Over the past two decades, social psychological research on prejudice has been dominated by the implicit cognition paradigm (Meissner, Grigutsch, Koranyi, Müller, & Rothermund, 2019). This paradigm is based on the assumption that many individuals of the majority group (e.g., White US Americans) have an automatic tendency to discriminate against members of a stigmatized minority group (e.g., African Americans). It is assumed that this tendency is difficult to control because many people are unaware of their prejudices.
The implicit cognition paradigm also assumes that biases vary across individuals of the majority group. The most widely used measure of individual differences in implicit biases is the race Implicit Association Test (rIAT; Greenwald, McGhee, & Schwartz, 1998). Like any other measure of individual differences, the race IAT has to meet psychometric criteria to be a useful measure of implicit bias. Unfortunately, the race IAT has been used in hundreds of studies before its psychometric properties were properly evaluated in a program of validation research (Schimmack, 2021a, 2021b).
Meta-analytic reviews of the literature suggest that the race IAT is not as useful for the study of prejudice as it was promised to be (Greenwald et al., 1998). For example, Meissner et al. (2019) concluded that “the predictive value for behavioral criteria is weak and their incremental validity over and above self-report measures is negligible” (p. 1).
In response to criticism of the race IAT, Greenwald, Banaji, and Nosek (2015) argued that “statistically small effects of the implicit association test can have societally large effects” (p. 553). At the same time, Greenwald (1975) warned psychologists that they may be prejudiced against the null-hypothesis. To avoid this bias, he proposed that researchers should define a priori a range of effect sizes that are close enough to zero to decide in favor of the null-hypothesis. Unfortunately, Greenwald did not follow his own advice and a clear criterion for a small, but practically significant amount of predictive validity is lacking. This is a problem because estimates have decreased over time from r = .39 (McConnell & Leibold, 2001), to r = .24 in 2009 ( Greenwald, Poehlman, Uhlmann, and Banaji, 2009), to r = .148 in 2013 (Oswald, Mitchell, Blanton, Jaccard, & Tetlock (2013), and r = .097 in 2019 (Greenwald & Lai, 2020; Kurdi et al., 2019). Without a clear criterion value, it is not clear how this new estimate of predictive validity should be interpreted. Does it still provide evidence for a small, but practically significant effect, or does it provide evidence for the null-hypothesis (Greenwald, 1975)?
Measures are not Causes
To justify the interpretation of a correlation of r = .1 as small but important, it is important to revisit Greenwald et al.’s (2015) arguments for this claim. Greenwald et al. (2015) interpret this correlation as evidence for an effect of the race IAT on behavior. For example, they write “small effects can produce substantial discriminatory impact also by cumulating over repeated occurrences to the same person” (p. 558). The problem with this causal interpretation of a correlation between two measures is that scores on the race IAT have no influence on individuals’ behavior. This simple fact is illustrated in Figure 1. Figure 1 is a causal model that assumes the race IAT reflects valid variance in prejudice and prejudice influences actual behaviors (e.g., not voting for a Black political candidate). The model makes it clear that the correlation between scores on the race IAT (i.e., the iat box) and scores on a behavioral measures (i.e., the crit box) do not have a causal link (i.e., no path leads from the iat box to the crit box). Rather, the two measured variables are correlated because they both reflect the effect of a third variable. That is, prejudice influences race IAT scores and prejudice influences the variance in the criterion variable.
There is general consensus among social scientists that prejudice is a problem and that individual differences in prejudice have important consequences for individuals and society. The effect size of prejudice on a single behavior has not been clearly examined, but to the extent that race IAT scores are not perfectly valid measures of prejudice, the simple correlation of r = .1 is a lower limit of the effect size. Schimmack (2021) estimated that no more than 20% of the variance in race IAT scores is valid variance. With this validity coefficient, a correlation of r = .1 implies an effect of prejudice on actual behaviors of .1 / sqrt(.2) = .22.
Greenwald et al. (2015) correctly point out that effect sizes of this magnitude, r ~ .2, can have practical, real-world implications. The real question, however, is whether predictive validity of .1 justifies the use of the race IAT as a measure of prejudice. This question has to be evaluated in a comparison of predictive validity for the race IAT with other measures of prejudice. Thus, the real question is whether the race IAT has sufficient incremental predictive validity over other measures of prejudice. However, this question has been largely ignored in the debate about the utility of the race IAT (Greenwald & Lai, 2020; Greenwald et al., 2015; Oswald et al., 2013).
Kurdi et al. (2019) discuss incremental predictive validity, but this discussion is not limited to the race IAT and makes the mistake to correct for random measurement error. As a result, the incremental predictive validity for IATs of b = .14 is a hypothetical estimate for IATs that are perfectly reliable. However, it is well-known that IATs are far from perfectly reliable. Thus, this estimate overestimates the incremental predictive validity. Using Kurdi et al.’s data and limiting the analysis to studies with the race IAT, I estimated incremental predictive validity to be b = .08, 95%CI = .04 to .12. It is difficult to argue that this a practically significant amount of incremental predictive validity. At the very least, it does not justify the reliance on the race IAT as the only measure of prejudice or the claim that the race IAT is a superior measure of prejudice (Greenwald et al., 2009).
The meta-analytic estimate of b = .1 has to be interpreted in the context of evidence of substantial heterogeneity across studies (Kurdi et al., 2019). Kurdi et al. (2019) suggest that “it may be more appropriate to ask under what conditions the two [race IAT scores and criterion variables] are more or less highly correlated” (p. 575). However, little progress has been made in uncovering moderators of predictive validity. One possible explanation for this is that previous meta-analysis may have overlooked one important source of variation in effect sizes, namely publication bias. Traditional meta-analyses may be unable to reveal publication bias because they include many articles and outcome measures that did not focus on predictive validity. For example, Kurdi’s meta-analysis included a study by Luo, Li, Ma, Zhang, Rao, and Han (2015). The main focus of this study was to examine the potential moderating influence of oxytocin on neurological responses to pain expressions of Asian and White faces. Like many neurological studies, the sample size was small (N = 32), but the study reported 16 brain measures. For the meta-analysis, correlations were computed across N = 16 participants separately for two experimental conditions. Thus, this study provided as many effect sizes as it had participants. Evidently, power to obtain a significant result with N = 16 and r = .1 is extremely low, and adding these 32 effect sizes to the meta-analysis merely introduced noise. This may undermine the validity of meta-analytic results ((Sharpe, 1997). To address this concern, I conducted a new meta-analysis that differs from the traditional meta-analyses. Rather than coding as many effects from as many studies as possible, I only include focal hypothesis tests from studies that aimed to investigate predictive validity. I call this a focused meta-analysis.
Focused Meta-Analysis of Predictive Validity
Coding of Studies
I relied on Kurdi et al.’s meta-analysis to find articles. I selected only published articles that used the race IAT (k = 96). The main purpose of including unpublished studies is often to correct for publication bias (Kurdi et al., 2019). However, it is unlikely that only 14 (8%) studies that were conducted remained unpublished. Thus, the unpublished studies are not representative and may distort effect size estimates.
Coding of articles in terms of outcome measures that reflect discrimination yielded 60 studies in 45 articles. I examined whether this selection of studies influenced the results by limiting a meta-analysis with Kurdi et al.’s coding of studies to these 60 articles. The weighted average effect size was larger than the reported effect size, a = .167, se = .022, 95%CI = .121 to .212. Thus, Kurdi et al.’s inclusion of a wide range of studies with questionable criterion variables diluted the effect size estimate. However, there remained substantial variability around this effect size estimate using Kurdi et al.’s data, I2 = 55.43%.
The focused coding produced one effect-size per study. It is therefore not necessary to model a nested structure of effect sizes and I used the widely used metafor package to analyze the data (Viechtbauer, 2010). The intercept-only model produced a similar estimate to the results for Kurdi et al.’s coding scheme, a = .201, se = .020, 95%CI = .171 to .249. Thus, focal coding does seem to produce the same effect size estimate as traditional coding. There was also a similar amount of heterogeneity in the effect sizes, I2 = 50.80%.
