scores on the basis of peer ratings (n = 183; mean 2.35 [95% CI 2.29, 2.41]), expert supervisor ratings (n = 183; mean 2.44 [95% CI 2.36, 2.51]), and independent ratings for a randomly selected 10% of sessions (n = 40; mean 2.64 [95% CI 2.42, 2.87]) were similar. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Counselling for alcohol problems trial flow chart. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care; HAP, Healthy Activity Programme. https://doi.org/10.1371/journal.pmed.1002386.g001 Impact on clinical outcomes Table 1 describes the intervention effect on all primary and secondary clinical outcomes at 12 months. The proportion with remission (AUDIT < 8) (54.3% versus 31.9%; aPR 1.71 [95% CI 1.32, 2.22]; p < 0.001) was significantly higher in the CAP plus EUC arm than in the EUC alone arm. Analysis of mean standard ethanol consumption showed a significantly higher proportion of participants reporting no alcohol consumption in the past 14 days in the CAP plus EUC arm than in the EUC alone arm (45.1% versus 26.4%; aOR 1.92 [95% CI 1.19, 3.10]; p = 0.008), but no difference in consumption among those who reported any drinking in this period. The proportion of participants in recovery (AUDIT < 8 at both 3 and 12 months) (27.4% versus 15.1%; aPR 1.90 [95% CI 1.21, 3.00]; p = 0.006) and mean percent of days abstinent (71.0% [SD 38.2] versus 55.0% [SD 39.8]; AMD 16.1 [95% CI 7.1, 25.0]; p = 0.001) were significantly higher in the CAP plus EUC arm than in the EUC alone arm. There was no evidence of an intervention effect on PHQ-9 scores, suicidal behaviour, and percentage of days of heavy drinking. The results were similar when adjusted for counsellor as a random effect, and when using complete case analyses (S3 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Effects of CAP plus EUC compared with EUC alone on primary and secondary clinical outcomes at 12 months. https://doi.org/10.1371/journal.pmed.1002386.t001 In repeated measures analyses for the primary outcomes, there was no significant interaction with time for mean standard ethanol consumption in the past 14 days (p = 0.09), amount of drinking among drinkers (p = 0.54), or remission (p = 0.17). We observed no evidence of significant effect modification by baseline AUDIT score, expectations of the usefulness of counselling, or readiness to change on the 2 primary outcomes (S4 Table). AUDIT scores at 3 and 12 months were available in 305 participants (80.9%). Compared to the EUC arm, a greater proportion in the intervention arm experienced a late remission (27.4% versus 15.7%) or were in recovery (27.4% versus 15.1%); in contrast, a greater proportion in the EUC arm remained harmful drinkers at both endpoints (59.1% versus 35.6%) (Fig 2). The remission rate showed an increase at 12 months (aPR 1.71 [95% CI 1.32, 2.22]), compared with 3 months (aPR 1.50 [95% CI 1.09, 2.07]) (Fig 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Clinical trajectories in participants with 3- and 12-month AUDIT data (n = 305) (complete case). Remission defined as AUDIT score < 8. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g002 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Remission in CAP plus EUC and EUC alone arms at 3 and 12 months. Remission defined as AUDIT score < 8. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g003 Other outcomes and mediation analyses There was no evidence of an intervention effect on SIP score, WHODAS 2.0 score, days unable to work, and perpetration of intimate partner violence. We observed no significant differences in the number of serious adverse events between the 2 arms (23 in CAP plus EUC versus 33 in EUC; p = 0.37) (S5 Table). Data on readiness to change at 3 months was available for 151 participants (38.8% in CAP plus EUC arm versus 41.3% in EUC arm; p = 0.62). There was no significant difference in age (mean [SD] 42.8 [10.7] versus 41.4 [11.8] years; p = 0.24) or baseline AUDIT score (mean [SD] 15.0 [2.2] versus 14.8 [2.1]; p = 0.38) between those for whom the data were available and those for whom they were not available. Our mediation results found evidence of the CAP intervention having a predictive role in increased readiness to change at 3 months, and of increased readiness to change having a predictive role in reduced drinking outcomes at 12 months; thus, patient-reported readiness to change at 3 months mediated the effects of the CAP intervention on drinking outcomes at 12 months, whereby the indirect effect (a × b) was −6.014 (95% CI −13.99, −0.046) (Fig 4; S6 and S7 Tables). These relations remained even after controlling for variables that were related to participants’ readiness to change scores or drinking outcomes, including baseline readiness to change, AUDIT and depression scores, which PHC the intervention was delivered in or by which counsellor, and patient education level. Patient-reported readiness to change could account for 54% of the total effect of CAP plus EUC. None of the models demonstrated evidence of multicollinearity between independent variables (variance inflation factor < 4). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Mediating effect of readiness to change at 3 months on mean standard ethanol consumption at 12 months (n = 151). Beta estimates (β) are unstandardised. Multiple linear regression models controlled for baseline readiness to change, AUDIT scores, and PHQ-9 scores, where the intervention was delivered (primary health centre) and who delivered it (health counsellor), and patient education. µp ≤ 0.10. *p < 0.05. ***p < 0.001. Variables as follows: β, Beta coefficient; a, a-path (CAP→mediator); b, b-path (mediator→outcome); c, direct effect (CAP→outcome); a × b, indirect effect. AUDIT, Alcohol Use Disorders Identification Test; Counselling for Alcohol Problems; PHQ-9, Patient Health Questionnaire 9. https://doi.org/10.1371/journal.pmed.1002386.g004 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Effect of CAP plus EUC compared with EUC alone on impact of harmful drinking, disability and intimate partner violence at 12 months. https://doi.org/10.1371/journal.pmed.1002386.t002 Costs and cost-effectiveness From the health system perspective, by 12 months, the mean estimated costs to the health system of providing the intervention were no longer significantly different from the costs of EUC, being slightly lower (though not statistically significantly so) than those for EUC, at $179.59 compared to $206.98 (mean difference −$27.40 [95% CI −$105.90, $51.10]; p = 0.49) (S8 Table). These costs had been significantly higher at 3 months due to the cost of providing CAP; by 12 months these costs were offset by reductions in the use of health services. From a wider societal perspective, which combines impacts on the health system with impacts on productivity costs, CAP plus EUC had a lower overall mean cost than EUC at 12 months of $484.31 per participant, but the difference between arms was not significant (mean difference −$223.12 [95% CI −$524.05, $77.82]; p = 0.15). There was no difference in mean QALYs gained per person at 12 months (mean difference 0.0006 [95% CI −0.091, 0.0102]). Table 3 provides an assessment of incremental cost-effectiveness. From a health system perspective, the CAP plus EUC arm dominates the EUC alone arm, with lower costs per additional remission (−$134 [95% CI −$598, $200]) or additional participant in recovery (−$269 [95% CI −$2,017, $608]) achieved at 12 months. It is difficult to draw conclusions on cost per QALY gained given the negligible difference in QALY outcomes between the 2 arms and thus the wide confidence intervals around incremental costs per QALY gained. To test the robustness of incremental cost-effectiveness ratio (ICER) results, cost-effectiveness analysis planes using 1,000 randomly resampled pairs of costs and remission outcomes or pairs of costs and recovery outcomes from both the health system and societal perspectives were used to generate further estimates of incremental cost per remission (Fig 5) or recovery gained (S1 Fig). Any observations in the southeast quadrant of these planes indicate that CAP plus EUC is cost-saving, having both lower costs and better outcomes than EUC, while observations in the northeast quadrant indicate that CAP plus EUC has increased costs and better outcomes than EUC. A threshold for what society is willing to pay for better outcomes must be determined. In this case we have assumed a very low threshold per additional remission achieved or additional participant in recovery of no more than the monthly wage for an unskilled manual worker in Goa ($415) [28]. This threshold is represented by a solid red line shown in the northeast quadrant. Fig 5A indicates that the ICER for CAP plus EUC compared to EUC has a 72% chance of being in the southeast quadrant—cost-saving per remission at 12 months from a health system perspective, i.e., having both lower costs and better remission outcomes than EUC—while there is a 28% chance of the ICER being in the northeast quadrant, where the intervention is still cost-effective even if costs are higher than for EUC, if an incremental cost per remission achieved threshold of $415 is applied. Overall, therefore, the case for investment is very strong, with a more than 99% likelihood that the intervention represents good value for money. In Fig 5B, when a societal perspective is used, where impacts on productivity losses are also considered, the likelihood of CAP plus EUC being cost-saving increases to 94% and the overall chances of its being cost-effective are over 99%. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Cost effectiveness planes: CAP plus EUC compared to EUC per remission achieved. (A) Health system perspective; (B) societal perspective. CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g005 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Cost-effectiveness analyses from health system and societal perspectives (costs in 2015 international dollars). https://doi.org/10.1371/journal.pmed.1002386.t003 Trial conduct A detailed description of the conduct of the trial is provided in the primary trial paper [14]. Between 28 October 2013 and 29 July 2015, 16,007 (21.7%) of the 73,887 adult male PHC attendees assessed met inclusion/exclusion criteria. Of these, 14,773 were screened for harmful drinking using AUDIT, of whom 679 (4.6%) were eligible (AUDIT score 12–19) for inclusion in the trial, and 378 (55.7%) consented to participate and were enrolled. A total of 190 participants were randomised to EUC alone, and 188 to CAP plus EUC. Of the former, 1 was subsequently excluded (erroneously enrolled in this trial as well as the one for depression), leaving a total of 189 participants in the EUC arm (Fig 1). The leading reasons for ineligibility for screening included age younger than 18 years or older than 65 years, already having been screened within the last 3 months, not planning to be resident in the study area for the duration of the study, and being resident outside of the study catchment areas. The common reasons for refusal to participate included ‘no interest’ in the trial (45.2%), ‘no time’ to participate (30.5%), and the patient’s belief that he did not have a problem (17.6%). There was no statistically significant difference in socio-demographic profile and baseline mean AUDIT score between those who consented and those who refused participation. Baseline characteristics were similar by arm. In all, 337 participants (89.4%) completed the primary outcomes at the 3-month post-enrolment endpoint, and 316 participants (83.8%) at the 12-month follow-up; rates were similar between arms. At the 12-month outcome evaluation, 315 participants completed PHQ-9, 312 completed the WHODAS 2.0, and 311 completed the CSRI. A total of 305 (81%) participants had primary outcome data for both follow-up time points. In all, only 30 (8%) participants did not have any follow-up data. Those lost to follow-up at 12 months were significantly younger (mean age [SD] 38.8 [11.8] versus 42.6 [11.2]; p = 0.02) (S2 Table), and this was consistent with the 3-month post-enrolment endpoint. Reasons for loss to follow-up were inability to track down the participant (29 [47.5%] of 61), refusal (20 [32.8%]), and death (12 [19.7%]). In all, 258 (81.1%) participants were seen within the 4-week window period for the 12-month assessment, and there were no statistically significant differences on baseline predictors of delayed 12-month outcome evaluation, i.e., outcome data collected outside the 4-week window period. In the CAP plus EUC arm, 131 (70%) of the participants had a planned discharge. The mean number of sessions for those who had a planned discharge was 2.8 (95% CI 2.7, 3.0), and for those who had an unplanned discharge it was 1.1 (95% CI 1.0, 1.3). Mean therapy quality scores on the basis of peer ratings (n = 183; mean 2.35 [95% CI 2.29, 2.41]), expert supervisor ratings (n = 183; mean 2.44 [95% CI 2.36, 2.51]), and independent ratings for a randomly selected 10% of sessions (n = 40; mean 2.64 [95% CI 2.42, 2.87]) were similar. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Counselling for alcohol problems trial flow chart. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care; HAP, Healthy Activity Programme. https://doi.org/10.1371/journal.pmed.1002386.g001 Impact on clinical outcomes Table 1 describes the intervention effect on all primary and secondary clinical outcomes at 12 months. The proportion with remission (AUDIT < 8) (54.3% versus 31.9%; aPR 1.71 [95% CI 1.32, 2.22]; p < 0.001) was significantly higher in the CAP plus EUC arm than in the EUC alone arm. Analysis of mean standard ethanol consumption showed a significantly higher proportion of participants reporting no alcohol consumption in the past 14 days in the CAP plus EUC arm than in the EUC alone arm (45.1% versus 26.4%; aOR 1.92 [95% CI 1.19, 3.10]; p = 0.008), but no difference in consumption among those who reported any drinking in this period. The proportion of participants in recovery (AUDIT < 8 at both 3 and 12 months) (27.4% versus 15.1%; aPR 1.90 [95% CI 1.21, 3.00]; p = 0.006) and mean percent of days abstinent (71.0% [SD 38.2] versus 55.0% [SD 39.8]; AMD 16.1 [95% CI 7.1, 25.0]; p = 0.001) were significantly higher in the CAP plus EUC arm than in the EUC alone arm. There was no evidence of an intervention effect on PHQ-9 scores, suicidal behaviour, and percentage of days of heavy drinking. The results were similar when adjusted for counsellor as a random effect, and when using complete case analyses (S3 Table). Download: PPT PowerPoint slide PNG larger image TIFF original image Table 1. Effects of CAP plus EUC compared with EUC alone on primary and secondary clinical outcomes at 12 months. https://doi.org/10.1371/journal.pmed.1002386.t001 In repeated measures analyses for the primary outcomes, there was no significant interaction with time for mean standard ethanol consumption in the past 14 days (p = 0.09), amount of drinking among drinkers (p = 0.54), or remission (p = 0.17). We observed no evidence of significant effect modification by baseline AUDIT score, expectations of the usefulness of counselling, or readiness to change on the 2 primary outcomes (S4 Table). AUDIT scores at 3 and 12 months were available in 305 participants (80.9%). Compared to the EUC arm, a greater proportion in the intervention arm experienced a late remission (27.4% versus 15.7%) or were in recovery (27.4% versus 15.1%); in contrast, a greater proportion in the EUC arm remained harmful drinkers at both endpoints (59.1% versus 35.6%) (Fig 2). The remission rate showed an increase at 12 months (aPR 1.71 [95% CI 1.32, 2.22]), compared with 3 months (aPR 1.50 [95% CI 1.09, 2.07]) (Fig 3). