Behav Res (2018) 50:1166–1186 DOI 10.3758/s13428-017-0935-1 The reliability paradox: Why robust cognitive tasks do not produce reliable individual differences 1 1 1 Craig Hedge & Georgina Powell & Petroc Sumner Published online: 19 July 2017 The Author(s) 2017. This article is an open access publication Abstract Individual differences in cognitive paradigms are such reliability estimates into account has the potential to qual- increasingly employed to relate cognition to brain structure, itatively change theoretical conclusions. The implications of chemistry, and function. However, such efforts are often un- our findings are that well-established approaches in experimen- fruitful, even with the most well established tasks. Here we tal psychology and neuropsychology may not directly translate to the study of individual differences in brain structure, chem- offer an explanation for failures in the application of robust cognitive paradigms to the study of individual differences. istry, and function, and alternative metrics may be required. Experimental effects become well established – and thus those tasks become popular – when between-subject variability is . . Keywords Reliability Individual differences Reaction low. However, low between-subject variability causes low re- . . time Difference scores Response control liability for individual differences, destroying replicable corre- lations with other factors and potentially undermining pub- lished conclusions drawn from correlational relationships. Though these statistical issues have a long history in psychol- ogy, they are widely overlooked in cognitive psychology and Individual differences have been an annoyance rather neuroscience today. In three studies, we assessed test-retest than a challenge to the experimenter. His goal is to reliability of seven classic tasks: Eriksen Flanker, Stroop, control behavior, and variation within treatments is stop-signal, go/no-go, Posner cueing, Navon, and Spatial- proof that he has not succeeded… For reasons both Numerical Association of Response Code (SNARC). statistical and philosophical, error variance is to be Reliabilities ranged from 0 to .82, being surprisingly low for reduced by any possible device. (Cronbach, 1957,p. most tasks given their common use. As we predicted, this 674) emerged from low variance between individuals rather than high measurement variance. In other words, the very reason The discipline of psychology consists of two historically such tasks produce robust and easily replicable experimental distinct approaches to the understanding of human behavior: effects – low between-participant variability – makes their use the correlational approach and the experimental approach as correlational tools problematic. We demonstrate that taking (Cronbach, 1957). The division between experimental and correlational approaches was highlighted as a failing by some theorists (Cronbach, 1957;Hull, 1945), whilst others suggest Electronic supplementary material The online version of this article that it may be the inevitable consequence of fundamentally (doi:10.3758/s13428-017-0935-1) contains supplementary material, which is available to authorized users. different levels of explanation (Borsboom, Kievit, Cervone, & Hood, 2009). The correlational, or individual differences, * Craig Hedge approach examines factors that distinguish between individ- firstname.lastname@example.org uals within a population (i.e., between-subject variance). Alternatively, the experimental approach aims to precisely characterize a cognitive mechanism based on the typical or School of Psychology, Cardiff University, Park Place, Cardiff CF10 3AT, UK average response to a manipulation of environmental Behav Res (2018) 50:1166–1186 1167 variables (i.e., within-subject variance). Cronbach (1957) encounter difficulty when trying to translate state-of-the art called for an integration between the disciplines, with the view experimental methods to studying individual differences that a mature science of human behavior and brain function (e.g., Ross, Richler, & Gauthier, 2015). By elucidating these would consist of frameworks accounting for both inter- and issues in tasks used prominently in both experimental and intra-individual variation. Whilst a full integration is far from correlational contexts, we hope to aid researchers looking to being realized, it is becoming increasingly common to see examine behavior from both perspectives. examinations of the neural, genetic, and behavioral correlates of performance on tasks with their origins in experimental research (e.g., Chen et al., 2015; Crosbie et al., 2013; The reliability of experimental effects Forstmann et al., 2012; Marhe, Luijten, van de Wetering, Smits, & Franken, 2013; L. Sharma, Markon, & Clark, Different meanings of reliability For experiments, a Breli- 2014; Sumner, Edden, Bompas, Evans, & Singh, 2010). able^ effect is one that nearly always replicates, one that is Such integration is not without obstacles (e.g., Boy & shown by most participants in any study and produces Sumner, 2014). Here, we highlight a general methodological consistent effect sizes. For example, in the recent BMany consequence of the historical divide between experimental labs 3^ project (Ebersole et al., 2016), which examined and correlational research. Specifically we ask whether tasks whether effects could be reproduced when the same proce- with proven pedigree as Breliable^ workhorses in the tradition dure was run in multiple labs, the Stroop effect was repli of experimental research are inevitably unsuitable for correla- cated in 100% of attempts, compared to much lower rates tional research, where Breliable^ means something different. for most effects tested.In the context of correlational re- This issue is likely to be ubiquitous across all domains where search, reliability refers to the extent to which a measure robust experimental tasks have been drawn into correlational consistently ranks individuals. This meaning of reliability studies, under the implicit assumption that a robust experi- is a fundamental consideration for individual differences mental effect will serve well as an objective measure of indi- research because the reliability of two measures limits the vidual variation. This has occurred, for example, to examine correlation that can be observed between them (Nunnally, individual differences in cognitive function, brain structure, 1970; Spearman, 1904). Classical test theory assumes that and genetic risk factors in neuropsychological conditions individuals have some Btrue^ value on the dimension of (e.g.. Barch, Carter, & Comm, 2008), or where individual interest, and the measurements we observe reflect their true difference analyses are performed as supplementary analyses score plus measurement error (Novick, 1966). In practice, in within-subject studies (c.f. Yarkoni & Braver, 2010). Many we do not know an individual’s true score, thus, reliability of the issues we discuss reflect long-recognized tensions in depends on the ability to consistently rank individuals at psychological measurement (Cronbach & Furby, 1970; two or more time points. Reliability is typically assessed Lord, 1956), though they are rarely discussed in contemporary with statistics like the IntraClass Correlation (ICC), which literature. The consequences of this are that researchers often takes the form: Variance between individuals ICC ¼ Variance between individuals þ Error variance þ Variance between sessions holding error variance constant. In other words, for two mea- Here, variance between sessions corresponds to systemat- ic changes between sessions across the sample. Error variance sures with identical Bmeasurement error,^ there will be lower reliability for the measure with more homogeneity. Measures corresponds to non-systematic changes between individuals’ with poor reliability are ill-suited to correlational research, as scores between sessions, i.e. the score for some individuals increases, while it decreases for others. Clearly, reliability de- the ability to detect relationships with other constructs will be compromised by the inability to effectively distinguish be- creases with higher measurement error, whilst holding vari- ance between participants constant. Critically, reliability also tween individuals on that dimension (Spearman, 1910). In contrast to the requirements for individual differences, decreases for smaller between-participant variance, whilst homogeneity is the ideal for experimental research. Whereas variance between individuals is the numerator in the ICC for- The two-way ICC can be calculated for absolute agreement or for consisten- cy of agreement. The latter omits the between-session variance term. Note also mula above, it appears as the denominator in the t-test (i.e., the that the error variance term does not distinguish between measurement error standard error of the mean). For an experimental task to pro- and non-systematic changes in the individuals’ true scores (Heize, 1969). duce robust and replicable results, it is disadvantageous for Some may therefore prefer to think of the coefficient as an indicator of there to be large variation in the within-subject effect. stability. 