However, results for publication bias differed. Whereas Kurdi et al.’s coding shows no evidence of publication bias, focused coding produced a significant relationship emerged, b = 1.83, se = .41, z = 4.54, 95%CI = 1.03 to 2.64. The intercept was no longer significant, a = .014, se = .0462, z = 0.31, 95%CI = -.077 to 95%CI = .105. This would imply that the race IAT has no incremental predictive validity. Adding sampling error as a predictor reduced heterogeneity from I2 = 50.80% to 37.71%. Thus, some portion of the heterogeneity is explained by publication bias.
Stanley (2017) recommends to accept the null-hypothesis when the intercept in the previous model is not significant. However, a better criterion is to compare this model to other models. The most widely used alternative model regresses effect sizes on the squared sampling error (Stanley, 2017). This model explained more of the heterogeneity in effect sizes as reflected in a reduction of unexplained heterogeneity from 50.80% to 23.86%. The intercept for this model was significant, a = .113, se = .0232, z = 4.86, 95%CI = .067 to .158.
Figure 2 shows the effect sizes as a function of sampling error and the regression lines for the three models.
Inspection of Figure 1 provides further evidence that the squared-SE model. The red line (squared sampling error) fits the data better than the blue line (sampling error) model. In particular for large samples, PET underestimates effect sizes.
The significant relationship between sample size (sampling error) and effect sizes implies that large effects in small studies cannot be interpreted at face value. For example, the most highly cited study of predictive validity had only a sample size of N = 42 participants (McConnell & Leibold, 2001). The squared-sampling-error model predicts an effect size estimate of r = .30, which is close to the observed correlation of r = .39 in that study.
In sum, a focal meta-analysis replicates Kurdi et al.’s (2019) main finding that the average predictive validity of the race IAT is small, r ~ .1. However, the focal meta-analysis also produced a new finding. Whereas the initial meta-analysis suggested that effect sizes are highly variable, the new meta-analysis suggests that a large portion of this variability is explained by publication bias.
I explored several potential moderator variables, namely (a) number of citations, (b) year of publication, (c) whether IAT effects were direct or moderator effects, (d) whether the correlation coefficient was reported or computed based on test statistics, and (e) whether the criterion was an actual behavior or an attitude measure. The only statistically significant result was a weaker correlation in studies that predicted a moderating effect of the race IAT, b = -.11, se = .05, z = 2.28, p = .032. However, the effect would not be significant after correction for multiple comparison and heterogeneity remained virtually unchanged, I2 = 27.15%.
During the coding of the studies, the article “Ironic effects of racial bias during interracial interactions” stood out because it reported a counter-intuitive result. in this study, Black confederates rated White participants with higher (pro-White) race IAT scores as friendlier. However, other studies find the opposite effect (e.g., McConnell & Leibold, 2001). If the ironic result was reported because it was statistically significant, it would be a selection effect that is not captured by the regression models and it would produce unexplained heterogeneity. I therefore also tested a model that excluded all negative effect. As bias is introduced by this selection, the model is not a test of publication bias, but it may be better able to correct for publication bias. The effect size estimate was very similar, a = .133, se = .017, 95%CI = .010 to .166. However, heterogeneity was reduced to 0%, suggesting that selection for significance fully explains heterogeneity in effect sizes.
In conclusion, moderator analysis did not find any meaningful moderators and heterogeneity was fully explained by publication bias, including publishing counterintuitive findings that suggest less discrimination by individuals with more prejudice. The finding that publication bias explains most of the variance is extremely important because Kurdi et al. (2019) suggested that heterogeneity is large and meaningful, which would suggest that higher predictive validity could be found in future studies. In contrast, the current results suggest that correlations greater than .2 in previous studies were largely due to selection for significance with small samples, which also explains unrealistically high correlations in neuroscience studies with the race IAT (cf. Schimmack, 2021b).
Predictive Validity of Self-Ratings
The predictive validity of self-ratings is important for several reasons. First, it provides a comparison standard for the predictive validity of the race IAT. For example, Greenwald et al. (2009) emphasized that predictive validity for the race IAT was higher than for self-reports. However, Kurdi et al.’s (2019) meta-analysis found the opposite. Another reason to examine the predictive validity of explicit measures is that implicit and explicit measures of racial attitudes are correlated with each other. Thus, it is important to establish the predictive validity of self-ratings to estimate the incremental predictive validity of the race IAT.
Figure 2 shows the results. The sampling-error model shows a non-zero effect size, but sampling error is large, and the confidence interval includes zero, a = .121, se = .117, 95%CI = -.107 to .350. Effect sizes are also extremely heterogeneous, I2 = 62.37%. The intercept for the squared-sampling-error model is significant, a = .176, se = .071, 95%CI = .036 to .316, but the model does not explain more of the heterogeneity in effect sizes than the squared-sampling-error model, I2 = 63.33%. To remain comparability, I use the squared-sampling error estimate. This confirms Kurdi et al.’s finding that self-ratings have slightly higher predictive validity, but the confidence intervals overlap. For any practical purposes, predictive validity of the race IAT and self-reports is similar. Repeating the moderator analyses that were conducted with the race IAT revealed no notable moderators.
Only 21 of the 60 studies reported information about the correlation between the race IAT and self-report measures. There was no indication of publication bias, and the effect size estimates of the three models converge on an estimate of r ~ .2 (Figure 3). Fortunately, this result can be compared with estimates from large internet studies (Axt, 2017) and a meta-analysis of implicit-explicit correlations (Hofmann et al., 2005). These estimates are a bit higher, r ~ .25. Thus, using an estimate of r = .2 is conservative for a test of the incremental predictive validity of the race IAT.
Incremental Predictive Validity
It is straightforward to estimate the incremental predictive validity of the race IAT and self-reports on the basis of the correlations between race IAT, self-ratings, and criterion variables. However, it is a bit more difficult to provide confidence intervals around these estimates. I used a simulated dataset with missing values to reproduce the correlations and sampling error of the meta-analysis. I then regressed, the criterion on the implicit and explicit variable. The incremental predictive validity for the race IAT was b = .07, se = .02, 95%CI = .03 to .12. This finding implies that the race IAT on average explains less than 1% unique variance in prejudice behavior. The incremental predictive validity of the explicit measure was b = .165, se = .03, 95%CI = .11 to .23. This finding suggests that explicit measures explain between 1 and 4 percent of the variance in prejudice behaviors.
Assuming that there is no shared method variance between implicit and explicit measures and criterion variables and that implicit and explicit measures reflect a common construct, prejudice, it is possible to fit a latent variable model to the correlations among the three indicators of prejudice (Schimmack, 2021). Figure 4 shows the model and the parameter estimates.
According to this model, prejudice has a moderate effect on behavior, b = .307, se = .043. This is consistent with general findings about effects of personality traits on behavior (Epstein, 1973; Funder & Ozer, 1983). The loading of the explicit variable on the prejudice factor implies that .582^2 = 34% of the variance in self-ratings of prejudice is valid variance. The loading of the implicit variable on the prejudice factor implies that .353^2 = 12% of the variance in race IAT scores is valid variance. Notably, similar estimates were obtained with structural equation models of data that are not included in this meta-analysis (Schimmack, 2021). Using data from Cunningham et al., (2001) I estimated .43^2 = 18% valid variance. Using Bar-Anan and Vianello (2018), I estimated .44^2 = 19% valid variance. Using data from Axt, I found .44^2 = 19% valid variance, but 8% of the variance could be attributed to group differences between African American and White participants. Thus, the present meta-analytic results are consistent with the conclusion that no more than 20% of the variance in race IAT scores reflects actual prejudice that can influence behavior.
In sum, incremental predictive validity of the race IAT is low for two reasons. First, prejudice has only modest effects on actual behavior in a specific situation. Second, only a small portion of the variance in race IAT scores is valid.