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Clinical trajectories in participants with 3- and 12-month AUDIT data (n = 305) (complete case). Remission defined as AUDIT score < 8. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g002 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Remission in CAP plus EUC and EUC alone arms at 3 and 12 months. Remission defined as AUDIT score < 8. AUDIT, Alcohol Use Disorders Identification Test; CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g003 Other outcomes and mediation analyses There was no evidence of an intervention effect on SIP score, WHODAS 2.0 score, days unable to work, and perpetration of intimate partner violence. We observed no significant differences in the number of serious adverse events between the 2 arms (23 in CAP plus EUC versus 33 in EUC; p = 0.37) (S5 Table). Data on readiness to change at 3 months was available for 151 participants (38.8% in CAP plus EUC arm versus 41.3% in EUC arm; p = 0.62). There was no significant difference in age (mean [SD] 42.8 [10.7] versus 41.4 [11.8] years; p = 0.24) or baseline AUDIT score (mean [SD] 15.0 [2.2] versus 14.8 [2.1]; p = 0.38) between those for whom the data were available and those for whom they were not available. Our mediation results found evidence of the CAP intervention having a predictive role in increased readiness to change at 3 months, and of increased readiness to change having a predictive role in reduced drinking outcomes at 12 months; thus, patient-reported readiness to change at 3 months mediated the effects of the CAP intervention on drinking outcomes at 12 months, whereby the indirect effect (a × b) was −6.014 (95% CI −13.99, −0.046) (Fig 4; S6 and S7 Tables). These relations remained even after controlling for variables that were related to participants’ readiness to change scores or drinking outcomes, including baseline readiness to change, AUDIT and depression scores, which PHC the intervention was delivered in or by which counsellor, and patient education level. Patient-reported readiness to change could account for 54% of the total effect of CAP plus EUC. None of the models demonstrated evidence of multicollinearity between independent variables (variance inflation factor < 4). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Mediating effect of readiness to change at 3 months on mean standard ethanol consumption at 12 months (n = 151). Beta estimates (β) are unstandardised. Multiple linear regression models controlled for baseline readiness to change, AUDIT scores, and PHQ-9 scores, where the intervention was delivered (primary health centre) and who delivered it (health counsellor), and patient education. µp ≤ 0.10. *p < 0.05. ***p < 0.001. Variables as follows: β, Beta coefficient; a, a-path (CAP→mediator); b, b-path (mediator→outcome); c, direct effect (CAP→outcome); a × b, indirect effect. AUDIT, Alcohol Use Disorders Identification Test; Counselling for Alcohol Problems; PHQ-9, Patient Health Questionnaire 9. https://doi.org/10.1371/journal.pmed.1002386.g004 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 2. Effect of CAP plus EUC compared with EUC alone on impact of harmful drinking, disability and intimate partner violence at 12 months. https://doi.org/10.1371/journal.pmed.1002386.t002 Costs and cost-effectiveness From the health system perspective, by 12 months, the mean estimated costs to the health system of providing the intervention were no longer significantly different from the costs of EUC, being slightly lower (though not statistically significantly so) than those for EUC, at $179.59 compared to $206.98 (mean difference −$27.40 [95% CI −$105.90, $51.10]; p = 0.49) (S8 Table). These costs had been significantly higher at 3 months due to the cost of providing CAP; by 12 months these costs were offset by reductions in the use of health services. From a wider societal perspective, which combines impacts on the health system with impacts on productivity costs, CAP plus EUC had a lower overall mean cost than EUC at 12 months of $484.31 per participant, but the difference between arms was not significant (mean difference −$223.12 [95% CI −$524.05, $77.82]; p = 0.15). There was no difference in mean QALYs gained per person at 12 months (mean difference 0.0006 [95% CI −0.091, 0.0102]). Table 3 provides an assessment of incremental cost-effectiveness. From a health system perspective, the CAP plus EUC arm dominates the EUC alone arm, with lower costs per additional remission (−$134 [95% CI −$598, $200]) or additional participant in recovery (−$269 [95% CI −$2,017, $608]) achieved at 12 months. It is difficult to draw conclusions on cost per QALY gained given the negligible difference in QALY outcomes between the 2 arms and thus the wide confidence intervals around incremental costs per QALY gained. To test the robustness of incremental cost-effectiveness ratio (ICER) results, cost-effectiveness analysis planes using 1,000 randomly resampled pairs of costs and remission outcomes or pairs of costs and recovery outcomes from both the health system and societal perspectives were used to generate further estimates of incremental cost per remission (Fig 5) or recovery gained (S1 Fig). Any observations in the southeast quadrant of these planes indicate that CAP plus EUC is cost-saving, having both lower costs and better outcomes than EUC, while observations in the northeast quadrant indicate that CAP plus EUC has increased costs and better outcomes than EUC. A threshold for what society is willing to pay for better outcomes must be determined. In this case we have assumed a very low threshold per additional remission achieved or additional participant in recovery of no more than the monthly wage for an unskilled manual worker in Goa ($415) [28]. This threshold is represented by a solid red line shown in the northeast quadrant. Fig 5A indicates that the ICER for CAP plus EUC compared to EUC has a 72% chance of being in the southeast quadrant—cost-saving per remission at 12 months from a health system perspective, i.e., having both lower costs and better remission outcomes than EUC—while there is a 28% chance of the ICER being in the northeast quadrant, where the intervention is still cost-effective even if costs are higher than for EUC, if an incremental cost per remission achieved threshold of $415 is applied. Overall, therefore, the case for investment is very strong, with a more than 99% likelihood that the intervention represents good value for money. In Fig 5B, when a societal perspective is used, where impacts on productivity losses are also considered, the likelihood of CAP plus EUC being cost-saving increases to 94% and the overall chances of its being cost-effective are over 99%. Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Cost effectiveness planes: CAP plus EUC compared to EUC per remission achieved. (A) Health system perspective; (B) societal perspective. CAP, Counselling for Alcohol Problems; EUC, enhanced usual care. https://doi.org/10.1371/journal.pmed.1002386.g005 Download: PPT PowerPoint slide PNG larger image TIFF original image Table 3. Cost-effectiveness analyses from health system and societal perspectives (costs in 2015 international dollars). https://doi.org/10.1371/journal.pmed.1002386.t003 Discussion We report on the sustained effects, cost-effectiveness, and role of readiness to change in mediating the effectiveness of CAP, a brief psychological treatment for harmful drinking delivered by lay counsellors in routine primary care settings, in a randomised controlled trial in India. Our findings demonstrate (1) that the effects of CAP on remission and abstinence outcomes were not just maintained at 12 months but enhanced in comparison to those observed at 3 months post-enrolment [14], indicating evidence of sustained recovery among harmful drinkers, (2) that the healthcare costs of provision of CAP are offset over 12 months, (3) that CAP produces gains in terms of productivity that have real implications for the individuals involved and for the larger society in which they are embedded, and (4) that patient-reported readiness to change at 3 months mediated the effect of CAP on mean standard ethanol consumption at 12 months. To our knowledge, this is the first randomised controlled trial to evaluate the sustained effectiveness and cost-effectiveness of a brief treatment for harmful drinking delivered by lay counsellors in a low- or middle-income country. The existing evidence base on brief interventions for hazardous or harmful drinking is for delivery by health professionals (e.g., general practitioners, practice nurses) and relates to briefer forms of advice and counselling [29]. Thus, CAP adds to the existing evidence base on 3 main parameters: being targeted specifically at harmful drinkers, being delivered by lay counsellors, and involving a specific psychological treatment intervention. In addition, very few studies in the global literature have assessed what accounts for trial results; our mediation results highlight that patients who were already engaged in changing their behaviours at 3 months were more likely to have reduced drinking alcohol at 12 months. Importantly, this finding suggests a confirmation of the theoretical basis of the motivational interviewing stance of CAP. In addition to the sustained clinical effects, an important economic consideration in favour of CAP is that, over time, the additional costs of providing CAP were offset by reductions in subsequent utilisation of health services; thus, we also observed a high probability of the intervention being cost-saving from a health system perspective, indicating it represented good value for money for policymakers. Although brief interventions have been shown to be effective in the short term, there is a decay in impact over time [7]. Our findings indicate that the effect of CAP on the outcome of remission was sustained between 3 and 12 months, potentially because of the effect of the treatment on readiness to change at 3 months. In addition to motivating the drinker to make a change in thought and action, CAP also provides the harmful drinker with tools to change behaviour and handle a variety of underlying problems. This skill transfer from the counsellor to the harmful drinker potentially empowers the latter to autonomously make changes without the need for continued reinforcement by the counsellor. This would be consistent with findings about cognitive behavioural interventions that demonstrate sustained impact beyond the intervention delivery period due to transfer of skills and people’s empowerment to use them [30,31]. Finally, the mediating role of ‘readiness to change’ on 12-month outcomes parallels previous brief intervention findings [32] and a recent treatment study that identified a large effect of 3-month stage of change on 12-month outcomes [33]. These results underscore the importance of making gains during treatment, particularly securing abstinence after 3 months, in relation to 12-month drinking outcomes. Our findings (a significant effect on remission and abstinence status, yet not on reduction of the amount of alcohol consumed amongst those who did consume alcohol at 12 months) are consistent with the findings at the 3-month outcome evaluation and possibly reflect the prevailing cultural norms that stress the importance of abstinence in India [34]. At 3 months, we also found a greater effect of CAP on those who were not already trying to make a change in their drinking behaviour compared with those who had already started to make a change, which indicates that the treatment enhanced motivation to change. In this paper we now demonstrate that readiness to change at 3 months does mediate the effect of CAP on the amount of alcohol consumed at 12 months, bearing in mind the key role of abstinence in the findings of this study. Notwithstanding the notable benefits of CAP in terms of drinking outcomes, it is clear that CAP did not have an effect on harmful drinking per se (mean standard ethanol consumption) or on the impact of harmful drinking on other domains such as disability and perpetration of domestic violence. There could be several reasons for the absence of these findings. It is possible that it takes longer than 12 months for change in heavy drinking patterns to translate into reduced levels of alcohol problems and into benefits in other related spheres of life, and hence we were not able to detect any differences between the 2 arms. Finally, due to the fluctuating clinical course of AUDs, the symptoms of harmful drinking vary significantly depending on the functional state of the individual, e.g., a harmful drinker with intermittent drinking bouts may show little impact of drinking on other domains of life between bouts, which makes it difficult to consistently measure these outcomes. A key methodological limitation of this trial is reliance on self-reported drinking as the primary outcome. If drinking is under-reported in both randomised arms, this biases effect estimates towards the null. If social desirability bias disproportionately affects the intervention arm, this could lead to exaggeration of treatment effectiveness [35,36]. However, neither biological indicators nor collateral reports are regarded as sufficiently accurate for use in alcohol treatment trials [37]. Another limitation is the relatively high rate of refusal to participate in the trial, but this is very similar to other primary care trials that rely on opportunistic screening to identify participants with AUDs [38]. Finally, we did not adjust for multiple testing although we conducted analyses for 2 primary outcomes. There are also methodological strengths, such as minimal assessments at baseline to avoid assessment reactivity [39], as discussed in the 3-month outcome paper [14]. While the inclusion here of a mediation analysis is a key strength in a pragmatic trial for a psychological treatment for an AUD, we were able to examine mediation in only half of our sample because of the post hoc decision to measure this particular variable in the trial. However, this sub-sample was comparable to the whole sample enrolled in the trial. In addition, we did not measure other potential variables such as self-efficacy or behavioural skills that may mediate the effectiveness of psychological treatments. Nevertheless, the identification of readiness to