1168 Behav Res (2018) 50:1166–1186 Interestingly, it is possible for us to be perfectly aware of this Method for statistical calculations, without realising (as we previously didn't) that the meanings of a Breliable^ task for experimental Participants and correlational research are not only different, but can be opposite in this critical sense. Participants in Study 1 were 50 (three male) undergraduate students aged 18–21 years (M = 19.5 years, SD=0.9). Participants in Study 2 were 62 (12 male) undergraduate stu- Present study dents aged 18–47 years (M = 20.5 years, SD=4.98). Participants in Study 3 were 42 (five male) undergraduate The issues we discuss have broad implications for cog- students aged 18–40 years (M = 20.4 years, SD=3.5). All nitive psychology and cognitive neuroscience. Recent re- participants gave informed written consent prior to participa- views have highlighted the potential for individual dif- tion in accordance with the revized Declaration of Helsinki ferences approaches to advance our understanding of the (2013), and the experiments were approved by the local Ethics relationship between brain structure and function (Kanai Committee. &Rees, 2011). The way in which we measure and con- ceptualize cognitive processes has largely been built on Design and procedure within-subject paradigms, though their strengths in ex- perimental contexts may make these paradigms sub- Participants completed the tasks (four in Studies 1 and 2, three optimal for individual differences. Here, in three studies, in Study 3) in each of two 90-min sessions taking place 3 we evaluate the re-test reliability of seven commonly weeks apart, at the same time of day. Seven participants in used and robust tasks, spanning the domains of cognitive Study 1 and five participants in Study 2 were unable to attend control, attention, processing style, and numerical-spatial their second session exactly 3 weeks later, and were associations. In doing so, we not only provide sorely rescheduled to between 20 and 28 days following their first needed information on these measures, but also evaluate session. Each participant completed the tasks in the same or- the relationship between robust experimental paradigms der in both of their sessions (in order not to introduce between- and reliable individual differences in real data using co- session variance associated with order), and the order of tasks hort sizes and trial numbers similar to, or greater than, was counterbalanced across participants using a Latin square. most imaging studies. In addition, we illustrate how tak- Though counterbalancing is common practice in experimental ing the reliability of these measures into account has the studies, it is often preferable to administer tasks in a fixed power to change the conclusions we draw from statistical order when correlating variables (though not all do, see e.g., tests. Aichert et al., 2012; Wöstmann et al., 2013). However, our First, we examined the reliability of the Eriksen flanker primary focus here was the re-test reliability of the tasks, and a task, Stroop task, go/no-go task, and the stop-signal task, fixed order could cause one task to appear more reliable than which we then replicated in Study 2. These tasks are all another due to presentation order rather than the task itself. considered to be measures of impulsivity, response inhibi- Following completion of the tasks, participants completed the tion or executive functioning (Friedman & Miyake, 2004; UPPS-P impulsive behavior scale (Lynam, Smith, Whiteside, & Stahletal., 2014). In Study 3, we examined the Posner Cyders, 2006; Whiteside & Lynam, 2001), which we commonly cueing task (Posner, 1980), the Navon task (Navon, administer in our lab. We include reliability information for the 1977), and a spatial-numerical association of response UPPS-P components as a reference for the levels of reliability codes (SNARC) effect paradigm (Dehaene, Bossini, & attainable in our sample with a measure constructed for the pur- Giraux, 1993). These tasks are used to measure the con- pose of measuring individual differences. structs of attentional orienting, perceptual processing style, Participants were tested in groups of up to nine, at separate and the automatic association between magnitude and stations in a multi-station lab, separated by dividers. The ex- space (i.e., the Bmental number line^), respectively. These perimenter was present throughout the session to monitor tasks were selected because they were all originally devel- compliance with instructions. Participants were instructed to oped in experimental contexts, and we believed they would be as fast and as accurate as possible in all tasks, and were be familiar to most readers. Further, all these tasks have given written and verbal instructions before each task. Each since been used in the context of individual differences, task in Studies 1 and 2 consisted of five blocks of approxi- and their underlying neural correlates. A Google Scholar mately 4 min each, and participants received feedback about search for the term Bindividual differences^ within articles their average reaction times (RTs) and error rates after each citing the original papers for each task produces at least block. The tasks in Study 3 consisted of four blocks. Figure 1 400 citations for each. For conciseness, we combine the displays the format of the tasks used. The stop-signal task was reporting of our methods and results across all studies. implemented using STOP-IT (Verbruggen, Logan, & Stevens, Behav Res (2018) 50:1166–1186 1169 Fig. 1 Schematic representation of tasks used and their conditions. duration of 1,250 ms (c.f. Verbruggen et al., 2008). In all other tasks, Studies 1 and 2 featured the flanker, Stroop, go/no-go and stop-signal stimuli were presented until a response was given. An Inter-Stimulus tasks. Study 3 featured the Posner cueing, SNARC and Navon tasks. Interval (ISI) of 750 ms was used in all tasks. Stimuli sizes are enlarged Trials were presented intermixed in a randomized order. In the Go/no- for illustration go and Stop-signal tasks, visual stimuli were presented for a fixed 2008), all other tasks were implemented in PsychoPy (Peirce, advice) taken from Friedman and Miyake (2004) matched for 2007, 2013). An Inter-Stimulus Interval (ISI) of 750 ms was length and frequency (neutral condition), or a color word cor- used for all tasks. responding to one of the other response options (incongruent). Stimuli were presented until a response was given. Participants completed 240 trials in each condition (720 in Eriksen flanker task Participants responded to the direction total). The primary indices of control are the RT cost (incon- of a centrally presented arrow (left or right) using the \ and / gruent RT – congruent RT) and error rate cost (congruent keys. On each trial, the central arrow (1 cm × 1 cm) was errors – incongruent errors). flanked above and below by two other symbols separated by 0.75 cm (see, e.g., Boy, Husain, & Sumner, 2010; White, Ratcliff, & Starns, 2011). Flanking stimuli were arrows Go/No-go task Participants were presented with a series of pointing in the same direction as the central arrow (congruent letters (Arial, font size 70) in the center of the screen. Each condition), straight lines (neutral condition), or arrows block consisted of four letters, presented with equal probabil- pointing in the opposite direction to the central arrow (congru- ity. Participants were instructed to respond with the space bar ent condition). Stimuli were presented until a response was to three of the four letters (go trials), and to refrain from given. Participants completed 240 trials in each condition (720 responding if the fourth letter appeared (no-go trials). The in total). The primary indices of control are the RT cost (in- response rule was presented to participants at the beginning congruent RT – congruent RT) and error rate cost (congruent of each block, and displayed at the bottom of the screen errors – incongruent errors). throughout the block to reduce memory demands. A new set of letters was used for each block, to lessen the impact of Stroop task Participants responded to the color of a centrally learned, automatic associations (c.f. Verbruggen & Logan, presented word (Arial, font size 70), which could be red (z 2008). Stimuli were presented for a fixed duration of 1,250 key), blue (x key), green (n key), or yellow (m key). (c.f. Ilan ms. Participants completed 600 trials in total (75% go). The & Polich, 1999; Macleod, 1991; D. Sharma & McKenna, primary measures are commission errors (responses to no-go 1998). The word could be the same as the font color (congru- stimuli), omission errors (non-responses to go stimuli), and ent condition), one of four non-color words (lot, ship, cross, RT to go stimuli. 