In the 1990s, social psychologists embraced the idea that behavior is often influenced by processes that occur without conscious awareness. This assumption triggered the implicit revolution (Greenwald & Banaji, 2017). The implicit paradigm provided a simple explanation for low correlations between self-ratings of prejudice and implicit measures of prejudice, r ~ .2. Accordingly, many people are not aware how prejudice their unconscious is. The Implicit Association Test seemed to support this view because participants showed more prejudice on the IAT than on self-report measures. First studies of predictive validity also seemed to support this new model of prejudice (McConnell & Leibold, 2001), and the first meta-analysis suggested that implicit bias has a stronger influence on behavior than self-reported attitudes (Greenwald, Poehlman, Uhlmann, & Banaji, 2009, p. 17).
However, the following decade produced many findings that require a reevaluation of the evidence. Greenwald et al. (2009) published the largest test (N = 1057) of predictive validity. This study examined the ability of the race IAT to predict racial bias in the 2008 US presidential election. Although the race IAT was correlated with voting for McCain versus Obama, incremental predictive validity was close to zero and no longer significant when explicit measures were included in the regression model. Then subsequent meta-analyses produced lower estimates of predictive validity and it is no longer clear that predictive validity, especially incremental predictive validity, is high enough to reject the null-hypothesis. Although incremental predictive validity may vary across conditions, no conditions have been identified that show practically significant incremental predictive validity. Unfortunately, IAT proponents continue to make misleading statements based on single studies with small samples. For example, Kurdi et al. claimed that “effect sizes tend to be relatively large in studies on physician–patient interactions” (p. 583). However, this claim was based on a study with just 15 physicians, which makes it impossible to obtain precise effect size estimates about implicit bias effects for physicians.
Beyond Nil-Hypothesis Testing
Just like psychology in general, meta-analyses also suffer from the confusion of nil-hypothesis testing and null-hypothesis testing. The nil-hypothesis is the hypothesis that an effect size is exactly zero. Many methodologists have pointed out that it is rather silly to take the nil-hypothesis at face value because the true effect size is rarely zero (Cohen, 1994). The more important question is whether an effect size is sufficiently different from zero to be theoretically and practically meaningful. As pointed out by Greenwald (1975), effect size estimation has to be complemented with theoretical predictions about effect sizes. However, research on predictive validity of the race IAT lacks clear criteria to evaluate effect size estimates.
As noted in the introduction, there is agreement about the practical importance of statistically small effects for the prediction of discrimination and other prejudiced behaviors. The contentious question is whether the race IAT is a useful measure of dispositions to act prejudiced. Viewed from this perspective, focus on the race IAT is myopic. The real challenge is to develop and validate measures of prejudice. IAT proponents have often dismissed self-reports as invalid, but the actual evidence shows that self-reports have some validity that is at least equal to the validity of the race IAT. Moreover, even distinct self-report measures like the feeling thermometer and the symbolic racism have incremental predictive validity. Thus, prejudice researchers should use a multi-method approach. At present it is not clear that the race IAT can improve the measurement of prejudice (Greenwald et al., 2009; Schimmack, 2021a).
This article introduced a new type of meta-analysis. Rather than trying to find as many vaguely related studies and to code as many outcomes as possible, focused meta-analysis is limited to the main test of the key hypothesis. This approach has several advantages. First, the classic approach creates a large amount of heterogeneity that is unique to a few studies. This noise makes it harder to find real moderators. Second, the inclusion of vaguely related studies may dilute effect sizes. Third, the inclusion of non-focal studies may mask evidence of publication bias that is virtually present in all literatures. Finally, focal meta-analysis are much easier to do and can produce results much faster than the laborious meta-analyses that psychologists are used to. Even when classic meta-analysis exist, they often ignore publication bias. Thus, an important task for the future is to complement existing meta-analysis with focal meta-analysis to ensure that published effect sizes estimates are not diluted by irrelevant studies and not inflated by publication bias.
Enthusiasm about implicit biases has led to interventions that aim to reduce implicit biases. This focus on implicit biases in the real world needs to be reevaluated. First, there is no evidence that prejudice typically operates outside of awareness (Schimmack, 2021a). Second, individual differences in prejudice have only a modest impact on actual behaviors and are difficult to change. Not surprisingly, interventions that focus on implicit bias are not very infective. Rather than focusing on changing individuals’ dispositions, interventions may be more effective by changing situations. In this regard, the focus on internal factors is rather different from the general focus in social psychology on situational factors (Funder & Ozer, 1983). In recent years, it has become apparent that prejudice is often systemic. For example, police training may have a much stronger influence on racial disparities in fatal use of force than individual differences in prejudice of individual officers (Andersen, Di Nota, Boychuk, Schimmack, & Collins, 2021).
The present meta-analysis of the race IAT provides further support for Meissner et al.’s (2019) conclusion that IATs “predictive value for behavioral criteria is weak and their incremental validity over and above self-report measures is negligible” (p. 1). The present meta-analysis provides a quantitative estimate of b = .07. Although researchers can disagree about the importance of small effect sizes, I agree with Meissner that the gains from adding a race IAT to the measurement of prejudice is negligible. Rather than looking for specific contexts in which the race IAT has higher predictive validity, researchers should use a multi-method approach to measure prejudice. The race IAT may be included to further explore its validity, but there is no reason to rely on the race IAT as the single most important measure of individual differences in prejudice.
Funder, D.C., & Ozer, D.J. (1983). Behavior as a function of the situation. Journal of Personality and Social Psychology, 44, 107–112.
Kurdi, B., Seitchik, A. E., Axt, J. R., Carroll, T. J., Karapetyan, A., Kaushik, N., et al. (2019). Relationship between the implicit association test and intergroup behavior: a meta-analysis. American Psychologist. 74, 569–586. doi: 10.1037/amp0000364
After I posted this post, I learned about a published meta-analysis and new studies of incidental anchoring by David Shanks and colleagues that came to the same conclusion (Shanks et al., 2020).
“The most expensive car in the world costs $5 million. How much does a new BMW 530i cost?”
According to anchoring theory, information about the most expensive car can lead to higher estimates for the cost of a BMW. Anchoring effects have been demonstrated in many credible studies since the 1970s (Kahneman & Tversky, 1973).
A more controversial claim is that anchoring effects even occur when the numbers are unrelated to the question and presented incidentally (Criticher & Gilovich, 2008). In one study, participants saw a picture of a football player and were asked to guess how likely it is that the player will sack the football player in the next game. The player’s number on jersey was manipulated to be 54 or 94. The study produced a statistically significant result suggesting that a higher number makes people give higher likelihood judgments. This study started a small literature on incidental anchoring effects. A variation on this them are studies that presented numbers so briefly on a computer screen that most participants did not actually see the numbers. This is called subliminal priming. Allegedly, subliminal priming also produced anchoring effects (Mussweiler & Englich (2005).
Since 2011, many psychologists are skeptical whether statistically significant results in published articles can be trusted. The reason is that researchers only published results that supported their theoretical claims even when the claims were outlandish. For example, significant results also suggested that extraverts can foresee where pornographic images are displayed on a computer screen even before the computer randomly selected the location (Bem, 2011). No psychologist, except Bem, believes these findings. More problematic is that many other findings are equally incredible. A replication project found that only 25% of results in social psychology could be replicated (Open Science Collaboration, 2005). So, the question is whether incidental and subliminal anchoring are more like classic anchoring or more like extrasensory perception.
There are two ways to assess the credibility of published results when publication bias is present. One approach is to conduct credible replication studies that are published independent of the outcome of a study. The other approach is to conduct a meta-analysis of the published literature that corrects for publication bias. A recent article used both methods to examine whether incidental anchoring is a credible effect (Kvarven et al., 2020). In this article, the two approaches produced inconsistent results. The replication study produced a non-significant result with a tiny effect size, d = .04 (Klein et al., 2014). However, even with bias-correction, the meta-analysis suggested a significant, small to moderate effect size, d = .40.
