The World Bank Economic Review

Gaddis, Isis; Oseni, Gbemisola; Palacios-Lopez, Amparo; Pieters, Janneke

doi: 10.1093/wber/lhaa012pmid: N/A

Abstract This study examines recall bias in farm labor through a randomized survey experiment in Ghana, comparing farm labor estimates from an end-of-season recall survey with data collected weekly throughout the agricultural season. Recall households report 10 percent more farm labor per person-plot, which can be explained by recall households’ underreporting of “marginal” plots and household workers. This “selective” omission by recall households, denoted as listing bias, alters the composition of plots and workers across treatment arms and inflates average farm labor hours per person-plot in the recall group. Since listing bias, in this setting, dominates other forms of recall bias at higher levels of aggregation (i.e., when farm labor per person-plot is summed at the plot, person, or household level), farm labor productivity is overestimated for recall households. Consistent with the notion that recall bias is linked to the cognitive burden of reporting on past events, there is no recall bias among more educated households. recall bias, measurement error, farm labor, agricultural productivity, gender, Ghana 1. Introduction Agriculture plays a key role in the economies of Sub-Saharan Africa. Across the continent, the sector contributes approximately 18 percent to GDP and accounts for 56 percent of the employed population (ILO 2016; World Bank 2017). Agriculture serves as a key livelihood strategy for many poor families in rural areas, where labor-intensive, smallholder farming is the predominant source of income. Agricultural growth has been found to be more effective than nonagricultural growth in reducing extreme poverty (Christiaensen, Demery, and Kuhl 2011). One of the most important agriculture inputs in developing countries is the labor provided by family members on their own farms, denoted in this paper as farm labor and commonly measured in hours or days over an extended reference period, such as the last season or the last year. Data on farm labor are important for a range of literature strands in development economics – such as analyses of agricultural productivity (e.g., Restuccia and Santaeulalia-Llopis 2017; Gollin and Udry 2019), agricultural household models (e.g., LaFave and Thomas 2016), rural labor markets (e.g., Dillon, Brummund, and Mwabu 2019), and gender differences in agriculture (e.g., O'Sullivan et al. 2014; Damon and McCarthy 2019). A range of recent studies, for example, highlight lack of access to family members’ labor, particularly male labor, as one of the main factors constraining women farmers and a key determinant of the gender gap in agricultural productivity (O'Sullivan et al. 2014; Kilic, Palacios-Lopez, and Goldstein 2015). Measuring farm labor, however, is fraught with empirical difficulties. The most common approach is to ask survey respondents to recall the amount of time each member of the household spent on farm activities during the previous agricultural season (end-of-season recall).1 While this extended reference period minimizes the impact of seasonality, it can lead to difficulties for respondents when recalling how much time various members of the household worked on the farm over the entire season. Recall is further hindered by the informal nature of smallholder agriculture where working hours are highly irregular, with periods of low labor activity after planting and prior to harvest. In addition, since irrigation is limited and rain-fed agriculture is the norm across much of Africa, the reliance on weather leads to added unpredictability. These features render measurement of farm labor in developing countries extraordinarily challenging. While several recent papers highlight shortcomings in agricultural statistics in developing countries (Fermont and Benson 2011; Gollin, Lagakos, and Waugh 2014a, b; de Janvry, Sadoulet, and Suri 2017), there are very few empirical studies that evaluate the reliability of survey-based measures of agricultural labor. An exception is Arthi et al. (2018), who show that end-of-season recall overestimates farm labor per person per plot by more than 200 percent in the Mara region of Tanzania. Their study also documents competing forms of recall bias, as end-of-season recall simultaneously leads to underreporting of cultivated plots and household farm workers. This paper builds upon the results from Tanzania to estimate recall bias in farm labor in the Ashanti and Brong Ahafo regions of Ghana. Two approaches to collecting farm labor data are compared. One group of farmers was interviewed weekly about farm labor for each of the seven days preceding the interviews, which is considered the resource-intensive benchmark. Another group was interviewed at the end of the agricultural season (i.e., after harvest) about farm labor for the entire season, hence using the traditional end-of-season recall method. Comparing these two groups provides an estimate of bias in the end-of-season recall of farm labor hours, denoted here as recall bias, that is, recall bias at the intensive margin. While this research design is broadly similar to the one used in Tanzania, this study made one key methodological refinement by visiting recall households at the beginning of the agricultural season to collect an initial listing of plots and household workers. This allows for further analysis on the extent to which the recall method can lead to biased reporting on the number of cultivated plots and household farm workers, denoted here as listing bias, that is, recall bias at the extensive margin. This alteration in the research design builds upon the results reported in Arthi et al. (2018), which showed a significant underreporting of plots and households. However, the Tanzania experiment visited recall households only once, at the end of the season, and this limited the types of analyses that could be performed. In addition, while both research settings are characterized by smallholder agriculture, especially maize farming, there are important differences between the two study contexts. For example, smallholder farmers in Ghana's Ashanti and Brong Ahafo regions cultivate fewer but larger plots than farmers in the Mara region of Tanzania. Labor markets in the study area in Ghana are also more integrated, as evidenced by the greater prevalence of agricultural wage labor. Hence, one objective of the present study is to explore whether the Tanzania results hold in a somewhat different setting, and to assess the relationship between recall bias and contextual factors. This paper makes several contributions. First, it shows that recall bias in farm labor per person per plot (i.e., the unit at which labor is reported by the survey respondents) is much smaller in the Ghanaian than in the Tanzanian setting, which highlights that estimates of recall bias are highly context-dependent and cautions against extrapolating recall bias across populations. Second, the results demonstrate that, in the research setting of Ghana, recall bias in farm labor at the person-plot level can be accounted for by bias in listings of plots and household farm workers. This complements the findings of Arthi et al. (2018), who document that listing bias runs counter to recall bias in farm labor at the person-plot level. The results reveal that recall households report more hours of farm labor per person per plot because they fail to list “marginal” plots and farm workers. This “selective” omission of marginal plots and household workers by recall households alters the composition of plots and workers across treatment arms and inflates average farm labor hours per person per plot in the recall group. Listing bias, hence, not only counteracts but explains recall bias in farm labor at the person-plot level, at least in this context. Surprisingly, once the analysis controls for listing bias, farmers in this study setting report fairly accurately on the number of hours of farm labor provided per person per plot. Third, recall bias is strongly associated with educational attainment. There is no significant recall bias in hours worked per person per plot for more educated households, who tend to be better at recalling all their plots. This is consistent with the notion that recall bias is linked to the cognitive burden of reporting on events that occurred in the past. This educational gradient may also explain, at least in part, why recall bias in this study for Ghana is much lower than Arthi et al. (2018) found for Tanzania, given that education levels among sampled farmers are higher in Ghana than in Tanzania. Fourth, there are important, yet complex, gender differences in recall bias in this study setting. Female farm workers are less likely to be listed than male farm workers, but this gender difference in listing bias is mitigated by the fact that women also work fewer hours per plot than men. And finally, this paper illustrates the implications of its findings for empirical research, especially the analysis of agricultural productivity. The results in this study provide nuance to the conclusions reached by Arthi et al. (2018), who argue that recall-style modules tend to understate agricultural productivity. In settings such as the one in this study, where listing bias is the dominant source of reporting bias, the recall method underestimates farm labor at higher levels of aggregation, such as the plot or household levels, and overestimates the labor productivity of household-operated farms. The remainder of the paper is structured as follows. Section 2 provides an overview of the measurement of farm labor. Section 3 describes the experimental design of the study. Section 4 estimates recall bias in farm labor and explores the role of listing bias. Section 5 analyzes heterogeneity by education and gender. Section 6 compares the results in Ghana to those obtained by Arthi et al. (2018) for Tanzania and puts forth some tentative explanations for why they differ. Section 7 documents recall bias at different levels of aggregation and implications for the analysis of agricultural productivity. Section 8 concludes. 2. Measuring Farm Labor Measuring labor in smallholder farming is inherently complex and prone to measurement error.2 Like informal household enterprises in other sectors, smallholder farmers rarely keep any records; thus respondents rely on recall strategies to report on labor and other inputs. The seasonality and irregularity of smallholder agriculture pose additional challenges, especially if the objective is to obtain measures of farm labor for the entire season. The current practices on how to collect data on farm labor, that is, the labor provided by family members on their own farm (excluding hired labor), differ widely across surveys. Household surveys, such as those conducted under the World Bank's Living Standards Measurement Study – Integrated Surveys on Agriculture (LSMS-ISA) initiative, typically collect data on farm labor in a dedicated agricultural module.3 However, these modules differ with respect to the unit of data collection, recall period, sequencing of questions, selection of respondent(s), and so on. The following paragraphs elaborate on the first two of these issues, that is, the unit of data collection and the recall period, which are important features of the analysis in this paper. Unit of Data Collection The majority of household surveys with a focus on agriculture use the plot as the main unit of data collection (FAO 2017). This reflects a long-standing guidance for the design and implementation of household surveys in developing countries. Reardon and Glewwe (2000) recommend that in countries with “hard-to-survey” agricultural sectors, which includes most smallholder farming in Sub-Saharan Africa, data on farm inputs and practices should be collected at the plot level (as opposed to the farm or household level). This is because a single farm may consist of multiple plots – cultivated under different production systems – and farmers tend to refer to each plot when they describe agricultural production activities. In such a situation, plot-level data collection reflects the natural flow of conversation between the enumerator and the farmer. In addition, collecting data at the plot level yields more observations than collecting data at the household level, enables the analyst to control for land quality, and facilitates the analysis of agricultural productivity (as the plot can be used to link crops to inputs) and intrahousehold differences (e.g., productivity gaps between male- and female-managed plots). For data on farm labor, the recommended practice is to collect such data either in terms of aggregate person-days per plot, or to ask, specifically, about each household member's labor input on each plot (Reardon and Glewwe 2000). The former approach is used in the 2009 Ghana Socio-Economic Panel Survey, which asks (for men, women, and children separately) about the number of days, average hours per day, and average number of workers who provided family labor on each plot during the last major/minor seasons.4 An example of the latter approach is the 2014/15 Tanzania National Panel Survey (NPS), which asks “during the long rainy season 2014, how many days did [NAME] spend on the following activities on this [PLOT]?” This is followed by a question about the “typical number of hours per day worked by an individual on this [PLOT].” Many other agricultural surveys follow variants of this latter approach, including the 2015/16 Ghana agricultural labor survey used in this study.5 A major advantage of collecting data on farm labor by person and by plot (denoted here as person-plot level) is that, due to the high level of granularity, it can accommodate different analytic approaches at the analysis stage. The main unit at which farm labor is reported and/or embedded in the empirical analysis of several recent studies, is shown in table A1.1 ( appendix A1). Studies concerned with gender differences in agriculture tend to aggregate at the plot level (often with normalization for plot size). This allows for the comparison of productivity levels between plots managed by male and female farmers and for assessing the role of labor shortages as one of the underlying constraints (Fisher and Kandiwa 2014; O'Sullivan et al. 2014; Aguilar et al. 2015; Andrews, Golan, and Lay 2015; Kilic, Palacios-Lopez, and Goldstein 2015; Oseni et al. 2015; Palacios-Lopez and Lopez 2015; Ali et al. 2016; Damon and McCarthy 2019). Other analyses of agricultural productivity aggregate either at the plot level (Gollin and Udry 2019) or at the household level (Restuccia and Santaeulalia-Llopis 2017; André, Delesalle, and Dumas 2019; Dillon, Brummund, and Mwabu 2019). McCullough (2017) aggregates farm labor at the person level to compare labor productivity between farm and nonfarm household enterprises. This illustrates that different levels of aggregation serve different purposes. Collecting data on farm labor at the person-plot level keeps all higher levels of aggregation – that is, plot, person, and household levels – open for analysis. This, of course, assumes that greater granularity in data collection does not undermine data quality, so that there is no analytical cost to greater disaggregation. The results from this paper caution that this may not necessarily be the case, as different levels of data collection may be more or less prone to different forms of recall bias. Despite the advantages highlighted above, data collection at the person-plot level can be challenging in practice. In a first step, enumerators need to compile a comprehensive list (roster) of household members and agricultural plots. Plot rosters, in particular, are notoriously difficult to compile. While most farmers have an intuitive understanding of what constitutes a plot of land, they may forget to mention marginal plots, that is, plots that are not farmed intensively during the season. Hence, enumerators need to probe carefully to ensure that all relevant plots are listed as per the standardized definition used in the survey.6 In addition, it may be difficult for the respondent to identify which members of the household worked on each plot during the reference period, particularly if the responses are provided by a proxy respondent on behalf of other household members. Finally, respondents may not find the concept of farm labor per person per plot intuitively meaningful, and therefore face difficulties in reporting on the number of days and hours that individual household members worked on each plot. Arthi et al. (2018) highlight that participants of focus group discussions in the Mara region of Tanzania requested to report on farm labor with reference to units of one or two acres, which is somewhat larger than the average plot size in the region. These challenges can be compounded by the length of the recall period, as discussed in the next section. In this paper, and consistent with Arthi et al. (2018), the principal unit of data collection and analysis is farm labor per person per plot. However, higher levels of aggregation, that is, farm labor per plot, per person and per household, are also reported. The latter are, as shown in table A1.1 ( appendix A1), more widely used at the analysis stage. This helps in assessing the potential direction of bias for analyses that use higher levels of aggregation. There are two main advantages to using the person-plot level as a starting point. First, to provide guidance to survey designers, it appears useful to assess recall bias directly at the unit at which the data are typically collected in household surveys. Second, this approach helps further disentangle the proximate causes of bias at higher levels of aggregation – that is, incomplete listings of plots and household members (recall bias in listings or, simply, listing bias – that is, bias at the extensive margin) and recall bias in terms of the number of days and hours of farm labor at the person-plot level, conditional on being listed (i.e., bias at the intensive margin). Recall Bias Most agricultural surveys ask respondents to report on farm labor over an extended reference period, such as the previous agricultural season. An example of this approach is the Tanzania NPS introduced earlier, which asked respondents to recall each household member's labor input during the “long rainy season 2014.” The main advantages of using an extended reference period are the reduction in cost and logistical burden of data collection and ensuring consistency between measures of farm labor and measures of seasonal crop production. This consistency is crucial to an analysis of labor or total factor productivity. The flip side of using an extended reference period is that it increases the burden on the respondents, by requiring them to recall events that occurred several months in the past, and to perform complex mental calculations to arrive at averages. Different cognitive processes suggest that recall bias may be linked to the length of the recall period (see Schwarz and Oyserman 2001; Arthi et al. 2018 for more detailed discussions). The most obvious explanation is that respondents forget to report events that took place long ago. Conversely, forward telescoping, where respondents report events that occurred outside the reference period, may be more prevalent with shorter reference periods (Kjellsson, Clarke, and Gerdtham 2014). In addition, there is evidence that the length of the recall period may have a bearing on how respondents interpret survey questions. Winkielman, Knäuper, and Schwarz (1998), for example, show that the longer the recall period, the more likely respondents are to interpret questions about frequencies as referring to rare, major events only (see also Igou, Bless, and Schwarz 2002). This potential change in question interpretation makes it difficult to attribute a negative correlation between the frequencies of reported events and the length of the reference period to forgetting. The salience and periodicity of the event to be reported also have important implications for the respondents’ strategy to respond to survey questions (Menon 1993; Arthi et al. 2018). Respondents tend to use rate-based estimations to report on regular events with a low level of salience (e.g., weekly hours at the gym), but recall and count strategies for irregular and more salient events (e.g., number of marathons run in a year). With respect to events that are neither regular nor salient, such as farm labor provided over a long reference period, both strategies break down, and respondents may resort to impression-based estimates, based on generic assumptions or value judgments (e.g., the importance of the event in one's daily life), which are particularly prone to bias (Conrad, Brown, and Cashman 1998). Several studies have found a positive association between the level of education – or direct measures of cognitive skills – and recall ability. Peters (1988), in comparing lifecycle data from a retrospective marital history with panel reports for the same individuals in the United States, shows that more educated respondents report more consistently on marital events. McAuliffe, DiFranceisco, and Reed (2010) find that arithmetic skills predict the accuracy of retrospective self-reports of sexual activity (also in the United States). While evidence from the United States may not necessarily extend to developing countries, given potentially large differences in education systems, survey methods, and so on, a few studies have found similar associations in Asia and Africa. Beckett et al. (1999, 2001) show that the reliability of reports in the Malaysian Family Life Surveys is higher for more educated respondents. Abebe (2013) finds that recall errors in sales revenues and output among Ethiopian shoemakers are negatively correlated with respondents’ years of schooling. This literature suggests that the accuracy of reports on farm labor may be positively related to educational attainment, as a proxy for cognitive skills. 3. Study Design and Context This paper draws on the 2015 Ghana agricultural labor survey (World Bank 2015a), a specialized dataset collected by the Institute of Statistical, Social and Economic Research (ISSER) of the University of Ghana and the World Bank during the 2015 main rainy season (roughly March to September 2015) in the Mampong Municipal, Ejura Sekyedumasi, Nkoranza South, and Pru districts, which are located in the Ashanti and Brong Ahafo regions of Ghana. A random sample of 720 agricultural households was selected from 20 enumeration areas (henceforth denoted as villages) and then randomly assigned to one of three alternative survey designs – a recall arm, a weekly visit arm, and a weekly phone arm.7 Since the phone arm was intended primarily as a proof of concept (i.e., to document implementation challenges of soliciting high-frequency labor data using phone surveys), the results from this arm are not reported in this paper.8 The survey was implemented using Computer-Assisted Personal Interview (CAPI). All households were administered a baseline survey at the beginning of the 2015 long rainy season, which collected a listing of plots and household members, and identified which household members had already worked on each plot since the beginning of land preparation for the long rainy season.9 In addition, the baseline survey captured core demographic and plot-specific information. After the main harvest, households were administered an endline survey, which was modeled after the design of the LSMS-ISA survey questionnaires, that is, a multitopic household survey with an agricultural production module.10 Farm labor hours were captured as follows in the recall and weekly visit arms (see the supplementary online appendix S1, available at The World Bank Economic Review website, for further details): Recall: The households in this group were interviewed only twice, during the baseline in March 2015 and the endline in October/November 2015. In the endline survey, the agricultural labor module for this group asked one household respondent (the most knowledgeable person regarding the activities on the plot) to identify all household members who worked on each of the household's plots during the long rainy season 2015, and for those members, data were collected on (i) total days per person per plot spent across five activities and (ii) typical hours per day worked per person per plot on each activity.11 This group mimics the way LSMS-ISA and other agricultural surveys collect data on farm labor (see section 2). It is important to note that even though the CAPI application at endline was pre-populated with the baseline rosters of household members and plots, enumerators were instructed (at endline) to ask for additional household members and plots, that may not have been listed at baseline, and to add those to the respective rosters. This step occurred prior to the collection of farm labor data, so that respondents could immediately report on farm labor for newly listed plots and household members. Weekly visit: In addition to the baseline survey in March 2015 and the endline survey in October/November 2015, the households in this group were visited weekly from April to September 2015, that is, over the course of the 2015 rainy season. Farm labor for these households was captured as follows. At baseline (visit 0), respondents were asked about the total number of days and hours each household member had worked on each plot since the beginning of land preparation for the main rainy season. This was to ensure that the survey did not miss out on any labor input for the current season that may have occurred before the beginning of field work. At the first weekly visit (visit 1), respondents were asked to report on the number of hours each household member had worked on each plot since the baseline visit, and the range of activities performed (but not hours per activity). During subsequent weekly visits (visits 2–23) respondents were asked to report on the number of hours each household member had worked on each plot during each day over the past week, and the range of activities performed. At endline (visit 24), respondents were asked to report on the total number of days and the average number of hours per day each household member had worked on each plot since the last weekly visit. The design for this group minimizes recall periods and (mostly) avoids the need for complex aggregations and calculation of averages – farm labor estimates for this group are considered as the benchmark. Similar to the recall group, the CAPI application for both the weekly visit surveys and the endline was pre-populated with plots and household members that had been listed during earlier interviews. However, enumerators were instructed to inquire, at each weekly visit and at endline, about additional household members and plots