1170 Behav Res (2018) 50:1166–1186 Stop-signal task Participants were instructed to respond to the their fixation on the central fixation point/cue. Participants identity of a centrally presented stimulus (square or circle: completed 640 trials (128 invalid) in total. The key measure 1.6 cm × 1.6 cm) using the \ and / keys. On 25% of trials (stop of interest is the difference in RTs to stimuli following valid trials), participants heard a tone through a set of headphones compared to invalid cues. that indicated that they should withhold their response on that trial. The tone was initially presented 250 ms after the visual Spatial-numerical association of response codes (SNARC) stimulus appeared, and was adjusted using a tracking proce- task Participants were required to determine whether a cen- dure by which the latency increased by 50 ms following a trally presented white digit (1–9, excluding 5; Arial, font size successfully withheld response, and decreased by 50 ms fol- 70) was greater or less than five. Before each block, partici- lowing a failure to withhold a response. The latency of the pants were instructed that they were to respond either such that tone is referred to as the Stop-Signal Delay (SSD). Stimuli Z correspondedtodigitslessthanfiveand M digitsgreater were presented for a fixed duration of 1,250ms. Participants than five, or vice versa. This rule alternated across blocks, completed 600 trials in total (75% go). The primary measures with the first block being counter-balanced across participants, are Stop-Signal Reaction Time (SSRT), and go RT. There are and participants receiving consistent order in both of their two common methods of calculating SSRT: the mean method sessions. As in previous studies (e.g., Rusconi, Dervinis, (SSRTm) and the integration method (SSRTi; Logan, 1981; Verbruggen, & Chambers, 2013), eight Bbuffer^ trials were Logan & Cowan, 1984). The mean method consists of presented at the start of each block to accommodate the subtracting the participant’s mean SSD from their mean go change in response rules. These buffer trials were subsequent- RT. In the integration method, instead of the mean go RT, ly discarded for analysis. Participants were also presented with the mean SSD is subtracted from the nth fastest RT, where n feedback if they gave an incorrect response, lasting 1,000 ms. corresponds to the percentage of stop trials on which partici- Participants completed 640 trials in total (320 with each map- pants failed to inhibit their responses. For example, if a par- ping), not including buffer trials. The SNARC effect is the key ticipant responded on 60% of stop trials, the 60th percentile of variable of interest, which is calculated as the difference be- their RT distribution is subtracted from the mean SSD. tween RTs and error rates on trials in which the required re- Accurate estimation of SSRT using the mean method relies sponse aligns with the relative magnitude of the stimulus com- upon the tracking procedure converging on successful stop- pared to when they are misaligned. Participants are expected ping on 50% of stop trials. It has been argued that the integra- to respond more quickly to smaller numbers with the left hand tion method should be favoured when this assumption is not and larger numbers with the right. met, for example, if participants strategically adjust their re- sponses by slowing down over the course of the session (Verbruggen, Chambers, & Logan, 2013). We report the reli- Navon task Participants were presented with composite letter abilities of both methods here, but restrict subsequent analyses stimuli; large BH^ or BS^ characters (3 cm × 4.5 cm) com- to only the recommended integration method. prised of smaller BS^ or BH^ (0.4 cm × 0.7 cm) characters. Stimuli could either be consistent, in which the same character Posner cueing task At the start of each trial, participants appeared at the global and local levels, or inconsistent (e.g., a viewed two boxes (6 cm × 6 cm), located 7.5 cm from a large H composed of smaller S characters). Stimuli were pre- central fixation point to the inside edge. An arrow cue (2 cm sented at one of four possible locations and remained on × 1.5 cm) appeared in the center of the screen directing par- screen until a response was given. The stimuli were presented ticipants’ attention to either the left or the right box. After a 0.5 cm above or below and 2 cm to the left or right of fixation. stimulus onset asynchrony (SOA) of 300, 400, 500, or 600 Before each block, participants were instructed that they were ms, an X (2 cm × 2 cm) then appeared in the left or right box. to respond to either the global or local character. The response Participants were instructed to respond as quickly as possible rule alternated across blocks, and was counter-balanced, as with the space bar to the critical stimulus, but to not respond with the SNARC task. Further, as with the SNARC task, par- before it appeared. The cue correctly predicted the location of ticipants were presented with eight buffer trials, and feedback the stimulus on 80% of trials, and participants were instructed to incorrect response. Participants completed 640 trials in total of this probability beforehand. The SOAs were chosen to (320 per mapping, of which 160 each were consistent and make the onset of the stimulus unpredictable, and previous inconsistent). We derived five effects of interest from this task. research has shown that the cueing benefit peaks at approxi- We calculated the difference between congruent RTs for re- mately 300 ms and is consistent throughout this range of sponses to global versus local stimuli as an indication of par- SOAs (Cheal & Lyon, 1991; Muller & Rabbitt, 1989). If par- ticipants’ bias towards global or local processing (with healthy ticipants responded before the stimulus appeared, they were participants typically showing a global bias). Further, interfer- given feedback lasting 2,500 ms instructing them not to re- ence effects in both errors and RTs (Incongruent - congruent) spond prematurely. Participants were instructed to maintain can be derived for global and local stimuli separately. Behav Res (2018) 50:1166–1186 1171 UPPS-P impulsive behavior scale The UPPS-P is a 59-item Summary level data, as well as the raw data for our behav- questionnaire that measures five components of impulsivity: ioral tasks, are available on the Open Science Framework negative urgency, premeditation, perseverance, sensation seek- (https://osf.io/cwzds/) ing, and positive urgency (Lynam et al., 2006; Whiteside & Lynam, 2001). Results Data analysis Task performance Data were not included if participants did not return for Studies 1 and 2 A full report of the descriptive statistics the follow-up session (3,2,2 for the three studies respec- for each measure can be seen in Supplementary Material B. tively). Participants' data were not analysed for a given All expected experimental effects were observed, and means task if they show very low compliance, defined as: accu- and standard deviations for RTs and error rates for all tasks racy below 60% in either session for overall performance were comparable to samples from the general population in the flanker, Stroop, Navon, and SNARC tasks, re- reported in the literature (see Supplementary Material C). sponses to go stimuli in the go/no-go task, discrimination Thus, despite a possible expectation that students would performance on go trials in the stop-signal task. For the show restricted variance, our sample was not consistently Posner task, participants were also required to have antic- more or less variable than samples taken from the general ipatory response rates (i.e., responding before the stimulus population. Scatter plots for the key measures are shown in appears) of less than 10%. For the stop signal task, par- Fig. 2. ticipants’ data were not included if their data produced a negative SSRT, or if they responded on more than 90% of Study 3 Again, performance was comparable to previous re- stop-signal trials in either session, as an SSRT could not ports in the literature (Navon, 1977;Posner, 1980;Rusconi be meaningfully calculated. A participant’s data was re- et al., 2013). As in Navon’s original study, the conflict effect in movedentirelyiftheyfellbelow thesecriteriafor twoor the RTs did not reach significance when participants were more tasks within a single session, otherwise data were instructed to respond to the global characters and ignore the only excluded for the individual task. After these exclu- local characters – presumably reflecting the preferential pro- sions, 47 and 57 participants remained for the flanker and cessing of global features. Scatter plots for the key measures go/no-go tasks in Study 1 and 2, respectively, 47 and 56 are shown in Fig. 3. in the Stroop task, and 45 and 54 in the stop-signal task. All participants met the inclusion criteria in Study 3. The calculation of mean RTs excluded RTs below 100 ms and Task reliabilities greater than three times the each individual’smedianab- solute deviation (Hampel, 1974; Leys, Ley, Klein, Studies 1 and 2 None of the behavioral measures in Bernard, & Licata, 2013). Studies 1 and 2 (see Table 1) exceeded reliabilities of .8, Reliabilities were calculated using Intraclass Correlation typically considered excellent or of a clinically required Coefficients (ICC) using a two-way random effects model standard (Cicchetti & Sparrow, 1981; Fleiss, 1981; Landis for absolute agreement. In the commonly cited Shrout and & Koch, 1977). Two indices of response control exceeded Fleiss (1979; see also McGraw & Wong, 1996)nomenclature, a standard of good/substantial reliability (.6) in both ses- this