The data for the meta-analysis were obtained from an unpublished thesis (Henriksson, 2015). I suspected that the meta-analysis might have coded some studies incorrectly. Therefore, I conducted a new meta-analysis, using the same studies and one new study. The main difference between the two meta-analysis is that I coded studies based on the focal hypothesis test that was used to claim evidence for incidental anchoring. The p-values were then transformed into fisher-z transformed correlations and and sampling error, 1/sqrt(N – 3), based on the sample sizes of the studies.
Whereas the old meta-analysis suggested that there is no publication bias, the new meta-analysis showed a clear relationship between sampling error and effect sizes, b = 1.68, se = .56, z = 2.99, p = .003. Correcting for publication bias produced a non-significant intercept, b = .039, se = .058, z = 0.672, p = .502, suggesting that the real effect size is close to zero.
Figure 1 shows the regression line for this model in blue and the results from the replication study in green. We see that the blue and green lines intersect when sampling error is close to zero. As sampling error increases because sample sizes are smaller, the blue and green line diverge more and more. This shows that effect sizes in small samples are inflated by selection for significance.
However, there is some statistically significant variability in the effect sizes, I2 = 36.60%, p = .035. To further examine this heterogeneity, I conducted a z-curve analysis (Bartos & Schimmack, 2021; Brunner & Schimmack, 2020). A z-curve analysis converts p-values into z-statistics. The histogram of these z-statistics shows publication bias, when z-statistics cluster just above the significance criterion, z = 1.96.
Figure 2 shows a big pile of just significant results. As a result, the z-curve model predicts a large number of non-significant results that are absent. While the published articles have a 73% success rate, the observed discovery rate, the model estimates that the expected discovery rate is only 6%. That is, for every 100 tests of incidental anchoring, only 6 studies are expected to produce a significant result. To put this estimate in context, with alpha = .05, 5 studies are expected to be significant based on chance alone. The 95% confidence interval around this estimate includes 5% and is limited at 26% at the upper end. Thus, researchers who reported significant results did so based on studies with very low power and they needed luck or questionable research practices to get significant results.
A low discovery rate implies a high false positive risk. With an expected discovery rate of 6%, the false discovery risk is 76%. This is unacceptable. To reduce the false discovery risk, it is possible to lower the alpha criterion for significance. In this case, lowering alpha to .005 produces a false discovery risk of 5%. This leaves 5 studies that are significant.
One notable study with strong evidence, z = 3.70, examined anchoring effects for actual car sales. The data came from an actual auction of classic cars. The incidental anchors were the prices of the previous bid for a different vintage car. Based on sales data of 1,477 cars, the authors found a significant effect, b = .15, se = .04 that translates into a standardized effect size of d = .2 (fz = .087). Thus, while this study provides some evidence for incidental anchoring effects in one context, the effect size estimate is also consistent with the broader meta-analysis that effect sizes of incidental anchors are fairly small. Moreover, the incidental anchor in this study is still in the focus of attention and in some way related to the actual bid. Thus, weaker effects can be expected for anchors that are not related to the question at all (a player’s number) or anchors presented outside of awareness.
There is clear evidence that evidence for incidental anchoring cannot be trusted at face value. Consistent with research practices in general, studies on incidental and subliminal anchoring suffer from publication bias that undermines the credibility of the published results. Unbiased replication studies and meta-analysis suggest that incidental anchoring effects are either very small or zero. Thus, there exists currently no empirical support for the notion that irrelevant numeric information can bias numeric judgments. More research on anchoring effects that corrects for publication bias is needed.
Social psychologists have failed to clean up their act and their literature. Here I show unusually high effect sizes in non-retracted articles by Sanna, who retracted several articles. I point out that non-retraction does not equal credibility and I show that co-authors like Norbert Schwarz lack any motivation to correct the published record. The inability of social psychologists to acknowledge and correct their mistakes renders social psychology a para-science that lacks credibility. Even meta-analyses cannot be trusted because they do not correct properly for the use of questionable research practices.
When I grew up, a popular German Schlager was the song “Aber bitte mit Sahne.” The song is about Germans love of deserts with whipped cream. So, when I saw articles by Sanna, I had to think about whipped cream, which is delicious. Unfortunately, articles by Sanna are the exact opposite. In the early 2010s, it became apparent that Sanna had fabricated data. However, unlike the thorough investigation of a similar case in the Netherlands, the extent of Sanna’s fraud remains unclear (Retraction Watch, 2012). The latest count of Sanna’s retracted articles was 8 (Retraction Watch, 2013).
WebOfScience shows 5 retraction notices for 67 articles, which means 62 articles have not been retracted. The question is whether these article can be trusted to provide valid scientific information? The answer to this question matters because Sanna’s articles are still being cited at a rate of over 100 citations per year.
Meta-Analysis of Ease of Retrieval
The data are also being used in meta-analyses (Weingarten & Hutchinson, 2018). Fraudulent data are particularly problematic for meta-analysis because fraud can produce large effect size estimates that may inflate effect size estimates. Here I report the results of my own investigation that focusses on the ease-of-retrieval paradigm that was developed by Norbert Schwarz and colleagues (Schwarz et al., 1991).
The meta-analysis included 7 studies from 6 articles. Two studies produced independent effect size estimates for 2 conditions for a total of 9 effect sizes.
Sanna, L. J., Schwarz, N., & Small, E. M. (2002). Accessibility experiences and the hindsight bias: I knew it all along versus it could never have happened. Memory & Cognition, 30(8), 1288–1296. https://doi.org/10.3758/BF03213410 [Study 1a, 1b]
Sanna, L. J., Schwarz, N., & Stocker, S. L. (2002). When debiasing backfires: Accessible content and accessibility experiences in debiasing hindsight. Journal of Experimental Psychology: Learning, Memory, and Cognition, 28(3), 497–502. https://doi.org/10.1037/0278-73220.127.116.117 [Study 1 & 2]
Sanna, L. J., & Schwarz, N. (2003). Debiasing the hindsight bias: The role of accessibility experiences and (mis)attributions. Journal of Experimental Social Psychology, 39(3), 287–295. https://doi.org/10.1016/S0022-1031(02)00528-0 [Study 1]
Sanna, L. J., Chang, E. C., & Carter, S. E. (2004). All Our Troubles Seem So Far Away: Temporal Pattern to Accessible Alternatives and Retrospective Team Appraisals. Personality and Social Psychology Bulletin, 30(10), 1359–1371. https://doi.org/10.1177/0146167204263784 [Study 3a]
Sanna, L. J., Parks, C. D., Chang, E. C., & Carter, S. E. (2005). The Hourglass Is Half Full or Half Empty: Temporal Framing and the Group Planning Fallacy. Group Dynamics: Theory, Research, and Practice, 9(3), 173–188. https://doi.org/10.1037/1089-2618.104.22.168 [Study 3a, 3b]
Carter, S. E., & Sanna, L. J. (2008). It’s not just what you say but when you say it: Self-presentation and temporal construal. Journal of Experimental Social Psychology, 44(5), 1339–1345. https://doi.org/10.1016/j.jesp.2008.03.017 [Study 2]
When I examined Sanna’s results, I found that all 9 of these 9 effect sizes were extremely large with effect size estimates being larger than one standard deviation. A logistic regression analysis that predicted authorship (With Sanna vs. Without Sanna) showed that the large effect sizes in Sanna’s articles were unlikely to be due to sampling error alone, b = 4.6, se = 1.1, t(184) = 4.1, p = .00004 (1 / 24,642).
These results show that Sanna’s effect sizes are not typical for the ease-of-retrieval literature. As one of his retracted articles used the ease-of retrieval paradigm, it is possible that these articles are equally untrustworthy. As many other studies have investigated ease-of-retrieval effects, it seems prudent to exclude articles by Sanna from future meta-analysis.