change as a mediator suggests the importance of assessing this variable as a treatment outcome in interim analyses of longer term outcomes. A key strength of this trial was the use of minimal exclusion criteria to determine eligibility for participation. Our findings have important clinical and policy implications. Despite evidence supporting the effectiveness of brief psychological interventions for AUDs and their selection as a best practice intervention for inclusion in a universal package of interventions for mental and substance use disorders, primary care in the global context has been slow to address the needs of problem drinkers [7,40]. This lack of implementation is due to multiple knowledge, attitudinal, and logistical barriers to implementation [41], including the fact that the majority of research has been conducted in high-income countries, in specialist alcohol treatment settings, and with treatment provided by specialised healthcare providers, all of which greatly limit generalisability to primary care and to LMICs because of varying drinking patterns, acceptability of psychological treatments or acknowledgment of a drinking problem, and lack of specialist health resources. Thus, CAP with its contextual sensitivity to primary care, treatment-naïve populations and suitability for delivery by lay counsellors in primary care, can potentially help to overcome these barriers globally. Furthermore, the importance of our findings cannot be overemphasised for a disorder with a relapsing and remitting course, in which sustained clinical effects are good value for the money. Finally, the scalability of CAP is enhanced by the fact that the lay counsellors had no prior professional mental health training (as would be the case in most real-world settings) and that they were concurrently delivering a different psychological treatment for depression (as would be the case in the real world) [10]. Future research on CAP may include the assessment of potential treatment-, therapist-, and patient-relevant variables on clinical outcomes within the CAP intervention arm, follow-ups of the trial cohorts to assess longer term enduring effects, and the evaluation of methods for scaling up the intervention when delivered by routine healthcare personnel. Supporting information S1 CONSORT Checklist. https://doi.org/10.1371/journal.pmed.1002386.s001 (DOC) S1 Fig. Cost-effectiveness planes: CAP plus EUC compared to EUC alone per recovery achieved. https://doi.org/10.1371/journal.pmed.1002386.s002 (DOCX) S2 Fig. Cost-effectiveness acceptability curve: Willingness to pay per remission achieved via counselling for alcohol problems from a health system perspective. https://doi.org/10.1371/journal.pmed.1002386.s003 (DOCX) S1 Table. Secondary outcomes at 12 months. https://doi.org/10.1371/journal.pmed.1002386.s004 (DOCX) S2 Table. Baseline characteristics of completers of outcome evaluation and those lost to follow-up. 1Includes those who completed the 3- and 12-month evaluations (n = 305) and those who completed only the 12-month evaluation (n = 11). 2Includes those who completed only the 3-month evaluation (n = 31) and those who dropped out before the 3-month evaluation (n = 30). https://doi.org/10.1371/journal.pmed.1002386.s005 (DOCX) S3 Table. Intervention effect on outcomes at 12 months (complete case analysis and random effects). 1Among those with observed data at 12 months. 2Number of participants for whom AUDIT and Alcohol Timeline Followback were available. 3Including imputed outcome data for those with missing data. 4Analysed with a zero-inflated negative binomial model that fits 2 parameters in 1 model, i.e., the proportion with response of zero (e.g., no drinking in 14 days or no days unable to work) and the mean count (e.g., ethanol consumption or days unable to work) among people with a non-zero (positive) response. https://doi.org/10.1371/journal.pmed.1002386.s006 (DOCX) S4 Table. Interaction effect of readiness to change, expectations of treatment, and drinking severity (AUDIT score) at baseline on the effect of CAP on primary outcomes. https://doi.org/10.1371/journal.pmed.1002386.s007 (DOCX) S5 Table. Description of serious adverse events over 12 months by arm. https://doi.org/10.1371/journal.pmed.1002386.s008 (DOCX) S6 Table. Means and 95% CIs for key variables used in mediation analyses. https://doi.org/10.1371/journal.pmed.1002386.s009 (DOCX) S7 Table. Mediation results examining patient-reported readiness to change at 3 months on mean standard ethanol consumption at 12 months (n = 151). Beta estimates (β) are unstandardised. Multiple linear regression models controlled for baseline AUDIT score, baseline PHQ-9 score, where the intervention was delivered (primary health centre) and who delivered it (health counsellor), and patient education. µp ≤ 0.10. *p < 0.05. ***p < 0.001. https://doi.org/10.1371/journal.pmed.1002386.s010 (DOCX) S8 Table. Mean costs (2015 international dollars) and QALYs gained per person over 12 months. https://doi.org/10.1371/journal.pmed.1002386.s011 (DOCX) S1 Text. Study protocol. The effectiveness and cost-effectiveness of lay-counsellor-delivered psychological treatments for harmful and dependent drinking and moderate to severe depression in primary care in India: PREMIUM study protocol for randomised controlled trials. https://doi.org/10.1371/journal.pmed.1002386.s012 (PDF) S2 Text. Counselling for Alcohol Problems (CAP) manual. https://doi.org/10.1371/journal.pmed.1002386.s013 (PDF) S3 Text. Statistical analysis plan for the PREMIUM randomised controlled trials of the effectiveness and cost-effectiveness of lay-counsellor-delivered psychological treatments for harmful and dependent drinking and moderate to severe depression in primary care in India. https://doi.org/10.1371/journal.pmed.1002386.s014 (DOC) Acknowledgments We acknowledge the generous partnership and support of the Directorate of Health Services of the Government of Goa.

doi: 10.1371/journal.pmed.1002382pmid: 28880867

Background Sickle cell disease (SCD), a congenital hemolytic anemia that exacts terrible global morbidity and mortality, is driven by polymerization of mutated sickle hemoglobin (HbS) in red blood cells (RBCs). Fetal hemoglobin (HbF) interferes with this polymerization, but HbF is epigenetically silenced from infancy onward by DNA methyltransferase 1 (DNMT1). Methods and findings To pharmacologically re-induce HbF by DNMT1 inhibition, this first-in-human clinical trial (NCT01685515) combined 2 small molecules—decitabine to deplete DNMT1 and tetrahydrouridine (THU) to inhibit cytidine deaminase (CDA), the enzyme that otherwise rapidly deaminates/inactivates decitabine, severely limiting its half-life, tissue distribution, and oral bioavailability. Oral decitabine doses, administered after oral THU 10 mg/kg, were escalated from a very low starting level (0.01, 0.02, 0.04, 0.08, or 0.16 mg/kg) to identify minimal doses active in depleting DNMT1 without cytotoxicity. Patients were SCD adults at risk of early death despite standard-of-care, randomized 3:2 to THU–decitabine versus placebo in 5 cohorts of 5 patients treated 2X/week for 8 weeks, with 4 weeks of follow-up. The primary endpoint was ≥ grade 3 non-hematologic toxicity. This endpoint was not triggered, and adverse events (AEs) were not significantly different in THU-decitabine—versus placebo-treated patients. At the decitabine 0.16 mg/kg dose, plasma concentrations peaked at approximately 50 nM (Cmax) and remained elevated for several hours. This dose decreased DNMT1 protein in peripheral blood mononuclear cells by >75% and repetitive element CpG methylation by approximately 10%, and increased HbF by 4%–9% (P < 0.001), doubling fetal hemoglobin-enriched red blood cells (F-cells) up to approximately 80% of total RBCs. Total hemoglobin increased by 1.2–1.9 g/dL (P = 0.01) as reticulocytes simultaneously decreased; that is, better quality and efficiency of HbF-enriched erythropoiesis elevated hemoglobin using fewer reticulocytes. Also indicating better RBC quality, biomarkers of hemolysis, thrombophilia, and inflammation (LDH, bilirubin, D-dimer, C-reactive protein [CRP]) improved. As expected with non-cytotoxic DNMT1-depletion, platelets increased and neutrophils concurrently decreased, but not to an extent requiring treatment holds. As an early phase study, limitations include small patient numbers at each dose level and narrow capacity to evaluate clinical benefits. Conclusion Administration of oral THU-decitabine to patients with SCD was safe in this study and, by targeting DNMT1, upregulated HbF in RBCs. Further studies should investigate clinical benefits and potential harms not identified to date. Trial registration ClinicalTrials.gov, NCT01685515 Why was this study done? Sickle cell disease, one of the most frequent inherited diseases in humans, is driven by aggregation and precipitation of less soluble sickle cell hemoglobin in red blood cells—this destroys red blood cells and blocks blood vessels, causing organ damage, suffering, and early death. Fetal hemoglobin, expressed in red blood cells until infancy, mixes with sickle cell hemoglobin and promotes its dissolution. Individuals who naturally express high levels of fetal hemoglobin beyond infancy thus receive some protection from sickle complications. To mimic this natural state using drugs, one relevant observation was that fetal hemoglobin is increased during recovery of bone marrow from extreme stress. This led to evaluation and approval of the cytotoxic (cell killing) drug hydroxyurea, the only drug approved to treat sickle cell disease. This approach to fetal hemoglobin induction, however, is limited in potency and sustainability. Our goal was to increase fetal hemoglobin by inhibiting an enzyme, DNA methyltransferase 1 (DNMT1), involved in shutting off the fetal hemoglobin gene from infancy onward. What did the researchers do and find? We used the drug decitabine to inhibit DNMT1. However, decitabine is very rapidly inactivated in the body by another enzyme, cytidine deaminase (CDA). We therefore combined it with a CDA inhibitor, tetrahydrouridine (THU). Oral THU and decitabine were given to patients with severe, symptomatic sickle cell disease who had not derived benefit from the standard treatment of hydroxyurea. Oral THU-decitabine was safe and well-tolerated by the patients. Measurement of decitabine levels in the blood confirmed that THU enabled oral absorption of very small doses of oral decitabine. Measurements of DNMT1 protein levels and DNA methylation confirmed that this decitabine exposure was sufficient to deplete DNMT1 from cells. DNMT1 depletion by decitabine produced large increases in fetal hemoglobin and increased numbers of healthy red blood cells. What do these findings mean? Oral THU-decitabine to deplete DNMT1 safely increased fetal hemoglobin and numbers of healthy red blood cells. Since this was a first-in-human study, only a small number of patients were treated and for a fairly short time. Further clinical studies are therefore needed. Introduction Sickle cell disease (SCD) is a congenital hemolytic anemia caused by polymerization and precipitation of mutated sickle hemoglobin (HbS, α2βS2) in red blood cells (RBCs). This decreases RBC life span by >90%, causing severe anemia. The unhealthy RBCs also adhere to and occlude blood vessels. Ensuing tissue hypoxia damages all organs, triggers severe pain, and compromises immunity. In low-income countries, most children with SCD do not survive to adulthood. Even in high-income countries, morbidity can be severe and life spans are reduced by several decades—the median life expectancy for people with SCD in the United States is approximately 45 years [1,2]. RBCs at the fetal stage of life contain fetal hemoglobin (HbF, α2γ2). Normal adult hemoglobin (HbA, α2β2) polymerizes with HbS, while HbF intercalates with but does not polymerize with HbS [3–5]. HbF thus interrupts SCD pathophysiology at its inception [3,4], and higher HbF correlates with fewer vaso-occlusive pain crises, less renal damage, less pulmonary hypertension, fewer strokes, and longer survival [1,6–12] (reviewed in [5]). That is, any increase in HbF provides some benefit. Those few SCD patients who inherit HbF at 20%–30% of total hemoglobin (hereditary persistence of fetal hemoglobin, HPFH) have essentially normal life spans [13–15]. Decades of research has hence been directed towards pharmacologic recapitulation of this naturally selected protective state [5]. A key observation directing early efforts was that HbF is enriched during bone marrow recovery from extreme stress [16–21]. Cytotoxic (cell killing) drugs can create such stress, leading to evaluation in SCD of the oral ribonucleotide reductase inhibitor hydroxyurea [20–22]. In a pivotal trial, hydroxyurea (15–35 mg/kg) increased HbF for 2 years in approximately 50% of the adult SCD patients treated [22,23]. HbF induction correlated strongly with increased RBC half-life [24,25], fewer pain crises [23], and better quality of life [26]. Trial patients with HbF levels >0.5 g/dL survived longer [8]. Average HbF increases at 2 years, however, were modest (3.6%) [20–23,27]. Moreover, HbF increases were particularly unlikely in patients with the lowest baseline HbF levels and thus at highest risk of morbidity and mortality [23,25,28,29], and even patients with excellent initial HbF inductions demonstrated diminishing inductions over time [23,30]. Lower and less durable HbF increases also correlated with fewer reticulocytes (<300,000 × 109/L) and neutrophils (<7.5 × 109/L) at baseline. This correlation underscores that HbF induction by cytotoxicity requires reserves of hematopoietic precursors sufficient to repeatedly mount recoveries from bone marrow stress that destroys their counterparts [21,23]. Cumulative attrition of these reserves occurs via vaso-occlusion in the marrow and to the kidneys [23,25,28,29]. This is a problem even separate from considerations of sustainable HbF induction via cytotoxicity: in SCD, erythropoiesis has to operate at >10-fold the normal rate to barely sustain hemoglobin levels compatible with life, and dwindling compensatory capacity is a major cause of early death [8,23,31,32]. Therefore, new, non-cytotoxic, durable, and more potent methods of inducing HbF are needed. The chromatin-modifying enzyme DNA methyltransferase 1 (DNMT1) maintains methylation marks on DNA through cell division. DNMT1 is also a corepressor—it executes the biochemical work of silencing genes for sequence-specific DNA-binding factors, e.g., BCL11A and TR2/TR4, that direct epigenetic silencing of the HbF gene (γ-globin, HBG) [33–45]. The deoxycytidine analog decitabine can deplete DNMT1—a nitrogen substituted for a carbon in the decitabine pyrimidine ring covalently binds to DNMT1 and causes its degradation [46]. Importantly, the decitabine deoxyribose moiety is unmodified; thus, it can incorporate into the elongating DNA strand during S-phase without terminating chain extension or causing cytotoxicity [47,48]. High concentrations of