corresponds to ICC (2,1). This form of the ICC is sensitive sions: the Stroop RT cost (ICCs of .6 and .66 in Studies 1 to differences between session means. In Supplementary and 2 respectively) and commission errors on the go/no- Material A, we perform further analyses to account for poten- go task (ICC = .76 in both studies). The reliability of the tial outliers and distributional assumptions. The choice of sta- RT cost scores, calculated by taking the difference be- tistic does not affect our conclusions. We report reliabilities tween congruent and incongruent conditions for example, separately for Studies 1 and 2 in the main text so that consis- are generally lower than their components, and we exam- tency across samples can be observed. We combine the studies ine reasons for this below. For example, the flanker RT in supplementary analyses. cost in Study 1 has a reliably of .4, whereas the RTs for As both measurement error and between-participant vari- congruent and incongruent trials have reliabilities of .74 ability are important for the interpretation of reliability, we and .66 respectively. This is despite the flanker RT cost also report the standard error of measurement (SEM) for each having a relatively low SEM of 15 ms. Thus, measure- variable. The SEM is the square root of the error variance term ment error alone does not predict reliability. The scatter in the ICC calculation and reflects the 68% confidence interval plots in Fig. 2 show the SEMs for the critical measures to around an individual’s observed score. show the size of the error relative to the variance in the 1172 Behav Res (2018) 50:1166–1186 Fig. 2 Reliability of key measures from Studies 1 and 2 combined (Total N=99–104). Red marker indicates mean group performance from sessions 1 and 2. Error bars show ± 1 standard error of measurement (SEM). The SEM is the square root of the error variance term calculated from the intraclass correlation, and can be interpreted as the 68% confidence interval for an individual’sdata point. A large SEM relative to the between-subject variance contrib- utes to poor reliability data.The results for the stop signal task warrant expan- more conservative exclusion criterion did not improve up- sion. Large SEMs were observed for Go RT and mean on the reliability estimates for SSRTs (see Supplementary SSD in Study 1. We suspect that this is due to proactive Material A). slowing in a subset of participants in one session, who did not strategically adjust their responses in the same way in the other session. However, despite a reduced SEM and Study 3 (see Table 2) Only one behavioral measure had a higher reliability for go RTs in Study 2, the reliability of reliability in the nominally excellent range (.82): the con- SSRT did not increase. Though the integration method of flict effect when responding to local characters in the calculating SSRT was shown by Verbruggen et al. (2013) Navon task. An influential data point (an error cost of to be robust against gradual slowing within a session, it 43% in both sessions) contributed to this, though the will remain sensitive to more substantial strategic changes measure still shows good reliability (.74) if this individ- between sessions (c.f., Leotti & Wager, 2010). Adopting a ual is excluded. Behav Res (2018) 50:1166–1186 1173 Fig. 3 Reliability of key measures from Study 3 (N=40). Red marker indicates mean group performance from sessions 1 and 2. Error bars show ± 1 standard error of measurement. RT reaction time, SNARC Spatial-Numerical Association of Response Code 1174 Behav Res (2018) 50:1166–1186 Table 1 Intraclass correlations (ICCs) and standard errors of measurement (SEMs) for Studies 1 and 2. SEMs are in the measure’s original units (ms or % correct). Primary indices of response control are highlighted in bold; 95% confidence intervals in parentheses. Typical interpretations of ICC values are: excellent (.8), good/substantial (.6), and moderate (.4) levels of reliability (Cicchetti & Sparrow, 1981;Fleiss, 1981; Landis & Koch, 1977) Task Measure ICCs SEMs Study 1 Study 2 Study 1 Study 2 Flanker task Congruent RT .74 (.52–.86) .69 (.40 –.83) 24 (20–30) 20 (17–24) Neutral RT .73 (.48–.86) .61 (.32–.78) 23 (19–29) 21 (18–26) Incongruent RT .66 (.36–.81) .62 (.31–.79) 32 (27–40) 28 (24–35) RT cost .40 (.12–.61).57 (.36–.72) 15 (13–19) 15 (13–18) Congruent errors .46 (.20–.66) .37 (.13–.58) 4.78 (3.97–6.0) 5.24 (4.43–6.43) Neutral errors .45 (.19–.65) .39 (.14–.59) 4.95 (4.11–6.22) 5.16 (4.36–6.33) Incongruent errors .71 (.54–.83) .58 (.34–.74) 4.67 (3.88–5.86) 5.76 (4.86–7.07) Error cost .58 (.35–.74).72 (.57–.83) 3.77 (3.14–4.74) 3.12 (2.64–3.83) Stroop task Congruent RT .77 (.49–.88) .72 (.49–.84) 33 (27 –41) 31 (26–38) Neutral RT .74 (.36–.88) .73 (.45–.86) 34 (28–43) 34 (28–41) Incongruent RT .67 (.25–.85) .70 (.10–.88) 42 (35–52) 33 (28–40) RT cost .60 (.31–.78).66 (.26–.83) 21 (17–26) 24 (20–29) Congruent errors .36 (.10–.58) .42 (.16–.62) 3.35 (2.78–4.20) 3.02 (2.55–3.71) Neutral errors .45 (.19–.65) .51 (.25–.69) 3.52 (2.92–4.42) 3.17 (2.67–3.89) Incongruent errors .62 (.40–.77) .39 (.15–.59) 3.78 (3.14–4.75) 3.89 (3.28–4.78) Error cost .48 (.23–.67).44 (.20–.63) 3.13 (2.60 –3.94) 2.45 (2.07–3.02) Go/No-go task Go RT .74 (.58–.85) .63 (.44–.77) 31 (25–38) 37 (31–46) Commission errors .76 (.58–.87).76 (.60–.86) 5.36 (4.45–6.73) 6.46 (5.46–7.93) Omission errors .69 (.51–.82) .42 (.19–.61) 1.52 (1.27–1.91) 3.73 (3.15–4.57) Stop-signal task Go RT .35 (.08–.57) .57 (.28–.75) 107 (88–135) 57 (48–70) Mean SSD .34 (.07–.57) .54 (.32–.70 ) 127 (105–161) 71 (60–88) SSRT mean .47 (.21–.67).43 (.19–.62) 32 (27–41) 28 (24–35) SSRT integration .36 (.08–.59).49 (.26–.66) 39 (32–49) 35 (29–43) UPPS-P Negative U. .72 (.54–.83) .73 (.58–.83) .30 (.25–.38) .29 (.25–.36) Premeditation .70 (.51–.82) .85 (.75–.91) .26 (.21–.32) .18 (.15–.22) Perseverance .73 (.57–.84) .78 (.65–.86) .29 (.24–.36) .21 (.18–.26) Sensation Seek. .87 (.78–.93) .89 (.82–.94) .24 (.20–.30) .21 (.18–.26) Positive U. .80 (.66–.88) .81 (.70–.88) .25 (.21–.32) .29 (.24–.36) RT reaction time, SSD Stop-Signal Delay, SSRT Stop-Signal Reaction Time, UPPS-P impulsive behavior scale The reliability of the Posner cueing effect was good (.7), What happens to variance in within-subject effects? though also influenced by an outlying data point (ICC = .56 if excluded). The reliabilities for all other behavioral effects of The relationship between reliability and the sources of vari- interest were poor (ICCs <.25). ance in the RT measures is shown in Fig. 4, which plots the three components of variance from which the ICC is calculat- ed. Each bar decomposes the relative variance accounted for How many trials should be administered? We found that by differences between participants (white), differences be- the literature on these seven tasks also lacks information to tween sessions (e.g., practice effects, gray), and error variance guide researchers on how many trials to run, and different (black). Correlational research (and the ICC) relies on the studies can choose very different numbers without any explicit proportion of variance accounted for by individual differ- discussion or justification. For those interested in the use of ences, and the standard subtractions (e.g., to calculate the these tasks for individual differences, we provide information Stroop RT cost) do not improve this signal-to-noise ratio – if on the relationship between reliability and trial numbers in anything, it is reduced, explaining why difference scores are Supplementary Material D. generally lower in reliability than their components. The Behav Res (2018) 50:1166–1186 1175 Table 2 Intraclass correlations (ICCs) and standard errors of measure- are: excellent (.8), good/substantial (.6), and moderate (.4) levels of reli- ment (SEMs) for Study 3. SEMs are in the measure’s original units (ms or ability (Cicchetti & Sparrow, 1981; Fleiss, 1981; Landis & Koch, 1977). % correct). Primary variables of interest are highlighted in bold; 95% The Global precedence effect was calculated as local congruent RT – confidence intervals in parentheses. Typical interpretations of ICC values global congruent RT Measure ICC SEM Posner task Valid RT .80 (.61–.90) 16 (13–20) Invalid RT .79 (.56–.89) 21 (18–28) Cueing effect .70 (.50–.83) 13 (10–16) SNARC task Congruent RT .69 (.49–.82) 29 (24–37) Incongruent RT .74 (.56–.86) 26 (21–33) SNARC effect RT .22 (0–.49) 16 (13–21) Congruent errors .67(.45–.81) 2.04 (1.67–2.62) Incongruent errors .58 (.33–.75) 2.66 (2.18–3.42) SNARC effect errors .03 (0–.34) 2.30 (1.88–2.95) Navon task Local congruent RT .69 (.49–.83) 29 (24–38) Local incongruent RT .68 (.45–.83) 30 (24–38) Local RT cost .14 (0–.43) 19 (15–24) Local congruent errors .56 (.30–.74) 1.23 (1.01–1.58) Local incongruent errors .80 (.65–.89) 4.25 (3.48–5.46) Local error cost .82 (.69–.90) 3.68 (3.01–4.72) Global congruent RT .63 (.40–.78) 34 (28–43) Global incongruent RT .70 (.50–.83) 30 (25–39) Global RT cost 0 (0–.18) 14 (11–17) Global congruent errors .60 (.36–.76) 2.22 (1.82–2.86) Global incongruent errors .71 (.51–.84) 1.96 (1.61–2.52) Global error cost .17 (0–.46) 2.67 (2.19–3.43) Global precedence effect (RT) 0 (0–.29) 24 (20–31) UPPS-P Negative U. .78 (.63–.88) 