These articles should also not be cited as evidence for specific claims about ease-of-retrieval effects for the specific conditions that were used in these studies. As the meta-analysis shows, there have been no credible replications of these studies and it remains unknown how much ease of retrieval may play a role under the specified conditions in Sanna’s articles.
The blog post is also a warning for young scientists and students of social psychology that they cannot trust researchers who became famous with the help of questionable research practices that produced too many significant results. As the reference list shows, several articles by Sanna were co-authored by Norbert Schwarz, the inventor of the ease-of-retrieval paradigm. It is most likely that he was unaware of Sanna’s fraudulent practices. However, he seemed to lack any concerns that the results might be too good to be true. After all, he encountered replicaiton failures in his own lab.
“of course, we had studies that remained unpublished. Early on we experimented with different manipulations. The main lesson was: if you make the task too blatantly difficult, people correctly conclude the task is too difficult and draw no inference about themselves. We also had a couple of studies with unexpected gender differences” (Schwarz, email communication, 5/18,21).
So, why was he not suspicious when Sanna only produced successful results? I was wondering whether Schwarz had some doubts about these studies with the help of hindsight bias. After all, a decade or more later, we know that he committed fraud for some articles on this topic, we know about replication failures in larger samples (Yeager et al., 2019), and we know that the true effect sizes are much smaller than Sanna’s reported effect sizes (Weingarten & Hutchinson, 2018).
Hi Norbert, thank you for your response. I am doing my own meta-analysis of the literature as I have some issues with the published one by Evan. More about that later. For now, I have a question about some articles that I came across, specifically Sanna, Schwarz, and Small (2002). The results in this study are very strong (d ~ 1). Do you think a replication study powered for 95% power with d = .4 (based on meta-analysis) would produce a significant result? Or do you have concerns about this particular paradigm and do not predict a replication failure? Best, Uli (email
His response shows that he is unwilling or unable to even consider the possibility that Sanna used fraud to produce the results in this article that he co-authored.
Uli, that paper has 2 experiments, one with a few vs many manipulation and one with a facial manipulation. I have no reason to assume that the patterns won’t replicate. They are consistent with numerous earlier few vs many studies and other facial manipulation studies (introduced by Stepper & Strack, JPSP, 1993). The effect sizes always depend on idiosyncracies of topic, population, and context, which influence accessible content and accessibility experience. The theory does not make point predictions and the belief that effect sizes should be identical across decades and populations is silly — we’re dealing with judgments based on accessible content, not with immutable objects.
This response is symptomatic of social psychologists response to decades of research that has produced questionable results that often fail to replicate (see Schimmack, 2020, for a review). Even when there is clear evidence of questionable practices, journals are reluctant to retract articles that make false claims based on invalid data (Kitayama, 2020). And social psychologist Daryl Bem wants rather be remembered as loony para-psychologists than as real scientists (Bem, 2021).
The problem with these social psychologists is not that they made mistakes in the way they conducted their studies. The problem is their inability to acknowledge and correct their mistakes. While they are clinging to their CVs and H-Indices to protect their self-esteem, they are further eroding trust in psychology as a science and force junior scientists who want to improve things out of academia (Hilgard, 2021). After all, the key feature of science that distinguishes it from ideologies is the ability to correct itself. A science that shows no signs of self-correction is a para-science and not a real science. Thus, social psychology is currently para-science (i.e., “Parascience is a broad category of academic disciplines, that are outside the scope of scientific study, Wikipedia).
The only hope for social psychology is that young researchers are unwilling to play by the old rules and start a credibility revolution. However, the incentives still favor conformists who suck up to the old guard. Thus, it is unclear if social psychology will ever become a real science. A first sign of improvement would be to retract articles that make false claims based on results that were produced with questionable research practices. Instead, social psychologists continue to write review articles that ignore the replication crisis (Schwarz & Strack, 2016) as if repression can bend reality.
In 2002, Daniel Kahneman was awarded the Nobel Prize for Economics. He received the award for his groundbreaking work on human irrationality in collaboration with Amos Tversky in the 1970s.
In 1999, Daniel Kahneman was the lead editor of the book “Well-Being: The foundations of Hedonic Psychology.” Subsequently, Daniel Kahneman conducted several influential studies on well-being.
The aim of the book was to draw attention to hedonic or affective experiences as an important, if not the sole, contributor to human happiness. He called for a return to Bentham’s definition of a good life as a life filled with pleasure and devoid of pain a.k.a displeasure.
The book was co-edited by Norbert Schwarz and Ed Diener, who both contributed chapters to the book. These chapters make contradictory claims about the usefulness of life-satisfaction judgments as an alternative measure of a good life.
Ed Diener is famous for his conception of wellbeing in terms of a positive hedonic balance (lot’s of pleasure, little pain) and high life-satisfaction. In contrast, Schwarz is known as a critic of life-satisfaction judgments. In fact, Schwarz and Strack’s contribution to the book ended with the claim that “most readers have probably concluded that there is little to be learned from self-reports of global well-being” (p. 80).
To a large part, Schwarz and Strack’s pessimistic view is based on their own studies that seemed to show that life-satisfaction judgments are influenced by transient factors such as current mood or priming effects.
“the obtained reports of SWB are subject to pronounced question-order- effects because the content of preceding questions influences the temporary accessibility of relevant information” (Schwarz & Strack, p. 79).
There is only one problem with this claim; it is only true for a few studies conducted by Schwarz and Strack. Studies by other researchers have produced much weaker and often not statistically reliable context effects (see Schimmack & Oishi, 2005, for a meta-analysis). In fact, a recent attempt to replicate Schwarz and Strack’s results in a large sample of over 7,000 participants failed to show the effect and even found a small, but statistically significant effect in the opposite direction (ManyLabs2).
Figure 1 summarizes the results of the meta-analysis from Schimmack and Oishi 2005), but it is enhanced by new developments in meta-analysis. The blue line in the graph regresses effect sizes (converted into Fisher-z scores) onto sampling error (1/sqrt(N -3). Publication bias and other statistical tricks produce a correlation between effect size and sampling error. The slope of the blue line shows clear evidence of publication bias, z = 3.85, p = .0001. The intercept (where the line meets zero on the x-axis) can be interpreted as a bias-corrected estimate of the real effect size. The value is close to zero and not statistically significant, z = 1.70, p = .088. The green line shows the effect size in the replication study, which was also close to zero, but statistically significant in the opposite direction. The orange vertical red line shows the average effect size without controlling for publication bias. We see that this naive meta-analysis overestimates the effect size and falsely suggests that item-order effects are a robust phenomenon. Finally, the graph highlights the three results from studies by Strack and Schwarz. These results are clear outliers and even above the biased blue regression line. The biggest outlier was obtained by Strack et al. (1991) and this is the finding that is featured in Kahneman’s book, even though it is not reproducible and clearly inflated by sampling error. Interestingly, sampling error is also called noise and Kahneman wrote a whole new book about the problems of noise in human judgments.
While the figure is new, the findings were published in 2005, several years before Kahneman wrote his book “Thinking Fast and Slow). He was simply to lazy to use the slow process of a thorough literature research to write about life-satisfaction judgments. Instead, he relied on a fast memory search that retrieved a study by his buddy. Thus, while the chapter is a good example of biases that result from fast information processing, it is not a good chapter to tell readers about life-satisfaction judgments.
To be fair, Kahneman did inform his readers that he is biased against life-satisfaction judgments. Having come to the topic of well-being from the study of the mistaken memories of colonoscopies and painfully cold hands, I was naturally suspicious of global satisfaction with life as a valid measure of well-being (Kindle Locations 6796-6798). Later on, he even admits to his mistake. Life satisfaction is not a flawed measure of their experienced well-being, as I thought some years ago. It is something else entirely (Kindle Location 6911-6912).