that had not been previously listed. These newly listed household members and plots were immediately added to the rosters, so that respondents could report on farm labor for newly listed plots and household members. While the overall design of this study is very similar to Arthi et al. (2018), there is one significant difference. This study fielded a baseline survey to all households, including households in the recall group, which allowed collecting a baseline listing of plots and household workers. This listing of plots and household workers plays a crucial role, because all data on farm labor were collected at the person-plot level. However, as described above, respondents could add plots and household workers that were not listed at baseline during subsequent visits – that is, during visits 1 to 24 (weekly visits, endline) in the weekly visit group, and during the endline in the recall group. This design variation follows from the results in Arthi et al. (2018), who document that underreporting of plots and household workers in the recall group counteracts overestimation of farm labor per person per plot. Having access to a baseline survey for all households facilitates the exploration of bias in listings of plots and household workers, but it may also explain some of the differences in results between this study and that of Arthi et al. (2018). This issue is further discussed in section 6, which compares the results obtained for Ghana and Tanzania. The field work design randomized households within villages. The within-village randomization is aimed at balancing micro-agroecological characteristics that may affect the allocation of farm labor, and are difficult to capture in the available survey and satellite data. The fraction of households included in the study sample (across all treatment arms) at the village level varies between 25 and 63 percent. A potential concern is that the weekly visits affected reporting of recall households. Since such intra-village spillovers would be more likely to occur in villages where a larger proportion of the total household population was sampled, a potential test is to correlate mean person-plot hours of farm labor reported by recall households against the share of households sampled at the village level. The results show a small and statistically insignificant correlation of −0.14, which provides confidence that intra-cluster contamination is minimal. Similarly, there is no significant correlation between the share of households sampled and village-specific regression estimates of recall bias in person-plot hours (results available on request). The recall group followed the common practice for agricultural labor modules of asking the manager of the plot (primary decision maker of the day-to-day operations on the plot) to report on labor inputs for all household members. This practice implies that many responses are provided by proxy respondents in standard recall modules. In addition, agricultural modules are typically fielded during a single visit, which makes it operationally difficult to interview multiple household members (who may not be at home during the time of the visit, or may not have time to participate in the survey). Interviewers of the weekly visit group were instructed to interview each member of the household if possible; however, if they were not at home during the interview, they too had to rely on proxy respondents. Moreover, in the weekly visit group, the respondent for questions on farm labor could vary across the 25 visits to the households. Self-reporting rates are slightly higher among weekly visit households (with 43 percent of person-plot farm labor hours being self-reported on most visits) than among recall households (with 33 percent being self-reported at endline). Though the difference in self-reporting across treatment arms is not very large, its endogeneity to treatment assignment and to the household member's profile of economic activity implies that proxy respondent effects cannot be convincingly analyzed with the setup used in this study, though such effects could, of course, play a role. There was some attrition at different stages of field work. In the weekly visit group, 17 households from the original sample of 243 dropped out during the course of the season, resulting in a final sample of 226 households in this group. In the recall group, 6 out of 239 households dropped out, leaving a final sample of 233 households. Though attrition is related to treatment, this is unlikely to affect the estimates as the number of households lost is small. In table A1.2 ( appendix A1), attritor households are similar to households in the final sample, with the exception of household size and distance between the household's residence and plots. As discussed below, these characteristics are unbalanced across treatment groups in the final sample, so that it is important to control for them in the analyses. Household, individual, and plot characteristics for the final sample across the weekly visit and recall arms, drawing on the baseline survey, are shown in table 1. For most of the traits presented in this table, households are well balanced across survey arms, but there are some exceptions. In the weekly visit group, the average household consists of 5.8 members – of whom 1.6 are children younger than 10 years of age – and cultivates 2.6 plots. The average plot is located within a 54-minute walk from the household's residence. Of all individuals aged 10 years and older, 55 percent worked on one or more household plots between the start of land preparations and the baseline survey. However, households in the recall group are significantly smaller, have fewer (cultivated) plots, and are further away from their plots, compared to households in the weekly visit group. Because of these baseline differences, the empirical analysis controls for household size, number of plots, and the average distance between the plots and the residence at baseline. Cropping patterns are very similar across arms, with maize being the most important crop in both arms, followed by yam and groundnut. Table 1. Sample Characteristics in Baseline Survey by Treatment Arm . Weekly visit . Recall . Household size 5.814 5.086** (0.228) (0.168) Male household head 0.752 0.807 (0.029) (0.026) Number of children (age < 10) 1.646 1.575 (0.100) (0.096) Number of persons who worked on household plot (age 10+) 2.226 2.043 (0.093) (0.097) Number of plots listed 2.571 2.348* (0.085) (0.088) Number of plots intended for cultivation 2.509 2.236** (0.086) (0.083) N (households) 226 233 Age 22.974 22.744 (0.514) (0.584) Male 0.493 0.500 (0.014) (0.015) Worked on household plot since start of season (age 10+) 0.550 0.582 (0.016) (0.017) Has no schooling (age 10+) 0.307 0.329 (0.015) (0.016) N (individuals, all ages) 1,314 1,185 Distance plot to residence (min. walking) 53.601 62.706*** (1.958) (2.234) Proportion of plots cultivating beans/peas 0.119 0.122 (0.013) (0.014) Proportion of plots cultivating cassava 0.100 0.122 (0.012) (0.014) Proportion of plots cultivating groundnuts 0.203 0.219 (0.017) (0.018) Proportion of plots cultivating maize 0.487 0.439 (0.021) (0.021) Proportion of plots cultivating yam 0.222 0.258 (0.017) (0.019) N (plots) 581 547 . Weekly visit . Recall . Household size 5.814 5.086** (0.228) (0.168) Male household head 0.752 0.807 (0.029) (0.026) Number of children (age < 10) 1.646 1.575 (0.100) (0.096) Number of persons who worked on household plot (age 10+) 2.226 2.043 (0.093) (0.097) Number of plots listed 2.571 2.348* (0.085) (0.088) Number of plots intended for cultivation 2.509 2.236** (0.086) (0.083) N (households) 226 233 Age 22.974 22.744 (0.514) (0.584) Male 0.493 0.500 (0.014) (0.015) Worked on household plot since start of season (age 10+) 0.550 0.582 (0.016) (0.017) Has no schooling (age 10+) 0.307 0.329 (0.015) (0.016) N (individuals, all ages) 1,314 1,185 Distance plot to residence (min. walking) 53.601 62.706*** (1.958) (2.234) Proportion of plots cultivating beans/peas 0.119 0.122 (0.013) (0.014) Proportion of plots cultivating cassava 0.100 0.122 (0.012) (0.014) Proportion of plots cultivating groundnuts 0.203 0.219 (0.017) (0.018) Proportion of plots cultivating maize 0.487 0.439 (0.021) (0.021) Proportion of plots cultivating yam 0.222 0.258 (0.017) (0.019) N (plots) 581 547 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; ** at the 5 percent level; * at the 10 percent level. Open in new tab Table 1. Sample Characteristics in Baseline Survey by Treatment Arm . Weekly visit . Recall . Household size 5.814 5.086** (0.228) (0.168) Male household head 0.752 0.807 (0.029) (0.026) Number of children (age < 10) 1.646 1.575 (0.100) (0.096) Number of persons who worked on household plot (age 10+) 2.226 2.043 (0.093) (0.097) Number of plots listed 2.571 2.348* (0.085) (0.088) Number of plots intended for cultivation 2.509 2.236** (0.086) (0.083) N (households) 226 233 Age 22.974 22.744 (0.514) (0.584) Male 0.493 0.500 (0.014) (0.015) Worked on household plot since start of season (age 10+) 0.550 0.582 (0.016) (0.017) Has no schooling (age 10+) 0.307 0.329 (0.015) (0.016) N (individuals, all ages) 1,314 1,185 Distance plot to residence (min. walking) 53.601 62.706*** (1.958) (2.234) Proportion of plots cultivating beans/peas 0.119 0.122 (0.013) (0.014) Proportion of plots cultivating cassava 0.100 0.122 (0.012) (0.014) Proportion of plots cultivating groundnuts 0.203 0.219 (0.017) (0.018) Proportion of plots cultivating maize 0.487 0.439 (0.021) (0.021) Proportion of plots cultivating yam 0.222 0.258 (0.017) (0.019) N (plots) 581 547 . Weekly visit . Recall . Household size 5.814 5.086** (0.228) (0.168) Male household head 0.752 0.807 (0.029) (0.026) Number of children (age < 10) 1.646 1.575 (0.100) (0.096) Number of persons who worked on household plot (age 10+) 2.226 2.043 (0.093) (0.097) Number of plots listed 2.571 2.348* (0.085) (0.088) Number of plots intended for cultivation 2.509 2.236** (0.086) (0.083) N (households) 226 233 Age 22.974 22.744 (0.514) (0.584) Male 0.493 0.500 (0.014) (0.015) Worked on household plot since start of season (age 10+) 0.550 0.582 (0.016) (0.017) Has no schooling (age 10+) 0.307 0.329 (0.015) (0.016) N (individuals, all ages) 1,314 1,185 Distance plot to residence (min. walking) 53.601 62.706*** (1.958) (2.234) Proportion of plots cultivating beans/peas 0.119 0.122 (0.013) (0.014) Proportion of plots cultivating cassava 0.100 0.122 (0.012) (0.014) Proportion of plots cultivating groundnuts 0.203 0.219 (0.017) (0.018) Proportion of plots cultivating maize 0.487 0.439 (0.021) (0.021) Proportion of plots cultivating yam 0.222 0.258 (0.017) (0.019) N (plots) 581 547 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; ** at the 5 percent level; * at the 10 percent level. Open in new tab 4. Recall Bias in Farm Labor In the surveys administered to the recall and weekly visit households, farm labor is reported per person for each plot. As discussed in section 2, the main measure of farm labor is season-wide hours per person per plot (though other levels of aggregation are reported in section 7). In this measure, only those plots for which farm labor was reported at least once during the season are included. The analysis considers all individuals aged 10 years and older reporting at least 1 hour of labor on any household plot at any point in time during the agricultural season. Main Results Households in the weekly visit group report farm labor at 25 points in time, starting with the baseline survey (visit 0) and ending with the endline survey (visit 24). Baseline, weekly visit, and endline hours are then summed up to arrive at season-wide hours of farm labor per person per plot. Recall households are only asked to provide a listing of plots and household members working in agriculture at baseline, while all information on farm labor is provided in the endline survey. Data on the number of days worked throughout the season and the typical number of hours worked per day are combined to calculate season-wide hours of farm labor per person per plot. As shown in table 2, recall households report 19 more hours (18 percent) of farm labor per person per plot over the season. This difference is statistically significant at the 1 percent level. Table 2. Recall Bias in Farm Labor per Person per Plot, Descriptive Estimate . Weekly visit . Recall . Difference . Season-wide hours per person per plot 106.40 125.72 19.32*** (2.81) (4.75) (5.16) Number of person-plots 2,787 1,675 . Weekly visit . Recall . Difference . Season-wide hours per person per plot 106.40 125.72 19.32*** (2.81) (4.75) (5.16) Number of person-plots 2,787 1,675 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors in parentheses. T-test on difference in means with *** denoting the difference is significant at the 1 percent level. Open in new tab Table 2. Recall Bias in Farm Labor per Person per Plot, Descriptive Estimate . Weekly visit . Recall . Difference . Season-wide hours per person per plot 106.40 125.72 19.32*** (2.81) (4.75) (5.16) Number of person-plots 2,787 1,675 . Weekly visit . Recall . Difference . Season-wide hours per person per plot 106.40 125.72 19.32*** (2.81) (4.75) (5.16) Number of person-plots 2,787 1,675 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors in parentheses. T-test on difference in means with *** denoting the difference is significant at the 1 percent level. Open in new tab As discussed in the previous section, households in the weekly visit group were slightly larger and cultivated slightly more plots at baseline. In addition, their plots were at a shorter distance from their residence than households in the recall group. It is important to adjust for these differences when making comparisons. In table 3, recall and weekly visit households are pooled to regress season-wide hours per person per plot on an indicator variable, which equals unity for households in the recall group, and controls for the household number of plots and workers at baseline, and the average distance to their plots.12 This delivers an estimate of recall bias of about 10 hours per person per plot, controlling for differences in observable characteristics at baseline. Though lower than the descriptive estimate above (which is due to the inclusion of control variables, which account for nearly half of the observed mean difference reported in table 2), it is still about 10 percent of the average in the weekly visit group, and the difference is statistically significant at the 5 percent level. Table 3. Recall Bias in Farm Labor per Person per Plot, Regression Estimate . Season-wide hours per person per plot . Recall 10.317** (5.203) N 4,462 R2 0.024 . Season-wide hours per person per plot . Recall 10.317** (5.203) N 4,462 R2 0.024 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size and number of plots, and the average distance between the household's residence and the plots (all at baseline). ** denotes significance at the 5 percent level. Open in new tab Table 3. Recall Bias in Farm Labor per Person per Plot, Regression Estimate . Season-wide hours per person per plot . Recall 10.317** (5.203) N 4,462 R2 0.024 . Season-wide hours per person per plot . Recall 10.317** (5.203) N 4,462 R2 0.024 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size and number of plots, and the average distance between the household's residence and the plots (all at baseline). ** denotes significance at the 5 percent level. Open in new tab A potential concern of the identification strategy used in this paper is that the weekly visits to farm households may have had behavioral impacts, which would confound the estimate of recall bias. The analysis relies on the identifying assumption that the survey methodology affects the quality of the data only, not behavior. Though it seems unlikely, there is a possibility that weekly visits and repeated interviews about farm labor activities may have induced farmers in the weekly visit group to organize their farm work more carefully or to spend more time farming than they would otherwise do (akin to Hawthorne effects). As a robustness check, and to rule out the possibility that the survey methodology affected actual farm labor and not just its measurement, differences in maize yields between weekly visit and recall households for plots listed at baseline are analyzed.13 The focus is on maize because it is the most common crop in the study area, cultivated on just under half of all baseline plots (see table 1). Since the survey instrument and the timing of the interviews for capturing harvest and plot size were the same for weekly visit and recall households, they should not have an impact on measured yields among plots listed at baseline. But because the harvest is measured at endline, any differences in behavior and labor input across the two groups during the season would be expected to affect yields. The results in table A1.3 ( appendix A1) show reassuringly that there is no significant difference in maize yields between weekly visit and recall households on baseline plots. This provides further confidence that the survey method did not affect farm labor, at least not to the extent that farm labor affected maize yields. Listings of Plots and Household Workers Providing accurate information on farm labor at the person-plot level requires respondents to be able to recall several components of farm-related activities, including an accurate listing of cultivated plots, and an accurate listing of household members working on those plots. Arthi et al. (2018) show that in Tanzania both the number of plots and the number of farm workers were underreported in the recall survey, and that the least-salient persons and plots were omitted. This section explores the link between recall bias in listings of plots and workers on the one hand, and recall bias in person-plot hours on the other hand. The results show that listing bias can in fact account for recall bias in person-plot hours, by changing the composition of person-plots across treatment arms. It is important to recap how respondents in the recall and weekly visit groups provide a listing of plots cultivated by the household. Recall households were interviewed twice – at the beginning of the season (baseline) and after the main harvest (endline). At baseline, respondents were asked to list all plots owned and/or expected to be cultivated during the 2015 long rainy season. At endline, respondents in the recall group were presented with the baseline list of plots and asked to add any additional plots that were owned and/or had been cultivated during the 2015 long rainy season, but had not yet been listed. Conversely, households in the weekly visit group were visited 23 times between the baseline and the endline, and during each of these visits, they could add plots that they currently owned and/or had cultivated since the last visit but that had not yet been listed. These weekly visits could make it easier to recall all plots cultivated during the season compared to the recall households, who face a lag of 23 weeks between the first visit and the endline, and may have forgotten to list all additional plots that were added after baseline. This hypothesis is explored in fig. 1, which shows the cumulative number of cultivated plots listed per household, that is, the number of cultivated plots reported up to a given week (visit number) in the season. At baseline, households in the weekly visit group reported on average 2.5 plots for cultivation, compared with 2.3 plots for recall households. By the time of the endline survey, households in the weekly visit group reported a cumulative total of 3.0 plots for cultivation, compared with only 2.5 plots for recall households. Both at baseline and at endline, the difference across treatment arms is statistically significant, but the fact that the gap doubles over time suggests that the survey method accounts for a significant part of the difference at endline. Figure 1. Open in new tabDownload slide Cumulative Number of Cultivated Plots, by Visit Number Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey.Note: Recall households were only interviewed at baseline (visit 0) and endline (visit 24). Cultivated plots are plots the household reported as used for cultivation. Figure 1. Open in new tabDownload slide Cumulative Number of Cultivated Plots, by Visit Number Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey.Note: Recall households were only interviewed at baseline (visit 0) and endline (visit 24). Cultivated plots are plots the household reported as used for cultivation. Similar considerations apply to the listing of household members working in agriculture. Households in the recall group reported at baseline and at endline which household members had been working on each plot since the beginning of the season. In contrast, households in the weekly visit group reported on a weekly basis. This is visually assessed in fig. 2, which shows the number of farm workers per household, which is calculated as the cumulative total of persons aged 10 and older who have been listed as having worked on one of the household's plots. At endline, households in the recall arm report 2.8 farm workers on average, compared to a cumulative total of 4.2 workers in weekly visit households. The difference is much smaller at baseline (2.1 vs. 2.3 workers), again suggesting that the survey method matters for the number of household workers reported.14 This listing bias mostly reflects that households in the weekly visit group report on more household workers engaged in farm labor compared with the recall group, though reporting of additional household members also plays a role (results available on request). Figure 2. Open in new tabDownload slide Cumulative Number of Household Workers, by Visit Number Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey.Note: Recall households were only interviewed at baseline (visit 0) and endline (visit 24). Household workers denotes persons aged 10 + reported of doing any agricultural labor. Figure 2. Open in new tabDownload slide Cumulative Number of Household Workers, by Visit Number Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey.Note: Recall households were only interviewed at baseline (visit 0) and endline (visit 24). Household workers denotes persons aged 10 + reported of doing any agricultural labor. A double difference estimator is used to quantify the effect of the survey method on the number of plots and household workers reported (table 4). For households in the weekly visit group, the number of plots and household workers increases by 0.5 and 1.9, respectively, between baseline and endline. This is much more than the increase of 0.2 and 0.7, respectively, in the recall group.15 Both double difference estimators of listing bias due to recall (−0.3 for plots and −1.1 for household workers) are statistically significant. Table 4. Double Difference Estimator of Bias in Listings of Plots and Household Workers . No. of cultivated plots listed per household . No. of workers listed per household . Endline 0.531*** 1.885*** (0.059) (0.128) Endline * Recall −0.320*** −1.116*** (0.088) (0.167) N 908 908 R2 0.156 0.393 . No. of cultivated plots listed per household . No. of workers listed per household . Endline 0.531*** 1.885*** (0.059) (0.128) Endline * Recall −0.320*** −1.116*** (0.088) (0.167) N 908 908 R2 0.156 0.393 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects; standard errors clustered at household level are in parentheses; *** denotes significance at the 1 percent level. Open in new tab Table 4. Double Difference Estimator of Bias in Listings of Plots and Household Workers . No. of cultivated plots listed per household . No. of workers listed per household . Endline 0.531*** 1.885*** (0.059) (0.128) Endline * Recall −0.320*** −1.116*** (0.088) (0.167) N 908 908 R2 0.156 0.393 . No. of cultivated plots listed per household . No. of workers listed per household . Endline 0.531*** 1.885*** (0.059) (0.128) Endline * Recall −0.320*** −1.116*** (0.088) (0.167) N 908 908 R2 0.156 0.393 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects; standard errors clustered at household level are in parentheses; *** denotes significance at the 1 percent level. Open in new tab The question whether bias in listings of plots and household workers accounts for recall bias in farm labor at the person-plot level is explored in table 5. Column (1) repeats the benchmark estimate of recall bias in farm labor per person per plot from table 3. Column (2) further includes an indicator variable, which equals unity if the plot was listed at baseline as well as its interaction with the main recall variable. This specification allows for the testing of two hypotheses. First, season-wide hours per person per plot may differ between plots listed at baseline and plots that were added later, so that differences in the composition of plots between the recall and weekly visit groups may explain recall bias in the number of hours reported. Second, recall bias itself might differ between plots listed at baseline and plots added later. Column (3) uses an analogue specification but distinguishes between household members listed as farm workers at baseline and those that were added later. Column (4) includes both sets of variables. Table 5. Listings of Plots and Household Workers and Recall Bias in Farm Labor per Person per Plot . Season-wide hours per person per plot . . (1) . (2) . (3) . (4) . Recall 10.317** 4.347 4.843 5.016 (5.203) (12.914) (8.222) (13.540) Plot listed at baseline 76.250*** 69.612*** (8.150) (7.913) Recall * Plot listed at baseline 1.703 −4.933 (13.989) (13.627) Person listed as farm worker at baseline 91.235*** 87.082*** (6.198) (6.142) Recall * Person listed as farm worker at baseline −2.579 −2.087 (10.324) (10.263) N 4,462 4,462 4,462 4,462 R2 0.024 0.052 0.090 0.112 . Season-wide hours per person per plot . . (1) . (2) . (3) . (4) . Recall 10.317** 4.347 4.843 5.016 (5.203) (12.914) (8.222) (13.540) Plot listed at baseline 76.250*** 69.612*** (8.150) (7.913) Recall * Plot listed at baseline 1.703 −4.933 (13.989) (13.627) Person listed as farm worker at baseline 91.235*** 87.082*** (6.198) (6.142) Recall * Person listed as farm worker at baseline −2.579 −2.087 (10.324) (10.263) N 4,462 4,462 4,462 4,462 R2 0.024 0.052 0.090 0.112 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size and number of plots, and the average distance between the household's residence and the plots (all at baseline). *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Table 5. Listings of Plots and Household Workers and Recall Bias in Farm Labor per Person per Plot . Season-wide hours per person per plot . . (1) . (2) . (3) . (4) . Recall 10.317** 4.347 4.843 5.016 (5.203) (12.914) (8.222) (13.540) Plot listed at baseline 76.250*** 69.612*** (8.150) (7.913) Recall * Plot listed at baseline 1.703 −4.933 (13.989) (13.627) Person listed as