0.22 (0.18–0.29) Premeditation .88 (.78–.93) 0.14 (0.12–0.18) Perseverance .90 (.81–.94) 0.18 (0.14–0.23) Sensation Seek. .91 (.83–.95) 0.16 (0.13–0.20) Positive U. .85 (.67–.93) 0.20 (0.17–0.26) RT reaction time, UPPS-P impulsive behavior scale, SNARC Spatial-Numerical Association of Response Code equivalent plot for errors can be seen in Supplementary four response control tasks administered in Studies 1 Material E. We also plot the absolute variance components and 2 before and after accounting for the reliability of in Supplementary Material E. In absolute terms, the total the measures. Response control provides a useful illustra- amount of variance is reduced in the difference scores often tive example of this issue, as it is often assumed that a by a factor of 3 or 4 relative to their components. This is common response control trait underlies performance on desirable in an experimental task, in which any variation in these tasks (for a review, see Bari & Robbins, 2013), the effect of interest is detrimental. though this assumption has received mixed support from correlational research (Aichert et al., 2012; Cyders & Coskunpinar, 2011; Fan, Flombaum, McCandliss, How does accounting for reliability affect Thomas, & Posner, 2003; Friedman & Miyake, 2004; between-task correlations? Hamilton et al., 2015; Ivanov, Newcorn, Morton, & Tricamo, 2011; Khng & Lee, 2014; Scheres et al., 2004; As noted in the introduction, the reliability of two mea- L. Sharma et al., 2014; Stahl et al., 2014; Wager et al., sures will attenuate the magnitude of the correlation that 2005). can be observed between them. As an illustration of this Spearman’s Rho correlations can be seen in Table 3.We phenomenon, we examine the correlations between the combined the data from Studies 1 and 2 to maximize statistical 1176 Behav Res (2018) 50:1166–1186 Fig. 4 Relative size of variance components for reaction time (RT) mea- gray), and error variance (black). The intraclass correlation (ICC) reflects sures in Studies 1 and 2 (A: Total N=99–104) and Study 3 (B: N=40). The the proportion of the total variance attributed to variance between indi- size of the bar is normalized for the total amount of variance in the viduals, and is printed above each bar. SSD Stop-Signal Delay,SSRT Stop- measure (see Supplementary Material E), and subdivided into variance Signal Reaction Time, SNARC Spatial-Numerical Association of accounted for by differences between participants (white), variance Response Code accounted for by differences between sessions (e.g., practice effects, Table 3 Spearman’s rho correlations between measures of response control. Data are combined across Study 1 and 2 (total N = 99–104), and averaged across sessions 1 and 2. Correlations significant at p<.05 are highlighted Flanker RT cost Flanker Error cost Stroop RT cost Stroop Error cost Go/no-go Com. Flanker RT cost Flanker Error cost .29** Stroop RT cost .14 -.14 Stroop Error cost -.10 -.01 .28** Go/no-go Com. -.14 .18 -.14 .05 SSRT Int. -.14 .14 -.06 -.01 .52*** ***p<.001 **p<.01 *p<.05 RT reaction time, Go/no-go Com. commission errors in the go/no-go task, SSRT Int. stop signal reaction time calculated using the integration method Behav Res (2018) 50:1166–1186 1177 Table 4 Disattenuated Spearman’s rho correlations between measures of response control. Correlations that would be significant at p<.05 (N=100) are highlighted Flanker RT cost Flanker Error cost Stroop RT cost Stroop Error cost Go/no-go Com. Flanker RT cost Flanker Error cost .50* Stroop RT cost .25* -.21* Stroop Error cost -.20* -.02 .51* Go/no-go Com. -.22* .25* -.21* .09 SSRT Int. -.31* .26* -.11 -.03 .90* RT reaction time, Go/no-go Com. commission errors in the go/no-go task, SSRT Int. stop signal reaction time calculated using the integration method power. In order to examine the impact of reliability, in Table 4, relationships are consistent with a single underlying response we also estimated the dissatenuated correlation coefficients control construct. For example, whereas SSRT shows a posi- using Spearman’s(1904)formula: tive correlation with flanker error costs, it shows a negative correlation with flanker RT costs. These may suggest other SamplecorrelationðÞ x; y factors moderating the relationships between these measures, pﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃ }True}correlationðÞ x; y ¼ ReliabilityðÞ x :ReliabilityðÞ y such as speed-accuracy trade-offs that carry some consistency across tasks. Spearman noted that the correlation that is observed be- For reference, we include the raw and disattenuated corre- tween two measures will be attenuated (weakened) by mea- lations for the measures used in Study 3 in the Supplementary surement error. Assuming that the reliability coefficient re- Material F. flects the noise in each measure individually, he proposed the disattenuation formula as a means to Bcorrect^ the corre- lation obtained from a sample. As the formula depends on sample estimates of the correlation and reliabilities, it is itself Discussion an estimate, and not intended here for inference (for discussions of interpretative issues, see Muchinsky, 1996; Across many research, educational, or clinical contexts, when Winne & Belfry, 1982). We present them to illustrate the im- finding a group level effect, it is often theoretically meaningful pact of reliability on theoretical conclusions, especially when to ask what factors of the individual predict effectiveness. It is using the traditional approach of statistical thresholds, though not intuitive, and rarely discussed, that such questions may be the attenuation of effect sizes is not unique to the null hypoth- at odds with each other because one requires low and one esis significance testing framework. For ease of comparison, requires high variability between individuals (Rogosa, correlations significant at p<.05 are highlighted. 1988), even though the statistical issues have been long Focusing first on the observed correlations in Table 3 there known. The challenges highlighted by our data are also cause is little support for a relationship between these measures. to reflect upon the way in which researchers evaluate para- Consistent with some observations (Reynolds, Ortengren, digms for this purpose; it should not be assumed that robust Richards, & de Wit, 2006), though inconsistent with others experimental paradigms will translate well to correlational (Aichert et al., 2012), we observed a strong correlation be- studies. In fact, they are likely to be sub-optimal for correla- tween SSRT and commission errors on the go/no-go task. tional studies for the same reasons that they produce robust Otherwise, if we were making a dichotomous decision as to experimental effects. Our findings, as well as observations whether different response control tasks were related, we from elsewhere in the literature, indicate that this challenge would fail to reject the null hypothesis by traditional currently exists across most domains of cognitive neurosci- standards. ence and psychology (De Schryver, Hughes, Rosseel, & De The disattenuated correlations in Table 4 paint a somewhat Houwer, 2016;Hahn et al., 2011; Lebel & Paunonen, 2011; different picture. Note that the dissatenuated correlation will Ross et al., 2015). We discuss the practical and theoretical always be higher than the observed correlations when the implications of this below, including the way in which sub- reliabilities are less than one. The increase in the correlations optimal reliabilities should be interpreted; the extent to in Table 4 is therefore unsurprising. If we apply the same which these problems generalize to other populations; statistical thresholds however, the dissatenuated correlations and the challenge this poses to resource intensive research lead us to different qualitative conclusions about the relation- such as neuroimaging, where it is not easy just to increase ships between measures. Note that not all of these participant numbers. 