However, insight into his bias was not enough to motivate him to search for evidence that may contradict his bias. This is known as confirmation bias. Even ideal-prototypes of scientists like Nobel Laureates are not immune to this fallacy. Thus, this example shows that we cannot rely on simple cues like “professor at Ivy League,” “respected scientists,” or “published in prestigious journals.” to trust scientific claims. Scientific claims need to be backed up by credible evidence. Unfortunately, social psychology has produced a literature that is not trustworthy because studies were only published if they confirmed theories. It will take time to correct these mistakes of the past by carefully controlling for publication bias in meta-analyses and by conducting pre-registered studies that are published even if they falsify theoretical predictions. Until then, readers should be skeptical about claims based on psychological ‘science,’ even if they are made by a Nobel Laureate.
Citation: Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17(4), 551-566. http://dx.doi.org/10.1037/a0029487
In 2011 I wrote a manuscript in response to Bem’s (2011) unbelievable and flawed evidence for extroverts’ supernatural abilities. It took nearly two years for the manuscript to get published in Psychological Methods. While I was proud to have published in this prestigious journal without formal training in statistics and a grasp of Greek notation, I now realize that Psychological Methods was not the best outlet for the article, which may explain why even some established replication revolutionaries do not know it (comment: I read your blog, but I didn’t know about this article). So, I decided to publish an abridged (it is still long), lightly edited (I have learned a few things since 2011), and commented (comments are in […]) version here.
I also learned a few things about titles. So the revised version, has a new title.
Finally, I can now disregard the request from the editor, Scott Maxwell, on behave of reviewer Daryl Bem, to change the name of my statistical index from magic index to incredibilty index. (the advantage of publishing without the credentials and censorship of peer-review).
For readers not familiar with experimental social psychology, it is also important to understand what a multiple study article is. Most science are happy with one empirical study per article. However, social psychologists didn’t trust the results of a single study with p < .05. Therefore, they wanted to see internal conceptual replications of phenomena. Magically, Bem was able to provide evidence for supernatural abilities in not just 1 or 2 or 3 studies, but 8 conceptual replication studies with 9 successful tests. The chance of a false positive result in 9 statistical tests is smaller than the chance of finding evidence for the Higgs-Bosson particle, which was a big discovery in physics. So, readers in 2011 had a difficult choice to make: either supernatural phenomena are real or multiple study articles are unreal. My article shows that the latter is likely to be true, as did an article by Greg Francis.
Aside from Alcock’s demonstration of a nearly perfect negative correlation between effect sizes and sample sizes and my demonstration of insufficient variance in Bem’s p-values, Francis’s article and my article remain the only article that question the validity of Bem’s origina findings. Other articles have shown that the results cannot be replicated, but I showed that the original results were already too good to be true. This blog post explains, how I did it.
Why most multiple-study articles are false: An Introduction to the Magic Index
(the article formerly known as “The Ironic Effect of Significant Results on the Credibility of Multiple-Study Articles”)
Cohen (1962) pointed out the importance of statistical power for psychology as a science, but statistical power of studies has not increased, while the number of studies in a single article has increased. It has been overlooked that multiple studies with modest power have a high probability of producing nonsignificant results because power decreases as a function of the number of statistical tests that are being conducted (Maxwell, 2004). The discrepancy between the expected number of significant results and the actual number of significant results in multiple-study articles undermines the credibility of the reported
results, and it is likely that questionable research practices have contributed to the reporting of too many significant results (Sterling, 1959). The problem of low power in multiple-study articles is illustrated using Bem’s (2011) article on extrasensory perception and Gailliot et al.’s (2007) article on glucose and self-regulation. I conclude with several recommendations that can increase the credibility of scientific evidence in psychological journals. One major recommendation is to pay more attention to the power of studies to produce positive results without the help of questionable research practices and to request that authors justify sample sizes with a priori predictions of effect sizes. It is also important to publish replication studies with nonsignificant results if these studies have high power to replicate a published finding.
Less is more, except of course for sample size. (Cohen, 1990, p. 1304)
In 2011, the prestigious Journal of Personality and Social Psychology published an article that provided empirical support for extrasensory perception (ESP; Bem, 2011). The publication of this controversial article created vigorous debates in psychology
departments, the media, and science blogs. In response to this debate, the acting editor and the editor-in-chief felt compelled to write an editorial accompanying the article. The editors defended their decision to publish the article by noting that Bem’s (2011) studies were performed according to standard scientific practices in the field of experimental psychology and that it would seem inappropriate to apply a different standard to studies of ESP (Judd & Gawronski, 2011).
Others took a less sanguine view. They saw the publication of Bem’s (2011) article as a sign that the scientific standards guiding publication decisions are flawed and that Bem’s article served as a glaring example of these flaws (Wagenmakers, Wetzels, Borsboom,
& van der Maas, 2011). In a nutshell, Wagenmakers et al. (2011) argued that the standard statistical model in psychology is biased against the null hypothesis; that is, only findings that are statistically significant are submitted and accepted for publication.
This bias leads to the publication of too many positive (i.e., statistically significant) results. The observation that scientific journals, not only those in psychology,
publish too many statistically significant results is by no means novel. In a seminal article, Sterling (1959) noted that selective reporting of statistically significant results can produce literatures that “consist in substantial part of false conclusions” (p.
Three decades later, Sterling, Rosenbaum, and Weinkam (1995) observed that the “practice leading to publication bias have [sic] not changed over a period of 30 years” (p. 108). Recent articles indicate that publication bias remains a problem in psychological
journals (Fiedler, 2011; John, Loewenstein, & Prelec, 2012; Kerr, 1998; Simmons, Nelson, & Simonsohn, 2011; Strube, 2006; Vul, Harris, Winkielman, & Pashler, 2009; Yarkoni, 2010).
Other sciences have the same problem (Yong, 2012). For example, medical journals have seen an increase in the percentage of retracted articles (Steen, 2011a, 2011b), and there is the concern that a vast number of published findings may be false (Ioannidis,
However, a recent comparison of different scientific disciplines suggested that the bias is stronger in psychology than in some of the older and harder scientific disciplines at the top of a hierarchy of sciences (Fanelli, 2010).
It is important that psychologists use the current crisis as an opportunity to fix problems in the way research is being conducted and reported. The proliferation of eye-catching claims based on biased or fake data can have severe negative consequences for a
science. A New Yorker article warned the public that “all sorts of well-established, multiply confirmed findings have started to look increasingly uncertain. It’s as if our facts were losing their truth: claims that have been enshrined in textbooks are suddenly unprovable” (Lehrer, 2010, p. 1).
If students who read psychology textbooks and the general public lose trust in the credibility of psychological science, psychology loses its relevance because
objective empirical data are the only feature that distinguishes psychological science from other approaches to the understanding of human nature and behavior. It is therefore hard to exaggerate the seriousness of doubts about the credibility of research findings published in psychological journals.
In an influential article, Kerr (1998) discussed one source of bias, namely, hypothesizing after the results are known (HARKing). The practice of HARKing may be attributed to the
high costs of conducting a study that produces a nonsignificant result that cannot be published. To avoid this negative outcome, researchers can design more complex studies that test multiple hypotheses. Chances increase that at least one of the hypotheses
will be supported, if only because Type I error increases (Maxwell, 2004). As noted by Wagenmakers et al. (2011), generations of graduate students were explicitly advised that this questionable research practice is how they should write scientific manuscripts
It is possible that Kerr’s (1998) article undermined the credibility of single-study articles and added to the appeal of multiple-study articles (Diener, 1998; Ledgerwood & Sherman, 2012). After all, it is difficult to generate predictions for significant effects
that are inconsistent across studies. Another advantage is that the requirement of multiple significant results essentially lowers the chances of a Type I error, that is, the probability of falsely rejecting the null hypothesis. For a set of five independent studies,
the requirement to demonstrate five significant replications essentially shifts the probability of a Type I error from p < .05 for a single study to p < .0000003 (i.e., .05^5) for a set of five studies.