decitabine, however, do produce off-target anti-metabolite effects and cytotoxicity, in significant part via the uridine moiety degradation products that can misincorporate into DNA or inhibit thymidylate synthase [49,50]. Decitabine regimens approved by the US Food and Drug Administration (FDA) for the treatment of myeloid cancer, having evolved out of the traditional cytotoxic intent of oncology, utilize such cytotoxic doses and require pulse-cycled administration to recover from cytotoxic side effects. We therefore redesigned decitabine application for non-cytotoxic, molecularly-targeted therapy of non-malignant and malignant diseases [43,51–54]. Specifically, we selected demonstrably non-cytotoxic yet DNMT1-depleting doses, used a subcutaneous route of administration to blunt Cmax, and administered these doses frequently and in distributed fashion (2–3X/week) to increase the fraction of target cells exposed in S-phase, as DNMT1-depletion by decitabine is S-phase–dependent [43,51–54]. This approach increased HbF by >10% in SCD patients who had no HbF response to hydroxyurea in the pivotal clinical trial (i.e., a mean change in HbF after 2 years of treatment with hydroxyurea of 0.3%) [42,43,55]. Hindering wide clinical application of decitabine in this way, however, are a number of limitations with its pharmacology: it has a very brief plasma half-life of only minutes [56,57] (a problem since DNMT1-depletion is S-phase, and hence exposure-time, dependent); has negligible solid tissue distribution (a problem when target cells reside in solid tissues, e.g., erythroid precursors in the spleen in β-thalassemia); and hence also has negligible oral bioavailability (a problem for worldwide and long-term therapy). These pharmacology problems have a common cause: rapid deamination/inactivation of decitabine to uridine degradation products by the pyrimidine metabolism enzyme cytidine deaminase (CDA) that is highly expressed in tissues such as the intestines and liver [58–62]. Thus, we combined a CDA inhibitor, oral tetrahydrouridine (THU), with oral decitabine: THU is a uridine analog competitive inhibitor of CDA that, although not FDA-approved for any indication (new chemical entity), has not caused toxicity to animals or to humans in several clinical trials, including a trial with oral administration exceeding a year [40,59–61,63–69]. Here, building on encouraging results from pre-clinical in vivo studies [70], we report the first-in-human clinical translation of oral THU–decitabine for HbF induction in SCD. Specific goals were to evaluate safety of oral THU–decitabine and recommend a phase 2 dose for DNMT1-depletion and HbF induction in SCD [70]. Materials and methods Ethics statement All research involving human participants was approved by the Cleveland Clinic and University of Illinois at Chicago Institutional Review Boards (IRBs), and all clinical investigation was conducted according to the principles expressed in the Declaration of Helsinki. Written informed consent was obtained from the participants on the IRB approved protocol. The protocol number was Case 10z11. The United States FDA Investigational New Drug number is 112,914. Study design This was a single-blind dose-escalating phase 1 clinical trial with a maximum of 5 decitabine dose levels. Five patients were enrolled at each dose level, randomized with 3:2 odds to study drugs versus placebo (5 cohorts of 5 randomized patients). This design was not altered during the course of the study. Patient population Written informed consent was obtained prior to treatment in all patients. The treatment population was adult (≥18 years of age) SCD (SS or S-β-thalassemia) patients who despite standard-of-care hydroxyurea for ≥6 months (or being intolerant or unwilling to take hydroxyurea) were at risk of early death as defined by published criteria [8]. These criteria were at least 1 of the following: (i) HbF <0.5 g/dL, (ii) 3 or more pain episodes per year requiring parenteral narcotics, (iii) 1 or more acute chest syndrome episodes, and (iv) total hemoglobin <9 g/dL and absolute reticulocyte count ≤250,000 × 109/L. Interventions Decitabine and THU were synthesized by Ash Stevens (Detroit, MI). Drugs were stored in glass bottles at −20°C. Bottles were opened after equilibration to room temperature. The appropriate amount of drug was weighed out and reconstituted with water for consumption by patients in the clinic within 30 minutes of drug reconstitution. Placebo was an equivalent amount of water without study drug. Fixed-dose oral THU 10 mg/kg was administered 60 minutes before oral decitabine at 0.01, 0.02, 0.04, 0.08, or 0.16 mg/kg (Figs 1, 2A and 2B). Repeat dose administration 2X/week for 8 weeks, instead of single dose administration, was used to assess safety and efficacy—to increase the likelihood that the dose identified for further studies would be safe and efficacious for the intended application of chronic disease modification (Fig 2A and 2B). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Fetal hemoglobin (HbF) blocks polymerization of deoxy sickle hemoglobin (HbS), the root cause of sickle cell disease (SCD) pathophysiology, and is the most powerful known disease modifier. (A) Polymerization of deoxy HbS drives all SCD pathophysiology; In contrast to HbF, normal adult hemoglobin (HbA, ẞ-chains) can participate in polymerization. (B) The gene for HbF (HBG) is silenced by DNA methyltransferase 1 (DNMT1). Although DNA-binding factors, e.g., BCL11A, direct this silencing, the biochemical work of epigenetic repression is executed by chromatin-modifying enzymes, amongst which DNMT1 is central. Decitabine depletes DNMT1 and can do so without cytotoxicity because in contrast to other cytidine analogues (e.g., cytarabine) the deoxyribose moiety (green dotted circle) is natural, although higher concentrations do cause anti-metabolite effects and DNA damage, in part by degradation into uridine counterparts that misincorporate into DNA. (C) Several pharmacologic limitations of decitabine hinder safe, effective, practical clinical translation. The limitations have a common cause, the enzyme cytidine deaminase (CDA). Tetrahydrouridine (THU) inhibits CDA. No toxicities have been found for THU in animals or humans. https://doi.org/10.1371/journal.pmed.1002382.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Design rationale, schema, flow, and patient characteristics. (A) Decitabine regimens approved by the US Food and Drug Administration (FDA) to treat myeloid malignancy utilize cytotoxic decitabine doses (red zone), requiring pulse-cycled administration to recover from cytotoxic side effects. This clinical trial instead escalated oral decitabine doses from almost zero (0.01 mg/kg) gradually upward to find the minimum doses required to deplete DNA methyltransferase 1 (DNMT1) without cytotoxicity (green zone) when administered after oral tetrahydrouridine (THU) 10 mg/kg. Because such doses are non-cytotoxic, they can be administered frequently in distributed fashion to increase the fraction of target cells subject to S-phase–dependent DNMT1 depletion. (B) The study schema. (C) Flow of patients through the trial. (D) Patient clinical characteristics at baseline. Abbreviations: ACS, acute chest syndrome; AVN, acute vascular necrosis; CVA, cerebral vascular accident; ED/Hosp, emergency department/hospital; PE/DVT, pulmonary embolus/deep vein thrombosis. (E) Patient demographics and baseline laboratory variables. Median and range showed for continuous variables. P values Wilcoxon ranked sums 2-tailed or Fisher exact test. https://doi.org/10.1371/journal.pmed.1002382.g002 Patients at each dose level were monitored weekly to determine if next treatments should be withheld based on laboratory endpoints; in previous clinical trials, the most sensitive indices of decitabine biologic activity were an increase in the platelet count and a decrease in the absolute neutrophil count (ANC). The plan was to use threshold values of these parameters not associated with clinical toxic events, being within the range observed in patients with SCD during their routine care with hydroxyurea and/or splenectomy, to trigger dose modification, and thereby maintain safety [43,51]. These thresholds were ANC <1.5 × 109/L and platelets >1,200 × 109/L. Non-hematologic toxicity ≥grade 3 attributed to study drug was also to trigger a dose modification, as was decitabine Cmax > 0.2 μM. Drug was to be held until recovery below these thresholds, when drug was to be restarted with a 25% decrease in dose. Concurrent hydroxyurea therapy was explicitly disallowed, with a requirement for a 28-day washout period from the last hydroxyurea dose to initiation of study drug or placebo. Outcomes The primary endpoint was ≥ grade 3 non-hematologic toxicity. In addition, the a priori study design required dose modification for platelets >1,200 × 109/L, or neutrophils <1.5 × 109/L. Our goal was to provide evidence in favor of a null hypothesis that patients in treated groups (oral THU-decitabine 2X/week over 8 weeks; n = 15) do not experience treatment-related events requiring dose modification more than patients in the placebo group (n = 10). Secondary endpoints included (i) sickle cell crisis frequency (efficacy), (ii) coagulation (D-dimer) and inflammatory (C-reactive protein [CRP]) pathway activity (efficacy), (iii) HbF levels measured by high-performance liquid chromatography (HPLC) (efficacy and pharmacodynamics of decitabine), (iv) DNA methylation levels at repetitive elements in buffy coat DNA (pharmacodynamics of decitabine), and (v) DNMT1 levels in buffy coat cells (pharmacodynamics of decitabine). A priori secondary endpoints not measured for cost and technical reasons were CDA genotype and CDA functional activity in serum. Sample size The study employed a randomized design to identify an oral dose of decitabine that can be administered twice a week in combination with oral THU over an 8-week period without requiring dose modification. We used a standard 3+3 dose escalation design with at most 5 dose levels. There would thus have been 6 in the maximum dose group if a dose-limiting toxicity had been detected. Such a 6-patient group would have detected at least 1 toxicity with a probability of 0.88 if it occurred in 30% of the population; this value is calculated as 1 minus the probability of zero toxicities, i.e., 1 − 0.76. Ten patients were treated with placebos, 2 at each dose level, so the maximum sample size was 15 + 10 = 25. If a dose modification was required because of ANC < 1.5 × 109/L or platelets > 1200 × 109/L or ≥ grade 3 non-hematologic toxicity attributed to the study drug, in 1 or more of the 3 patients who received the study drug at a dose-level cohort, the plan was to accrue another cohort of 5 new patients (3:2 study-drug:placebo) with the treatment dose based on the cumulative dose administered to patients receiving the study drug in the preceding cohort. The Safety and Intent-To-Treat (ITT) populations included all enrolled patients receiving at least one dose of decitabine. Randomization procedures Randomization was at the University of Illinois at Chicago by Dr. Michael Pacini using a randomization table created on www.randomization.com. Patients were randomly allocated to study drug treatment versus placebo. Blinding Patients, but not investigators, were blinded as to the assigned treatment. The experimental treatment was highly diluted in water. Therefore, the method of patient blinding was administration of water placebo with similar appearance, volume, and taste as the study drug. Pharmacokinetics Blood was collected for pharmacokinetic analysis at 0, 2, 4, and 24 hours after the first decitabine dose (week 1). Blood samples were drawn over a period of less than 1 minute into tubes pre-loaded with heparin and THU 10 μg/ml (to prevent in vitro metabolism by CDA) and immediately transferred onto ice. Samples were then centrifuged as soon as possible at 600 g for 5 minutes at 4°C. After separation, plasma was transferred in 0.2 ml aliquots into pre-frozen vials and stored frozen at −80°C until shipment to Ohio State University for analysis (shipment on dry ice) by a liquid chromatography tandem mass spectrometry (LCMS/MS) method that has been previously described in detail for determination of decitabine in human, baboon, mouse, and rat plasma [56,57,70]. Pharmacokinetic data were analyzed using non-compartmental methods or a 2-compartment model with instantaneous/intravenous input using the R package PKLMfit. The model-fitting method allowed estimation of terminal half-lives for some data sets. The AUClast (the area under the curve from the time of dosing to the last measurable concentration) was calculated by the linear trapezoidal method. DNMT1 protein measurement by flow cytometry of peripheral blood mononuclear cells (pharmacodynamic analyses) Phlebotomized whole blood was layered over Histopaque. The interface was collected and washed with phosphate-buffered saline (PBS). Cell suspensions of approximately 200,000 cells were fixed with 4% paraformaldehyde for 30 minutes on ice. Cells were spun down, washed in PBS, and suspended in 70% ethanol and stored at −20°C for subsequent batched analyses. For analyses, patient samples were thawed and centrifuged. All procedures were performed on ice and all centrifugations were done at 400 g for 5 minutes at 4°C. The pellet was hydrated overnight in 1 ml sterile, distilled water to partially reverse the alcohol fixation. After incubation, samples were centrifuged and then resuspended in 1 ml PBS/2% bovine serum albumin (BSA) and incubated for 30 minutes to block nonspecific antibody binding. Following centrifugation, unlabeled anti-DNMT1 antibody [EPR 3522] (0.0625 μg/test; Abcam; catalog no. ab92314) was added in a final volume of 100 μl and incubated for 1 hour. Samples were washed 3 times: each wash was a 10-minute incubation with 1 ml PBS/2% BSA followed by centrifugation. After the third wash, CD64-Alexa Fluor 488 (5 μl/test; BioLegend; catalog no. 305010), Cyclin A2-PE (4μl/test; Beckman Coulter; catalog no. B15092), CD33-APC/Cy7 (5 μl/test; BioLegend; catalog no. 366614), and F(ab′)2-goat anti-rabbit IgG (H+L) Alexa Fluor 647 (0.0938 μg/test; Life Technologies; catalog no. A21246) were added in a final volume of 100 μl and incubated for 1 hour. After the incubation and without washing, 3.5 ml PBS containing 0.5 μg/ml DAPI was added to each sample. All samples were analyzed on an Attune NxT Acoustic Focusing Cytometer (Life Technologies) at a flow rate of 500 μl per minute. Compensation was performed with CompBeads Set Anti-Mouse Ig, κ (BD Biosciences; catalog no. 552843) and Flow Cytometry Protein G Antibody Binding Beads (Bangs Laboratories, Inc.; catalog no. 554/11863). Data analysis. Data were normalized to the instrument using 8-peak SPHERO Rainbow Calibration Particles (Spherotech; catalog no. RCP-30-5A). WinList 3D v8.0 (Verity Software House) was used for post-acquisition analysis. Doublet discrimination was performed using the DAPI area and peak signals. Gated