1178 Behav Res (2018) 50:1166–1186 Translating experimental effects to correlational experimentally manipulate behavior on measures con- studies structed to reliably measure individual differences. For example, self-report measures such as the UPPS-P are The reliability of a measure is an empirical question and a developed with the explicit purpose of assessing stable prerequisite for effective correlational research. Clearly traits (Whiteside & Lynam, 2001), such that they should reliability cannot be assumed on the basis of robustness be purposefully robust to natural or induced situational in within-subject contexts. Success in within-subject con- variation. Nevertheless, some studies have looked at the texts does not necessarily exclude a task from consider- UPPS-P dimensions as outcome variables, for example, in ation in individual differences contexts, or vice versa. a longitudinal study on alcohol use (Kaizer, Bonsu, Hypothetically, an effect could produce reliable between- Charnigo, Milich, & Lynam, 2016). As noted previously, subject variation, but also a mean difference large enough whether a measure is effective for a given aim is an em- so that it can be consistently reproduced across different pirical question, though we believe these broader consid- samples. However, the reliabilities of many the measures erations can provide useful guidance. reported here, spanning the domains of attention, cogni- tive control, and processing style, are much lower than most researchers would expect, and fall short of outlined Difficulties with difference scores standards (Barch et al., 2008; Cicchetti & Sparrow, 1981; Fleiss, 1981;Landis& Koch, 1977). There are direct im- Statistical concerns regarding the reliability of difference plications of this for initiatives recommending and scores in correlational research have been noted previous- employing some of the measures we evaluated (e.g., the ly (Caruso, 2004; Cronbach & Furby, 1970;Lord, 1956). Stroop and stop-signal tasks; Barch, Braver, Carter, Generally speaking, the difference between two measures Poldrack, & Robbins, 2009; Hamilton et al., 2015), and is less reliable than the individual measures themselves for the way in which experimental tasks are evaluated for when the measures are highly correlated and have similar this purpose in the future. variance (Edwards, 2001; Rogosa, 1988, 1995;Willet, It is important to emphasize that these results do not 1988; Zimmerman & Williams, 1998; Zumbo, 1999). In indicate that these paradigms are not replicable, valid, or part, this reflects the propagation of error from two com- robust measures of their respective constructs. For exam- ponent measures to the composite score, but the main ple, the global precedence effect from the Navon task was reason is that any subtraction that successfully reduces highly robust, and generally of a similar magnitude in between-participant variance (and thus reduces Berror,^ each session of each study. It also does not preclude the as defined in experimental research) is likely to increase use of these tasks for examining between-group differ- the proportion of measurement error relative to between- ences in experimental designs. The difference between participant variance (see Fig. 4). In within-subject de- group means may be sufficiently large so as to be detect- signs, we often subtract a baseline of behavioral perfor- able, for example, if one or both groups are located at mance or neural activity precisely because we expect extreme points on the continuum. Rather, our results sug- strong correlations between participants’ performance in gest that these measures do not consistently distinguish multiple conditions, and thus by definition the subtraction between individuals within a population. Such difficulties will reduce between participant variance relative to error with inter-task correlations and reliability have been variance. There are notable exceptions in our data with discussed previously in studies of executive functioning, the Flanker and Navon task error scores. Errors in con- in the context of the Btask impurity^ problem (Friedman gruent trials in these tasks are uncommon, and there is & Miyake, 2004; Miyake et al., 2000). Individual differ- little variation in the baseline. As such, the difference ences in a given task will likely capture only a subset of score primarily reflects incongruent errors. The same is Bexecutive functions,^ in addition to domain specific not true of RTs, where individuals strongly co-vary in mechanisms. Moreover, as Cronbach (1957) highlighted, their responses to congruent and incongruent trials. the goal of the experimentalist is to minimize individual However, it does not follow that tasks without differ- differences, and many of the tasks we examine come orig- ence scores are preferable. In principle, subtracting a inally from this tradition. As a result, these tasks may tap baseline measure in order to control for unwanted in to aspects of executive functioning that are relatively between-participant variance is not at odds with the goal consistent across individuals compared to those that dif- of examining individual differences in performance on ferentiate between them. that task. After all, one wants to measure individual dif- In noting that measures are constructed to achieve dif- ferences in a specific factor, not just obtain any between- ferent aims in experimental and correlational research, we participant variance. For example, simple and choice RTs can also consider whether it is problematic to attempt to correlate with measures of general intelligence (Deary, Behav Res (2018) 50:1166–1186 1179 Der, & Ford, 2001;Jensen, 1998). Omitting the baseline some truth to these positions, it does not preclude consid- subtraction from a task could produce between-task cor- eration of the implications of poor reliability. relations for this reason, but would not aid our under- An immediate consequence of a failure to consider standing of the specific underlying mechanism(s). reliability in correlational studies is that effect sizes will generally be underestimated. If a researcher conducts an a priori power analysis without factoring in reliability, The impact of reliability on statistical power – they bias themselves towards finding a null effect. A less is Bgood^ good enough? intuitive consequence is that the published literature can overestimate effects (Loken & Gelman, 2017). Though The past decade has seen increasing attention paid to the on average correlation estimates are attenuated by mea- failure of the biomedical sciences to always appropriately surement error, noise can also produce spuriously high consider statistical power (Button et al., 2013b; Ioannidis, correlations on occasion. When spuriously high estimates 2005). Reliability is a crucial consideration for power in are selected for by a bias to publish significant findings correlational research, and the importance of reliable mea- the average published correlation becomes an overesti- surement has been emphasized in many landmark psycho- mate. In combination, these factors are challenges to metric texts (e.g., Guilford, 1954; Gulliksen, 1950; both reproducibility and theoretical advancement. Nunnally, 1970). Despite this, there are no definitive Consideration of reliability is not completely absent guidelines for interpreting reliability values (Crocker & from the cognitive and imaging literature (e.g., Algina, 1986). While .6 is nominally considered good Salthouse, McGuthry, & Hambrick, 1999; Shah, Cramer, by commonly cited criteria (Cicchetti & Sparrow, 1981; Ferguson, Birn, & Anderson, 2016; Yarkoni & Braver, Fleiss, 1981; Landis & Koch, 1977), more conservative 2010). However, our informal discussions with colleagues criteria have been given as a requirement for the use of and peers suggest that it is not routine to factor reliability cognitive tasks in treatment development, citing a mini- estimates into power analyses, and it is exceedingly rare mum of .7 and optimal value of .9 (Barch et al., 2008). to see this reported explicitly in published power calcula- Nevertheless, it has been argued that the issue of reliabil- tions. It is also potentially problematic that researchers ity has been somewhat trivialised in contemporary person- tend to underestimate the sample sizes necessary to detect ality research, with one review noting that B…researchers small effects (Bakker, Hartgerink, Wicherts, & van der almost invariably concluded that their stability correla- Maas, 2016). To illustrate these issues concretely, tions were ‘adequate’ or ‘satisfactory,’ regardless of the Table 5 shows some numerical examples of the impact size of the coefficient or the length of the retest interval.^ of different reliabilities on sample size calculations. This compares the sample size required for the assumed under- (Watson, 2004, p.326). Researchers might also assume that RT-based measures are inherently more noisy than lying correlation with that required for the attenuated cor- self-report (e.g., Lane, Banaji, Nosek, & Greenwald, relation. This calculation, sometimes attributed to 2007), and that holding all measures to a clinical standard Nunnally (1970), rearranges Spearman’s(1904)correction is overly restrictive (Nunnally, 1978). While there may be for attenuation formula that we applied earlier: pﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃﬃ rmðÞ easure A; measure B¼ rtðÞ rue A; true B reliabilityðÞ Measure A reliabilityðÞ Measure B required greatly exceed those typically used in most cog- Two things are apparent from Table 5. First, the mag- nitude of reliability for a measure has a substantial impact nitive and neurophysiological research. on required sample sizes. Even for reliability nominally considered to be Bgood^ (>.6) by commonly cited criteria Challenges for cognitive neuroscience and clinical (Cicchetti & Sparrow, 1981; Fleiss, 1981; Landis & Koch, research 1977), the required sample sizes are about three times higher than what would be specified if reliability had Though the required sample sizes indicated in Table 5 are not not been taken in to account. Second, even with moderate insurmountable in all research contexts, they are particularly (r = .3) true effect sizes assumed, the sample sizes challenging for areas that are resource intensive, or access to 1180 Behav Res (2018) 50:1166–1186 Table 5 The relationship between the true correlation, reliabilities, and correlations in personality and behavioral