This is approximately the same stringent criterion that is being used in particle physics to claim a true discovery (Castelvecchi, 2011). It has been overlooked, however, that researchers have to pay a price to meet more stringent criteria of credibility. To demonstrate significance at a more stringent criterion of significance, it is
necessary to increase sample sizes to reduce the probability of making a Type II error (failing to reject the null hypothesis). This probability is called beta. The inverse probability (1 – beta) is called power. Thus, to maintain high statistical power to demonstrate an effect with a more stringent alpha level requires an
increase in sample sizes, just as physicists had to build a bigger collider to have a chance to find evidence for smaller particles like the Higgs boson particle.
Yet there is no evidence that psychologists are using bigger samples to meet more stringent demands of replicability (Cohen, 1992; Maxwell, 2004; Rossi, 1990; Sedlmeier & Gigerenzer, 1989). This raises the question of how researchers are able to replicate findings in multiple-study articles despite modest power to demonstrate significant effects even within a single study. Researchers can use questionable research
practices (e.g., snooping, not reporting failed studies, dropping dependent variables, etc.; Simmons et al., 2011; Strube, 2006) to dramatically increase the chances of obtaining a false-positive result. Moreover, a survey of researchers indicated that these
practices are common (John et al., 2012), and the prevalence of these practices has raised concerns about the credibility of psychology as a science (Yong, 2012).
An implicit assumption in the field appears to be that the solution to these problems is to further increase the number of positive replication studies that need to be presented to ensure scientific credibility (Ledgerwood & Sherman, 2012). However, the assumption that many replications with significant results provide strong evidence for a hypothesis is an illusion that is akin to the Texas sharpshooter fallacy (Milloy, 1995). Imagine a Texan farmer named Joe. One day he invites you to his farm and shows you a target with nine shots in the bull’s-eye and one shot just outside the bull’s-eye. You are impressed by his shooting abilities until you find out that he cannot repeat this performance when you challenge him to do it again.
[So far, well-known Texan sharpshooters in experimental social psychology have carefully avoided demonstrating their sharp shooting abilities in open replication studies to avoid the embarrassment of not being able to do it again].
Over some beers, Joe tells you that he first fired 10 shots at the barn and then drew the targets after the shots were fired. One problem in science is that reading a research
article is a bit like visiting Joe’s farm. Readers only see the final results, without knowing how the final results were created. Is Joe a sharpshooter who drew a target and then fired 10 shots at the target? Or was the target drawn after the fact? The reason why multiple-study articles are akin to a Texan sharpshooter is that psychological studies have modest power (Cohen, 1962; Rossi, 1990; Sedlmeier & Gigerenzer, 1989). Assuming
60% power for a single study, the probability of obtaining 10 significant results in 10 studies is less than 1% (.6^10 = 0.6%).
I call the probability to obtain only significant results in a set of studies total power. Total power parallels Maxwell’s (2004) concept of all-pair power for multiple comparisons in analysis-of variance designs. Figure 1 illustrates how total power decreases with the number of studies that are being conducted. Eventually, it becomes extremely unlikely that a set of studies produces only significant results. This is especially true if a single study has modest power. When total power is low, it is incredible that a set
of studies yielded only significant results. To avoid the problem of incredible results, researchers would have to increase the power of studies in multiple-study articles.
Table 1 shows how the power of individual studies has to be adjusted to maintain 80% total power for a set of studies. For example, to have 80% total power for five replications, the power of each study has to increase to 96%.
Table 1 also shows the sample sizes required to achieve 80% total power, assuming a simple between-group design, an alpha level of .05 (two-tailed), and Cohen’s
(1992) guidelines for a small (d = .2), moderate, (d = .5), and strong (d = .8) effect.
[To demonstrate a small effect 7 times would require more than 10,000 participants.]
In sum, my main proposition is that psychologists have falsely assumed that increasing the number of replications within an article increases credibility of psychological science. The problem of this practice is that a truly programmatic set of multiple studies
is very costly and few researchers are able to conduct multiple studies with adequate power to achieve significant results in all replication attempts. Thus, multiple-study articles have intensified the pressure to use questionable research methods to compensate for low total power and may have weakened rather than strengthened the credibility of psychological science.
[I believe this is one reason why the replication crisis has hit experimental social psychology the hardest. Other psychologists could use HARKing to tell a false story about a single study, but experimental social psychologists had to manipulate the data to get significance all the time. Experimental cognitive psychologists also have multiple study articles, but they tend to use more powerful within-subject designs, which makes it more credible to get significant results multiple times. The multiple study BS design made it impossible to do so, which resulted in the publication of BS results.]
What Is the Allure of Multiple-Study Articles?
One apparent advantage of multiple-study articles is to provide stronger evidence against the null hypothesis (Ledgerwood & Sherman, 2012). However, the number of studies is irrelevant because the strength of the empirical evidence is a function of the
total sample size rather than the number of studies. The main reason why aggregation across studies reduces randomness as a possible explanation for observed mean differences (or correlations) is that p values decrease with increasing sample size. The
number of studies is mostly irrelevant. A study with 1,000 participants has as much power to reject the null hypothesis as a meta-analysis of 10 studies with 100 participants if it is reasonable to assume a common effect size for the 10 studies. If true effect sizes vary across studies, power decreases because a random-effects model may be more appropriate (Schmidt, 2010; but see Bonett, 2009). Moreover, the most logical approach to reduce concerns about Type I error is to use more stringent criteria for significance (Mudge, Baker, Edge, & Houlahan, 2012). For controversial or very important research findings, the significance level could be set to p < .001 or, as in particle physics, to p <
[Ironically, five years later we have a debate about p < .05 versus p < .005, without even thinking about p < .0000005 or any mention that even a pair of studies with p < .05 in each study effectively have an alpha less than p < .005, namely .0025 to be exact.]
It is therefore misleading to suggest that multiple-study articles are more credible than single-study articles. A brief report with a large sample (N = 1,000) provides more credible evidence than a multiple-study article with five small studies (N = 40, total
N = 200).
The main appeal of multiple-study articles seems to be that they can address other concerns (Ledgerwood & Sherman, 2012). For example, one advantage of multiple studies could be to test the results across samples from diverse populations (Henrich, Heine, & Norenzayan, 2010). However, many multiple-study articles are based on samples drawn from a narrowly defined population (typically, students at the local university). If researchers were concerned about generalizability across a wider range of individuals, multiple-study articles should examine different populations. However, it is not clear why it would be advantageous to conduct multiple independent studies with different populations. To compare populations, it would be preferable to use the same procedures and to analyze the data within a single statistical model with population as a potential moderating factor. Moreover, moderator tests often have low power. Thus, a single study with a large sample and moderator variables is more informative than articles that report separate analyses with small samples drawn from different populations.
Another attraction of multiple-study articles appears to be the ability to provide strong evidence for a hypothesis by means of slightly different procedures. However, even here, single studies can be as good as multiple-study articles. For example, replication across different dependent variables in different studies may mask the fact that studies included multiple dependent variables and researchers picked dependent variables that produced significant results (Simmons et al., 2011). In this case, it seems preferable to
demonstrate generalizability across dependent variables by including multiple dependent variables within a single study and reporting the results for all dependent variables.
One advantage of a multimethod assessment in a single study is that the power to
demonstrate an effect increases for two reasons. First, while some dependent variables may produce nonsignificant results in separate small studies due to low power (Maxwell, 2004), they may all show significant effects in a single study with the total sample size
of the smaller studies. Second, it is possible to increase power further by constraining coefficients for each dependent variable or by using a latent-variable measurement model to test whether the effect is significant across dependent variables rather than for each one independently.
Multiple-study articles are most common in experimental psychology to demonstrate the robustness of a phenomenon using slightly different experimental manipulations. For example, Bem (2011) used a variety of paradigms to examine ESP. Demonstrating
a phenomenon in several different ways can show that a finding is not limited to very specific experimental conditions. Analogously, if Joe can hit the bull’s-eye nine times from different angles, with different guns, and in different light conditions, Joe
truly must be a sharpshooter. However, the variation of experimental procedures also introduces more opportunities for biases (Ioannidis, 2005).