farm worker at baseline 91.235*** 87.082*** (6.198) (6.142) Recall * Person listed as farm worker at baseline −2.579 −2.087 (10.324) (10.263) N 4,462 4,462 4,462 4,462 R2 0.024 0.052 0.090 0.112 . Season-wide hours per person per plot . . (1) . (2) . (3) . (4) . Recall 10.317** 4.347 4.843 5.016 (5.203) (12.914) (8.222) (13.540) Plot listed at baseline 76.250*** 69.612*** (8.150) (7.913) Recall * Plot listed at baseline 1.703 −4.933 (13.989) (13.627) Person listed as farm worker at baseline 91.235*** 87.082*** (6.198) (6.142) Recall * Person listed as farm worker at baseline −2.579 −2.087 (10.324) (10.263) N 4,462 4,462 4,462 4,462 R2 0.024 0.052 0.090 0.112 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size and number of plots, and the average distance between the household's residence and the plots (all at baseline). *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab The results in columns (2) to (4) do not provide any evidence for the second hypothesis that recall bias differs between plots (household workers) listed at baseline and those that were added later, as the relevant interaction effects are insignificant in all three specifications. Conversely, reported season-wide hours per person per plot are significantly higher for plots and household workers listed at baseline than for plots and household workers added later (columns (2) to (4)), and controlling for this characteristic renders the main effect of the recall variable insignificant. Together, these results provide significant support for the first hypothesis that compositional differences explain recall bias in farm labor at the person-plot level. Season-wide hours of farm labor per person per plot are higher for recall households because they fail to list all plots and household workers. These omitted plots and persons have, on average, fewer hours of farm labor than the plots and persons that were listed at baseline. In other words, recall households report fewer “marginal” plots and farm workers than weekly visit households, which inflates their average hours per person per plot. By means of illustration, assume that there are two types of plots. Type A plots use 400 hours of labor per person and type B plots use 200 hours of labor per person. Households in the recall and weekly visit groups both cultivate on average 2 type A plots and 2 type B plots. Both groups correctly list type A plots and report 400 hours of farm labor per person for these plots. However, recall households on average only list one type B plot with 200 hours of labor, whereas weekly visit households list both type B plots with 200 hours of labor. In such a scenario, one would estimate total season hours per person per plot at 333 for recall households, compared with 300 for weekly visit households – a positive recall bias of 33 hours per person per plot, but this recall bias would disappear if the analysis controlled for plot type. In other words, it is the listing bias in plots that drives compositional differences across the two groups and overall recall bias in season-wide person-plot hours. Besides fewer hours of farm labor, do other person or plot characteristics predict under-reporting? As discussed by Beegle, Carletto, and Himelein (2012), salience may be an important factor affecting this type of “extensive margin” recall bias. Arthi et al. (2018) show that the persons and plots reported by recall households are indeed relatively more salient (plots are more likely to be owned by the household and to be close to the residence, while persons are more likely to be male adults whose main occupation is farming). Since the study in Ghana collected baseline data for recall and weekly visit households, it is possible to analyze this question using a double difference estimation. An indicator variable of whether the person or plot was added after the baseline survey is regressed on various indicators of person or plot salience, interacted with the recall variable, and controlling for household fixed effects. The expectation is that more salient persons and plots are less likely to be added after baseline (as they would have been listed at baseline), and that this effect is weaker among recall households. In other words, persons and plots added after baseline by recall households are hypothesized to be more salient compared to persons and plots that weekly visit households added after baseline. For persons, the empirical evidence supports this hypothesis. As shown in table 6, recall households are more likely to add male workers and workers who state that their main occupation is farming. In terms of age and household headship, the results show that household heads and household members of prime working age (15–50 years) are less likely to be added after the baseline, but this effect holds for recall and weekly visit households alike. Table 6. Individual Characteristics and Bias in Listings of Farm Workers . Farm worker was added after baseline . Farmer by main occupation −0.273*** (0.036) Recall*Farmer by main occupation 0.138** (0.062) Male 0.060** (0.030) Recall*Male 0.111** (0.051) Age 15–50 −0.142*** (0.031) Recall*Age 15–50 0.036 (0.053) Household head −0.384*** (0.035) Recall*Household head −0.064 (0.057) N 1,521 R2 0.278 . Farm worker was added after baseline . Farmer by main occupation −0.273*** (0.036) Recall*Farmer by main occupation 0.138** (0.062) Male 0.060** (0.030) Recall*Male 0.111** (0.051) Age 15–50 −0.142*** (0.031) Recall*Age 15–50 0.036 (0.053) Household head −0.384*** (0.035) Recall*Household head −0.064 (0.057) N 1,521 R2 0.278 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Table 6. Individual Characteristics and Bias in Listings of Farm Workers . Farm worker was added after baseline . Farmer by main occupation −0.273*** (0.036) Recall*Farmer by main occupation 0.138** (0.062) Male 0.060** (0.030) Recall*Male 0.111** (0.051) Age 15–50 −0.142*** (0.031) Recall*Age 15–50 0.036 (0.053) Household head −0.384*** (0.035) Recall*Household head −0.064 (0.057) N 1,521 R2 0.278 . Farm worker was added after baseline . Farmer by main occupation −0.273*** (0.036) Recall*Farmer by main occupation 0.138** (0.062) Male 0.060** (0.030) Recall*Male 0.111** (0.051) Age 15–50 −0.142*** (0.031) Recall*Age 15–50 0.036 (0.053) Household head −0.384*** (0.035) Recall*Household head −0.064 (0.057) N 1,521 R2 0.278 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab For plots (table 7), there is no evidence that salience predicts why recall households are more prone to under-reporting of plots. Large plots are less likely to be added after baseline by recall and weekly visit households alike. Plot distance, ownership, gender of the manager, and maize cultivation are not associated with being listed. Table 7. Plot Characteristics and Bias in Listings of Plots . Plot was added after baseline . Large plot (> = 75th percentile) −0.101** (0.041) Recall*Large plot −0.035 (0.064) Nearby (distance 30 min or less) 0.062 (0.049) Recall*Nearby −0.052 (0.075) Plot owned −0.090 (0.089) Recall*Plot owned 0.059 (0.142) Male manager 0.027 (0.051) Recall*Male manager −0.036 (0.084) Any maize −0.053 (0.035) Recall*Any maize 0.028 (0.054) N 1,226 R2 0.028 . Plot was added after baseline . Large plot (> = 75th percentile) −0.101** (0.041) Recall*Large plot −0.035 (0.064) Nearby (distance 30 min or less) 0.062 (0.049) Recall*Nearby −0.052 (0.075) Plot owned −0.090 (0.089) Recall*Plot owned 0.059 (0.142) Male manager 0.027 (0.051) Recall*Male manager −0.036 (0.084) Any maize −0.053 (0.035) Recall*Any maize 0.028 (0.054) N 1,226 R2 0.028 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects. ** denotes significance at the 5 percent level. Open in new tab Table 7. Plot Characteristics and Bias in Listings of Plots . Plot was added after baseline . Large plot (> = 75th percentile) −0.101** (0.041) Recall*Large plot −0.035 (0.064) Nearby (distance 30 min or less) 0.062 (0.049) Recall*Nearby −0.052 (0.075) Plot owned −0.090 (0.089) Recall*Plot owned 0.059 (0.142) Male manager 0.027 (0.051) Recall*Male manager −0.036 (0.084) Any maize −0.053 (0.035) Recall*Any maize 0.028 (0.054) N 1,226 R2 0.028 . Plot was added after baseline . Large plot (> = 75th percentile) −0.101** (0.041) Recall*Large plot −0.035 (0.064) Nearby (distance 30 min or less) 0.062 (0.049) Recall*Nearby −0.052 (0.075) Plot owned −0.090 (0.089) Recall*Plot owned 0.059 (0.142) Male manager 0.027 (0.051) Recall*Male manager −0.036 (0.084) Any maize −0.053 (0.035) Recall*Any maize 0.028 (0.054) N 1,226 R2 0.028 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household fixed effects. ** denotes significance at the 5 percent level. Open in new tab Taken together, this section presents evidence that recall households omit plots and farm workers to a greater extent than weekly visit households, and that this listing bias can account for recall bias in person-plot farm labor hours through a compositional effect. As recall households omit persons and plots with fewer farm labor hours, their average person-plot hours are biased upwards. Gender and main occupation are significant predictors of omission of persons, while for plots there is no evidence that salience matters (other than the plot's average season-wide hours of farm labor per person). Conditional on being listed at baseline, there is no recall bias in person-plot hours. This suggests, perhaps surprisingly, that respondents in this setting can accurately recall farm labor hours conditional on listing persons and plots. 5. Heterogeneity: The Role of Education and Gender This section explores whether recall bias varies by education and gender, starting with the relationship between education and recall bias. As discussed in section 2, several studies have found a positive association between the level of education – or direct measures of cognitive skills – and recall ability. Based on the literature, the accuracy of reports on farm labor is expected to be positively linked to educational attainment, as a proxy for cognitive skills, so that recall bias is lower among more educated households. Panel A in table A1.4 ( appendix A1) shows that recall households report, on average, 44.2 hours per person per plot more (about 25 percent) than weekly visit households among less educated households, whereas the difference is only 2.3 hours and not statistically significant among more educated households. The regression estimates of recall bias, controlling for baseline characteristics, are shown in table 8. To test for heterogeneity in recall bias by level of education, the regression includes an indicator variable that equals unity if at least one member of the household has attained education above the primary level, and its interaction with the main recall variable.16 The results provide support for the education hypothesis. Both variables are negative and significant, confirming the descriptive evidence that more educated households report fewer hours per person per plot and that recall bias for them is significantly lower than for less-educated households. The estimates confirm that there is no significant recall bias for households with above primary educational attainment (see bottom row), while households with lower education on average overestimate season-wide hours by approximately 37 hours per person per plot. Table 8. Recall Bias in Farm Labor per Person per Plot and Education, Regression Estimate . Season-wide hours per person per plot . Recall 36.794*** (8.251) Hh education above primary −22.421*** (6.471) Recall * Above primary −42.694*** (10.444) N 4,462 R2 0.040 Total recall bias for educated households −5.900 (6.535) . Season-wide hours per person per plot . Recall 36.794*** (8.251) Hh education above primary −22.421*** (6.471) Recall * Above primary −42.694*** (10.444) N 4,462 R2 0.040 Total recall bias for educated households −5.900 (6.535) Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for the household numbers of workers and plots, and the average distance between the household's residence and the plots (all at baseline). Hh education refers to the highest level of education attained by any household member. Standard errors in parentheses. *** denotes significance at the 1 percent level. Open in new tab Table 8. Recall Bias in Farm Labor per Person per Plot and Education, Regression Estimate . Season-wide hours per person per plot . Recall 36.794*** (8.251) Hh education above primary −22.421*** (6.471) Recall * Above primary −42.694*** (10.444) N 4,462 R2 0.040 Total recall bias for educated households −5.900 (6.535) . Season-wide hours per person per plot . Recall 36.794*** (8.251) Hh education above primary −22.421*** (6.471) Recall * Above primary −42.694*** (10.444) N 4,462 R2 0.040 Total recall bias for educated households −5.900 (6.535) Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for the household numbers of workers and plots, and the average distance between the household's residence and the plots (all at baseline). Hh education refers to the highest level of education attained by any household member. Standard errors in parentheses. *** denotes significance at the 1 percent level. Open in new tab Since recall bias in person-plot hours is mainly driven by listing bias, the latter should also show an educational gradient. This is explored in table 9, by analyzing heterogeneity in the listing of plots and household workers. The first two columns show the double difference estimate of listing bias in plots by household education, while the third and fourth columns estimate listing bias in persons by household education. The results show that less-educated households have significant listing bias in plots as well as persons. Yet the more educated households have no listing bias in plots (column 2) although they still show listing bias in workers (column 4). Hence more educated households do a better job of recalling all their plots, but still fail to list all farm workers (but note that listing bias in plots alone can account for recall bias in person-plot hours, as was shown in column (2) of table 5). This may be explained by the mobility of household members within the period of study, making it particularly difficult to recall all household members who worked on each plot but are not physically present at the time of the endline interview. As reported in table A1.5 ( appendix A1), furthermore, a comparison of less- and more-educated households within the weekly visit group shows that the more-educated households have more marginal workers, and in particular a higher number of workers whose main occupation is not farming (as shown in table 6, these workers are less likely to be listed by recall households). There is no difference in total plot-level hours and number of plots between less- and more-educated households. Hence, more-educated households may be better at listing farm workers as well as plots, ceteris paribus, but for farm workers this is counteracted by the fact that they have more marginal farm workers. Table 9. Double Difference Estimator of Bias in Listings of Plots and Household Workers by Education . No. of plots listed per household . No. of workers listed per household . . Low education . High education . Low education . High education . . (1) . (2) . (3) . (4) . Endline 0.600*** 0.476*** 1.630*** 2.087*** (0.086) (0.080) (0.159) (0.191) Endline * Recall −0.568*** −0.045 −1.162*** −1.058*** (0.115) (0.136) (0.202) (0.261) N 452 456 452 456 R2 0.179 0.175 0.373 0.422 . No. of plots listed per household . No. of workers listed per household . . Low education . High education . Low education . High education . . (1) . (2) . (3) . (4) . Endline 0.600*** 0.476*** 1.630*** 2.087*** (0.086) (0.080) (0.159) (0.191) Endline * Recall −0.568*** −0.045 −1.162*** −1.058*** (0.115) (0.136) (0.202) (0.261) N 452 456 452 456 R2 0.179 0.175 0.373 0.422 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: All estimations include household fixed effects; education refers to the highest level of education attained by any household member. Standard errors clustered at household level are in parentheses. *** denotes significance at the 1 percent level. Open in new tab Table 9. Double Difference Estimator of Bias in Listings of Plots and Household Workers by Education . No. of plots listed per household . No. of workers listed per household . . Low education . High education . Low education . High education . . (1) . (2) . (3) . (4) . Endline 0.600*** 0.476*** 1.630*** 2.087*** (0.086) (0.080) (0.159) (0.191) Endline * Recall −0.568*** −0.045 −1.162*** −1.058*** (0.115) (0.136) (0.202) (0.261) N 452 456 452 456 R2 0.179 0.175 0.373 0.422 . No. of plots listed per household . No. of workers listed per household . . Low education . High education . Low education . High education . . (1) . (2) . (3) . (4) . Endline 0.600*** 0.476*** 1.630*** 2.087*** (0.086) (0.080) (0.159) (0.191) Endline * Recall −0.568*** −0.045 −1.162*** −1.058*** (0.115) (0.136) (0.202) (0.261) N 452 456 452 456 R2 0.179 0.175 0.373 0.422 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: All estimations include household fixed effects; education refers to the highest level of education attained by any household member. Standard errors clustered at household level are in parentheses. *** denotes significance at the 1 percent level. Open in new tab Recall bias may also differ between male and female workers. Time use data from Africa show that women often carry out different roles and activities simultaneously, rather than sequentially. This holds particularly for childcare, which is typically embedded within other, economic activities (Blackden and Wodon 2006). This may make it more difficult to recall farm labor for female than for male household workers. Moreover, the previous section showed that recall households are more likely to omit female workers than male workers, which also suggests that recall bias in person-plot hours should be larger for women.17 The empirical results portray a more nuanced picture. Panel B in table A1.4 ( appendix A1) summarizes hours per person per plot for male and female workers. Male farmers work almost 50 percent more hours per plot than female farmers, but contrary to expectation the recall bias appears to be greater for males than for females. Column (1) of table 10 presents the regression estimate, using an indicator variable that equals unity if the worker is female and the interaction between this variable and the recall variable. The results show that women work around 40 hours per plot less than men over the season. The point estimates further suggest that season-wide hours per plot are overestimated by 17 hours for males, compared with only 1 hour for females (see bottom row), but the difference as indicated by the interaction term is just below the 10 percent significance threshold. Contrary to expectations, there is no indication that recall bias is larger for women. If anything, the point estimates suggest the opposite. Table 10. Recall Bias in Farm Labor per Person per Plot and Gender, Regression Estimate . Season-wide hours per person per plot . . All . Men . Women . . (1) . (2) . (3) . Recall 17.328** 8.854 2.207 (7.085) (13.595) (9.221) Female −39.695*** (6.204) Recall * Female −16.379 (10.136) Person listed as farm worker at baseline 111.819*** 64.071*** (10.059) (7.128) Recall * Person listed as farm worker at baseline −0.594 −6.207 (16.672) (11.905) N 4,462 2,290 2,172 R2 0.043 0.108 0.064 Total recall bias for females 0.948 (7.373) . Season-wide hours per person per plot . . All . Men . Women . . (1) . (2) . (3) . Recall 17.328** 8.854 2.207 (7.085) (13.595) (9.221) Female −39.695*** (6.204) Recall * Female −16.379 (10.136) Person listed as farm worker at baseline 111.819*** 64.071*** (10.059) (7.128) Recall * Person listed as farm worker at baseline −0.594 −6.207 (16.672) (11.905) N 4,462 2,290 2,172 R2 0.043 0.108 0.064 Total recall bias for females 0.948 (7.373) Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for the household numbers of workers and plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Table 10. Recall Bias in Farm Labor per Person per Plot and Gender, Regression Estimate . Season-wide hours per person per plot . . All . Men . Women . . (1) . (2) . (3) . Recall 17.328** 8.854 2.207 (7.085) (13.595) (9.221) Female −39.695*** (6.204) Recall * Female −16.379 (10.136) Person listed as farm worker at baseline 111.819*** 64.071*** (10.059) (7.128) Recall * Person listed as farm worker at baseline −0.594 −6.207 (16.672) (11.905) N 4,462 2,290 2,172 R2 0.043 0.108 0.064 Total recall bias for females 0.948 (7.373) . Season-wide hours per person per plot . . All . Men . Women . . (1) . (2) . (3) . Recall 17.328** 8.854 2.207 (7.085) (13.595) (9.221) Female −39.695*** (6.204) Recall * Female −16.379 (10.136) Person listed as farm worker at baseline 111.819*** 64.071*** (10.059) (7.128) Recall * Person listed as farm worker at baseline −0.594 −6.207 (16.672) (11.905) N 4,462 2,290 2,172 R2 0.043 0.108 0.064 Total recall bias for females 0.948 (7.373) Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for the household numbers of workers and plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Additional regressions in columns (2) and (3) of table 10 show that for both men and women, listing bias can account for recall bias in person-plot hours. However, the difference in total hours between workers listed at baseline and those added later is much larger for men (men listed at baseline work 112 hours more than men added after the baseline, while women listed at baseline work 64 hours more than women added after the baseline). This suggests that for female farm workers, the impact of listing bias is mitigated as the baseline workers differ less from the “omitted” workers. In all, the analysis in this section suggests that recall ability is positively related to educational attainment, since more-educated households are better able to accurately list all their plots at endline, at least in this study setting. Hence, there is no significant recall bias in hours worked per person per plot for more-educated households. Somewhat surprisingly, there is no significant recall bias for female farm workers (as opposed to male farm workers) in this study. The estimation results indicate that this can be explained by the fact that omitted female workers are more similar to the listed female workers than is the case for male workers. 6. Comparison between Ghana and Tanzania As mentioned earlier, the design of this study evolved from an earlier survey experiment, which was conducted in the Mara region of Tanzania in 2014 (Arthi et al. 2018). The main difference in design of the two experiments is related to the way information was captured for the recall group. In the Tanzania case, the recall households were interviewed only once at the end of the season. In Ghana, the recall households were visited at the beginning of the agricultural season for the baseline survey, which collected an initial listing of plots and household workers, and again at the end of the season. The Tanzania approach allows for the comparison of the treatment group with what would be a “typical” cross-sectional household survey that is conducted at the end of the agricultural season without any information from the start or during the season. Conversely, the Ghana approach resembles a panel survey, which draws on an earlier roster of household members and plots. The latter facilitates controlling for differences in baseline characteristics and disentangling the possible sources of recall bias by allowing more rigorous estimates of listing bias. The results of both studies are summarized in table 11. Columns 3 and 4 replicate table 2, and columns 1 and 2 are the equivalent numbers for Tanzania. Weekly visit households in Tanzania report 39.5 hours of farm labor per person per plot, which is significantly less than in Ghana (106.4 hours). However, this difference can be easily explained by differences in plot size, with plots being much smaller in Tanzania (0.3 ha for weekly visit households) than in Ghana (1.2 ha). The large difference in recall bias (not controlling for baseline differences) is also striking – 18 percent in Ghana, versus 207 percent in Tanzania. What would explain such a large difference in the magnitude of recall bias? Table 11. Farm Labor per Person per Plot, Ghana and Tanzania . Tanzania . Ghana . . Weekly visit . Recall . Weekly Visit . Recall . Season-wide hours per person per plot 39.5 121.3*** 106.4 125.7*** (1.03) (3.44) (2.81) (4.75) . Tanzania . Ghana . . Weekly visit . Recall . Weekly Visit . Recall . Season-wide hours per person per plot 39.5 121.3*** 106.4 125.7*** (1.03) (3.44) (2.81) (4.75) Source: Authors’ analysis based on data from the 2014 Tanzania agricultural labor survey (Arthi et al. 2018) and the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. *** Denotes significantly different from weekly visit estimate at the 1 percent level. Open in new tab Table 11. Farm Labor per Person per Plot, Ghana and Tanzania . Tanzania . Ghana . . Weekly visit . Recall . Weekly Visit . Recall . Season-wide hours per person per plot 39.5 121.3*** 106.4 125.7*** (1.03) (3.44) (2.81) (4.75) . Tanzania . Ghana . . Weekly visit . Recall . Weekly Visit . Recall . Season-wide hours per person per plot 39.5 121.3*** 106.4 125.7*** (1.03) (3.44) (2.81) (4.75) Source: Authors’ analysis based on data from the 2014 Tanzania agricultural labor survey (Arthi et al. 2018) and the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. *** Denotes significantly different from weekly visit estimate at the 1 percent level. Open in new tab The information on listing bias in Ghana and Tanzania, which helps to understand the difference in recall bias shown in table 11, are provided in table 12. The simple difference estimator of listing bias presented in the top panel is equal to the difference in the average number of workers (plots) at endline between weekly visit and recall households, and can be compared between Ghana and Tanzania. The bottom panel shows the double difference estimator of listing bias, which nets out baseline differences. Given that Tanzania did not collect baseline information for recall households, the double difference estimator can only be calculated for Ghana. Table 12. Bias in Listings of Plots and Household Workers, Ghana and Tanzania . . Tanzania . Ghana . Listing bias (simple difference) Workers −1.5*** −1.4*** Plots −2.3*** −0.6*** Listing bias (double difference) Workers N/A −1.1*** Plots N/A −0.3*** . . Tanzania . Ghana . Listing bias (simple difference) Workers −1.5*** −1.4*** Plots −2.3*** −0.6*** Listing bias (double difference) Workers N/A −1.1*** Plots N/A −0.3*** Source: Authors’ analysis based on data from the 2014 Tanzania agricultural labor survey (Arthi et al. 2018) and the 2015 Ghana agricultural labor survey. Note: *** Denotes the estimator of listing bias due to recall is significant at the 1 