singlet events were displayed in a bivariate plot of cyclin A2 versus DNA content to identify S + G2 + M phase cells as both cyclin A2 positive and >2C DNA. These color-evented cells were used as a guide to set the boundary between DNMT1 positive and negative events. The median DNMT1-negative value was subtracted from the median DNMT1-positive value. This net value was further processed by normalization using linear regression of 8 peak bead sets between runs performed on different days. Methylation level of LINE-1 repetitive element CpG by pyrosequencing DNA was purified from peripheral blood mononuclear cells (isolated by Ficoll-Hypaque density centrifugation) using the Wizard Genomic DNA Purification Kit (Promega). DNA was bisulfite-converted using EZ DNA Lightning Methylation kit (Zymo Research). The PCR primers were 10 pmol of 5′- TTTTTTGAGTTAGGTGTGGG-3′ and 10 pmol of biotinylated-5′-TCTCACTAAAAAATACCAAAC-3′. PCR cycling conditions were: cycle temperature of 94°C for 30 seconds, 60°C for 30 seconds, and 72°C for 30 seconds, for 45 cycles to consume all the biotinylated primers. The biotinylated strand was captured on streptavidin sepharose beads (Amersham Biosciences, Uppsala, Sweden) and annealed with the sequencing primer 5′-GGGTGGGAGTGAT-3′. The methylation degree of long interspersed nuclear elements (LINE-1) was computed at 3 CpG sites pyrosequenced with the Pyromark Q24 Pyrosequencer (Qiagen) using the dispensation order GTCGATTAGTAGTCAGTCGTATTGTATC. Clinical pathology tests Blood counts, blood chemistries, total bilirubin, HbF, LDH, and D-dimer levels were standard clinical pathology tests through the CLIA-certified Clinical Pathology Laboratory at the University of Illinois at Chicago. Measurement of HbF levels Analysis of globin chains was performed on a TSP Spectra HPLC system using a LiChristopher 100 RP-8 column and a gradient of acetonitrile-methanol-NaCl as per the standard CLIA-certified Clinical Pathology Laboratory methods at University of Illinois at Chicago. For quantification of F-cells by flow cytometry, peripheral blood samples were fixed and stained with phycoerythrin-conjugated anti-HbF (Caltag) per manufacturer’s instructions. A normal adult negative control and cord blood positive control were run with each Becton-Dickinson FacsCalibur (Sunnyvale, CA) analysis. Statistics For statistical comparisons of adverse events (AEs) between placebo and each dose group, we performed exact tests of the null hypothesis that the rate parameters of Poisson distributed AEs are equal. Relative risks are given as the ratio of such rate parameters. Thus, differences are insignificant if relative risks confidence intervals include 1. The R function poisson.test(), an exact test, was used. Pain, the most frequent AE, was analyzed similarly. For time course analyses of HbF and total hemoglobin endpoints in placebo versus each dose group, linear functions of time were fitted to each patient’s time course of measurements on-treatment. The slopes of such fits versus the dose that the patient received were fitted to linear dose-response to generate P values of such slopes of slopes, i.e., lines in dose-response plots. This approach controls for inter-patient differences in initial values as per the planned mixed-effects modeling. Ethics statement All research involving human participants was approved by the Cleveland Clinic and University of Illinois at Chicago Institutional Review Boards (IRBs), and all clinical investigation was conducted according to the principles expressed in the Declaration of Helsinki. Written informed consent was obtained from the participants on the IRB approved protocol. The protocol number was Case 10z11. The United States FDA Investigational New Drug number is 112,914. Study design This was a single-blind dose-escalating phase 1 clinical trial with a maximum of 5 decitabine dose levels. Five patients were enrolled at each dose level, randomized with 3:2 odds to study drugs versus placebo (5 cohorts of 5 randomized patients). This design was not altered during the course of the study. Patient population Written informed consent was obtained prior to treatment in all patients. The treatment population was adult (≥18 years of age) SCD (SS or S-β-thalassemia) patients who despite standard-of-care hydroxyurea for ≥6 months (or being intolerant or unwilling to take hydroxyurea) were at risk of early death as defined by published criteria [8]. These criteria were at least 1 of the following: (i) HbF <0.5 g/dL, (ii) 3 or more pain episodes per year requiring parenteral narcotics, (iii) 1 or more acute chest syndrome episodes, and (iv) total hemoglobin <9 g/dL and absolute reticulocyte count ≤250,000 × 109/L. Interventions Decitabine and THU were synthesized by Ash Stevens (Detroit, MI). Drugs were stored in glass bottles at −20°C. Bottles were opened after equilibration to room temperature. The appropriate amount of drug was weighed out and reconstituted with water for consumption by patients in the clinic within 30 minutes of drug reconstitution. Placebo was an equivalent amount of water without study drug. Fixed-dose oral THU 10 mg/kg was administered 60 minutes before oral decitabine at 0.01, 0.02, 0.04, 0.08, or 0.16 mg/kg (Figs 1, 2A and 2B). Repeat dose administration 2X/week for 8 weeks, instead of single dose administration, was used to assess safety and efficacy—to increase the likelihood that the dose identified for further studies would be safe and efficacious for the intended application of chronic disease modification (Fig 2A and 2B). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 1. Fetal hemoglobin (HbF) blocks polymerization of deoxy sickle hemoglobin (HbS), the root cause of sickle cell disease (SCD) pathophysiology, and is the most powerful known disease modifier. (A) Polymerization of deoxy HbS drives all SCD pathophysiology; In contrast to HbF, normal adult hemoglobin (HbA, ẞ-chains) can participate in polymerization. (B) The gene for HbF (HBG) is silenced by DNA methyltransferase 1 (DNMT1). Although DNA-binding factors, e.g., BCL11A, direct this silencing, the biochemical work of epigenetic repression is executed by chromatin-modifying enzymes, amongst which DNMT1 is central. Decitabine depletes DNMT1 and can do so without cytotoxicity because in contrast to other cytidine analogues (e.g., cytarabine) the deoxyribose moiety (green dotted circle) is natural, although higher concentrations do cause anti-metabolite effects and DNA damage, in part by degradation into uridine counterparts that misincorporate into DNA. (C) Several pharmacologic limitations of decitabine hinder safe, effective, practical clinical translation. The limitations have a common cause, the enzyme cytidine deaminase (CDA). Tetrahydrouridine (THU) inhibits CDA. No toxicities have been found for THU in animals or humans. https://doi.org/10.1371/journal.pmed.1002382.g001 Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 2. Design rationale, schema, flow, and patient characteristics. (A) Decitabine regimens approved by the US Food and Drug Administration (FDA) to treat myeloid malignancy utilize cytotoxic decitabine doses (red zone), requiring pulse-cycled administration to recover from cytotoxic side effects. This clinical trial instead escalated oral decitabine doses from almost zero (0.01 mg/kg) gradually upward to find the minimum doses required to deplete DNA methyltransferase 1 (DNMT1) without cytotoxicity (green zone) when administered after oral tetrahydrouridine (THU) 10 mg/kg. Because such doses are non-cytotoxic, they can be administered frequently in distributed fashion to increase the fraction of target cells subject to S-phase–dependent DNMT1 depletion. (B) The study schema. (C) Flow of patients through the trial. (D) Patient clinical characteristics at baseline. Abbreviations: ACS, acute chest syndrome; AVN, acute vascular necrosis; CVA, cerebral vascular accident; ED/Hosp, emergency department/hospital; PE/DVT, pulmonary embolus/deep vein thrombosis. (E) Patient demographics and baseline laboratory variables. Median and range showed for continuous variables. P values Wilcoxon ranked sums 2-tailed or Fisher exact test. https://doi.org/10.1371/journal.pmed.1002382.g002 Patients at each dose level were monitored weekly to determine if next treatments should be withheld based on laboratory endpoints; in previous clinical trials, the most sensitive indices of decitabine biologic activity were an increase in the platelet count and a decrease in the absolute neutrophil count (ANC). The plan was to use threshold values of these parameters not associated with clinical toxic events, being within the range observed in patients with SCD during their routine care with hydroxyurea and/or splenectomy, to trigger dose modification, and thereby maintain safety [43,51]. These thresholds were ANC <1.5 × 109/L and platelets >1,200 × 109/L. Non-hematologic toxicity ≥grade 3 attributed to study drug was also to trigger a dose modification, as was decitabine Cmax > 0.2 μM. Drug was to be held until recovery below these thresholds, when drug was to be restarted with a 25% decrease in dose. Concurrent hydroxyurea therapy was explicitly disallowed, with a requirement for a 28-day washout period from the last hydroxyurea dose to initiation of study drug or placebo. Outcomes The primary endpoint was ≥ grade 3 non-hematologic toxicity. In addition, the a priori study design required dose modification for platelets >1,200 × 109/L, or neutrophils <1.5 × 109/L. Our goal was to provide evidence in favor of a null hypothesis that patients in treated groups (oral THU-decitabine 2X/week over 8 weeks; n = 15) do not experience treatment-related events requiring dose modification more than patients in the placebo group (n = 10). Secondary endpoints included (i) sickle cell crisis frequency (efficacy), (ii) coagulation (D-dimer) and inflammatory (C-reactive protein [CRP]) pathway activity (efficacy), (iii) HbF levels measured by high-performance liquid chromatography (HPLC) (efficacy and pharmacodynamics of decitabine), (iv) DNA methylation levels at repetitive elements in buffy coat DNA (pharmacodynamics of decitabine), and (v) DNMT1 levels in buffy coat cells (pharmacodynamics of decitabine). A priori secondary endpoints not measured for cost and technical reasons were CDA genotype and CDA functional activity in serum. Sample size The study employed a randomized design to identify an oral dose of decitabine that can be administered twice a week in combination with oral THU over an 8-week period without requiring dose modification. We used a standard 3+3 dose escalation design with at most 5 dose levels. There would thus have been 6 in the maximum dose group if a dose-limiting toxicity had been detected. Such a 6-patient group would have detected at least 1 toxicity with a probability of 0.88 if it occurred in 30% of the population; this value is calculated as 1 minus the probability of zero toxicities, i.e., 1 − 0.76. Ten patients were treated with placebos, 2 at each dose level, so the maximum sample size was 15 + 10 = 25. If a dose modification was required because of ANC < 1.5 × 109/L or platelets > 1200 × 109/L or ≥ grade 3 non-hematologic toxicity attributed to the study drug, in 1 or more of the 3 patients who received the study drug at a dose-level cohort, the plan was to accrue another cohort of 5 new patients (3:2 study-drug:placebo) with the treatment dose based on the cumulative dose administered to patients receiving the study drug in the preceding cohort. The Safety and Intent-To-Treat (ITT) populations included all enrolled patients receiving at least one dose of decitabine. Randomization procedures Randomization was at the University of Illinois at Chicago by Dr. Michael Pacini using a randomization table created on www.randomization.com. Patients were randomly allocated to study drug treatment versus placebo. Blinding Patients, but not investigators, were blinded as to the assigned treatment. The experimental treatment was highly diluted in water. Therefore, the method of patient blinding was administration of water placebo with similar appearance, volume, and taste as the study drug. Pharmacokinetics Blood was collected for pharmacokinetic analysis at 0, 2, 4, and 24 hours after the first decitabine dose (week 1). Blood samples were drawn over a period of less than 1 minute into tubes pre-loaded with heparin and THU 10 μg/ml (to prevent in vitro metabolism by CDA) and immediately transferred onto ice. Samples were then centrifuged as soon as possible at 600 g for 5 minutes at 4°C. After separation, plasma was transferred in 0.2 ml aliquots into pre-frozen vials and stored frozen at −80°C until shipment to Ohio State University for analysis (shipment on dry ice) by a liquid chromatography tandem mass spectrometry (LCMS/MS) method that has been previously described in detail for determination of decitabine in human, baboon, mouse, and rat plasma [56,57,70]. Pharmacokinetic data were analyzed using non-compartmental methods or a 2-compartment model with instantaneous/intravenous input using the R package PKLMfit. The model-fitting method allowed estimation of terminal half-lives for some data sets. The AUClast (the area under the curve from the time of dosing to the last measurable concentration) was calculated by the linear trapezoidal method. DNMT1 protein measurement by flow cytometry of peripheral blood mononuclear cells (pharmacodynamic analyses) Phlebotomized whole blood was layered over Histopaque. The interface was collected and washed with phosphate-buffered saline (PBS). Cell suspensions of approximately 200,000 cells were fixed with 4% paraformaldehyde for 30 minutes on ice. Cells were spun down, washed in PBS, and suspended in 70% ethanol and stored at −20°C for subsequent batched analyses. For analyses, patient samples were thawed and centrifuged. All procedures were performed on ice and all centrifugations were done at 400 g for 5 minutes at 4°C. The pellet was hydrated overnight in 1 ml sterile, distilled water to partially reverse the alcohol fixation. After incubation, samples were centrifuged and then resuspended in 1 ml PBS/2% bovine serum albumin (BSA) and incubated for 30 minutes to block nonspecific antibody binding. Following centrifugation, unlabeled anti-DNMT1 antibody [EPR 3522] (0.0625 μg/test; Abcam; catalog no. ab92314) was added in a final volume of 100 μl and incubated for 1 hour. Samples were washed 3 times: each wash was a 10-minute incubation with 1 ml PBS/2% BSA followed by centrifugation. After the third wash, CD64-Alexa Fluor 488 (5 μl/test; BioLegend; catalog no. 305010), Cyclin A2-PE (4μl/test; Beckman Coulter; catalog no. B15092), CD33-APC/Cy7 (5 μl/test; BioLegend; catalog no. 366614), and F(ab′)2-goat anti-rabbit IgG (H+L) Alexa Fluor 647 (0.0938 μg/test; Life Technologies; catalog no. A21246) were added in a final volume of 100 μl and incubated for 1 hour. After the incubation and without washing, 3.5 ml PBS containing 0.5 μg/ml DAPI was added to each sample. All samples were analyzed