research observed observable correlation in two variables. The BTrue r^ is the correlation we that <3% of effects were large by Cohen’s (1988) commonly would expect to observe given a reliability of 1 for both measures. The BN cited criteria of .5, and 75% of effects were .29 and below true^ is the sample size that would be required to observe the underlying effect, which is what is normally reported from power calculations. The (Gignac & Szodorai, 2016). There is certainly a higher range BObservable r^ is the expected correlation after accounting for reliability, of effect sizes reported in imaging studies (e.g., Vul et al., corresponding to a recalculated sample size requirement (N obs.). Power 2009), though it is likely that these are inflated by the preva- calculations were performed using G*Power (Faul, Erdfelder, Buchner, & lence of small samples, publication bias and questionable re- Lang, 2009; Faul, Erdfelder, Lang, & Buchner, 2007), assuming α =.05 and β =.8 search practices (Button et al., 2013b; John, Loewenstein, & Prelec, 2012). Therefore, we believe that the effect sizes and Reliability sample sizes reported in Table 5 are representative, even op- timistic, for the ranges common to most research questions. True r Measure A Measure B Observable r N true N obs. .7 .8 .8 .56 13 22 .7 .6 .6 .42 13 42 Measurement error or state-dependence .7 .4 .7 .37 13 55 .5 .8 .8 .4 29 46 We have largely discussed issues of task construction and .5 .6 .6 .3 29 84 measurement. An alternative possibility is that participants .5 .4 .7 .26 29 113 simply fluctuate in their ability to perform these tasks over .3 .8 .8 .24 84 133 time and contexts. There is evidence, for example, that .3 .6 .6 .18 84 239 SSRTs are sensitive to strategic changes (Leotti & Wager, .3 .4 .7 .16 84 304 2010), and that SSRTs and go/no-go performance are disrupted by alcohol (e.g., Caswell, Morgan, & Duka, 2013; de Wit, Crean, & Richards, 2000; Dougherty, Marsh-Richard, Hatzis, Nouvion, & Mathias, 2008; Mulvihill, Skilling, & participants is difficult. Concerns about measurement reliabil- VogelSprott, 1997; Weafer & Fillmore, 2008), indicating that ity has also been raised in neuroimaging (e.g., Bennett & performance on these tasks is not impermeable. Miller, 2010; Mikkelsen, Singh, Sumner, & Evans, 2015; Nevertheless, there is evidence for stability for some tasks Vul, Harris, Wimkielman, & Pashler, 2009;Wang, Abdi, in our data. Low ICCs in a homogenous sample are not nec- Bakhadirov, Diaz-Arrastia, & Devous, 2012). For example, essarily indicative of substantial changes in performance. The it has been estimated that the average reliability of voxel- low SEMs in the flanker RT cost indicate that participants wise blood-oxygen-level-dependent functional magnetic res- generally perform the task similarly in both sessions, even onance imaging is .5 (Bennett & Miller, 2010). This is similar though the relative ranking between individuals is not consis- to the average of the estimates for our behavioral measures tent. Further, if the low ICCs we observe were primarily due to (.45). Assuming reliabilities of .5 for both measures and a variation in psychological or physiological factors over the large (R= .5) Btrue^ underlying correlation, a sample size of course of 3 weeks, we might expect high reliabilities when 123 would be required to adequately power correlations be- comparing performance in the first half of each session to the tween cognition and functional imaging. Such sample sizes second half, or comparing odd and even numbered trials. are rare, including in our own previous work (Boy, Evans, However, these within-session reliabilities (Supplementary et al., 2010; see also Yarkoni and Braver, 2010). Material G) show similarly sub-optimal reliability for the Given the prohibitive time and costs of behavioral, imag- key measures (see also Khng & Lee, 2014). An exception to ing, and neuropsychological studies, one might question the this is the stop-signal reaction time, where the odd vs. even utility of pursuing individual differences research. It has been trial comparison produces estimates between .82 and .89 for argued that it is not optimal to pursue large sample sizes in the integration method. This is likely in part because the track- neuroimaging because effects that require large samples are ing procedure used will produce a high reliability for the SSD not sufficiently large to be of practical or theoretical impor- when taking alternating trials. tance (Friston, 2012, though see commentaries; Button et al., We would generally expect measurements taken closely 2013a; Friston, 2013; Ingre, 2013; Lindquist, Caffo, & together in time to yield higher estimates of reliability than Crainiceanu, 2013). The extent to which an effect size is con- those taken at more distant points, even within a single testing sidered meaningful will vary according to the research ques- session. However, there are sources of variance outside the tion, though there is little guidance on what our normative construct of interest that could increase or decrease reliability expectations should be. A recent meta-analysis of 708 estimates. Time-series analysis of RTs suggests that there is a Behav Res (2018) 50:1166–1186 1181 correlation between the speeds of consecutive responses given to minimize between-subject variance, and thus successful by an individual, which decreases as the number of interven- tasks in that context should be expected to have low reliability; ing trials increases (Gilden, Thornton, & Mallon, 1995; taking reliability into account could entirely change theoreti- Wagenmakers, Farrell, & Ratcliff, 2004). Estimates compar- cal inferences from correlational structure. ing odd to even numbered trials may appear to be more reli- able because they encompass such short-scale fluctuations. Alternatively, factors such as practice effects or fatigue may Future directions and recommendations decrease reliability by increasing measurement error, or by producing systematic shifts in performance between measure- Our consideration of reliability issues form part of a broader ment points (e.g., individuals being slower in the second half concern that studying individual differences is challenging for of trials compared to the first). The analyses we conduct in laboratory-based research, particularly in resource-intensive Supplementary Materials D and G explore these as possible contexts such as neuroimaging. With these global issues in reasons for the sub-optimal reliabilities that we observed. mind, we discuss approaches that could help to optimize re- Taken together, these suggest that the key issue is simply that search designs using cognitive tasks. Note that although the individuals do not differ enough from one another to reliably majority of discussion focuses on analysis methods, one overcome measurement fluctuations. should not expect to create inter-subject variability from a task that is designed to produce homogenous performance. Generalizability of findings to other populations. Researchers should be mindful of these properties at the stages of task design/selection and power analysis. For several of If between-participant variance differs markedly between pop- these approaches, it is undetermined or untested whether they ulations, the population with higher variance will show higher improve reliability estimates for the contexts we focus on reliability, unless measurement noise increases proportionally. here, though some have shown promise in other areas. We used a (predominantly female) student sample, who might show restricted variance compared to a general population. Alternative measurement approaches The independent ex- However, our comparisons indicate that they have similar levels amination of mean RTs or mean error rates belies the richness of variability to samples taken from a general population, which of the data provided by many behavioral tasks. The practice of also did not show consistently higher reliability estimates (see considering RT and errors costs as independent and inter- Supplementary Material C1 and C2). Further, the components changeable measures of performance has been questioned in of UPPS-P, a self-report measure of impulsivity, showed reli- several areas (e.g., Draheim, Hicks, & Engle, 2016; Ratcliff & abilities between .7–.9, indicating that reliable measurement is Rouder, 1998; Wickelgren, 1977). In the domain of task attainable in a student sample on measures designed to differ- switching, it has been suggested that composite scores of RT entiate between individuals. Finally, examples of sub-optimal costs and error rates are better able to predict performance in a reliability for robust within-subject effects are not limited to working memory task than RT costs alone (Draheim et al., student samples (e.g., attention networks in schizophrenic 2016; Hughes, Linck, Bowles, Koeth, & Bunting, 2014). patients and healthy controls; Hahn et al., 2011). Therefore, Further, Hughes et al. observed higher within-session reliabil- theissueswediscuss arelikelyto generalize to other samples. ities for composite RT-accuracy scores, relative to RT costs or Though our sample sizes are larger than many previous accuracy costs in isolation, but