percent level. Open in new tab Table 12. Bias in Listings of Plots and Household Workers, Ghana and Tanzania . . Tanzania . Ghana . Listing bias (simple difference) Workers −1.5*** −1.4*** Plots −2.3*** −0.6*** Listing bias (double difference) Workers N/A −1.1*** Plots N/A −0.3*** . . Tanzania . Ghana . Listing bias (simple difference) Workers −1.5*** −1.4*** Plots −2.3*** −0.6*** Listing bias (double difference) Workers N/A −1.1*** Plots N/A −0.3*** Source: Authors’ analysis based on data from the 2014 Tanzania agricultural labor survey (Arthi et al. 2018) and the 2015 Ghana agricultural labor survey. Note: *** Denotes the estimator of listing bias due to recall is significant at the 1 percent level. Open in new tab The simple difference estimator of bias in the listing of plots is significantly larger in Tanzania (2.3 fewer plots for recall households) than in Ghana (0.6 plots fewer plots in the recall group), while listing bias in household workers is similar (1.5 vs. 1.4 fewer workers in the recall group). In both experiments, the roster for weekly visit households is “cumulative,” as shown in figs. 1 and 2; this means that it has been updated throughout the season to capture all plots and all household workers involved in farm work. The fact that listing bias in plots is smaller in Ghana than in Tanzania might partly reflect the fact that recall households in Ghana were administered a baseline plot roster, which was updated once at endline and thereby helped to facilitate recall. As illustrated in section 4, listing bias is the driving force behind recall bias in farm labor per person per plot in Ghana – and this may partly explain the large difference between the two studies highlighted in table 11.18 Differences in agricultural production systems and rural labor markets could further contribute to the difference in listing bias of plots, though this hypothesis cannot be tested formally with the data at hand. Households in Ghana cultivate, on average, 2.6 plots of 1.2 ha, compared with 5.7 plots of 0.3 ha in Tanzania. The fact that households in Ghana cultivate significantly fewer, yet larger, plots than households in Tanzania could explain why they are able to provide a more accurate listing of plots already at baseline.19 Labor markets in the study area in Ghana are also more integrated, as evidenced by the greater prevalence of agricultural wage labor, and this may lead to a better mental accounting of plot-level labor inputs among the study population.20 Finally, differences in educational attainment could also play a role. In the study area in Ghana, 50 percent of households have at least one member with above primary education, compared with only 34 percent of households in the Mara region of Tanzania. Since it has been shown in section 5 that recall bias, and particularly listing bias for plots, declines with the level of education, the lower levels of education in Tanzania compared to Ghana are consistent with the observed differences in recall and listing bias. 7. Implications of Recall Bias for Empirical Research Sections 4 and 5 analyzed farm labor in season-wide hours per person per plot, which is the unit at which farm labor is reported in this survey. However, as discussed in section 2, other levels of aggregation (particularly farm labor per plot and per household) are of greater interest for most data users. As will be discussed in this section, listing bias – that is, the disproportionate omission of plots and household workers by recall households – mechanically depresses total farm labor hours (aggregated at the plot or household level) for this group. Due to this counteracting effect of listing bias on recall bias in farm labor at the person-plot level, “net” recall bias in farm labor is strongly affected by the aggregation level at which it is reported, both in direction and in magnitude. Recall Bias at Different Levels of Aggregation Farm labor hours at different levels of aggregation are summarized in table 13. Comparing recall households to weekly visit households, there is no significant difference in farm labor per person (panel A). Hence the recall bias in season-wide hours per person per plot (in table 2) is nullified by the lower number of plots listed.21 Farm labor per plot (panel B) is about 13 percent lower for recall households, and total farm labor per household (panel C) is about 30 percent lower compared to weekly visit households, and both differences are statistically significant. At these levels of aggregation, listing bias hence dominates other forms of recall bias in farm labor per person per plot.22 Or in other words, because recall households report farm labor for too few plots and (especially) too few household workers, farm labor per plot and per household is underestimated, even though farm labor per person per plot is overestimated. Table 13. Recall Bias in Aggregated Farm Labor, Descriptive Estimates . . Weekly visit . Recall . Difference . A. Season-wide hours per person (all household plots) 333.95 332.68 −1.27 (10.72) (18.80) (20.33) Number of observations (persons) 888 633 B. Season-wide hours per plot (all household persons) 432.29 374.71 −57.57** (17.90) (20.96) (27.41) Number of observations (plots) 686 562 C. Season-wide hours per household (all persons and plots) 1,312.16 923.63 −388.53*** (63.50) (86.09) (107.12) Number of observations (households) 226 228 . . Weekly visit . Recall . Difference . A. Season-wide hours per person (all household plots) 333.95 332.68 −1.27 (10.72) (18.80) (20.33) Number of observations (persons) 888 633 B. Season-wide hours per plot (all household persons) 432.29 374.71 −57.57** (17.90) (20.96) (27.41) Number of observations (plots) 686 562 C. Season-wide hours per household (all persons and plots) 1,312.16 923.63 −388.53*** (63.50) (86.09) (107.12) Number of observations (households) 226 228 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Includes individuals aged 10 + reported as having performed agricultural labor at any point in time during the season, and plots for which any agricultural labor was reported at any point in time during the season. Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors in parentheses. T-test on difference in means with *** denoting the difference is significant at the 1 percent level; ** at the 5 percent level. Open in new tab Table 13. Recall Bias in Aggregated Farm Labor, Descriptive Estimates . . Weekly visit . Recall . Difference . A. Season-wide hours per person (all household plots) 333.95 332.68 −1.27 (10.72) (18.80) (20.33) Number of observations (persons) 888 633 B. Season-wide hours per plot (all household persons) 432.29 374.71 −57.57** (17.90) (20.96) (27.41) Number of observations (plots) 686 562 C. Season-wide hours per household (all persons and plots) 1,312.16 923.63 −388.53*** (63.50) (86.09) (107.12) Number of observations (households) 226 228 . . Weekly visit . Recall . Difference . A. Season-wide hours per person (all household plots) 333.95 332.68 −1.27 (10.72) (18.80) (20.33) Number of observations (persons) 888 633 B. Season-wide hours per plot (all household persons) 432.29 374.71 −57.57** (17.90) (20.96) (27.41) Number of observations (plots) 686 562 C. Season-wide hours per household (all persons and plots) 1,312.16 923.63 −388.53*** (63.50) (86.09) (107.12) Number of observations (households) 226 228 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Includes individuals aged 10 + reported as having performed agricultural labor at any point in time during the season, and plots for which any agricultural labor was reported at any point in time during the season. Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors in parentheses. T-test on difference in means with *** denoting the difference is significant at the 1 percent level; ** at the 5 percent level. Open in new tab In table 14, regression estimates are provided that confirm a significant and negative recall bias in hours per plot and hours per household, controlling for the baseline number of plots, household size, and the average distance to the plots. This is smaller than the descriptive bias reported in table 13, but still large and statistically significant. Table 14. Recall Bias in Aggregated Farm Labor, Regression Estimates . Hours per person . Hours per plot . Hours per household . Recall −3.886 −53.686** −276.062*** (20.421) (26.992) (99.237) N 1,521 1,248 454 R2 0.036 0.067 0.204 . Hours per person . Hours per plot . Hours per household . Recall −3.886 −53.686** −276.062*** (20.421) (26.992) (99.237) N 1,521 1,248 454 R2 0.036 0.067 0.204 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Table 14. Recall Bias in Aggregated Farm Labor, Regression Estimates . Hours per person . Hours per plot . Hours per household . Recall −3.886 −53.686** −276.062*** (20.421) (26.992) (99.237) N 1,521 1,248 454 R2 0.036 0.067 0.204 . Hours per person . Hours per plot . Hours per household . Recall −3.886 −53.686** −276.062*** (20.421) (26.992) (99.237) N 1,521 1,248 454 R2 0.036 0.067 0.204 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; ** at the 5 percent level. Open in new tab Implications for Agricultural Productivity Measures Measures of farm labor can be of interest in isolation but are most commonly used in the context of analyzing agricultural productivity. As shown in table A1.6 ( appendix A1), common measures of agricultural productivity – such as labor productivity per-worker, labor productivity per-hour, and land productivity per-acre – can be affected by listing bias in plots and persons and recall bias in the number of hours per person-plot conditional on being listed. The table further distinguishes according to whether the unit of analysis is the plot or the household. Let's take the example of labor productivity per hour measured at the household level. Listing bias in persons increases the measured labor productivity per hour, because the labor input (measured in hours) of the nonlisted persons is not captured in the total hours that enter through the denominator. Listing bias in plots has ambiguous effects: since output is measured at the crop-plot level, any omitted plot reduces both the numerator (in terms of nonmeasured output) and the denominator (in terms of nonmeasured hours). The net effect depends on whether labor productivity is systematically lower or higher on omitted plots versus listed plots. Together, these two forms of listing bias in persons and plots are likely to increase household level per-hour labor productivity, but the net effect might be negative if omitted plots have substantially higher labor productivity, which seems unlikely. Additionally, recall bias in hours per person-plot conditional on being listed needs to be considered. If this bias is positive, as was the case in Tanzania, this would reduce measured productivity by increasing the denominator. However, in the context of this study in Ghana, there is no such recall bias conditional on being listed. Because of all these counteracting effects, the net effect of listing bias in plots, persons, and conditional recall bias is unclear a priori. Even though the net effects may be ambiguous, the table allows making the following predictions. First, measures of land productivity will in general be less affected by recall bias in farm labor than measures of labor productivity. However, land productivity can still be affected by listing bias in plots. Depending on whether the nonlisted plots are more (less) productive than the listed plots, the recall method will underestimate (overestimate) measured land productivity. Second, of all the productivity measures, labor productivity per worker measured at the plot level is most likely to be overestimated by the recall method. This is because listing bias in persons reduces the denominator, and there is no potentially counteracting effect of conditional recall bias. Third, even if labor productivity per worker is overestimated at the plot level, it could still be underestimated at the household level. This is because listing bias in plots reduces measured output (in the numerator) but may not necessarily reduce the number of workers (the denominator), unless some workers worked exclusively on nonlisted plots. To assess the impact on different measures of productivity empirically, data on crop production collected at endline are used. As discussed in section 3, the endline survey fielded a standard agricultural production module to all households, which asked households to report the quantity and value of crop harvested during the preceding (i.e., just completed) 2015 agricultural season (for each plot and crop). Hence, households in the weekly visit and recall groups reported on their plot-level harvest in the same manner. Using these harvest data, plot-level measures of land and labor productivity for maize (the most important crop in the sample), in kg per acre, per labor hour, and per worker, are computed.23 All measures are winsorized at 1 percent, and the analysis is conducted at the plot level. The regression estimates of recall bias are presented in table 15. Table 15. Recall Bias in Land and Labor Productivity (Maize) . Land productivity (i.e., yields) . Labor productivity (per hour) . Labor productivity (per worker) . . Kg/acre . Kg/hour . Kg/worker . . (1) . (2) . (3) . Recall 56.216 6.231* 436.454*** (51.136) (3.345) (127.417) N 486 486 486 R2 0.013 0.046 0.101 Control mean 727.35 15.87 902.56 . Land productivity (i.e., yields) . Labor productivity (per hour) . Labor productivity (per worker) . . Kg/acre . Kg/hour . Kg/worker . . (1) . (2) . (3) . Recall 56.216 6.231* 436.454*** (51.136) (3.345) (127.417) N 486 486 486 R2 0.013 0.046 0.101 Control mean 727.35 15.87 902.56 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: All dependent variables are winsorized (1 percent). Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; * at the 10 percent level. Control mean shows the mean value of the dependent variable for weekly visit households. Open in new tab Table 15. Recall Bias in Land and Labor Productivity (Maize) . Land productivity (i.e., yields) . Labor productivity (per hour) . Labor productivity (per worker) . . Kg/acre . Kg/hour . Kg/worker . . (1) . (2) . (3) . Recall 56.216 6.231* 436.454*** (51.136) (3.345) (127.417) N 486 486 486 R2 0.013 0.046 0.101 Control mean 727.35 15.87 902.56 . Land productivity (i.e., yields) . Labor productivity (per hour) . Labor productivity (per worker) . . Kg/acre . Kg/hour . Kg/worker . . (1) . (2) . (3) . Recall 56.216 6.231* 436.454*** (51.136) (3.345) (127.417) N 486 486 486 R2 0.013 0.046 0.101 Control mean 727.35 15.87 902.56 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: All dependent variables are winsorized (1 percent). Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. *** denotes significance at the 1 percent level; * at the 10 percent level. Control mean shows the mean value of the dependent variable for weekly visit households. Open in new tab The analysis shows no evidence of significant recall bias in maize yields (column 1), which broadly confirms the expectation that measures of land productivity should be fairly robust to the types of measurement bias that are the focus of this study. Maize yields are somewhat higher among recall households, but not statistically significantly so, suggesting that listing bias in plots does not affect yield measures (or, in other words, any productivity differences between omitted and listed plots are too small to affect average maize yields). However, measures of labor productivity in agriculture (columns 2 and 3) are significantly overestimated among recall households in this setting. In line with expectations, the recall effect is more significant (both economically and statistically) for labor productivity per worker (column 3) than for labor productivity per hour (column 2): this is because listing bias has a proportionately larger effect on the number of workers than on the number of hours per listed plot, as the omitted workers are the ones working relatively few hours. 8. Conclusion Data on agricultural labor are a key ingredient in understanding agricultural productivity in developing countries and informing policy making in rural areas. However, due to the seasonality and irregularity of farmers’ work schedules such data are difficult to collect, and research on the reliability of agricultural labor data and the best survey methods to collect them is scarce. This paper contributes to this literature by analyzing the data of a randomized survey experiment conducted in Ghana. The study was designed to allow for the comparison of farm labor estimates obtained from a recall survey conducted at the end of the season with data collected weekly throughout the season. The results show that, in this particular study context, the recall method overestimates farm labor per person per plot by about 10 percent, controlling for differences in baseline characteristics. This recall bias in farm labor at the person-plot level is accounted for by listing bias, as households in the recall group omit marginal plots and farm workers (those with relatively few hours of farm labor over the season). This selective omission of marginal plots and household workers by recall households changes the composition of plots and workers across treatment arms and inflates average farm labor hours per person per plot in the recall group. Besides working few hours, the omitted workers are more likely to be females and workers for whom farming is not their main occupation. Surprisingly, once the analysis controls for listing bias, farmers in this setting report fairly accurately on the number of hours of farm labor provided per person per plot. The results are consistent with the notion that recall households, due to the long reference period, forget to list marginal plots and household members. However, it could also be the case that the length of the reference period subtly changes the way farmers interpret questions about farm labor to exclude marginal plots and farm workers from their response. The study design does not allow disentangling these two mechanisms. The paper further explored heterogeneity by education and gender. More-educated households are better able to accurately list all their plots, even though they still underreport the number of farm workers. As a result, there is no significant recall bias in hours worked per person per plot for more-educated households (as opposed to households with lower levels of education). This educational gradient suggests that recall and listing bias may be explained by the cognitive burden of reporting on past events. Even though recall households are more likely to omit female workers than male workers, gender difference in recall bias are not significant. This is explained by the fact that females work fewer hours per plot compared to males, so that the omitted marginal female workers are more similar to the listed female workers than is the case for male workers. While it is common practice in household surveys to collect farm labor at the person-plot level, higher levels of aggregation (especially the plot level) are more widely used at the analysis stage. Because recall households report too few plots and too few farm workers, the end-of-season recall method underestimates farm labor per plot (and also per household). In settings such as this in Ghana, where listing bias is the dominant source of reporting bias, plot-level estimates of labor productivity in agriculture are therefore significantly overestimated by the recall method. The findings of this paper offer lessons for researchers and survey practitioners. First, the difference in the magnitude of recall bias between the Ghana and Tanzania studies (Arthi et al. 2018) highlights the need to understand the context in which a specific household survey will be implemented. A potential explanation for this difference in results is that the higher levels of education among smallholder farmers in the Ghanaian setting, combined with socioeconomic and agroecological characteristics of the study area (i.e., fewer but larger plots in Ghana and more integrated rural labor markets) attenuate recall bias in farm labor hours at the person-plot level compared to the Tanzanian setting. Second, the effect of the recall method on bias in farm labor hours depends, both in direction and in magnitude, on the level at which the data are aggregated at the analysis stage. This calls for exercising caution in extrapolating estimates of recall bias from one study to another. Third, the results highlight the need to pay careful attention to the listings of household members and plots, and the identification of cultivated plots and household members that are engaged in farm work, during survey implementation. Accurate capture of cultivated plots and household farm workers is not only important in and by itself, but it is also an important strategy to minimize recall bias in farm labor hours at all aggregation levels. Future methodological survey research should explore alternative methods to mitigate listing bias; for example, the use of specific terms (e.g., asking explicitly for small plots, kitchen gardens, etc., using local terminology whenever possible), clarifying statements (e.g., “Please identify all household members that worked on each plot, even if they only did so for a few hours.”), or increased use of self-respondents (as opposed to proxy respondents). In addition, it would be very useful to have a better understanding of the time profile of listing bias – such as if the respondents’ adding of plots and workers levels off at a specific point during the agricultural season or after a certain number of interactions with the interviewer – as this would provide further insights on what modifications to the way surveys are operationalized might help to reduce listing bias. Appendix A1: Additional Tables Table A1.1. Measures of Farm Labor and Aggregation Approaches Used by Empirical Studies Author(s) . Literature strand . Aggregation of labor data for analysis . Aguilar et al. (2015) Gender differences Labor per plot (normalized for plot size) Ali et al. (2016) Gender differences Labor per plot (normalized for plot size) André, Delesalle, and Dumas (2019) Child labor Labor per household Andrews, Golan, and Lay (2015) Gender differences Labor per plot (normalized for plot size) Damon and McCarthy (2019) Gender differences Labor per plot (normalized for plot size) de la O Campos, Covarrubias, and Patron (2016) Gender differences Labor per plot (normalized for plot size) Dillon, Brummund, and Mwabu (2019) Rural labor markets Labor per household Fisher and Kandiwa (2014) Gender differences Labor per plot (normalized for plot size) Gollin and Udry (2019) Agricultural productivity Labor per plot (normalized for plot size) Kilic, Palacios-Lopez, and Goldstein (2015) Gender differences Labor per plot (normalized for plot size) McCullough (2017) Productivity gaps across sectors Labor per person Oseni et al. (2015) Gender differences Labor per plot (normalized for plot size) O'Sullivan et al. (2014) Gender differences Labor per plot (normalized for plot size) Palacios-Lopez and Lopez (2015) Gender differences Labor per plot (normalized for plot size) Restuccia and Santaeulalia-Llopis (2017) Agricultural productivity Labor per household Author(s) . Literature strand . Aggregation of labor data for analysis . Aguilar et al. (2015) Gender differences Labor per plot (normalized for plot size) Ali et al. (2016) Gender differences Labor per plot (normalized for plot size) André, Delesalle, and Dumas (2019) Child labor Labor per household Andrews, Golan, and Lay (2015) Gender differences Labor per plot (normalized for plot size) Damon and McCarthy (2019) Gender differences Labor per plot (normalized for plot size) de la O Campos, Covarrubias, and Patron (2016) Gender differences Labor per plot (normalized for plot size) Dillon, Brummund, and Mwabu (2019) Rural labor markets Labor per household Fisher and Kandiwa (2014) Gender differences Labor per plot (normalized for plot size) Gollin and Udry (2019) Agricultural productivity Labor per plot (normalized for plot size) Kilic, Palacios-Lopez, and Goldstein (2015) Gender differences Labor per plot (normalized for plot size) McCullough (2017) Productivity gaps across sectors Labor per person Oseni et al. (2015) Gender differences Labor per plot (normalized for plot size) O'Sullivan et al. (2014) Gender differences Labor per plot (normalized for plot size) Palacios-Lopez and Lopez (2015) Gender differences Labor per plot (normalized for plot size) Restuccia and Santaeulalia-Llopis (2017) Agricultural productivity Labor per household Source: Authors’ compilation. Open in new tab Table A1.1. Measures of Farm Labor and Aggregation Approaches Used by Empirical Studies Author(s) . Literature strand . Aggregation of labor data for analysis . Aguilar et al. (2015) Gender differences Labor per plot (normalized for plot size) Ali et al. (2016) Gender differences Labor per plot (normalized for plot size) André, Delesalle, and Dumas (2019) Child labor Labor per household Andrews, Golan, and Lay (2015) Gender differences Labor per plot (normalized for plot size) Damon and McCarthy (2019) Gender differences Labor per plot (normalized for plot size) de la O Campos, Covarrubias, and Patron (2016) Gender differences Labor per plot (normalized for plot size) Dillon, Brummund, and Mwabu (2019) Rural labor markets Labor per household Fisher and Kandiwa (2014) Gender differences Labor per plot (normalized for plot size) Gollin and Udry (2019) Agricultural productivity Labor per plot (normalized for plot size) Kilic, Palacios-Lopez, and Goldstein (2015) Gender differences Labor per plot (normalized for plot size) McCullough (2017) Productivity gaps across sectors Labor per person Oseni et al. (2015) Gender differences Labor per plot (normalized for plot size) O'Sullivan et al. (2014) Gender differences Labor per plot (normalized for plot size) Palacios-Lopez and Lopez (2015) Gender differences Labor per plot (normalized for plot size) Restuccia and Santaeulalia-Llopis (2017) Agricultural productivity Labor per household Author(s) . Literature strand . Aggregation of labor data for analysis . Aguilar et al. (2015) Gender differences Labor per plot (normalized for plot size) Ali et al. (2016) Gender differences Labor per plot (normalized for plot size) André, Delesalle, and Dumas (2019) Child labor Labor per household Andrews, Golan, and Lay (2015) Gender differences Labor per plot (normalized for plot size) Damon and McCarthy (2019) Gender differences Labor per plot (normalized for plot size) de la O Campos, Covarrubias, and Patron (2016) Gender differences Labor per plot (normalized for plot size) Dillon, Brummund, and Mwabu (2019) Rural labor markets Labor per household Fisher and Kandiwa (2014) Gender differences Labor per plot (normalized for plot size) Gollin and Udry (2019) Agricultural productivity Labor per plot (normalized for plot size) Kilic, Palacios-Lopez, and Goldstein (2015) Gender differences Labor per plot (normalized for plot size) McCullough (2017) Productivity gaps across sectors Labor per person Oseni et al. (2015) Gender differences Labor per plot (normalized for plot size) O'Sullivan et al. (2014) Gender differences Labor per plot (normalized for plot size) Palacios-Lopez and Lopez (2015) Gender differences Labor per plot (normalized for plot size) Restuccia and Santaeulalia-Llopis (2017) Agricultural productivity Labor per household Source: Authors’ compilation. Open in new tab Table A1.2. Sample Characteristics in Baseline Survey by Attrition Status . Attritor . Non-attritor . Household size 3.739 5.444*** (0.427) (0.142) Male household head 0.739 0.780 (0.094) (0.019) Number of children (age < 10) 1.261 1.610 (0.283) (0.069) Number of persons who worked on household plot (age 10+) 1.304 2.133*** (0.277) (0.067) Number of plots 2.043 2.458 (0.213) (0.061) N (households) 23 459 Age 23.767 22.865 (2.160) (0.387) Male 0.465 0.497 (0.054) (0.010) Worked on household plot since start of season (age 10+) 0.566 0.565 (0.069) (0.012) Has no schooling (age 10+) 0.439 0.317* (0.066) (0.011) N (individuals, all ages) 86 2,499 Distance plot to residence (min. walking) 35.213 58.016*** (4.159) (1.486) Proportion of plots cultivating beans/peas 0.106 0.121 (0.045) (0.010) Proportion of plots cultivating cassava 0.106 0.111 (0.045) (0.009) Proportion of plots cultivating groundnuts 0.191 0.211 (0.058) (0.012) Proportion of plots cultivating maize 0.532 0.464 (0.074) (0.015) Proportion of plots cultivating yam 0.149 0.239 (0.052) (0.013) N (plots) 47 1,128 . Attritor . Non-attritor . Household size 3.739 5.444*** (0.427) (0.142) Male household head 0.739 0.780 (0.094) (0.019) Number of children (age < 10) 1.261 1.610 (0.283) (0.069) Number of persons who worked on household plot (age 10+) 1.304 2.133*** (0.277) (0.067) Number of plots 2.043 2.458 (0.213) (0.061) N (households) 23 459 Age 23.767 22.865 (2.160) (0.387) Male 0.465 0.497 (0.054) (0.010) Worked on household plot since start of season (age 10+) 0.566 0.565 (0.069) (0.012) Has no schooling (age 10+) 0.439 0.317* (0.066) (0.011) N (individuals, all ages) 86 2,499 Distance plot to residence (min. walking) 35.213 58.016*** (4.159) (1.486) Proportion of plots cultivating beans/peas 0.106 0.121 (0.045) (0.010) Proportion of plots cultivating cassava 0.106 0.111 (0.045) (0.009) Proportion of plots cultivating groundnuts 0.191 0.211 (0.058) (0.012) Proportion of plots cultivating maize 0.532 0.464 (0.074) (0.015) Proportion of plots cultivating yam 0.149 0.239 (0.052) (0.013) N (plots) 47 1,128 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; * at the 10 percent level. Open in new tab Table A1.2. Sample Characteristics in Baseline Survey by Attrition Status . Attritor . Non-attritor . Household size 3.739 5.444*** (0.427) (0.142) Male household head 0.739 0.780 (0.094) (0.019) Number of children (age < 10) 1.261 1.610 (0.283) (0.069) Number of persons who worked on household plot (age 10+) 1.304 2.133*** (0.277) (0.067) Number of plots 2.043 2.458 (0.213) (0.061) N (households) 23 459 Age 23.767 22.865 (2.160) (0.387) Male 0.465 0.497 (0.054) (0.010) Worked on household plot since start of season (age 10+) 0.566 0.565 (0.069) (0.012) Has no schooling (age 10+) 0.439 0.317* (0.066) (0.011) N (individuals, all ages) 86 2,499 Distance plot to residence (min. walking) 35.213 58.016*** (4.159) (1.486) Proportion of plots cultivating beans/peas 0.106 0.121 (0.045) (0.010) Proportion of plots cultivating cassava 0.106 0.111 (0.045) (0.009) Proportion of plots cultivating groundnuts 0.191 0.211 (0.058) (0.012) Proportion of plots cultivating maize 0.532 0.464 (0.074) (0.015) Proportion of plots cultivating yam 0.149 0.239 (0.052) (0.013) N (plots) 47 1,128 . Attritor . Non-attritor . Household size 3.739 5.444*** (0.427) (0.142) Male household head 0.739 0.780 (0.094) (0.019) Number of children (age < 10) 1.261 1.610 (0.283) (0.069) Number of persons who worked on household plot (age 10+) 1.304 2.133*** (0.277) (0.067) Number of plots 2.043 2.458 (0.213) (0.061) N (households) 23 459 Age 23.767 22.865 (2.160) (0.387) Male 0.465 0.497 (0.054) (0.010) Worked on household plot since start of season (age 10+) 0.566 0.565 (0.069) (0.012) Has no schooling (age 10+) 0.439 0.317* (0.066) (0.011) N (individuals, all ages) 86 2,499 Distance plot to residence (min. walking) 35.213 58.016*** (4.159) (1.486) Proportion of plots cultivating beans/peas 0.106 0.121 (0.045) (0.010) Proportion of plots cultivating cassava 0.106 0.111 (0.045) (0.009) Proportion of plots cultivating groundnuts 0.191 0.211 (0.058) (0.012) Proportion of plots cultivating maize 0.532 0.464 (0.074) (0.015) Proportion of plots cultivating yam 0.149 0.239 (0.052) (0.013) N (plots) 47 1,128 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; * at the 10 percent level. Open in new tab Table A1.3. Effect of the Recall Method on Maize Yields of Baseline Plots . Kg/acre . (1) Recall 15.713 (55.525) N 413 R2 0.007 . Kg/acre . (1) Recall 15.713 (55.525) N 413 R2 0.007 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Dependent variables are winsorized (1 percent). Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. Open in new tab Table A1.3. Effect of the Recall Method on Maize Yields of Baseline Plots . Kg/acre . (1) Recall 15.713 (55.525) N 413 R2 0.007 . Kg/acre . (1) Recall 15.713 (55.525) N 413 R2 0.007 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Dependent variables are winsorized (1 percent). Regressions control for household size, number of plots, and the average distance between the household's residence and the plots (all at baseline). Standard errors in parentheses. Open in new tab Table A1.4. Heterogeneity in Recall Bias in Farm Labor per Person per Plot, Descriptive Estimates A: By education . Weekly visit . Recall . Difference . Weekly visit . Recall . Difference . . Hh education primary or below . Hh education above primary . Season-wide hours per person per plot 123.8 168.0 44.20*** 96.1 98.3 2.27 (4.87) (10.25) (10.20) (3.39) (3.93) (5.36) Number of person-plots 1,037 658 1,750 1,017 B: By gender Weekly visit Recall Difference Weekly visit Recall Difference Male workers Female workers Season-wide hours per person per plot 126.49 151.94 25.45*** 85.84 96.71 10.87* (4.56) (7.34) (8.18) (3.14) (5.68) (5.97) Number of person-plots 1,410 880 1,337 795 A: By education . Weekly visit . Recall . Difference . Weekly visit . Recall . Difference . . Hh education primary or below . Hh education above primary . Season-wide hours per person per plot 123.8 168.0 44.20*** 96.1 98.3 2.27 (4.87) (10.25) (10.20) (3.39) (3.93) (5.36) Number of person-plots 1,037 658 1,750 1,017 B: By gender Weekly visit Recall Difference Weekly visit Recall Difference Male workers Female workers Season-wide hours per person per plot 126.49 151.94 25.45*** 85.84 96.71 10.87* (4.56) (7.34) (8.18) (3.14) (5.68) (5.97) Number of person-plots 1,410 880 1,337 795 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors are shown in parentheses. T-test on difference in means with *** denotes the difference is significant at the 1 percent level; * at the 10 percent level. Open in new tab Table A1.4. Heterogeneity in Recall Bias in Farm Labor per Person per Plot, Descriptive Estimates A: By education . Weekly visit . Recall . Difference . Weekly visit . Recall . Difference . . Hh education primary or below . Hh education above primary . Season-wide hours per person per plot 123.8 168.0 44.20*** 96.1 98.3 2.27 (4.87) (10.25) (10.20) (3.39) (3.93) (5.36) Number of person-plots 1,037 658 1,750 1,017 B: By gender Weekly visit Recall Difference Weekly visit Recall Difference Male workers Female workers Season-wide hours per person per plot 126.49 151.94 25.45*** 85.84 96.71 10.87* (4.56) (7.34) (8.18) (3.14) (5.68) (5.97) Number of person-plots 1,410 880 1,337 795 A: By education . Weekly visit . Recall . Difference . Weekly visit . Recall . Difference . . Hh education primary or below . Hh education above primary . Season-wide hours per person per plot 123.8 168.0 44.20*** 96.1 98.3 2.27 (4.87) (10.25) (10.20) (3.39) (3.93) (5.36) Number of person-plots 1,037 658 1,750 1,017 B: By gender Weekly visit Recall Difference Weekly visit Recall Difference Male workers Female workers Season-wide hours per person per plot 126.49 151.94 25.45*** 85.84 96.71 10.87* (4.56) (7.34) (8.18) (3.14) (5.68) (5.97) Number of person-plots 1,410 880 1,337 795 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: Reported hours worked have been winsorized at the top 1 percent of the distribution. Standard errors are shown in parentheses. T-test on difference in means with *** denotes the difference is significant at the 1 percent level; * at the 10 percent level. Open in new tab Table A1.5. Summary Statistics Weekly Visit Sample, by Household Education . Low education . High education . Persons  Minimum person-hours 210.050 119.603*** (26.892) (13.731)  Mean person-hours 409.816 331.118** (27.525) (18.102)  Maximum person-hours 655.930 621.579 (34.603) (28.340)  No. of workers 3.430 4.325*** (0.178) (0.197)  No. of workers, main occupation farming 2.390 2.714 (0.160) (0.173)  No. of workers, other main occupation 1.040 1.611*** (0.119) (0.153)  No. of male workers 1.750 2.151** (0.126) (0.119)  No. of female workers 1.680 2.175*** (0.106) (0.129) Plots  Minimum plot-hours 306.800 288.310 (45.804) (32.429)  Mean plot-hours 496.546 514.667 (45.569) (40.671)  Maximum plot-hours 739.920 776.532 (52.936) (59.828)  No. of plots 2.990 3.071 (0.127) (0.139) N 100 126 . Low education . High education . Persons  Minimum person-hours 210.050 119.603*** (26.892) (13.731)  Mean person-hours 409.816 331.118** (27.525) (18.102)  Maximum person-hours 655.930 621.579 (34.603) (28.340)  No. of workers 3.430 4.325*** (0.178) (0.197)  No. of workers, main occupation farming 2.390 2.714 (0.160) (0.173)  No. of workers, other main occupation 1.040 1.611*** (0.119) (0.153)  No. of male workers 1.750 2.151** (0.126) (0.119)  No. of female workers 1.680 2.175*** (0.106) (0.129) Plots  Minimum plot-hours 306.800 288.310 (45.804) (32.429)  Mean plot-hours 496.546 514.667 (45.569) (40.671)  Maximum plot-hours 739.920 776.532 (52.936) (59.828)  No. of plots 2.990 3.071 (0.127) (0.139) N 100 126 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: The rows minimum (maximum) person-hours show the average, across households, of hours worked by the household member who worked the smallest (highest) number of hours; similar for plot-hours. Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; ** at the 5 percent level. Open in new tab Table A1.5. Summary Statistics Weekly Visit Sample, by Household Education . Low education . High education . Persons  Minimum person-hours 210.050 119.603*** (26.892) (13.731)  Mean person-hours 409.816 331.118** (27.525) (18.102)  Maximum person-hours 655.930 621.579 (34.603) (28.340)  No. of workers 3.430 4.325*** (0.178) (0.197)  No. of workers, main occupation farming 2.390 2.714 (0.160) (0.173)  No. of workers, other main occupation 1.040 1.611*** (0.119) (0.153)  No. of male workers 1.750 2.151** (0.126) (0.119)  No. of female workers 1.680 2.175*** (0.106) (0.129) Plots  Minimum plot-hours 306.800 288.310 (45.804) (32.429)  Mean plot-hours 496.546 514.667 (45.569) (40.671)  Maximum plot-hours 739.920 776.532 (52.936) (59.828)  No. of plots 2.990 3.071 (0.127) (0.139) N 100 126 . Low education . High education . Persons  Minimum person-hours 210.050 119.603*** (26.892) (13.731)  Mean person-hours 409.816 331.118** (27.525) (18.102)  Maximum person-hours 655.930 621.579 (34.603) (28.340)  No. of workers 3.430 4.325*** (0.178) (0.197)  No. of workers, main occupation farming 2.390 2.714 (0.160) (0.173)  No. of workers, other main occupation 1.040 1.611*** (0.119) (0.153)  No. of male workers 1.750 2.151** (0.126) (0.119)  No. of female workers 1.680 2.175*** (0.106) (0.129) Plots  Minimum plot-hours 306.800 288.310 (45.804) (32.429)  Mean plot-hours 496.546 514.667 (45.569) (40.671)  Maximum plot-hours 739.920 776.532 (52.936) (59.828)  No. of plots 2.990 3.071 (0.127) (0.139) N 100 126 Source: Authors’ analysis based on data from the 2015 Ghana agricultural labor survey. Note: The rows minimum (maximum) person-hours show the average, across households, of hours worked by the household member who worked the smallest (highest) number of hours; similar for plot-hours. Standard errors in parentheses. T-test for difference between the two groups were done: *** denotes the difference is significant at the 1 percent level; ** at the 5 percent level. Open in new tab Table A1.6. Effect of the Recall Method on Measures of Agricultural Productivity, Mechanisms Productivity concept . Unit of analysis . . . Plot . Household . . . Measure . Direction of bias (recall method) . Measure . Direction of bias (recall method) . Labor productivity per-worker Output (plot)/workers (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average), ambiguous* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expectation Pr↑ Output (household)/workers (household) * Listing bias, persons: Pr↑* Listing bias, plots: probably Pr↓ (unless some workers worked exclusively on nonlisted plot)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous per-hour Output (plot)/hours (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Output (household)/hours (household) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Land productivity per-acre Output (plot)/acres (plot) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Output (household)/acres (household) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Productivity concept . Unit of analysis . . . Plot . Household . . . Measure . Direction of bias (recall method) . Measure . Direction of bias (recall method) . Labor productivity per-worker Output (plot)/workers (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average), ambiguous* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expectation Pr↑ Output (household)/workers (household) * Listing bias, persons: Pr↑* Listing bias, plots: probably Pr↓ (unless some workers worked exclusively on nonlisted plot)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous per-hour Output (plot)/hours (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Output (household)/hours (household) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Land productivity per-acre Output (plot)/acres (plot) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Output (household)/acres (household) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Source: Authors’ compilation. Note: Pr denotes productivity. Open in new tab Table A1.6. Effect of the Recall Method on Measures of Agricultural Productivity, Mechanisms Productivity concept . Unit of analysis . . . Plot . Household . . . Measure . Direction of bias (recall method) . Measure . Direction of bias (recall method) . Labor productivity per-worker Output (plot)/workers (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average), ambiguous* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expectation Pr↑ Output (household)/workers (household) * Listing bias, persons: Pr↑* Listing bias, plots: probably Pr↓ (unless some workers worked exclusively on nonlisted plot)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous per-hour Output (plot)/hours (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Output (household)/hours (household) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Land productivity per-acre Output (plot)/acres (plot) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Output (household)/acres (household) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Productivity concept . Unit of analysis . . . Plot . Household . . . Measure . Direction of bias (recall method) . Measure . Direction of bias (recall method) . Labor productivity per-worker Output (plot)/workers (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average), ambiguous* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expectation Pr↑ Output (household)/workers (household) * Listing bias, persons: Pr↑* Listing bias, plots: probably Pr↓ (unless some workers worked exclusively on nonlisted plot)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous per-hour Output (plot)/hours (plot) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Output (household)/hours (household) * Listing bias, persons: Pr↑* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: Pr↓(if bias is positive) or Pr↑ (if bias is negative)→ net effect ambiguous Land productivity per-acre Output (plot)/acres (plot) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Output (household)/acres (household) * Listing bias, persons: no effect* Listing bias, plots: Pr↓ (nonlisted plots more productive than average) or Pr↑ (nonlisted plots less productive than average)* Conditional recall bias in hours per person-plot: no effect→ net effect ambiguous, expect effect to be relatively small Source: Authors’ compilation. Note: Pr denotes productivity. Open in new tab Isis Gaddis (corresponding author) is a Senior Economist with the Gender Group at the World Bank and a Research Fellow at the Institute of Labor Economics (IZA); her email address is [email protected]. Gbemisola Oseni is a Senior Economist with the Development Data Group of the World Bank; her email address is [email protected]. Amparo Palacios-Lopez is also a Senior Economist with the Development Data Group of the World Bank; her email address is [email protected]. Janneke Pieters is an Assistant Professor with the Development Economics Group at Wageningen University and a Research Fellow at the Institute of Labor Economics (IZA); her email address is [email protected]. This work was supported by the U.K. Department for International Development (DFID) under the “Minding the (Data) Gap: Improving Measurements of Agricultural Productivity through Methodological Validation and Research” project (through the Trust Fund number 012853) and by the William and Flora Hewlett Foundation under the “Improving the Measurement of Subsistence Agriculture in the Framework of ICLS 19 and Its Implications for Gender Statistics” project (grant number 2015-2070). The authors gratefully acknowledge the comments from participants at the Annual Conference of the German Economic Association Research Group on Development Economics, the GLM|LIC Research Network Conference, the Conference of the Centre for the Study of African Economies, the International Conference on Globalization and Development, the Royal Economic Society Annual Conference, the World Statistics Congress and seminars at the ETH Zurich, Wageningen University, and the World Bank. The authors would further like to thank two anonymous referees for constructive comments. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development / World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent. A supplementary online appendix for this article can be found at The World Bank Economic Review website. Footnotes 1 Variants of this approach are used, for example, by the surveys conducted under the umbrella of the World Bank's Living Standards Measurement Study – Integrated Surveys on Agriculture (LSMS-ISA) initiative. 2 This section draws on Arthi et al. (2018). 3 Multitopic household surveys often also administer a general labor module, which gathers information on different types of employment and work (e.g., farm work, nonfarm household enterprise work, wage work, etc.) for each household member. These person-level measures of farm labor typically refer to the past seven days and cannot easily be extrapolated to the entire agricultural season. 4 The Ghana Living Standards Survey (GLSS) 5 uses an even more aggregated approach, asking about the number of male, female, and children's hours of family labor on each plot during the last major/minor seasons. 5 Other examples are multiple rounds of nationally representative LSMS-ISA surveys in Burkina Faso, Ethiopia, Malawi, Mali, Niger, Nigeria, Tanzania, and Uganda (World Bank 2015b) or specialized surveys with a focus on agriculture (e.g., Walker 2009 – Ghana; Mwungu et al. 2017 – Tanzania, Uganda). Another example would be the Agricultural Integrated Survey (AGRIS) designed by the Food and Agriculture Organization of the United Nations (FAO). They ask, for the holding, about the total number of months worked within the last N months, followed by questions on the average number of days per month and average number of hours per day. These questions are at the agricultural holding level and asked to every household member. 6 The survey definition of a plot may be, for example, a “continuous piece of land on which a unique crop or a mixture of crops is grown, under a uniform, consistent crop management system” (World Bank 2016). 7 Although the sample of 720 agricultural households was not designed to be representative of Ghana, neither the whole country nor meaningful parts of it, the districts were selected to capture some variation in agroecological characteristics. 8 The design of the phone arm was essentially the same as for the weekly visit group. However, instead of being visited in person, households were called once a week. 9 As per the experience of the study team, smallholder farmers in developing countries typically understand what is meant by the main agricultural season (which in the case of Ghana is the long rainy season), and when it begins. For the reference period (i.e., the long rainy season 2015), the survey instrument was designed to capture work that had been performed on the households’ plots for any type of crop – seasonal or nonseasonal. This was also highlighted in the enumerator instructions, which explicitly directed them to include work on plots with tree and permanent crops. 10 The baseline and endline surveys were timed as per the production cycle of maize – the most important crop in this area. 11 Five activities are distinguished : (1) land preparation and planting; (2) weeding; (3) ridging, fertilizing, and other nonharvest activities; (4) harvesting; and (4) supervision. 12 The results are very similar using inverse probability weighting to account for the lack of balance in some of the baseline characteristics. 13 As shown later in this paper, recall households list fewer additional plots during the season than weekly visit households, and plots that are listed during the season are structurally different from the ones listed at baseline. It is therefore important to compare baseline plots. 14 Some increase in the number of farm workers between the baseline and endline is to be expected, due to seasonal differences in labor demand, in- and out-migration of household members, etc. 15 This is the total effect of the Endline and the Endline * Recall coefficients (i.e., 0.531–0.320 = 0.2). 16 The highest level of educational attainment in the household is used to split the sample into less-educated (primary education or below) and more-educated households. This is based on the notion that the household's highest education level is a more suitable indicator of recall ability than the individual level of education of the person whose farm labor is reported, given the large share of proxy responses in the sample. An alternative approach, using the education level of the respondent, shows a regression estimate of recall bias of 11.6 hours for persons whose farm labor was reported by a respondent with primary education or less (significant at the 5 percent level), while recall bias is negative (‒4.7) and statistically insignificant for persons whose farm labor was reported by a respondent with above primary education. Results are available from the authors. 17 Double difference estimators by sex show that listing bias is statistically significant for both male and female workers and confirm that it is stronger for female workers. Results are available from the authors. 18 Unfortunately, it is not possible to compare the double difference estimator of listing bias across the two countries, which for Ghana is slightly smaller than the simple difference estimator. 19 A comparison of the distribution of person-plot hours between Ghana and Tanzania (not reported, but available from the authors on request) shows that weekly visit households in Tanzania report substantially more person-plots with less than 20 hours of farm labor compared to weekly visit households in Ghana, which could reflect the higher number of plots and smaller plot size in Tanzania. If such very low-frequency farm work is most likely to go unreported in end-of-season recall surveys, this may explain why recall bias is larger in Tanzania. In addition, the comparison indicates that recall households in Tanzania are less likely to report person-plots with 0–60 hours of farm labor compared to recall households in Ghana, which suggests that Tanzanian recall households had more difficulty reporting marginal person-plot hours. There is no evidence that farm labor is more irregular in Ghana than in Tanzania (results available on request). 20 In Ghana, 90 percent of weekly visit households used hired labor on at least one plot during the season, compared to 28 percent of households in Tanzania. 21 One may expect season-wide hours per person to be underestimated by recall households, due to their omission of plots. However, recall households omit only 0.3 plots (see table 4), which limits the effect this would have on hours per person. Furthermore, recall households report slightly more hours per person-plot conditional on the plot being listed at baseline (table 5), which, in this sample, offsets the mechanical reduction in person-hours due to the omission of plots. 22 In this setting, listing bias dominates other forms of bias at the plot level and household level, even though recall households omit relatively marginal plots and household workers. This shows that even though these marginal plots and household workers account for fewer farm labor hours than other (i.e., nonmarginal) plots and workers, they are still economically meaningful. In general, the extent to which listing bias outweighs other forms of recall bias in farm labor hours per person per plot at higher aggregation levels depends on the magnitude of each bias. 23 Hired labor is not included to maintain simplicity in the comparisons. 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This is an Open Access article distributed under the terms of the Creative Commons Attribution Non-Commercial License (https://creativecommons.org/licenses/by-nc/4.0/), which permits non-commercial re-use, distribution, and reproduction in any medium, provided the original work is properly cited. For commercial re-use, please contact [email protected] © The Author(s) 2020. Published by Oxford University Press on behalf of the International Bank for Reconstruction and Development / THE WORLD BANK.