on an Attune NxT Acoustic Focusing Cytometer (Life Technologies) at a flow rate of 500 μl per minute. Compensation was performed with CompBeads Set Anti-Mouse Ig, κ (BD Biosciences; catalog no. 552843) and Flow Cytometry Protein G Antibody Binding Beads (Bangs Laboratories, Inc.; catalog no. 554/11863). Data analysis. Data were normalized to the instrument using 8-peak SPHERO Rainbow Calibration Particles (Spherotech; catalog no. RCP-30-5A). WinList 3D v8.0 (Verity Software House) was used for post-acquisition analysis. Doublet discrimination was performed using the DAPI area and peak signals. Gated singlet events were displayed in a bivariate plot of cyclin A2 versus DNA content to identify S + G2 + M phase cells as both cyclin A2 positive and >2C DNA. These color-evented cells were used as a guide to set the boundary between DNMT1 positive and negative events. The median DNMT1-negative value was subtracted from the median DNMT1-positive value. This net value was further processed by normalization using linear regression of 8 peak bead sets between runs performed on different days. Data analysis. Data were normalized to the instrument using 8-peak SPHERO Rainbow Calibration Particles (Spherotech; catalog no. RCP-30-5A). WinList 3D v8.0 (Verity Software House) was used for post-acquisition analysis. Doublet discrimination was performed using the DAPI area and peak signals. Gated singlet events were displayed in a bivariate plot of cyclin A2 versus DNA content to identify S + G2 + M phase cells as both cyclin A2 positive and >2C DNA. These color-evented cells were used as a guide to set the boundary between DNMT1 positive and negative events. The median DNMT1-negative value was subtracted from the median DNMT1-positive value. This net value was further processed by normalization using linear regression of 8 peak bead sets between runs performed on different days. Methylation level of LINE-1 repetitive element CpG by pyrosequencing DNA was purified from peripheral blood mononuclear cells (isolated by Ficoll-Hypaque density centrifugation) using the Wizard Genomic DNA Purification Kit (Promega). DNA was bisulfite-converted using EZ DNA Lightning Methylation kit (Zymo Research). The PCR primers were 10 pmol of 5′- TTTTTTGAGTTAGGTGTGGG-3′ and 10 pmol of biotinylated-5′-TCTCACTAAAAAATACCAAAC-3′. PCR cycling conditions were: cycle temperature of 94°C for 30 seconds, 60°C for 30 seconds, and 72°C for 30 seconds, for 45 cycles to consume all the biotinylated primers. The biotinylated strand was captured on streptavidin sepharose beads (Amersham Biosciences, Uppsala, Sweden) and annealed with the sequencing primer 5′-GGGTGGGAGTGAT-3′. The methylation degree of long interspersed nuclear elements (LINE-1) was computed at 3 CpG sites pyrosequenced with the Pyromark Q24 Pyrosequencer (Qiagen) using the dispensation order GTCGATTAGTAGTCAGTCGTATTGTATC. Clinical pathology tests Blood counts, blood chemistries, total bilirubin, HbF, LDH, and D-dimer levels were standard clinical pathology tests through the CLIA-certified Clinical Pathology Laboratory at the University of Illinois at Chicago. Measurement of HbF levels Analysis of globin chains was performed on a TSP Spectra HPLC system using a LiChristopher 100 RP-8 column and a gradient of acetonitrile-methanol-NaCl as per the standard CLIA-certified Clinical Pathology Laboratory methods at University of Illinois at Chicago. For quantification of F-cells by flow cytometry, peripheral blood samples were fixed and stained with phycoerythrin-conjugated anti-HbF (Caltag) per manufacturer’s instructions. A normal adult negative control and cord blood positive control were run with each Becton-Dickinson FacsCalibur (Sunnyvale, CA) analysis. Statistics For statistical comparisons of adverse events (AEs) between placebo and each dose group, we performed exact tests of the null hypothesis that the rate parameters of Poisson distributed AEs are equal. Relative risks are given as the ratio of such rate parameters. Thus, differences are insignificant if relative risks confidence intervals include 1. The R function poisson.test(), an exact test, was used. Pain, the most frequent AE, was analyzed similarly. For time course analyses of HbF and total hemoglobin endpoints in placebo versus each dose group, linear functions of time were fitted to each patient’s time course of measurements on-treatment. The slopes of such fits versus the dose that the patient received were fitted to linear dose-response to generate P values of such slopes of slopes, i.e., lines in dose-response plots. This approach controls for inter-patient differences in initial values as per the planned mixed-effects modeling. Results Patient flow and characteristics The trial protocol is provided as S1 Text, the CONSORT statement as S2 Text, and the patient flow is shown in Fig 2C. Twenty-seven patients were screened and 25 eligible patients enrolled at the University of Illinois at Chicago with the first patient starting the study drug on Sept 5, 2012 and the last patient receiving the last dose of the study drug on Jan 6, 2016. Patients met inclusion criteria for high-risk disease despite standard of care, and hydroxyurea treatment was discontinued at least 28 days prior to initiation of the study drug or placebo [8] (Fig 2D). Placebo-treated patients were older than study drug–treated patients, a difference produced randomly. Median age of the 4 male and 21 female patients was 34 years (range 23–56) (Fig 2E). Baseline laboratory values reflected hemolytic anemia and were similar in drug- and placebo-treated patients (Fig 2E). AEs The primary endpoint of ≥ grade 3 non-hematologic toxicities was not triggered, nor did any patients trigger the platelets >1,200 × 109/L, or neutrophils <1.5 × 109/L thresholds requiring dose modification. There were no grade 4 AEs (Fig 3A). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Adverse events (AEs). (A) AEs with possible relatedness to the study drug (AEs other than “unrelated”) per judgement of the treating clinical teams. (B) All grade 3 AEs occurring in study drug—and placebo-treated patients. These grade 3 AEs were sickle cell complications judged to be unrelated to the study drug by the treating clinical teams. (C) Statistical comparison of grade 3 AEs between placebo and decitabine dose-level patients. R function poisson.test(), an exact test, was used. Abbreviation: ED/Hosp, emergency department/hospital. https://doi.org/10.1371/journal.pmed.1002382.g003 This study was not designed or powered to demonstrate clinical benefit (e.g., reduction in grade 3 AEs from SCD). Such grade 3 AEs unrelated to the study drug occurring in study drug–treated patients were sickle cell vaso-occlusive pain crises (X14) and a pulmonary embolus (Fig 3B). Of these 15 events in study drug–treated patients, 2 events occurred prior to study drug administration (between study enrollment and initiation of drug), and 6 events occurred after discontinuation of study drug, including 3 events in week 3 or 4 of post-drug follow-up (Fig 3B). The pulmonary embolus occurred in a patient with prior history of this complication and without baseline or on-treatment platelet count elevations (a cohort 2 patient). All patients except for one had required emergency room or hospital admission for sickle cell vaso-occlusive pain crises between 1 and 18 times in the 12 months prior to study enrollment (Fig 3B). By including the event occurring prior to study drug administration, the rate of grade 3 sickle cell vaso-occlusive pain crises was statistically significantly increased in cohort 4 versus placebo patients: cohort 4 patients had a rate of this complication in the 12 months preceding study enrollment that was more than 2-fold greater than the rate in placebo-treated patients (Fig 3B). The most frequent AE of any grade in placebo- and study drug–treated patients was pain from vaso-occlusive sickle cell crisis (Fig 3A). The rates of vaso-occlusive pain crisis AEs of all grades appeared lower in THU-decitabine dose level versus placebo-treated patients except in cohort 4, as noted above (Fig 4). The overall pattern of AEs was similar in placebo- and study drug–treated patients (Fig 4). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Adverse events (AEs) in placebo and decitabine dose-level patients (cohorts 1–5). (A) All AEs as per Common Terminology Criteria for Adverse Events (CTCAE) v 4.0. There were no grade 4 AEs. (B) Statistical comparison of all pain AEs in drug-treated versus placebo cohorts. R function poisson.test(), an exact test, was used. https://doi.org/10.1371/journal.pmed.1002382.g004 No patients discontinued the study drug or placebo because of AEs. Decitabine pharmacokinetics Samples for decitabine pharmacokinetic measurements by LCMS/MS were obtained immediately prior to and at 2, 4, and 24 hours after decitabine administration in 12 of 15 study drug–treated patients (dictated by venous access). Decitabine was detected in the plasma even at the lowest decitabine dose level of 0.01 mg/kg, and a dose-dependent increase was observed (Fig 5A). The highest dose of oral decitabine, 0.16 mg/kg (cohort 5), produced decitabine plasma concentrations at 2 hours from 39–54 nM (Cmax). The dose level below this, 0.08 mg/kg (cohort 4), produced Cmax of 9–21 nM (Fig 5A). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Pharmacokinetics (PK) and pharmacodynamics (PD) of oral tetrahydrouridine (THU)-decitabine. (A) Decitabine PK. Samples for PK analysis were obtained in 12 of the 15 patients who received the study drug. Times are listed in hours after administration of oral decitabine. Data points are measured values and curves are fits using the R package PKLMfit. The inset shows a close-up of hours 0–4. Decitabine was quantified by a validated liquid chromatography tandem mass spectrometry (LCMS/MS) method. (B) DNMT1 protein levels in peripheral blood mononuclear cells (PBMC) measured by flow cytometry in cohorts 4 and 5 (decitabine 0.08 mg/kb and 0.16 mg/kg, respectively) and in all placebo-treated patients. Analyses were blinded to treatment assignment. Shown are means of 2 independent measurements. (C) Methylation of long interspersed nuclear elements (LINE-1) repetitive element CpGs (3 individual CpGs) in PBMC in cohorts 4 and 5 placebo and drug-treated patients. Analyses were blinded to treatment assignment. Measurements were made by pyrosequencing. Shown are means of 2 independent measurements. https://doi.org/10.1371/journal.pmed.1002382.g005 Molecular pharmacodynamics The intended molecular pharmacodynamic effect with oral THU-decitabine therapy is DNMT1 depletion. DNMT1 protein levels were measured by flow cytometric analysis of peripheral blood mononuclear cells obtained at baseline, 3, 6, and 8 weeks after initiation of treatment. DNMT1 protein levels decreased by >75% from baseline in 2 of the 3 decitabine 0.16 mg/kg–treated patients (cohort 5), and by approximately 50% in all 0.08 mg/kg–treated patients (cohort 4), but not in patients with lower decitabine doses or in placebo-treated patients (Fig 5B). An expected consequence of DNMT1 depletion is reduction in DNA methylation at LINE-1 repetitive element CpGs, a measurement that has been used in other clinical trials of DNMT1-depleting drugs [71]. LINE-1 CpG methylation was measured in peripheral blood mononuclear cells obtained at baseline, 4, 8, and 10 weeks after initiation of therapy. LINE-1 CpG methylation decreased consistently by approximately 10% with decitabine at 0.16 mg/kg (cohort 5), but not with lower decitabine doses or in placebo-treated patients (Fig 5C). Induction of HbF The primary efficacy objective with non-cytotoxic DNMT1 depletion in patients with SCD is to increase HbF expression in erythroid precursors, and thereby to decrease HbS polymerization and stop the SCD pathophysiological cascade at its inception (Fig 1). HbF was measured by HPLC in the Clinical Pathology Laboratory and also by flow cytometric quantification of HbF content in individual RBCs. HbF percentage (HbF%) increases by HPLC were observed with decitabine 0.08 mg/kg and 0.16 mg/kg (cohorts 4 and 5, respectively), but not with other decitabine dose levels or placebo (Fig 6A–6D, S1 Fig, S1 Data). Rates of increase in HbF% (time-slope estimates) increased with dose (P < 0.001) (Fig 6B). The largest HbF increases were in cohort 5 with increases of 4%, 9%, and 9%, corresponding to absolute HbF increases of 0.4, 0.85, and 1.1 g/dL from baseline (Fig 6A–6D). Upon study drug discontinuation, HbF plateaued for 2 weeks and then began to decline (Fig 6A and 6C). By flow cytometry, major increases in RBC enriched for HbF (F-cells) were observed in cohorts 4 and 5, with the largest F-cell increases in cohort 5 patients, up 2.1-, 2.1- and 1.4-fold, thereby reaching levels up to approximately 40%, 65%, and 80% of total RBCs, respectively (Fig 6E and 6F, S2 Fig). F-cells did not increase with placebo (Fig 6E and 6F). F-cells plateaued in the 2 weeks after study drug discontinuation (Fig 6D). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 6. Fetal hemoglobin (HbF) induction in cohort 4 and 5 patients. (A) HbF percentage (HbF%) over time in cohorts 4 and 5 (decitabine 0.08 mg/kg and 0.16 mg/kg, respectively) patients. (B) Statistical analysis of the rates of change in HbF% with increasing doses of decitabine (0 = placebo); P value determined by linear regression. (C) Change in HbF% from pretreatment to week 8 or 10. (D) Absolute HbF levels. (E) Proportion of red blood cells (RBCs) expressing high levels of HbF (F-cells) in cohort 4 and 5 patients. (F) Raw F-cell flow cytometry data for cohort 5 tetrahydrouridine (THU)-decitabine—and placebo-treated patients. Abbreviation: FS, forward scatter. https://doi.org/10.1371/journal.pmed.1002382.g006 Total hemoglobin and other hematology/efficacy parameters Non-cytotoxic DNMT1 depletion by decitabine in vitro and in vivo is known to bias commitment decisions of multi-potent hematopoietic precursors towards erythroid and megakaryocyte lineage-fate and away from granulocyte-monocyte fate [43,51,53,72]. That is, non-cytotoxic DNMT1 depletion is expected to increase hemoglobin and platelets and concurrently decrease neutrophils. Hemoglobin levels increased in all cohort 4 and 5 (0.08 and 0.16 mg/kg, respectively) patients (in one cohort 4 patient, an isolated large increase in hemoglobin and ANC coincided with a pneumonia diagnosis and dehydration) (Fig 7A, S1 Fig, S1 Data). The total hemoglobin increases from baseline to maximum during 8 weeks of treatment at 0.16 mg/kg dose (cohort 5) were 1.2, 1.8, and 1.9 g/dL (Fig 7A). Rates of increase in total hemoglobin (time-slope estimates) increased with dose (P = 0.01) (Fig 7B). Total hemoglobin increased even as reticulocyte counts decreased; that is, better quality and efficiency of HbF-enriched erythropoiesis permitted increases in hemoglobin with fewer reticulocytes (Fig 7C). Also indicating better RBC quality were biomarkers of hemolysis, thrombophilia, and inflammation, namely serum LDH, total bilirubin, D-dimer, and CRP levels, all of which improved in cohorts 4 and 5 (Fig 7D–7G, S1 Fig, S1 Data). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 7. Blood counts and other parameters in cohort 4 (decitabine 0.08 mg/kg) and 5 (decitabine 0.16 mg/kg) tetrahydrouridine (THU)-decitabine–treated patients. (A) Total hemoglobin. (B) Statistical analysis of the rates of change in total hemoglobin (Hbg) with increasing doses of decitabine (0 = placebo); P value determined by linear regression. (C) Absolute reticulocyte counts (ARC). (D, E) LDH and total bilirubin. These are biomarkers of hemolysis. (F) D-dimer. A biomarker of coagulation activation. (G) C-reactive protein (CRP). A biomarker of inflammation. (H) Platelets. (I) Absolute neutrophil counts (ANC). https://doi.org/10.1371/journal.pmed.1002382.g007 In parallel, as expected with non-cytotoxic DNMT1 depletion, platelets increased concurrently with neutrophil decreases (Fig 7H and 7I). Platelet and neutrophil counts on therapy did not reach a priori–defined triggers for dose modification: neither a platelet count of >1,200 × 109/L, nor an ANC <1.5 ×109/L, were reached, as the highest platelet count on therapy was 1,122 × 109/L in a patient with a pretreatment count of 733 × 109/L, and the lowest ANC on therapy was 1.6 × 109/L in a patient with a pretreatment count of 1.8 × 109/L (Fig 7H and 7I). In contrast to the clear trends in myeloid lineages, there was no clear pattern of change in absolute lymphocyte counts on therapy (S1 Fig). All blood counts reverted towards baseline 2 weeks after discontinuation of study drug (Fig 7). Patient flow and characteristics The trial protocol is provided as S1 Text, the CONSORT statement as S2 Text, and the patient flow is shown in Fig 2C. Twenty-seven patients were screened and 25 eligible patients enrolled at the University of Illinois at Chicago with the first patient starting the study drug on Sept 5, 2012 and the last patient receiving the last dose of the study drug on Jan 6, 2016. Patients met inclusion criteria for high-risk disease despite standard of care, and hydroxyurea treatment was discontinued at least 28 days prior to initiation of the study drug or placebo [8] (Fig 2D). Placebo-treated patients were older than study drug–treated patients, a difference produced randomly. Median age of the 4 male and 21 female patients was 34 years (range 23–56) (Fig 2E). Baseline laboratory values reflected hemolytic anemia and were similar in drug- and placebo-treated patients (Fig 2E). AEs The primary endpoint of ≥ grade 3 non-hematologic toxicities was not triggered, nor did any patients trigger the platelets >1,200 × 109/L, or neutrophils <1.5 × 109/L thresholds requiring dose modification. There were no grade 4 AEs (Fig 3A). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 3. Adverse events (AEs). (A) AEs with possible relatedness to the study drug (AEs other than “unrelated”) per judgement of the treating clinical teams. (B) All grade 3 AEs occurring in study drug—and placebo-treated patients. These grade 3 AEs were sickle cell complications judged to be unrelated to the study drug by the treating clinical teams. (C) Statistical comparison of grade 3 AEs between placebo and decitabine dose-level patients. R function poisson.test(), an exact test, was used. Abbreviation: ED/Hosp, emergency department/hospital. https://doi.org/10.1371/journal.pmed.1002382.g003 This study was not designed or powered to demonstrate clinical benefit (e.g., reduction in grade 3 AEs from SCD). Such grade 3 AEs unrelated to the study drug occurring in study drug–treated patients were sickle cell vaso-occlusive pain crises (X14) and a pulmonary embolus (Fig 3B). Of these 15 events in study drug–treated patients, 2 events occurred prior to study drug administration (between study enrollment and initiation of drug), and 6 events occurred after discontinuation of study drug, including 3 events in week 3 or 4 of post-drug follow-up (Fig 3B). The pulmonary embolus occurred in a patient with prior history of this complication and without baseline or on-treatment platelet count elevations (a cohort 2 patient). All patients except for one had required emergency room or hospital admission for sickle cell vaso-occlusive pain crises between 1 and 18 times in the 12 months prior to study enrollment (Fig 3B). By including the event occurring prior to study drug administration, the rate of grade 3 sickle cell vaso-occlusive pain crises was statistically significantly increased in cohort 4 versus placebo patients: cohort 4 patients had a rate of this complication in the 12 months preceding study enrollment that was more than 2-fold greater than the rate in placebo-treated patients (Fig 3B). The most frequent AE of any grade in placebo- and study drug–treated patients was pain from vaso-occlusive sickle cell crisis (Fig 3A). The rates of vaso-occlusive pain crisis AEs of all grades appeared lower in THU-decitabine dose level versus placebo-treated patients except in cohort 4, as noted above (Fig 4). The overall pattern of AEs was similar in placebo- and study drug–treated patients (Fig 4). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 4. Adverse events (AEs) in placebo and decitabine dose-level patients (cohorts 1–5). (A) All AEs as per Common Terminology Criteria for Adverse Events (CTCAE) v 4.0. There were no grade 4 AEs. (B) Statistical comparison of all pain AEs in drug-treated versus placebo cohorts. R function poisson.test(), an exact test, was used. https://doi.org/10.1371/journal.pmed.1002382.g004 No patients discontinued the study drug or placebo because of AEs. Decitabine pharmacokinetics Samples for decitabine pharmacokinetic measurements by LCMS/MS were obtained immediately prior to and at 2, 4, and 24 hours after decitabine administration in 12 of 15 study drug–treated patients (dictated by venous access). Decitabine was detected in the plasma even at the lowest decitabine dose level of 0.01 mg/kg, and a dose-dependent increase was observed (Fig 5A). The highest dose of oral decitabine, 0.16 mg/kg (cohort 5), produced decitabine plasma concentrations at 2 hours from 39–54 nM (Cmax). The dose level below this, 0.08 mg/kg (cohort 4), produced Cmax of 9–21 nM (Fig 5A). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 5. Pharmacokinetics (PK) and pharmacodynamics (PD) of oral tetrahydrouridine (THU)-decitabine. (A) Decitabine PK. Samples for PK analysis were obtained in 12 of the 15 patients who received the study drug. Times are listed in hours after administration of oral decitabine. Data points are measured values and curves are fits using the R package PKLMfit. The inset shows a close-up of hours 0–4. Decitabine was quantified by a validated liquid chromatography tandem mass spectrometry (LCMS/MS) method. (B) DNMT1 protein levels in peripheral blood mononuclear cells (PBMC) measured by flow cytometry in cohorts 4 and 5 (decitabine 0.08 mg/kb and 0.16 mg/kg, respectively) and in all placebo-treated patients. Analyses were blinded to treatment assignment. Shown are means of 2 independent measurements. (C) Methylation of long interspersed nuclear elements (LINE-1) repetitive element CpGs (3 individual CpGs) in PBMC in cohorts 4 and 5 placebo and drug-treated patients. Analyses were blinded to treatment assignment. Measurements were made by pyrosequencing. Shown are means of 2 independent measurements. https://doi.org/10.1371/journal.pmed.1002382.g005 Molecular pharmacodynamics The intended molecular pharmacodynamic effect with oral THU-decitabine therapy is DNMT1 depletion. DNMT1 protein levels were measured by flow cytometric analysis of peripheral blood mononuclear cells obtained at baseline, 3, 6, and 8 weeks after initiation of treatment. DNMT1 protein levels decreased by >75% from baseline in 2 of the 3 decitabine 0.16 mg/kg–treated patients (cohort 5), and by approximately 50% in all 0.08 mg/kg–treated patients (cohort 4), but not in patients with lower decitabine doses or in placebo-treated patients (Fig 5B). An expected consequence of DNMT1 depletion is reduction in DNA methylation at LINE-1 repetitive element CpGs, a measurement that has been used in other clinical trials of DNMT1-depleting drugs [71]. LINE-1 CpG methylation was measured in peripheral blood mononuclear cells obtained at baseline, 4, 8, and 10 weeks after initiation of therapy. LINE-1 CpG methylation decreased consistently by approximately 10% with decitabine at 0.16 mg/kg (cohort 5), but not with lower decitabine doses or in placebo-treated patients (Fig 5C). Induction of HbF The primary efficacy objective with non-cytotoxic DNMT1 depletion in patients with SCD is to increase HbF expression in erythroid precursors, and thereby to decrease HbS polymerization and stop the SCD pathophysiological cascade at its inception (Fig 1). HbF was measured by HPLC in the Clinical Pathology Laboratory and also by flow cytometric quantification of HbF content in individual RBCs. HbF percentage (HbF%) increases by HPLC were observed with decitabine 0.08 mg/kg and 0.16 mg/kg (cohorts 4 and 5, respectively), but not with other decitabine dose levels or placebo (Fig 6A–6D, S1 Fig, S1 Data). Rates of increase in HbF% (time-slope estimates) increased with dose (P < 0.001) (Fig 6B). The largest HbF increases were in cohort 5 with increases of 4%, 9%, and 9%, corresponding to absolute HbF increases of 0.4, 0.85, and 1.1 g/dL from baseline (Fig 6A–6D). Upon study drug discontinuation, HbF plateaued for 2 weeks and then began to decline (Fig 6A and 6C). By flow cytometry, major increases in RBC enriched for HbF (F-cells) were observed in cohorts 4 and 5, with the largest F-cell increases in cohort 5 patients, up 2.1-, 2.1- and 1.4-fold, thereby reaching levels up to approximately 40%, 65%, and 80% of total RBCs, respectively (Fig 6E and 6F, S2 Fig). F-cells did not increase with placebo (Fig 6E and 6F). F-cells plateaued in the 2 weeks after study drug discontinuation (Fig 6D). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 6. Fetal hemoglobin (HbF) induction in cohort 4 and 5 patients. (A) HbF percentage (HbF%) over time in cohorts 4 and 5 (decitabine 0.08 mg/kg and 0.16 mg/kg, respectively) patients. (B) Statistical analysis of the rates of change in HbF% with increasing doses of decitabine (0 = placebo); P value determined by linear regression. (C) Change in HbF% from pretreatment to week 8 or 10. (D) Absolute HbF levels. (E) Proportion of red blood cells (RBCs) expressing high levels of HbF (F-cells) in cohort 4 and 5 patients. (F) Raw F-cell flow cytometry data for cohort 5 tetrahydrouridine (THU)-decitabine—and placebo-treated patients. Abbreviation: FS, forward scatter. https://doi.org/10.1371/journal.pmed.1002382.g006 Total hemoglobin and other hematology/efficacy parameters Non-cytotoxic DNMT1 depletion by decitabine in vitro and in vivo is known to bias commitment decisions of multi-potent hematopoietic precursors towards erythroid and megakaryocyte lineage-fate and away from granulocyte-monocyte fate [43,51,53,72]. That is, non-cytotoxic DNMT1 depletion is expected to increase hemoglobin and platelets and concurrently decrease neutrophils. Hemoglobin levels increased in all cohort 4 and 5 (0.08 and 0.16 mg/kg, respectively) patients (in one cohort 4 patient, an isolated large increase in hemoglobin and ANC coincided with a pneumonia diagnosis and dehydration) (Fig 7A, S1 Fig, S1 Data). The total hemoglobin increases from baseline to maximum during 8 weeks of treatment at 0.16 mg/kg dose (cohort 5) were 1.2, 1.8, and 1.9 g/dL (Fig 7A). Rates of increase in total hemoglobin (time-slope estimates) increased with dose (P = 0.01) (Fig 7B). Total hemoglobin increased even as reticulocyte counts decreased; that is, better quality and efficiency of HbF-enriched erythropoiesis permitted increases in hemoglobin with fewer reticulocytes (Fig 7C). Also indicating better RBC quality were biomarkers of hemolysis, thrombophilia, and inflammation, namely serum LDH, total bilirubin, D-dimer, and CRP levels, all of which improved in cohorts 4 and 5 (Fig 7D–7G, S1 Fig, S1 Data). Download: PPT PowerPoint slide PNG larger image TIFF original image Fig 7. Blood counts and other parameters in cohort 4 (decitabine 0.08 mg/kg) and 5 (decitabine 0.16 mg/kg) tetrahydrouridine (THU)-decitabine–treated patients. (A) Total hemoglobin. (B) Statistical analysis of the rates of change in total hemoglobin (Hbg) with increasing doses of decitabine (0 = placebo); P value determined by linear regression. (C) Absolute reticulocyte counts (ARC). (D, E) LDH and total bilirubin. These are biomarkers of hemolysis. (F) D-dimer. A biomarker of coagulation activation. (G) C-reactive protein (CRP). A biomarker of inflammation. (H) Platelets. (I) Absolute neutrophil counts (ANC). https://doi.org/10.1371/journal.pmed.1002382.g007 In parallel, as expected with non-cytotoxic DNMT1 depletion, platelets increased concurrently with neutrophil decreases (Fig 7H and 7I). Platelet and neutrophil counts on therapy did not reach a priori–defined triggers for dose modification: neither a platelet count of >1,200 × 109/L, nor an ANC <1.5 ×109/L, were reached, as the highest platelet count on therapy was 1,122 × 109/L in a patient with a pretreatment count of 733 × 109/L, and the lowest ANC on therapy was 1.6 × 109/L in a patient with a pretreatment count of 1.8 × 109/L (Fig 7H and 7I). In contrast to the clear trends in myeloid lineages, there was no clear pattern of change in absolute lymphocyte counts on therapy (S1 Fig). All blood counts reverted towards baseline 2 weeks after discontinuation of study drug (Fig 7). Discussion This first-in-human clinical trial evaluated safety of oral THU-decitabine, and identified an appropriate dose, for DNMT1 depletion and HbF induction in SCD [70]. Oral THU-decitabine was safe and well-tolerated in this study and produced a wide decitabine concentration-time profile (low Cmax, long Tmax) ideal for non-cytotoxic DNMT1 depletion, since DNMT1 depletion can occur at low nanomolar concentrations but depends on exposure timing [46,73–75]. Increases in fetal and total hemoglobin expected to be clinically significant were produced at the highest decitabine dose administered, 0.16 mg/kg, accompanied by improvements in laboratory biomarkers of hemolysis, coagulation, and inflammation. The side effects were a concurrent increase in platelets and decrease in neutrophils, expected with non-cytotoxic DNMT1 depletion. The main limitation was narrow ability to document clinical benefits, because this was a first-in-human study with a single-blind design, with only a small number of patients treated at each decitabine dose level, and for only 8 weeks. Non-blinding of investigators could produce over- or under-reporting of AEs. The major rationale for not blinding investigators to treatment assignment was the intent to use intra-patient dose modification for decitabine Cmax > 0.2 μM, study drug–related ≥ grade 3 toxicity, platelets > 1,200 × 109/L, or neutrophils < 1.5 × 109/L. In the study, intra-patient dose modification was not triggered. Doses of