only when using a response retest reliability studies of these tasks, it has been argued that deadline procedure. samples approaching 250 are necessary for a stable estimate of Alternatively, mathematical models of decision making the (Pearson’s) correlation effect size (Schonbrodt & Perugini, such as the drift-diffusion model (Ratcliff, 1978; Ratcliff & 2013). Using simulations, they defined stability as the point at Rouder, 1998; Ratcliff, Smith, Brown, & McKoon, 2016) which the Bobserved^ correlation did not deviate from a spec- decompose RTand accuracy into parameters thought to reflect ified window (±.1) around the Btrue^ effect with the addition decision processes. The combination of modelling techniques of more data points. However, the point of stability is depen- with imaging methods has also been discussed (Forstmann, dent on the size of the underlying correlation, and the degree Ratcliff, & Wagenmakers, 2016; Forstmann & Wagenmakers, of uncertainty one is willing to accept. For example, assuming 2015). Recently, Lerche and Voss (2017) observed that the a confidence (power) level of 80% and a population correla- retest reliability of key diffusion model parameters was similar tion of R = .7, the point of stability for a window of ±.15 was to that of overall accuracy and mean RT in lexical decision, N=28. Therefore, ICCs as low as the ones we observe are recognition memory, and an associative priming task. unlikely if the population ICC is excellent. However, the parameters they extracted reflect processes The student population we used is typical of most cognitive (e.g., information processing speed) in individual conditions and imaging studies, but regardless of population, the main or across conditions, rather than a within-subject effect anal- points of this paper will remain true: experimental designs aim ogous to an RT cost. It is possible to create difference scores 1182 Behav Res (2018) 50:1166–1186 from model parameters, though these may be subject to the addition to the time required to administer multiple tasks or same statistical issues noted previously. Thus, while there may sessions, may make the approach infeasible for many re- be theoretical value in such modelling approaches, whether searchers. Finally, Item Response Theory (IRT; see, e.g., they improve reliability estimates for experimental effects is Hambleton, Swaminathan, & Rogers, 1991; Lord & Novick, an open question. 1968) has arguably superseded classical test theory in educa- Another suggested alternative to difference scores is to use tional testing. The goal of IRT is to characterize the relation- residualized differences (Cronbach & Furby, 1970;DuBois, ship between typically a single latent trait (e.g., maths ability) 1957; Friedman & Miyake, 2004). This entails a regression and the probability of a binary response (e.g., correct or incor- approach in which scores in the baseline condition (e.g., con- rect) on individual test items. The resulting item response gruent RT) are used to predict incongruent RTs, and an indi- curve captures both the location of each item with respect to vidual’s residual from their predicted value is taken as the the latent trait (i.e., its difficulty), and the sensitivity of the index of performance. Residualized scores show improved item to differing levels of ability (i.e., its slope). Though not reliability over standard difference scores in some situations, easily applicable to the current format of most experimental though their interpretation is not straightforward (for a review, tasks, the contribution of IRT to educational testing is notable see Willet, 1988). Evaluating the theoretical strengths and if constructing new tests for the purposes of cognitive and weaknesses of all these approaches is beyond the scope of clinical measurement. the current paper. From a methodological perspective, the re- liability of any composite measure or modelled parameter will Interactions in experimental designs In addition to factoring not be perfect, and thus needs to be empirically measured and reliability into power calculations as detailed above, within- accounted for. subject designs can be used to examine associations and dis- sociations between measures. For example, the absence of Alternative statistical approaches In our reliability analyses, correlations in our data between SSRT and the Stroop task we adopted the ANOVA-based approach to estimating com- implies no relationship between performance in these tasks. ponents of variance (McGraw & Wong, 1996;Shrout& In contrast, shared mechanisms have been implicated in ex- Fleiss, 1979). This is perhaps the most commonly used meth- perimental studies that have combined the tasks, where Stroop od in psychology, produced by popular packages such as stimuli are used in place of the typical two choice stimuli used SPSS. Variance components can alternatively be estimated in the SST (Kalanthroff, Goldfarb, & Henik, 2013; via the use of linear mixed-effects (LMMs) and generalized Verbruggen, Liefooghe, & Vandierendonck, 2004). linear mixed-effects models (GLLMs; Nakagawa & Verbruggen et al. observed longer SSRTs on incongruent trials Schielzeth, 2010). These models allow greater flexibility in relative to neutral trials, suggesting that the mechanisms un- dealing with distributional assumptions and confounding var- derlying the resolution of conflict between stimuli overlaps iables. Structural equation models have also grown increas- with the mechanisms underlying response inhibition in the ingly popular in psychology (Anderson & Gerbing, 1988)asa SST. Within-subject designs may be more appropriate to ex- method to examine relationships between constructs theorized amine interactions and dissociations between underlying to underlie observable behaviors (Anderson & Gerbing, mechanisms when individual differences per se are not the 1988). Factor analysis and structural equation modelling have primary focus (for further examples in cognitive control and been used previously to examine commonality among re- other areas, see, e.g., Awh, Vogel, & Oh, 2006;Boy,Husain, sponse inhibition and executive functioning tasks (see, e.g., et al., 2010;Hedge, Oberauer, &Leonards, 2015). Aichert et al., 2012; Friedman & Miyake, 2004; Stahl et al., 2014). An attractive feature of this approach is they allow for measurement error to be modelled separately from variance Conclusions shared between measures. Latent variable models have also been applied to reliability estimates in the form of latent state- In concluding their prominent discussion of the reliability of trait models. (Newsom, 2015;Steyer, Schmitt, &Eid, 1999; difference scores, Cronbach and Furby (1970)offered thead- Steyer & Schmitt, 1990). They typically use data from three or vice, BIt appears that investigators who ask questions regard- more sessions, and can dissociate variance that is stable across ing gain scores would ordinarily be better advised to frame sessions from session specific and residual (error) variance. their questions in other ways^ (p. 80). This damning statement Notably, one study has also applied this approach to the pa- has been qualified in subsequent work (Rogosa, 1988; rameters of the drift-diffusion model derived from multiple Zimmerman & Williams, 1998;Zumbo, 1999), though as il- tasks (Schubert, Frischkorn, Haemann, & Voss, 2016). A lim- lustrated by our findings, robust experimental effects do not iting factor is that structural equation models typically require necessarily translate to optimal methods of studying individ- large samples, with suggestions typically falling in the 100s ual differences. We suggest that this is because experimental (c.f. Wolf, Harrington, Clark, & Miller, 2013). This, in designs have been developed and naturally selected for Behav Res (2018) 50:1166–1186 1183 Academy of Sciences of the United States of America, 107(24), providing robust effects, which means low between- 11134–11139. doi:10.1073/pnas.1001925107 participant variance. Cronbach (1957) called for a bridging Boy, F., & Sumner, P. (2014). Visibility predicts priming within but not of the gap between experimental and correlational research between people: a cautionary tale for studies of cognitive individual in psychology, and we support this goal. However, our find- differences. Journal of Experimental Psychology: General, 143(3), 1011–1025. doi:10.1037/a0034881 ings suggest more caution is required when translating tools Button, K. S., Ioannidis, J. P. A., Mokrysz, C., Nosek, B. A., Flint, J., used to understand mechanisms in one context to the other. Robinson, E. S. J., & Munafo, M. R. (2013a). Confidence and pre- cision increase with high statistical power. Nature Reviews Author note This work was supported by the ESRC (ES/K002325/1) Neuroscience, 14(8). doi: 10.1038/nrn3475-c4. and by the Wellcome Trust (104943/Z/14/Z). The authors would like to Button, K. S., Ioannidis, J. P. A., Mokrysz, C., Nosek, B. A., Flint, J., thank Ulrich Ettinger and Chris Chambers for providing us with their data Ro binson, E. S. J., & Munafo, M. R. (2013b). Power failure: why for comparative analyses. small sample size undermines the reliability of neuroscience. 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