Evans, David K; Ngatia, Mũthoni

doi: 10.1093/wber/lhaa004pmid: N/A

Abstract In recent decades, the number of evaluated interventions to improve access to school has multiplied, but few studies report long-term impacts. This paper reports the impact of an educational intervention that provided school uniforms to children in poor communities in Kenya. The program used a lottery to determine who would receive a school uniform. Receiving a uniform reduced school absenteeism by 37 percent for the average student (7 percentage points) and by 55 percent for children who initially had no uniform (15 percentage points). Eight years after the program began, there is no evidence of sustained impact of the program on highest grade completed or primary school completion rates. A bounding exercise suggests no substantive positive, long-term impacts. These results contribute to a small literature on the long-run impacts of educational interventions and demonstrate the risk of initial impacts depreciating over time. education, economic development, cost reduction, school uniforms, long-term impacts 1. Introduction User fees are a common feature of education in developing countries. Formal fees have now been abolished in many countries, but other significant costs remain, such as those associated with providing school uniforms and textbooks. These costs can be considerable. In Sierra Leone, for instance, the price of uniforms has been as great as the cost of fees required for school attendance (World Bank 2007). In Nigeria, where formal fees are no longer levied, books and uniforms cost 2.5 times more than official fees did before their elimination (Lincove 2009). These nontuition user fees are reported to have significant negative effects on enrollment. In Malawi and Uganda, a decade after tuition fees were abolished, half the households with children who have dropped out still cite lack of money as the main problem (UNESCO 2010). This paper takes advantage of a school uniform distribution program in Kenya in order to examine the impact of reducing user fees besides tuition on short-run school attendance and longer-run educational outcomes. The study examines a child sponsorship program that used a lottery to assign sponsorships to students in 12 study schools. Although not all winners of the lottery received uniforms, winning the lottery is highly correlated with receipt of a uniform and thus serves as an effective instrumental variable (IV). The study finds that receiving a uniform increases school attendance by 7.0 percentage points, which amounts to a 37 percent reduction in absenteeism. For children who did not already own a uniform, distributing a uniform reduces absenteeism by 55 percent. These effects persist even after the introduction of free primary education in Kenya. The study goes on to present results of the program eight years after its inception. Most education evaluations examine impacts after one year or less (McEwan 2015).1 This study observes no consistent pattern of long-term impacts, although the standard errors on long-term estimates are large, so the estimates are imprecise. However, a bounding exercise suggests that large long-term positive impacts can be ruled out. Eliminating user fees beyond tuition – such as uniforms – can increase school participation. Kremer, Moulin, and Namunyu (2003) evaluate a previous child sponsorship program in which a nongovernmental organization provided a package including uniforms, textbooks, and classroom construction to a set of randomly selected schools. Dropout rates fell in the treatment schools, and over time pupils completed more schooling while class sizes also increased. The authors hypothesize that the bulk of the impacts come from the uniforms, as another evaluation in the same area provided textbooks with no impact on dropout rates (Glewwe, Kremer, and Moulin 2009), and dropout rates fell before classroom construction took place. In a narrower intervention, providing 2 school uniforms over the course of 18 months, Duflo, Dupas, and Kremer (2015) find that providing uniforms to schoolgirls reduced dropout rates. Elsewhere, Hidalgo et al. (2013) find that a free school uniform program had a negative impact on attendance in Ecuador – a higher-income environment than Kenya – using school-level randomized assignment of free uniforms. The authors hypothesize a sunk cost effect, by which parents who pay for their children's uniforms feel more committed to the school. Alternatively, a quasi-experimental analysis of a government school uniform distribution program in India found heterogeneous impacts, with positive effects for girls and historically-disadvantaged castes but negative effects for wealthier students (Adukia 2014). This further supports the idea that free uniforms may improve outcomes for the most disadvantaged students. School uniforms continue to be an important issue in schools in low- and middle-income countries. In 2018, the cost burden of uniforms on parents in Kenya was highlighted in the news media (Wanzala et al. 2018). In Tanzania, the cost of uniforms reportedly keeps the poorest children out of school (Martínez 2017). In Zambia, some schools have required parents to buy uniforms from the school itself, causing controversy (Lusaka Times 2019). This study's results also contribute to the extremely limited literature on long-term impacts of educational interventions in low-income environments. In the present study, to identify children for sponsorship, the implementing NGO first prioritized orphans. If there were remaining sponsorships, it used a lottery to determine which non-orphans would receive sponsorships and consequently a free uniform. Although not all winners of the lottery received uniforms, winning the lottery is highly correlated with receipt of a uniform and thus serves as an effective instrumental variable (IV). Since schools in Kenya already use uniforms, the present study is not measuring the effect of a student uniform policy per se, but rather the impact of paying for the uniforms. The results are thus less relevant to the debate over school uniforms in developed-country contexts, which focuses on the impact of uniform policies on reducing aggressive behaviors.2 The rest of the paper is organized as follows. Following a description of the context of the experiment in section 2, section 3 describes the data and the empirical strategy. Section 4 presents the results, and finally section 5 discusses some policy implications of the results and concludes. 2. Context Costs of Schooling In a range of countries, parents face many costs of education such as school fees and provision of uniforms. In Kenya, through 2002 students were required to pay school fees to attend primary school. In January 2003, a new government policy eliminated fees and provided free textbooks and notebooks to schools, which led to dramatic increases in school participation. However, uniforms remained a major cost of schooling. Kenyan schools each have their own uniform. Historically, students who did not pay their school fees or those who did not wear uniforms could be sent away from school. Whether they were sent away and for how long varied greatly at the discretion of the school's headmaster. Students would often not pay full fees at the beginning of the year and would fulfill these obligations as the year progressed. Over the last 15 years, several prominent officials in the Kenyan government have voiced their belief that head schoolteachers should not dismiss children who fail to wear a school uniform. However, it is difficult to find a clear expression of the official policy. Anecdotal evidence suggests that students were less likely to be sent away from school for failure to wear a uniform after 2002 than previously, but that students still feel stigmatized by the failure to wear a uniform and may be reprimanded by teachers. For example, recent news items have highlighted that parents are unable to send students to school for lack of funds to pay for uniforms (Kapchanga 2014) or that school uniforms in Kenya are “de rigueur” (Kantai 2014). The school uniforms provided in the project currently being studied cost between 325 and 550 Kenyan shillings (⁠|${\$}$|4.17 to |${\$}$|7.05 in 2002 U.S. dollars) for girls and between 405 and 550 (⁠|${\$}$|5.19 to |${\$}$|7.05) for boys.3 The variation in prices is because uniforms for each school require different materials and also because tailors local to each school were contracted to sew that school's uniforms. The Project This analysis was possible in the context of an existing development project not designed by the authors. International Christelijk Steunfonds Africa (ICS), a Dutch nongovernmental organization, operated a child sponsorship program (CSP). Like many such programs, it provided benefits to the school and the community at large, rather than focusing resources only on sponsored children. The principal benefit targeted specifically to sponsored children was a free school uniform each year. In 2002, new schools entered this program. Within each school, a randomly selected subset of children received the benefits of individual sponsorship. This paper evaluates the impacts of those individually-targeted benefits.4 School-Level Benefits The schools in which CSP operated benefited from the program by receiving visits from nurses and agricultural extension officers, and grants for classroom construction, desks, and books. Specifically, a pair of ICS nurses visited each school several times a year and provided basic first aid to any child (sponsored or not) or local adult who requested it. An agricultural representative organized student clubs to grow crops on the school grounds. Upon inception into the program, each school received a sizeable grant for classroom construction, for desks, and for books. These benefits were schoolwide and not restricted to individual students. Child-Level Benefits Certain children within schools were selected for sponsorship. (The selection process is described below.) The standard individual benefit that sponsored children received was a school uniform; in June 2002, uniforms were distributed to all sponsored children who were still in school: 932 uniforms were distributed. Sponsored children went on to receive a uniform in June or July of 2003 and 2004 as well.5 In addition, sponsored children had their photo taken and sent to sponsors upon enrollment. Some sponsored children received additional letters or gifts from sponsors, but this was a small fraction. During the first two years of the program, only 6.5 percent of sponsored children received any communication from their sponsors; and only 3 percent of sponsored children received gifts.6 The infrequency of these gifts suggests that the bulk of this program's impact stems from the uniform provision and not from these idiosyncratic gifts, although the possible psychological impact of simply being identified for sponsorship by a donor organization cannot be ruled out. Selection of Schools and Program Participants In fall 2001, ICS selected 12 primary schools in Western Kenya to participate in the CSP. The 12 primary schools are all in Busia district, the westernmost district of Kenya's Western province. Busia district borders Uganda and is located just north of Lake Victoria. Through a qualitative process of local consultation, the NGO identified schools of particular vulnerability within the area. In January 2002, ICS organized a census of children in standards one through four (i.e., grades one through four) of the 12 selected schools. Based on that census, ICS selected all children who had experienced one or both parent deaths (i.e., orphans) to automatically receive sponsorships.7 Therefore out of the 876 sponsorships ICS had to allocate, 309 were assigned to orphans after the initial census. ICS then used a lottery to randomly select the remaining beneficiaries. All the remaining (i.e., non-orphan) students were automatically registered in the lottery. Since there were only a fixed number of sponsorships available, ICS determined that a lottery would be the fairest way to distribute the remaining sponsorships among other children. The result was that 550 non-orphans were randomly chosen for sponsorship, and 602 non-orphans were not chosen for sponsorship. Since sponsorships were not randomly allocated to the orphans, the effects of those sponsorships are not included in this analysis. Thus, the 550 non-orphans chosen were the group intended for treatment; and the 602 not chosen were intended as a comparison group. This is summarized in table 1. Table 1. Evolution of Study Sample . Original randomization . Matched with attendance data . Did not receive uniform . Received uniform . Found in Jan 2010 Tracking . Assigned to treatment 612 550 141 409 536 Assigned to comparison 693 602 491 111 580 Total 1,305 1,152 632 520 1,116 . Original randomization . Matched with attendance data . Did not receive uniform . Received uniform . Found in Jan 2010 Tracking . Assigned to treatment 612 550 141 409 536 Assigned to comparison 693 602 491 111 580 Total 1,305 1,152 632 520 1,116 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: This table illustrates the relationship between the original school census carried out in 2002, which the study used for the original randomization, the subsequent school attendance data, and the 2010 data that gathered longer-term outcomes. Among students from the original randomization who were matched to attendance data, the study shows how many received and did not receive uniforms. Open in new tab Table 1. Evolution of Study Sample . Original randomization . Matched with attendance data . Did not receive uniform . Received uniform . Found in Jan 2010 Tracking . Assigned to treatment 612 550 141 409 536 Assigned to comparison 693 602 491 111 580 Total 1,305 1,152 632 520 1,116 . Original randomization . Matched with attendance data . Did not receive uniform . Received uniform . Found in Jan 2010 Tracking . Assigned to treatment 612 550 141 409 536 Assigned to comparison 693 602 491 111 580 Total 1,305 1,152 632 520 1,116 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: This table illustrates the relationship between the original school census carried out in 2002, which the study used for the original randomization, the subsequent school attendance data, and the 2010 data that gathered longer-term outcomes. Among students from the original randomization who were matched to attendance data, the study shows how many received and did not receive uniforms. Open in new tab Next, a field officer from ICS went to the 12 schools to register those children selected for sponsorship in the program. For registration in the program, a child had to be present for a photograph to be taken and a small information card to be filled in, which would then be sent to the sponsor (with some basic information about the child, such as her preferred pastimes). ICS made efforts to ensure that sponsored children were in attendance on the day of registration. Schools and parents varied in their compliance. If a child intended for treatment was not present, then a replacement was selected from a list. If that replacement was not present, another was chosen. Because of that, some children who won the lottery for child sponsorship ultimately did not receive uniforms and vice-versa. ICS registered 809 children into the program. As a result, this study uses treatment assignment as an instrumental variable to estimate a local average treatment effect (LATE). The LATE parameter measures the average effect of treatment on compliers, that is, those students who received a uniform in 2002 because they were present on the day of the lottery and were randomized into the program. Table 2 presents the first-stage results: what is the probability that a child, having been randomized into the project, was actually registered or went on to receive a uniform? Table 2 indicates that 77 percent of children who won the lottery were actually registered as part of the child sponsorship program. Seventy-four percent of children who won the lottery went on to receive uniforms in June of that year. Being randomized into the program thus acts as an appropriate instrumental variable for actual registration in the program and later uniform receipt. Table 2. First-Stage Regressions . Dependent variable . . Initially registered in program (1) . Received uniform 2002 (2) . Randomized into program 0.565*** 0.541*** (0.024) (0.024) Mean among controls 0.193 0.184 Observations 1,152 1,152 R-squared 0.417 0.398 F-Statistic 49.76 . Dependent variable . . Initially registered in program (1) . Received uniform 2002 (2) . Randomized into program 0.565*** 0.541*** (0.024) (0.024) Mean among controls 0.193 0.184 Observations 1,152 1,152 R-squared 0.417 0.398 F-Statistic 49.76 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: All regressions include a full set of gender-school-standard fixed effects and controls for whether or not the child had a uniform previous to uniform distribution. *indicates significant with 90 percent confidence, **95 percent, ***99 percent. Open in new tab Table 2. First-Stage Regressions . Dependent variable . . Initially registered in program (1) . Received uniform 2002 (2) . Randomized into program 0.565*** 0.541*** (0.024) (0.024) Mean among controls 0.193 0.184 Observations 1,152 1,152 R-squared 0.417 0.398 F-Statistic 49.76 . Dependent variable . . Initially registered in program (1) . Received uniform 2002 (2) . Randomized into program 0.565*** 0.541*** (0.024) (0.024) Mean among controls 0.193 0.184 Observations 1,152 1,152 R-squared 0.417 0.398 F-Statistic 49.76 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: All regressions include a full set of gender-school-standard fixed effects and controls for whether or not the child had a uniform previous to uniform distribution. *indicates significant with 90 percent confidence, **95 percent, ***99 percent. Open in new tab 3. Data and Empirical Strategy The final data set the study uses consists of six smaller survey and administrative data sets with information about (1) students who won the sponsorship lottery in 2002, (2) students who were present in school on the date of registration in 2002, (3) a pupil questionnaire administered in 2002, (4) students who received uniforms in 2002, (5) pupil attendance from 2002 to 2006, and (6) a tracking questionnaire administered in 2010. The study has attendance information for each of the 12 schools from 2002 through the end of 2005. Attendance was gathered as field officers made unannounced visits to each school multiple times each year and recorded whether each child was present. From these multiple visits, an annual per-child attendance average is collected. The 2002 Pupil Questionnaire was carried out in mid-January 2002 before uniforms were distributed, and socioeconomic data were gathered on all children who were present at school that day. The Pupil Attendance data set has uniquely defined pupil identification numbers, and the 2002 Pupil Questionnaire and the 2010 follow-up survey use those same numbers. However, the data sets with information about the students who won the lottery, those who were present on the day of the lottery, and those who received uniforms do not include those pupil identification numbers. Therefore, names were matched manually and by computer. Some pupils in the various other data sets did not match any pupil in the Pupil Attendance data set. This may stem from the fact that sometimes children have several names and may only give a subset of those in one data-gathering exercise and a nonoverlapping subset in another exercise. It is also common for students to spell their names differently in different contexts and to change their names, further challenging the matching process. In total, the study matched attendance data for 805 pupils out of the 932 pupils who had been fitted for uniforms (86 percent). In 2010, eight years after initial uniform distribution, the study collected follow-up information on the students in the sample. Field officers were sent to the 12 program schools with a roster of students from the start of the program. They asked head teachers, teachers, and older students whether or not the student had finished primary school, whether they were still in school, and the highest grade completed. Field officers also examined official Ministry of Education Records at the school to get results from the Kenya Certificate of Primary Education (KCPE) exam, which students take at the end of eighth grade. Overall, the tracking rate was high; the study was able to collect information for about 95 percent of the students in the sample. Since the students usually live within close proximity of the school, in many cases teachers and older students knew what had happened to the students. School officials reported that 371 students (32 percent of the original sample) had completed Standard 8 and thus taken the KCPE Exam. KCPE results from 2005 through 2009 were copied from official statistics from the Ministry of Education. The study matched 328 out of these 371 students (88 percent) of pupils with KCPE results from the MoE. This study examined KCPE scores with the same school officials – at the school – who had helped the study track the students, to minimize any errors due to a failure to match children's names. The fact that it was possible to match KCPE results for the vast majority of the long-term tracked sample increases confidence that the same children are indeed being tracked. The principal regression sample consists of 1,152 children who are identified in the initial Randomization data set, the Recipient 2002 data set, and the Pupil Attendance data set. Table 3 compares children who won the lottery to those who did not across a set of basic characteristics – gender, age, school dummies, and age dummies, for which data are available for virtually all the children. There are no significant differences across any of these characteristics. For a smaller sample, the subset of children who were present when enumerators arrived at school for the baseline census, there is a wide array of variables. Table 4 compares children who won the lottery to children who did not win the lottery for the 780 children in school on the