oral decitabine administered after oral THU were escalated from a very low starting level (0.01 mg/kg), to find the minimal decitabine doses active in depleting DNMT1 without cytotoxicity. Our specific pharmacokinetic objectives were to (i) distribute decitabine through the most CDA-enriched tissues, intestines and liver, which need to be surmounted for oral bioavailability; (ii) extend decitabine half-life/Tmax to hours, instead of minutes, to increase S-phase–dependent DNMT1 depletion; (iii) avoid off-target cytotoxicity by maintaining Cmax in the range of >5 nM and <200 nM (nucleotide pool imbalance, DNA-damage, and cytotoxicity correlates with Cmax > 500 nM (reviewed in [76])). These pharmacokinetic objectives were met: mini-doses of oral decitabine administered 60 minutes after THU 10 mg/kg traversed the intestines and liver to produce systemic exposure with a wide decitabine concentration-time profile (Cmax approximately 50 nM at 0.16 mg/kg decitabine, Tmax of hours instead of minutes). By contrast, intravenous administration of decitabine produces a very high Cmax and very brief half-life of minutes. Although continuous intravenous or subcutaneous infusion can in principle lower Cmax and extend Tmax, such approaches are impractical, expensive, and do not solve the problem of negligible distribution into CDA-rich solid tissues—target cells residing in such tissues remain unexposed to treatment [62,77,78]. Increasing intravenous or subcutaneous dose is not a solution for uneven tissue distribution, since toxic exposures are produced in sensitive CDA-poor tissues (e.g., bone marrow) while negligible distribution into CDA-rich tissues persists [62,77]. Similarly, attempting to overcome the intestinal/liver CDA first-pass barrier with high oral doses risks luminal drug concentrations toxic to intestinal enterocytes while systemic exposures remain suboptimal [70,79]. Subcutaneous administration blunts Cmax but does not resolve short half-life and uneven tissue distribution problems [70]. The molecular pharmacodynamic objective of DNMT1 depletion and its corollary, hypomethylation of repetitive element LINE-1 CpG, were produced in peripheral blood mononuclear cells most consistently by oral decitabine 0.16 mg/kg (approximately 5 mg/m2). The degree of LINE-1 CpG hypomethylation generated was comparable to that produced by intravenous decitabine regimens FDA-approved to treat myeloid malignancies, that infuse an appoximately four-fold higher intravenous daily dose of 20 mg/m2/day for 5 days. However, instead of being pulse-cycled, the hypomethylation with oral THU-decitabine is sustained week to week [80,81]. Also contrasting with intravenous infusion, decitabine exposure was throughout CDA-rich solid tissues, demonstrated by its distribution through intestine and liver into plasma where it was measured. This is clinically pertinent beyond oral bioavailability, since target cells may reside in CDA-rich tissues, e.g., erythroid precursors in the spleen in β-thalassemia [62,77,80]. We previously compared head-to-head in the same non-human primates (n = 14) HbF induction by hydroxyurea or cytarabine versus 5-azacytidine (a prodrug of decitabine); 5-azacytidine produced 2 to 20-fold greater increases in HbF than cytarabine or hydroxyurea, without the cytotoxic side effects of cytarabine and hydroxyurea and with consistent effects in older animals less able to respond to cytarabine or hydroxyurea [21]. From this, we repositioned parenterally administered decitabine for non-cytotoxic DNMT1 depletion in SCD patients who had not benefitted from hydroxyurea. In these trials, HbF increases plateaued at >10% from baseline after 12 weeks of treatment, including in patients with essentially 0% HbF increases after 2 years of monitored treatment with hydroxyurea in the pivotal clinical trial [42,43]. The observations here are in line with these previous observations: 8 weeks of treatment with oral THU-decitabine 0.16 mg/kg 2X/week increased HbF 4%–9% from baseline, again in patients who had not benefitted from hydroxyurea. F-cells increased by >2-fold, up to approximately 80% of the total RBC population. Total hemoglobin increased 1.2–1.9 g/dL even as reticulocyte counts decreased, reflecting the better efficiency and quality of HbF-enriched erythropoiesis, also shown by improvements in biomarkers of hemolysis, thrombophilia, and inflammation (LDH, bilirubin, D-dimer, CRP). By way of comparison, transfusion of 1 unit of blood increases hemoglobin by approximately 1 g/dL, and hydroxyurea in the pivotal trial increased total hemoglobin by an average of 0.6 g/dL. Previous parenteral decitabine trials evaluated RBC adhesion to thrombospondin and laminin, RBC hemoglobin concentration, and RBC phosphatidylserine exposure, documenting improvements in these parameters as well [43,51]. In parallel, as expected with non-cytotoxic DNMT1 depletion, platelet counts increased while neutrophil counts concurrently decreased [43,51–53], although remaining within ranges observed in SCD or β-thalassemia patients receiving standard-of-care interventions such as splenectomy or hydroxyurea. Platelet increases and neutrophil decreases are dose/frequency–limiting parameters. In a previous clinical trial in which subcutaneous decitabine was administered up to 3X/week, the more frequent administration, expected to produce DNMT1 depletion in a greater fraction of the erythroid precursor population, did produce even larger increases in HbF and total hemoglobin; however, there were correspondingly greater platelet increases and neutrophil decreases [43]. Platelet increases in SCD, already a thrombophilia, are a concern. The trade-off with better RBC quality, however, is worth closer examination. Several groups have found that platelet activation in β-hemoglobinopathies is by diseased RBC and the endothelial damage they cause [82–94]. In thrombophilic myeloproliferative neoplasms also, thrombotic risk has been found to be a function of qualitative defects in RBC and platelets and not higher platelet counts (reviewed in [95]). Similarly, no link between higher platelets and thrombosis was observed in series of post-splenectomy β-thalassemia patients [91,92], nor during 12–15 years of follow-up of >5,000 normal individuals [96]. The improvement in RBC quality produced by HbF induction thus explains improvements in thrombophilia biomarkers (D-dimer, Von Willebrand factor [vWF] propeptide, RBC adhesion to thrombospondin and laminin, SVCAM1 [endothelial damage biomarker]) in this and previous studies of decitabine, despite concurrent platelet count increases to >800 × 109/L [43]. In short, an association between platelet count and thrombosis risk, though intuitive and possible, is not clear cut in ex and in vivo studies, while qualitative RBC defects, improved by HbF induction, are linked (reviewed in [83]). Future trials of non-cytotoxic DNMT1 depletion will need to continue to carefully monitor the risks/benefits of better RBC quality and higher platelets. Viscosity that increases with hematocrit also contributes to thrombophilia [97]. That non-cytotoxic DNMT1 depletion produces large increases in total hemoglobin could thus mean that this approach is less suited to SCD subtypes with relatively high hematocrits at baseline, e.g., S-β+-thalassemia or S-C disease, even if RBC quality is improved concurrently by HbF induction. This question will need evaluation in future clinical trials. Another risk is that high concentrations of decitabine can be DNA damaging and mutagenic and hence potentially pro-oncogenic. DNA damage can also be cytotoxic; this is a concern independent of potential oncogenicity because of the extraordinary demands on SCD bone marrow to compensate for severe hemolytic anemia—dwindling of such compensation by vaso-occlusive damage and age contributes to early death [8,23,31,32,98]. A major rationale for oral THU-decitabine, therefore, is creating decitabine pharmacology that reduces off-target anti-metabolite effects, DNA-damage, and cytotoxicity. First, combination with THU decreases formation of uridine degradation products that contribute significantly to off-target DNA damage and cytotoxicity [49,50]. Second, oral THU-decitabine produces a low Cmax–extended Tmax concentration-time profile that is conducive to DNMT1 depletion without measurable DNA damage or cytotoxicity, shown extensively in vitro (reviewed in [76]), in non-human primates [21,70], and in clinical trials in which very low doses of decitabine were administered subcutaneously by metronomic schedules [43,51,52]; the clinical trials documented non-cytotoxic DNMT1 depletion by a number of assays including bone marrow evaluation of DNMT1 protein levels, cellularity, γH2AX, and sub-G1 fraction, and peripheral blood evaluation of erythrocyte micronucleus and VDJ recombination assays [43,51,52]. Also regarding concerns of oncogenicity, DNMT1 is highly validated as a molecular target to prevent and treat cancer, offering a p53-independent mechanism of action distinct from conventional anti-metabolite therapy and preserving normal dividing cells (excellent therapeutic index) [43,51–54,76,99–103] (reviewed in [104]). These properties of DNMT1 as a molecular target for oncotherapy likely explain why decitabine and the related 5-azacytidine are the only drugs FDA-approved to treat all subtypes of myelodysplastic syndromes, a type of myeloid malignancy usually seen in the elderly in which better outcomes depend on improving blood counts [52,76,99,100,105,106]. Oral THU-decitabine, like standard-of-care hydroxyurea, could be teratogenic and should be restricted accordingly. Many patients with myeloid malignancies have been treated chronically for years with metronomic very-low-dose decitabine without significant side effects [52]. Although THU is a new chemical entity that is not FDA-approved for any indication, there have been no side effects observed in clinical trials, some with treatment durations up to and exceeding a year (reviewed in [70,107]). The absence of side effects with THU likely reflects the adaptive network structure of pyrimidine metabolism that is robust to inhibition of CDA; THU has been shown to have no effect on nucleotide pool sizes [108]. Also supporting that its inhibition can be non-detrimental to normal physiology is large natural variation in CDA levels between species [109]. Mostly, THU has been used to try to increase anti-metabolite, DNA-damaging effects of coadministered cytotoxic cytidine analogues, an approach that increases systemic toxicity. Here, by contrast, the intent was to create lower Cmax, extended Tmax, more equitable tissue distribution and decrease uridine degradation products of decitabine for non-cytotoxic (non-toxic), molecularly targeted therapy goals (reviewed in [76,99]). Fetal hemoglobin induction involves chromatin remodeling of the HbF gene locus (HBG) [110]. Cytotoxicity generates this remodeling indirectly, via bone marrow stress [21,110,111] (S3 Fig). The inefficiency of this approach versus directly inhibiting epigenetic enzymes is underscored by greater HbF increases produced by <1/1,000th the molar amount of decitabine versus hydroxyurea in the same patients (decitabine approximately 0.2 mg/kg 2X/week versus hydroxyurea approximately 20 mg/kg daily) [43,112] (S3 Fig). Several other drug development efforts are thus also directed towards direct inhibition of epigenetic enzymes that silence HbF (HBG). Besides DNMT1, enzymes targeted include histone deacetylases (HDAC), KDM1A/LSD1, and PRMT5. DNMT1-depleting and HDAC-inhibiting drugs are already FDA-approved for other clinical indications. Potential application of marketed HDAC inhibitors for HbF induction is limited by pleiotropic roles of HDAC in cells outside of chromatin, rendering it difficult to separate anti-metabolite/cytotoxicity from epigenetic effects [113–117]. The limitations of marketed parenteral decitabine also apply to 5-azacytidine, a decitabine prodrug. By depleting DNMT1 protein, decitabine and 5-azacytidine disrupt its scaffolding functions for other epigenetic enzymes such as LSD1/KDM1A [118,119]. This potent epigenetic effect, and its known safety profile, justify efforts to improve decitabine pharmacology and accessibility. HbF is the most powerful known natural modulator of the root cause of SCD pathophysiology. This clinical trial affirms that substantial HbF and total hemoglobin increases can be produced by inhibiting an epigenetic enzyme that mediates HbF silencing and by rationally avoiding cytotoxicity. The oral route of administration and safety profile of the agent used for this purpose, oral THU-decitabine, could have global health implications. Further clinical development and evaluation are thus warranted. Supporting information S1 Data. All patient laboratory data. https://doi.org/10.1371/journal.pmed.1002382.s001 (XLSX) S1 Fig. Changes in hematologic, hemolysis, thrombophilia, and inflammation biomarkers on therapy. Plots of median values in decitabine dose level and placebo cohorts. (A) HbF%. (B) Total hemoglobin. (C) Absolute reticulocyte counts (ARC). (D) Serum lactate dehydrogenase levels (LDH). (E) Total bilirubin levels. (F) D-dimer levels. (G) Serum C-reactive protein levels (CRP). (H) Platelet counts. (I) Absolute neutrophil counts (ANC). (J) Absolute lymphocyte counts (ALC). (K) Total white blood cell counts (WBC). https://doi.org/10.1371/journal.pmed.1002382.s002 (TIF) S2 Fig. F-cells in cohort 5—Original flow cytometry data. Peripheral blood samples were fixed and stained with phycoerythrin-conjugated anti-HbF (Caltag) per manufacturer’s instructions. Analysis on a Becton-Dickinson FacsCalibur (Sunnyvale, CA). https://doi.org/10.1371/journal.pmed.1002382.s003 (TIF) S3 Fig. Fetal hemoglobin induction requires chromatin remodeling, including DNA hypomethylation, of the HbF gene locus (γ-globin, HBG). Bone marrow stress, e.g., from cytotoxic drugs such as hydroxyurea, can create such remodeling during the recovery phase by surviving erythroid precursors [21,110,111]. An alternative approach is to remodel the HbF locus directly, e.g., by directly inhibiting DNMT1 using decitabine. The relative efficiencies of these approaches are illustrated by the greater HbF increases produced in the same non-human primates or human patients by decitabine approximately 0.2 mg/kg 2X/week, versus hydroxyurea approximately 20 mg/kg daily. That is, the molar amount of decitabine administered per week is <1/1,000th the amount of hydroxyurea administered per week [21,43]. https://doi.org/10.1371/journal.pmed.1002382.s004 (TIF) S1 Text. Clinical protocol document. https://doi.org/10.1371/journal.pmed.1002382.s005 (DOC) S2 Text. CONSORT statement. https://doi.org/10.1371/journal.pmed.1002382.s006 (DOC) Acknowledgments We would like to acknowledge the patients who participated in this clinical trial and the National Institutes of Health Rapid Access to Interventional Development (RAID) team (Jim Craddock, Pramod Terse, Joe Covey, and Vishnuvajjala Rao) that assisted with the IND-enabling studies.