day of the 2002 Pupil Questionnaire.8 Even in this smaller, more selected sample, few significant differences are observed (e.g., winners have slightly fewer meals at home per day, have fewer pens, were slightly more likely to have breathing trouble, and were less likely to cook regularly at home or work on the farm). There are no discernible patterns of difference between groups. Once school-grade-gender fixed effects are included, treatment and comparison groups (both intended and actual) are balanced in advance of the program (results not reported). Eighty percent of children registered in the program received uniforms; 78 percent of children who received uniforms had initially won the lottery. Table 3. Pre-Treatment Comparison of Winners and Losers of the Lottery . Winners . Losers . Difference (W-L) . Std Error for Diff . Female 0.462 0.477 −0.015 0.029 Age 9.559 9.669 −0.110 0.127 Young 0.393 0.350 0.042 0.029 School 1 0.087 0.081 0.006 0.016 School 2 0.076 0.076 0 0.016 School 3 0.033 0.037 −0.004 0.011 School 4 0.127 0.13 −0.002 0.02 School 5 0.096 0.091 0.005 0.017 School 6 0.091 0.088 0.003 0.017 School 7 0.08 0.081 −0.001 0.016 School 8 0.105 0.101 0.004 0.018 School 9 0.078 0.073 0.005 0.016 School 10 0.084 0.08 0.004 0.016 School 11 0.065 0.065 0.001 0.015 School 12 0.076 0.096 −0.02 0.017 Grade 1 0.335 0.307 0.027 0.028 Grade 2 0.291 0.272 0.018 0.027 Grade 3 0.236 0.251 −0.014 0.025 Grade 4 0.138 0.169 −0.031 0.021 . Winners . Losers . Difference (W-L) . Std Error for Diff . Female 0.462 0.477 −0.015 0.029 Age 9.559 9.669 −0.110 0.127 Young 0.393 0.350 0.042 0.029 School 1 0.087 0.081 0.006 0.016 School 2 0.076 0.076 0 0.016 School 3 0.033 0.037 −0.004 0.011 School 4 0.127 0.13 −0.002 0.02 School 5 0.096 0.091 0.005 0.017 School 6 0.091 0.088 0.003 0.017 School 7 0.08 0.081 −0.001 0.016 School 8 0.105 0.101 0.004 0.018 School 9 0.078 0.073 0.005 0.016 School 10 0.084 0.08 0.004 0.016 School 11 0.065 0.065 0.001 0.015 School 12 0.076 0.096 −0.02 0.017 Grade 1 0.335 0.307 0.027 0.028 Grade 2 0.291 0.272 0.018 0.027 Grade 3 0.236 0.251 −0.014 0.025 Grade 4 0.138 0.169 −0.031 0.021 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: These summary statistics are for the full sample of 1,152 students. A student is considered “young” here and in later tables if she is age 5–9. An F-statistic of joint significance across all these variables equals 0.38. Open in new tab Table 3. Pre-Treatment Comparison of Winners and Losers of the Lottery . Winners . Losers . Difference (W-L) . Std Error for Diff . Female 0.462 0.477 −0.015 0.029 Age 9.559 9.669 −0.110 0.127 Young 0.393 0.350 0.042 0.029 School 1 0.087 0.081 0.006 0.016 School 2 0.076 0.076 0 0.016 School 3 0.033 0.037 −0.004 0.011 School 4 0.127 0.13 −0.002 0.02 School 5 0.096 0.091 0.005 0.017 School 6 0.091 0.088 0.003 0.017 School 7 0.08 0.081 −0.001 0.016 School 8 0.105 0.101 0.004 0.018 School 9 0.078 0.073 0.005 0.016 School 10 0.084 0.08 0.004 0.016 School 11 0.065 0.065 0.001 0.015 School 12 0.076 0.096 −0.02 0.017 Grade 1 0.335 0.307 0.027 0.028 Grade 2 0.291 0.272 0.018 0.027 Grade 3 0.236 0.251 −0.014 0.025 Grade 4 0.138 0.169 −0.031 0.021 . Winners . Losers . Difference (W-L) . Std Error for Diff . Female 0.462 0.477 −0.015 0.029 Age 9.559 9.669 −0.110 0.127 Young 0.393 0.350 0.042 0.029 School 1 0.087 0.081 0.006 0.016 School 2 0.076 0.076 0 0.016 School 3 0.033 0.037 −0.004 0.011 School 4 0.127 0.13 −0.002 0.02 School 5 0.096 0.091 0.005 0.017 School 6 0.091 0.088 0.003 0.017 School 7 0.08 0.081 −0.001 0.016 School 8 0.105 0.101 0.004 0.018 School 9 0.078 0.073 0.005 0.016 School 10 0.084 0.08 0.004 0.016 School 11 0.065 0.065 0.001 0.015 School 12 0.076 0.096 −0.02 0.017 Grade 1 0.335 0.307 0.027 0.028 Grade 2 0.291 0.272 0.018 0.027 Grade 3 0.236 0.251 −0.014 0.025 Grade 4 0.138 0.169 −0.031 0.021 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: These summary statistics are for the full sample of 1,152 students. A student is considered “young” here and in later tables if she is age 5–9. An F-statistic of joint significance across all these variables equals 0.38. Open in new tab Table 4. Pre-Treatment Comparison of Winners and Losers of the Lottery . Winners . Losers . Difference (W-L) . Std error for diff . Demographics and Home Characteristics Female 0.47 0.47 0.00 0.04 Age 9.6 9.73 −0.13 0.14 School attendance (Jan−June '02) 0.86 0.85 0.01 0.02 Kids in same compound 2.31 2.02 0.29 0.28 Iron roof 0.4 0.4 −0.01 0.04 Toilet 0.85 0.86 −0.01 0.03 Meals per day 2.22 2.29 −0.07* 0.04 School requirements Pens 0.53 0.65 −0.12** 0.06 Pencils 1.23 1.26 −0.03 0.07 Books 0.21 0.21 0.00 0.05 Exercise books 4.92 5.04 −0.12 0.18 Bag 1.02 1.06 −0.04 0.05 Uniform shirts 0.77 0.8 −0.03 0.06 Uniform dresses 0.8 0.71 0.09 0.06 Self-reported health Headache 0.31 0.27 0.03 0.03 Flu 0.24 0.21 0.03 0.03 Coughing 0.17 0.17 0.00 0.03 Breathing 0.05 0.03 0.03** 0.01 Stomachache 0.25 0.21 0.04 0.03 Vomiting 0.09 0.07 0.02 0.02 Diarrhea 0.07 0.06 0.01 0.02 Work at home Cook 0.56 0.62 −0.06* 0.04 Fetch water 0.95 0.94 0.00 0.02 Wash clothes 0.75 0.78 −0.03 0.03 Fetch wood 0.78 0.8 −0.02 0.03 Clean house 0.84 0.83 0.02 0.03 Works on the Farm 0.66 0.74 −0.08** 0.03 Shoes 0.05 0.04 0.01 0.01 Uniform 0.66 0.66 0.00 0.03 Days absent 0.94 1.08 −0.14 0.28 Received uniform from ICS in 2002 0.81 0.22 0.59*** 0.03 . Winners . Losers . Difference (W-L) . Std error for diff . Demographics and Home Characteristics Female 0.47 0.47 0.00 0.04 Age 9.6 9.73 −0.13 0.14 School attendance (Jan−June '02) 0.86 0.85 0.01 0.02 Kids in same compound 2.31 2.02 0.29 0.28 Iron roof 0.4 0.4 −0.01 0.04 Toilet 0.85 0.86 −0.01 0.03 Meals per day 2.22 2.29 −0.07* 0.04 School requirements Pens 0.53 0.65 −0.12** 0.06 Pencils 1.23 1.26 −0.03 0.07 Books 0.21 0.21 0.00 0.05 Exercise books 4.92 5.04 −0.12 0.18 Bag 1.02 1.06 −0.04 0.05 Uniform shirts 0.77 0.8 −0.03 0.06 Uniform dresses 0.8 0.71 0.09 0.06 Self-reported health Headache 0.31 0.27 0.03 0.03 Flu 0.24 0.21 0.03 0.03 Coughing 0.17 0.17 0.00 0.03 Breathing 0.05 0.03 0.03** 0.01 Stomachache 0.25 0.21 0.04 0.03 Vomiting 0.09 0.07 0.02 0.02 Diarrhea 0.07 0.06 0.01 0.02 Work at home Cook 0.56 0.62 −0.06* 0.04 Fetch water 0.95 0.94 0.00 0.02 Wash clothes 0.75 0.78 −0.03 0.03 Fetch wood 0.78 0.8 −0.02 0.03 Clean house 0.84 0.83 0.02 0.03 Works on the Farm 0.66 0.74 −0.08** 0.03 Shoes 0.05 0.04 0.01 0.01 Uniform 0.66 0.66 0.00 0.03 Days absent 0.94 1.08 −0.14 0.28 Received uniform from ICS in 2002 0.81 0.22 0.59*** 0.03 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: These summary statistics are for the 780 children (out of the full sample of 1,209) who were present when enumerators arrived at school for the baseline census in Jan 2002, before the start of program. As such, they likely represent – on average – children slightly more likely to be in school. Open in new tab Table 4. Pre-Treatment Comparison of Winners and Losers of the Lottery . Winners . Losers . Difference (W-L) . Std error for diff . Demographics and Home Characteristics Female 0.47 0.47 0.00 0.04 Age 9.6 9.73 −0.13 0.14 School attendance (Jan−June '02) 0.86 0.85 0.01 0.02 Kids in same compound 2.31 2.02 0.29 0.28 Iron roof 0.4 0.4 −0.01 0.04 Toilet 0.85 0.86 −0.01 0.03 Meals per day 2.22 2.29 −0.07* 0.04 School requirements Pens 0.53 0.65 −0.12** 0.06 Pencils 1.23 1.26 −0.03 0.07 Books 0.21 0.21 0.00 0.05 Exercise books 4.92 5.04 −0.12 0.18 Bag 1.02 1.06 −0.04 0.05 Uniform shirts 0.77 0.8 −0.03 0.06 Uniform dresses 0.8 0.71 0.09 0.06 Self-reported health Headache 0.31 0.27 0.03 0.03 Flu 0.24 0.21 0.03 0.03 Coughing 0.17 0.17 0.00 0.03 Breathing 0.05 0.03 0.03** 0.01 Stomachache 0.25 0.21 0.04 0.03 Vomiting 0.09 0.07 0.02 0.02 Diarrhea 0.07 0.06 0.01 0.02 Work at home Cook 0.56 0.62 −0.06* 0.04 Fetch water 0.95 0.94 0.00 0.02 Wash clothes 0.75 0.78 −0.03 0.03 Fetch wood 0.78 0.8 −0.02 0.03 Clean house 0.84 0.83 0.02 0.03 Works on the Farm 0.66 0.74 −0.08** 0.03 Shoes 0.05 0.04 0.01 0.01 Uniform 0.66 0.66 0.00 0.03 Days absent 0.94 1.08 −0.14 0.28 Received uniform from ICS in 2002 0.81 0.22 0.59*** 0.03 . Winners . Losers . Difference (W-L) . Std error for diff . Demographics and Home Characteristics Female 0.47 0.47 0.00 0.04 Age 9.6 9.73 −0.13 0.14 School attendance (Jan−June '02) 0.86 0.85 0.01 0.02 Kids in same compound 2.31 2.02 0.29 0.28 Iron roof 0.4 0.4 −0.01 0.04 Toilet 0.85 0.86 −0.01 0.03 Meals per day 2.22 2.29 −0.07* 0.04 School requirements Pens 0.53 0.65 −0.12** 0.06 Pencils 1.23 1.26 −0.03 0.07 Books 0.21 0.21 0.00 0.05 Exercise books 4.92 5.04 −0.12 0.18 Bag 1.02 1.06 −0.04 0.05 Uniform shirts 0.77 0.8 −0.03 0.06 Uniform dresses 0.8 0.71 0.09 0.06 Self-reported health Headache 0.31 0.27 0.03 0.03 Flu 0.24 0.21 0.03 0.03 Coughing 0.17 0.17 0.00 0.03 Breathing 0.05 0.03 0.03** 0.01 Stomachache 0.25 0.21 0.04 0.03 Vomiting 0.09 0.07 0.02 0.02 Diarrhea 0.07 0.06 0.01 0.02 Work at home Cook 0.56 0.62 −0.06* 0.04 Fetch water 0.95 0.94 0.00 0.02 Wash clothes 0.75 0.78 −0.03 0.03 Fetch wood 0.78 0.8 −0.02 0.03 Clean house 0.84 0.83 0.02 0.03 Works on the Farm 0.66 0.74 −0.08** 0.03 Shoes 0.05 0.04 0.01 0.01 Uniform 0.66 0.66 0.00 0.03 Days absent 0.94 1.08 −0.14 0.28 Received uniform from ICS in 2002 0.81 0.22 0.59*** 0.03 Source: Authors' analysis of data gathered in 12 schools in western Kenya in 2002. Note: These summary statistics are for the 780 children (out of the full sample of 1,209) who were present when enumerators arrived at school for the baseline census in Jan 2002, before the start of program. As such, they likely represent – on average – children slightly more likely to be in school. Open in new tab In the main identification strategy, random assignment into the treatment group was used as an instrument for treatment (or receiving a sponsorship), measuring the local average treatment effect (LATE). Since there was some crossover from the comparison to the treatment group, the intent-to-treat strategy – in which groups are analyzed purely based on their initial assignment to treatment or comparison – would likely understate the true impacts. The initial randomization serves as an ideal instrument since it was randomly determined, thereby giving no reason to expect it would impact the outcome except through affecting the likelihood of treatment. Also, since the majority of children who were chosen for treatment actually received uniforms, the first stage is strong. The equation below is estimated: $$\begin{eqnarray} {\it Out{\!}come_{i{\!}j}} = \alpha + {\beta _1} {Uni{\!}f{\!}orm}_{i{\!}j} + {\beta _2}No\_Uni{\!}f{\!}orm\_Be{\!}f{\!}or{e_{i{\!}j}} + \rho \,\,School - Grade - Gende{r_j} + {\varepsilon _{i{\!}j}} \end{eqnarray}$$ where outcomeij is attendance (in the short run) or other outcomes (in the longer run) for student i in school-grade-gender cell j. Uniformij is an indicator for whether student i in school-grade-gender cell j received a uniform, and this is instrumented with random assignment into the sponsorship program. The study controls for whether or not the student had a uniform at the baseline (No_Uniform_Beforeij), and school-grade-gender fixed effects to account for any differences across groups of students not driven by the program.9 For analysis of heterogeneous treatment effects, a new instrument is created by interacting the subgroup indicator (e.g., a dummy variable for female or a dummy variable for young) with the original instrument (being randomized into the program).10 Although the study sometimes refers to the impact of sponsorship as the impact of receiving a uniform, sponsorship could potentially work through other mechanisms. First, sponsored children had their picture taken and were singled out, and that kind of attention could conceivably have self-esteem impacts that could affect school attendance.11 This could work together with the aforementioned moral support offered by sponsors to a few students. The study's current estimates cannot differentiate between these effects. However, those effects would be expected to be largest immediately after initiation of sponsorship, and the study does estimate separately the impacts of sponsorship in the six months between registration and initial uniform receipt and subsequent impacts. Significant effects appear only after uniform receipt, suggesting that sponsorship alone is not driving these effects. 4. Results This section presents the empirical results of the effects of uniform provision on school attendance, test scores, and long-run outcomes for the students in the program. School Attendance In table 5 Regressions 1 and 2, the study examines whether initial randomization or registration into the program had any effect on children's school attendance in the six months before distribution of uniforms. An insignificant positive impact on attendance appears. This small but insignificant impact of being registered in the program before the students receive uniforms might be a measure of the impact of the students’ expectations of program benefits. While this anticipatory effect of the program is positive, the effect of the program is only statistically significant after uniforms are distributed in June 2002 as shown in Regressions 3–5. In Regression 3, the study provides the intent-to-treat regression, measuring the simple impact of being randomized into the project on attendance after uniform distribution, and sees an effect of 3.8 percentage points on school attendance. The IV estimates of actually receiving a uniform in 2002 (Regression 4) on attendance after uniform distribution is 7.0 percentage points (standard error 2.5 percentage points). This constitutes a reduction in absenteeism of about 37 percent from a baseline level of 18.8 percent. (In table 5 Regression 5, the study provides an OLS estimate of receiving a uniform on school attendance, which is of the same order of magnitude as the IV estimate.)12 Table 5. IV and OLS Regressions (Using Randomization into the Program as an IV for Uniform Receipt) . Attendance Jan '02−June '02 . Attendance: Jun '02−Nov '05 . . OLS . IV . OLS . IV . OLS . . (1) . (2) . (3) . (4) . (5) . Initially registered in program 0.039 (0.026) Randomized into program 0.022 0.038*** (0.015) (0.014) Received uniform in 2002 0.070*** 0.055*** (0.026) (0.014) Didn't have uniform at baseline −0.048** −0.046** −0.038** −0.033** −0.034** (0.019) (0.019) (0.017) (0.017) (0.017) Mean among controls 0.825 0.812 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.218 0.226 0.109 0.114 0.115 . Attendance Jan '02−June '02 . Attendance: Jun '02−Nov '05 . . OLS . IV . OLS . IV . OLS . . (1) . (2) . (3) . (4) . (5) . Initially registered in program 0.039 (0.026) Randomized into program 0.022 0.038*** (0.015) (0.014) Received uniform in 2002 0.070*** 0.055*** (0.026) (0.014) Didn't have uniform at baseline −0.048** −0.046** −0.038** −0.033** −0.034** (0.019) (0.019) (0.017) (0.017) (0.017) Mean among controls 0.825 0.812 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.218 0.226 0.109 0.114 0.115 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2005. Note: All regressions include a full set of gender-school-standard fixed effects and controls for whether or not the child had a uniform previous to uniform distribution. F-Statistic for regression (1) = 585.08. F-Statistic for regression (3) = 520.20. Mean attendance among comparison students is 0.813 (s.e. 0.246). *indicates significant with 90 percent confidence, **95 percent, ***99 percent. The instrument is randomization into the program. Open in new tab Table 5. IV and OLS Regressions (Using Randomization into the Program as an IV for Uniform Receipt) . Attendance Jan '02−June '02 . Attendance: Jun '02−Nov '05 . . OLS . IV . OLS . IV . OLS . . (1) . (2) . (3) . (4) . (5) . Initially registered in program 0.039 (0.026) Randomized into program 0.022 0.038*** (0.015) (0.014) Received uniform in 2002 0.070*** 0.055*** (0.026) (0.014) Didn't have uniform at baseline −0.048** −0.046** −0.038** −0.033** −0.034** (0.019) (0.019) (0.017) (0.017) (0.017) Mean among controls 0.825 0.812 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.218 0.226 0.109 0.114 0.115 . Attendance Jan '02−June '02 . Attendance: Jun '02−Nov '05 . . OLS . IV . OLS . IV . OLS . . (1) . (2) . (3) . (4) . (5) . Initially registered in program 0.039 (0.026) Randomized into program 0.022 0.038*** (0.015) (0.014) Received uniform in 2002 0.070*** 0.055*** (0.026) (0.014) Didn't have uniform at baseline −0.048** −0.046** −0.038** −0.033** −0.034** (0.019) (0.019) (0.017) (0.017) (0.017) Mean among controls 0.825 0.812 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.218 0.226 0.109 0.114 0.115 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2005. Note: All regressions include a full set of gender-school-standard fixed effects and controls for whether or not the child had a uniform previous to uniform distribution. F-Statistic for regression (1) = 585.08. F-Statistic for regression (3) = 520.20. Mean attendance among comparison students is 0.813 (s.e. 0.246). *indicates significant with 90 percent confidence, **95 percent, ***99 percent. The instrument is randomization into the program. Open in new tab One question on mechanism is whether this program impact is based on a price change (i.e., receiving the uniform significantly reduces the cost of schooling) or if it is based on the positive impact of having a new uniform. If the effect of receiving the uniform is through the cost of schooling, then it is more likely to change once school fees were eliminated. School uniforms were first distributed as part of this program in June 2002. School fees were abolished in January 2003. In additional analysis, the study tests this (table S1.2). The study shows the standard specification (i.e., the impact of receiving a uniform on attendance over the subsequent three and a half years) in column (1), where a 7 percentage point (pp) impact on attendance is seen. In column (2), an interaction term is added for post-2003 to identify if there is a differential impact of the uniforms once school fees were eliminated. The interaction between post-2003 and “received a uniform” is statistically insignificant, suggesting no difference in impact once school fees were eliminated. That said, the magnitude of the point estimate drops, and the combined point estimate of the post-uniform effect and the post-uniform * post-free primary education effects roughly equals the post-uniform effect of column (1). Thus, while clear statistical evidence of the price impact is not found, the magnitudes suggest that the price change may play a role. In column (3), the analysis is restricted to attendance measures that were made in the second half of the school year because the post-uniform distribution measures in 2002 were in the second half of the school year, when there is normally lower average attendance. Again, no significant difference is seen. This suggests the interpretation that the impact is about receiving the new uniform, particularly since free primary education policy did not cover the cost of uniforms or other incidentals. The impact of the program may be larger for children who are traditionally at higher risk of dropping out – young children, girls, and poorer children. Regression 1 of table 6 shows an impact of 4.1 percentage points for boys and a larger (but not significantly different) effect of 10.9 percentage points for girls. Table 6 Regression 2 examines the effects for younger children (aged 5–9) versus older children (aged 10–14). The study observes an effect of 11 percentage points for younger children who received a uniform in 2002 (but again, not significantly different) relative to 4.7 percentage points for older children. Table 6. Effect of Free Uniforms on School Attendance by Gender and Age (using Randomization into the Program as an IV for Uniform Receipt) . Dependent variable attendance June '02 to Nov '05 . . (1) . (2) . (3) . (4) . Received uniform in 2002 0.041 0.047 0.048* −0.087 (0.032) (0.032) (0.028) (0.293) Female * Received uniform in 2002 0.068 (0.052) Young * Received uniform in 2002 0.063 (0.053) Young 0.004 (0.033) Received uniform 2002 * Didn't have uniform at baseline 0.098 (0.067) Received uniform in 2002 * Proportion of school who had uniform 0.222 (0.397) Didn't have uniform at baseline −0.033** −0.032* −0.078** −0.034** (0.017) (0.017) (0.037) (0.017) Mean attendance among controls 0.812 Observations 1,152 1,152 1,152 1,152 R-squared 0.111 0.112 0.107 0.111 . Dependent variable attendance June '02 to Nov '05 . . (1) . (2) . (3) . (4) . Received uniform in 2002 0.041 0.047 0.048* −0.087 (0.032) (0.032) (0.028) (0.293) Female * Received uniform in 2002 0.068 (0.052) Young * Received uniform in 2002 0.063 (0.053) Young 0.004 (0.033) Received uniform 2002 * Didn't have uniform at baseline 0.098 (0.067) Received uniform in 2002 * Proportion of school who had uniform 0.222 (0.397) Didn't have uniform at baseline −0.033** −0.032* −0.078** −0.034** (0.017) (0.017) (0.037) (0.017) Mean attendance among controls 0.812 Observations 1,152 1,152 1,152 1,152 R-squared 0.111 0.112 0.107 0.111 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2005. Note: All regressions include a full set of gender-school-standard fixed effects. Mean attendance among comparison students is 0.813 (s.e. 0.246). *indicates significant with 90 percent confidence, **95 percent, ***99 percent. A student is considered “young” if she is age 5–9; older children are age 10–14. The “female” dummy is excluded because it is collinear with the gender-school-standard fixed effects. Open in new tab Table 6. Effect of Free Uniforms on School Attendance by Gender and Age (using Randomization into the Program as an IV for Uniform Receipt) . Dependent variable attendance June '02 to Nov '05 . . (1) . (2) . (3) . (4) . Received uniform in 2002 0.041 0.047 0.048* −0.087 (0.032) (0.032) (0.028) (0.293) Female * Received uniform in 2002 0.068 (0.052) Young * Received uniform in 2002 0.063 (0.053) Young 0.004 (0.033) Received uniform 2002 * Didn't have uniform at baseline 0.098 (0.067) Received uniform in 2002 * Proportion of school who had uniform 0.222 (0.397) Didn't have uniform at baseline −0.033** −0.032* −0.078** −0.034** (0.017) (0.017) (0.037) (0.017) Mean attendance among controls 0.812 Observations 1,152 1,152 1,152 1,152 R-squared 0.111 0.112 0.107 0.111 . Dependent variable attendance June '02 to Nov '05 . . (1) . (2) . (3) . (4) . Received uniform in 2002 0.041 0.047 0.048* −0.087 (0.032) (0.032) (0.028) (0.293) Female * Received uniform in 2002 0.068 (0.052) Young * Received uniform in 2002 0.063 (0.053) Young 0.004 (0.033) Received uniform 2002 * Didn't have uniform at baseline 0.098 (0.067) Received uniform in 2002 * Proportion of school who had uniform 0.222 (0.397) Didn't have uniform at baseline −0.033** −0.032* −0.078** −0.034** (0.017) (0.017) (0.037) (0.017) Mean attendance among controls 0.812 Observations 1,152 1,152 1,152 1,152 R-squared 0.111 0.112 0.107 0.111 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2005. Note: All regressions include a full set of gender-school-standard fixed effects. Mean attendance among comparison students is 0.813 (s.e. 0.246). *indicates significant with 90 percent confidence, **95 percent, ***99 percent. A student is considered “young” if she is age 5–9; older children are age 10–14. The “female” dummy is excluded because it is collinear with the gender-school-standard fixed effects. Open in new tab It would be reasonable to expect receiving a uniform to be most important to children who do not already have one. The study includes an interaction for students who both receive a uniform but did not have a uniform at baseline (table 6 Regression 3) and finds that the attendance of students who receive a uniform and did not already have a uniform is estimated at 9.8 percentage points higher than those who already had a uniform (i.e., the total effect for those students is 14.6 percentage points, significant with 95 percent confidence), but that this difference is not statistically significant.13 While these higher point estimates for more vulnerable students are suggestive, the relatively small sample means that the study cannot rule out equality of impacts. The study examines the effect of receiving a uniform on test scores in the first three years of the program. The data were obtained by collecting test scores from all the study schools for these three years and matching those records to the sample. While a pattern of insignificant positive effects is observed, the match rate is low (between 30 percent and 50 percent, depending on the year). The study also tests for program impacts on student transfer – in case the program keeps participants from transferring to better schools, for example – and finds statistically insignificant impacts.14 The positive impact on attendance together with an insignificant impact on learning is consistent with other work in Kenya (Miguel and Kremer 2004) as well as work elsewhere in the world (Filmer and Schady 2014). Long-Run Effects The study collected follow-up data from the students in the sample in early 2010, eight years after the start of the program, to see whether the program had longer-term effects on the students’ education. The study proposes two mechanisms through which reducing absenteeism in early grades could have long-term consequences. The first mechanism is that reduced absenteeism in early grades can translate into reduced repetition (Lewin 2007). High rates of repetition mean that children are disproportionately old for their grade, which can lead to dropout (Manacorda 2012). Consequently, reducing repetition may reduce dropout rates. The second mechanism is that reduced absenteeism in early grades can translate into stronger foundational skills in those early grades, which mean that students are more capable of keeping up as they continue in school. Keeping up with the content is predictive of staying in school longer (Zuilkowski, Jukes, and Dubeck 2016). The study measures whether or not the students had completed primary school, their highest level of education, whether or not they were still in school, and their performance on the KCPE. Table 7 demonstrates that those students who were randomized into treatment are slightly more likely to have school officials identify the highest level of education attained by the student in 2010, whether the student is still in school in 2010, and whether the student participated in the Kenya Certificate of Primary Education exam. This biased attrition is itself an outcome, suggesting that the program led the children to be more known to school officials. This unbalanced attrition in long-term follow-up could affect the results; the study seeks to address this using Lee bounds.15 It does not find any difference in the likelihood of attriting by age, grade, or gender. Table 7. Correlates with Attrition in Follow-Up Data from 2010 . Missing completed primary school . Missing highest level of education . Missing still in school . Missing participated in KCPE exam . Missing standard deviations from mean KCPE score . Randomized into treatment −0.011 −0.049*** −0.031** −0.031** 0.013 (0.010) (0.018) (0.015) (0.015) (0.024) Mean missing rate among controls 0.037 0.125 0.083 0.083 0.698 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.122 0.132 0.108 0.108 0.287 . Missing completed primary school . Missing highest level of education . Missing still in school . Missing participated in KCPE exam . Missing standard deviations from mean KCPE score . Randomized into treatment −0.011 −0.049*** −0.031** −0.031** 0.013 (0.010) (0.018) (0.015) (0.015) (0.024) Mean missing rate among controls 0.037 0.125 0.083 0.083 0.698 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.122 0.132 0.108 0.108 0.287 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: All regressions include a full set of gender-school-standard fixed effects. *indicates significant with 90 percent confidence, **95 percent, ***99 percent. Open in new tab Table 7. Correlates with Attrition in Follow-Up Data from 2010 . Missing completed primary school . Missing highest level of education . Missing still in school . Missing participated in KCPE exam . Missing standard deviations from mean KCPE score . Randomized into treatment −0.011 −0.049*** −0.031** −0.031** 0.013 (0.010) (0.018) (0.015) (0.015) (0.024) Mean missing rate among controls 0.037 0.125 0.083 0.083 0.698 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.122 0.132 0.108 0.108 0.287 . Missing completed primary school . Missing highest level of education . Missing still in school . Missing participated in KCPE exam . Missing standard deviations from mean KCPE score . Randomized into treatment −0.011 −0.049*** −0.031** −0.031** 0.013 (0.010) (0.018) (0.015) (0.015) (0.024) Mean missing rate among controls 0.037 0.125 0.083 0.083 0.698 Observations 1,152 1,152 1,152 1,152 1,152 R-squared 0.122 0.132 0.108 0.108 0.287 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: All regressions include a full set of gender-school-standard fixed effects. *indicates significant with 90 percent confidence, **95 percent, ***99 percent. Open in new tab Table 8 displays three estimates on long-term outcomes: the intent-to-treat regression – measuring the simple impact of being randomized into the project, the IV estimate of actually receiving a uniform in 2002, and the simple OLS estimate of uniform receipt on long-term outcomes. It includes Lee bounds on the intent-to-treat estimates for those outcomes with biased attrition (Lee 2009; Tauchmann 2014). The bounding exercise assumes that attrition is monotonic: in other words, any subject who would not attrit if assigned to the control group, would also not attrit if assigned to the treatment group. The study believes that this is a reasonable assumption since students who received uniforms had better attendance rates, and so they may have been more memorable to the school officials interviewed. The results show that on aggregate there was no significant program impact on any of the long-term outcomes. The ITT (and IV) estimates (where the units are probabilities) are −0.036 (−0.066) for primary school completion, −0.069 (−0.126) for highest level of education, 0.005 (0.008) for still in school, and −0.014 (−0.025) for participation in the KCPE exam, and 0.024 (0.039) for KCPE score. While a 95 percent confidence interval includes zero, three of the five point estimates are negative, and the other two are small. For primary school completion, the upper bound is still relatively low: 0.026 for the IV estimate of primary school completion. In fact, the Lee bounds rule out sizeable positive impacts in the long run. While not strictly comparable, as the study does not measure cognitive gains in the short run, the fade-out observed is reminiscent of the fade-out of cognitive gains observed in some other studies (Schweinhart et al. 2005; Puma et al. 2010), including others that – like this one – take place after the earliest years of childhood have passed (Jacob, Lefgren, and Sims 2010; Andrabi et al. 2011).16 Table 8. Long-Term Impacts – 8 Years after Program Began . . Completed primary school . Highest level of education . Still in school . Participated in KCPE exam . Std deviations from mean KCPE score . . . (1) . (2) . (3) . (4) . (5) . Full Sample   ITT Randomized into the program −0.036 −0.069 0.005 −0.014 0.024 (0.026) (0.104) (0.028) (0.025) (0.129)   Lee bounds on ITT Lower −0.187 −0.010 −0.039 Upper 0.037 0.023 −0.017 Trimming proportion 0.049 0.030 0.030   IV Received uniform in 2002 −0.066 −0.126 0.008 −0.025 0.039 (0.047) (0.190) (0.050) (0.046) (0.205)   OLS Received uniform in 2002 −0.009 0.06 0.013 0.015 −0.04 (0.027) (0.106) (0.029) (0.026) (0.141) Mean among controls 0.362 7.486 0.656 0.301 0.009 Observations 1,116 1,033 1,072 1,072 328 . . Completed primary school . Highest level of education . Still in school . Participated in KCPE exam . Std deviations from mean KCPE score . . . (1) . (2) . (3) . (4) . (5) . Full Sample   ITT Randomized into the program −0.036 −0.069 0.005 −0.014 0.024 (0.026) (0.104) (0.028) (0.025) (0.129)   Lee bounds on ITT Lower −0.187 −0.010 −0.039 Upper 0.037 0.023 −0.017 Trimming proportion 0.049 0.030 0.030   IV Received uniform in 2002 −0.066 −0.126 0.008 −0.025 0.039 (0.047) (0.190) (0.050) (0.046) (0.205)   OLS Received uniform in 2002 −0.009 0.06 0.013 0.015 −0.04 (0.027) (0.106) (0.029) (0.026) (0.141) Mean among controls 0.362 7.486 0.656 0.301 0.009 Observations 1,116 1,033 1,072 1,072 328 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: All regressions include a full set of gender-school-standard fixed effects. Column (5) shows standard deviations from mean KCPE test scores by school, conditional on having taken the KCPE exam. Lee bounds are reported for outcomes for which the study observes biased attrition. *indicates significant with 90 percent confidence, **95 percent, ***99 percent Open in new tab Table 8. Long-Term Impacts – 8 Years after Program Began . . Completed primary school . Highest level of education . Still in school . Participated in KCPE exam . Std deviations from mean KCPE score . . . (1) . (2) . (3) . (4) . (5) . Full Sample   ITT Randomized into the program −0.036 −0.069 0.005 −0.014 0.024 (0.026) (0.104) (0.028) (0.025) (0.129)   Lee bounds on ITT Lower −0.187 −0.010 −0.039 Upper 0.037 0.023 −0.017 Trimming proportion 0.049 0.030 0.030   IV Received uniform in 2002 −0.066 −0.126 0.008 −0.025 0.039 (0.047) (0.190) (0.050) (0.046) (0.205)   OLS Received uniform in 2002 −0.009 0.06 0.013 0.015 −0.04 (0.027) (0.106) (0.029) (0.026) (0.141) Mean among controls 0.362 7.486 0.656 0.301 0.009 Observations 1,116 1,033 1,072 1,072 328 . . Completed primary school . Highest level of education . Still in school . Participated in KCPE exam . Std deviations from mean KCPE score . . . (1) . (2) . (3) . (4) . (5) . Full Sample   ITT Randomized into the program −0.036 −0.069 0.005 −0.014 0.024 (0.026) (0.104) (0.028) (0.025) (0.129)   Lee bounds on ITT Lower −0.187 −0.010 −0.039 Upper 0.037 0.023 −0.017 Trimming proportion 0.049 0.030 0.030   IV Received uniform in 2002 −0.066 −0.126 0.008 −0.025 0.039 (0.047) (0.190) (0.050) (0.046) (0.205)   OLS Received uniform in 2002 −0.009 0.06 0.013 0.015 −0.04 (0.027) (0.106) (0.029) (0.026) (0.141) Mean among controls 0.362 7.486 0.656 0.301 0.009 Observations 1,116 1,033 1,072 1,072 328 Source: Authors' analysis of data gathered in 12 schools in western Kenya between 2002 and 2010. Note: All regressions include a full set of gender-school-standard fixed effects. Column (5) shows standard deviations from mean KCPE test scores by school, conditional on having taken the KCPE exam. Lee bounds are reported for outcomes for which the study observes biased attrition. *indicates significant with 90 percent confidence, **95 percent, ***99 percent Open in new tab 5. Discussion This paper reports the impact of a program that reduces out-of-pocket costs of schooling through the distribution of free uniforms. As almost all schools globally have turned to a policy of officially free primary education, incidental expenses – including uniforms in Kenya and many other countries in Sub-Saharan Africa – become the primary out-of-pocket expense. Indeed, in Kenya, the cost of a uniform is the highest monetary outlay for primary school with the abolition of general school fees. The study finds that distributing uniforms results in a 37 percent reduction in student absenteeism (7 percentage points). For children who did not already own a uniform, distributing a uniform reduces absenteeism by 55 percent. Yet the study observes no long-term effects on the likelihood of completing primary school or on the number of years of education completed. These results reinforce the importance of collecting long-term follow-up data. This is particularly important given that the average impact evaluation of an instructional intervention gathers its follow-up data after 13 months of treatment and less than a month after treatment has concluded (McEwan 2015). In other words, very few evaluations explore the long-term impacts, but this is crucial to understanding the true return on educational interventions. While one might extrapolate from interventions that deliver long-term results – such as early childhood interventions like Perry Preschool (Heckman and Karapakula 2019), health interventions like deworming (Baird et al. 2016), or interventions that alleviate social or psychological constraints like some child sponsorship interventions (Wydick, Glewwe, and Rutledge 2013, 2016), there are simply too few interventions with long-term data to draw firm conclusions. This intervention, while including an element of child sponsorship, principally focuses on providing inputs once the children are already in primary school. Furthermore, it increases their attendance in an education system that is very weak (Uwezo 2016; Bold et al. 2017). Together, these potentially point to why long-term impacts did not come to fruition. Future systematic reviews should take care when interpreting short-term results, considering these results and others that demonstrate that long-term impacts may vary – sometimes dramatically – from initial effects. Gathering long-term data is costly, but without it, the trajectory of impacts resulting from the wide range of interventions currently being implemented remains a mystery. Most education interventions have the ultimate objective of improved long-term well-being – such as more learning, more completed schooling, or better labor market outcomes – and short-term educational improvements are merely a hopeful proxy. As more education studies gather long-term data, an essential understanding of the relationship between short-term and long-term gains may illuminate which investments truly change children's life trajectories. David K. Evans (corresponding author) is a Senior Fellow at the Center for Global Development, Washington, DC, USA, and a professor at the Pardee RAND Graduate School, Santa Monica, CA, USA. His email address is [email protected]. Mũthoni Ngatia is an Economist at the Africa Gender Innovation Lab and the WBG Gender Group at the World Bank, Washington, DC, USA. Her email address is [email protected]. The authors thank David Blackburn, Mariana Colacelli, Pascaline Dupas, Deon Filmer, Caroline Hoxby, Lawrence Katz, Edward Miguel, Owen Ozier, Seema Jayachandran, Bryce Ward, and participants at various seminars for comments. They also thank Amina Acosta, Pauline Ambani, Charles Kesa, Franklin Makokha, Hellen Masambu, Hellen Mukanda, Caroline Nekesa, Rachel Podolsky, Adina Rom, Evelyne Ruto, Maureen Wechuli, and Joseph Wasikhongo for research assistance, data gathering, programing, and insight into program administration. Special thanks to Michael Kremer for supporting this work at every stage. This article previously circulated as a working paper with the title ``School Costs, Short-Run Participation, and Long-Run Outcomes: Evidence from Kenya.'' A supplementary online appendix for this article can be found at The World Bank Economic Review website. Footnotes 1 This study's analysis of the data from McEwan's (2015) review of 77 randomized controlled trials of school-based interventions shows that only two gathered data more than a year after the completion of treatment. 2 Brunsma and Rockquemore (1998) examine cross-sectional tenth-grade students from the United States, controlling for observable characteristics, and find no impact on behavioral problems or attendance. In other work, Brunsma (2006) uses similar methods to look at school climate, academic achievement, and attendance using national U.S. data for kindergarten, first grade, and eighth grade, and finds no significant impacts. Other work finds positive relationships between uniforms and school climate in two South Carolina middle schools (Murray 1997) and on academic achievement (but without controlling for confounding factors) (Bodine 2003). Recent work in the United States finds some evidence for positive impacts on student attendance and teacher retention (Gentile and Imberman 2012). 3 The exchange rate is from January 2002, when uniforms were purchased, and is in 2002 dollars (CalcProfi 2019). 4 While the principal individual benefit studied in this paper is a school uniform, it is a child sponsorship program and thus speaks to that literature. Wydick, Glewwe, and Rutledge (2013) study the impact of child sponsorship and find large, statistically significant impacts on years of schooling; primary, secondary, and tertiary school completion; and the probability and quality of employment. The authors attribute these impacts – in part – to increases in children's aspirations. In a follow-up study, Wydick, Glewwe, and Rutledge (2016) estimating the impact of child sponsorship on adult income and wealth of formerly sponsored children find that child sponsorship increased monthly income by 13–17 percentage points over an untreated baseline of 75, principally from inducing higher future labor market participation. 5 While it is known that the intervention distributed uniforms in 2002, 2003, and 2004, and every effort was made to continue distribution to the same children, unfortunately data is lacking on how many children who received uniforms in 2002 went on to receive them in subsequent years. Crossover between the groups would bias the results downward. 6 The most common items sent were cards or letters (45 percent of children who received anything received only a letter, card, photograph, or drawing), and only a handful of children received anything larger than a pencil set or some exercise books (e.g., six children received a mattress, and seven children received a lantern). Letters, when received, commonly inquired about the child's school progress and other pleasantries. Again, only a small fraction of sponsored children received any communication from their sponsors in the first two years of the program. While one popular account of letter exchange in Zimbabwe indicates large impacts, these were accompanied by major financial support and – ultimately – an invitation to emigrate to the United States (Alifirenka, Ganda, and Welch 2015). 7 Children are referred to as “orphans” if they have either experienced one parent death or both parent deaths. 8 Children who were present for this survey were not statistically significantly more likely to have won the lottery. The point estimate on their having won the lottery is +4.6 percentage points, but with a standard error of 2.8. 9 The study does not cluster the standard errors as the treatment was assigned individually rather than based on clusters. This adheres to the guidance from Abadie et al. (2017): “The researcher should assess whether the sampling process is clustered or not, and whether the assignment mechanism is clustered. If the answer to both is no, one should not adjust the standard errors for clustering, irrespective of whether such an adjustment would change the standard errors.” 10 The study tests for balance across subgroups in the heterogeneous analysis by running a joint significance test of all variables in table 3, yielding an F-statistic of 0.39. 11 This fits with a small literature on how the framing of education benefits can affect their take-up. In Cambodia, when similar children received a scholarship labeled either as “poverty-based” or “merit-based,” those receiving the “merit-based” scholarship went on to exert more effort (Barrera-Osorio and Filmer 2016). 12 In table S1.1 in the supplementary online appendix, available with this article at The World Bank Economic Review website, the study re-runs the same set of regressions with no controls and again with school fixed effects as a robustness check. The results are very similar. 13 The study also examines the effect of the program on grade progression and finds no significant effect (see table S1.3). 14 The intent-to-treat estimate is −0.035 (s.e. 0.024), and the instrumental variables estimate is −0.063 (s.e. 0.045). 15 For a detailed explanation of the use of Lee bounds to deal with attrition, see Ksoll et al. (2014). 16 Table S1.4 displays long-run estimates for students who did not have a uniform at baseline – those with the largest point estimates in the short run – and similarly do not reveal any significant program impact. Furthermore, the point estimates are not systematically larger or smaller than those for the full sample. Larger standard errors for this smaller sample make it more difficult to rule out large positive or negative impacts. References Abadie A. , Athey S., Imbens G. 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