[This is my take down of social psychologists’ claim that multiple conceptual replications test theories, Stroebe & Strack, 2004]
The reason is that variation of experimental procedures allows researchers to discount null findings. Namely, it is possible to attribute nonsignificant results to problems with the experimental procedure rather than to the absence of an effect. In this way, empirical studies no longer test theoretical hypotheses because they can only produce two results: Either they support the theory (p < .05) or the manipulation did not work (p > .05). It is therefore worrisome that Bem noted that “like most social psychological experiments, the experiments reported here required extensive pilot testing” (Bem, 2011, p. 421). If Joe is a sharpshooter, who can hit the bull’s-eye from different angles and with different guns, why does he need extensive training before he can perform the critical shot?
The freedom of researchers to discount null findings leads to the paradox that conceptual replications across multiple studies give the impression that an effect is robust followed by warnings that experimental findings may not replicate because they depend “on subtle and unknown factors” (Bem, 2011, p. 422).
If experimental results were highly context dependent, it would be difficult to explain how studies reported in research articles nearly always produce the expected results. One possible explanation for this paradox is that sampling error in small samples creates the illusion that effect sizes vary systematically, although most of the variation is random. Researchers then pick studies that randomly produced inflated effect sizes and may further inflate them by using questionable research methods to achieve significance (Simmons et al., 2011).
[I was polite when I said “may”. This appears to be exactly what Bem did to get his supernatural effects.]
The final set of studies that worked is then published and gives a false sense of the effect size and replicability of the effect (you should see the other side of Joe’s barn). This may explain why research findings initially seem so impressive, but when other researchers try to build on these seemingly robust findings, it becomes increasingly uncertain whether a phenomenon exists at all (Ioannidis, 2005; Lehrer, 2010).
At this point, a lot of resources have been wasted without providing credible evidence for an effect.
[And then Stroebe and Strack in 2014 suggest that real replication studies that let the data determine the outcome are a waste of resources.]
To increase the credibility of reported findings, it would be better to use all of the resources for one powerful study. For example, the main dependent variable in Bem’s (2011) study of ESP was the percentage of correct predictions of future events.
Rather than testing this ability 10 times with N = 100 participants, it would have been possible to test the main effect of ESP in a single study with 10 variations of experimental procedures and use the experimental conditions as a moderating factor. By testing one
main effect of ESP in a single study with N = 1,000, power would be greater than 99.9% to demonstrate an effect with Bem’s a priori effect size.
At the same time, the power to demonstrate significant moderating effects would be much lower. Thus, the study would lead to the conclusion that ESP does exist but that it is unclear whether the effect size varies as a function of the actual experimental
paradigm. This question could then be examined in follow-up studies with more powerful tests of moderating factors.
In conclusion, it is true that a programmatic set of studies is superior to a brief article that reports a single study if both articles have the same total power to produce significant results (Ledgerwood & Sherman, 2012). However, once researchers use questionable research practices to make up for insufficient total power, multiple-study articles lose their main advantage over single-study articles, namely, to demonstrate generalizability across different experimental manipulations or other extraneous factors.
Moreover, the demand for multiple studies counteracts the demand for more
powerful studies (Cohen, 1962; Maxwell, 2004; Rossi, 1990) because limited resources (e.g., subject pool of PSY100 students) can only be used to increase sample size in one study or to conduct more studies with small samples.
It is therefore likely that the demand for multiple studies within a single article has eroded rather than strengthened the credibility of published research findings
(Steen, 2011a, 2011b), and it is problematic to suggest that multiple-study articles solve the problem that journals publish too many positive results (Ledgerwood & Sherman, 2012). Ironically, the reverse may be true because multiple-study articles provide a
false sense of credibility.
Joe the Magician: How Many Significant Results Are Too Many?
Most people enjoy a good magic show. It is fascinating to see something and to know at the same time that it cannot be real. Imagine that Joe is a well-known magician. In front of a large audience, he fires nine shots from impossible angles, blindfolded, and seemingly through the body of an assistant, who miraculously does not bleed. You cannot figure out how Joe pulled off the stunt, but you know it was a stunt. Similarly, seeing Joe hit the bull’s-eye 1,000 times in a row raises concerns about his abilities as a sharpshooter and suggests that some magic is contributing to this miraculous performance. Magic is fun, but it is not science.
[Before Bem’s article appeared, Steve Heine gave a talk at the University of Toront where he presented multiple studies with manipulations of absurdity (absurdity like Monty Python’s “Biggles: Pioneer Air Fighter; cf. Proulx, Heine, & Vohs, PSPB, 2010). Each absurd manipulation was successful. I didn’t have my magic index then, but I did understand the logic of Sterling et al.’s (1995) argument. So, I did ask whether there were also manipulations that did not work and the answer was affirmative. It was rude at the time to ask about a file drawer before 2011, but a recent twitter discussion suggests that it wouldn’t be rude in 2018. Times are changing.]
The problem is that some articles in psychological journals appear to be more magical than one would expect on the basis of the normative model of science (Kerr, 1998). To increase the credibility of published results, it would be desirable to have a diagnostic tool that can distinguish between credible research findings and those that are likely to be based on questionable research practices. Such a tool would also help to
counteract the illusion that multiple-study articles are superior to single-study articles without leading to the erroneous reverse conclusion that single-study articles are more trustworthy.
[I need to explain why I targeted multiple-study articles in particular. Even the personality section of JPSP started to demand multiple studies because they created the illusion of being more rigorous, e.g., the crazy glucose article was published in that section. At that time, I was still trying to publish as many articles as possible in JPSP and I was not able to compete with crazy science.]
Articles should be evaluated on the basis of their total power to demonstrate consistent evidence for an effect. As such, a single-study article with 80% (total) power is superior to a multiple-study article with 20% total power, but a multiple-study article with 80% total power is superior to a single-study article with 80% power.
The Magic Index (formerly known as the Incredibility Index)
The idea to use power analysis to examine bias in favor of theoretically predicted effects and against the null hypothesis was introduced by Sterling et al. (1995). Ioannidis and Trikalinos (2007) provided a more detailed discussion of this approach for the detection of bias in meta-analyses. Ioannidis and Trikalinos’s exploratory test estimates the probability of the number of reported significant results given the average power of the reported studies. Low p values suggest that there are too many significant results, suggesting that questionable research methods contributed to the reported results. In contrast, the inverse inference is not justified because high p values do not justify the inference that questionable research practices did not contribute to the results. To emphasize this asymmetry in inferential strength, I suggest reversing the exploratory test, focusing on the probability of obtaining more nonsignificant results than were reported in a multiple-study article and calling this index the magic index.
Higher values indicate that there is a surprising lack of nonsignificant results (a.k.a., shots that missed the bull’s eye). The higher the magic index is, the more incredible the observed outcome becomes.
Too many significant results could be due to faking, fudging, or fortune. Thus, the statistical demonstration that a set of reported findings is magical does not prove that questionable research methods contributed to the results in a multiple-study article. However, even when questionable research methods did not contribute to the results, the published results are still likely to be biased because fortune helped to inflate effect sizes and produce more significant results than total power justifies.
Computation of the Incredibility Index
To understand the basic logic of the M-index, it is helpful to consider a concrete example. Imagine a multiple-study article with 10 studies with an average observed effect size of d = .5 and 84 participants in each study (42 in two conditions, total N = 840) and all studies producing a significant result. At first sight, these 10 studies seem to provide strong support against the null hypothesis. However, a post hoc power analysis with the average effect size of d = .5 as estimate of the true effect size reveals that each study had
only 60% power to obtain a significant result. That is, even if the true effect size were d = .5, only six out of 10 studies should have produced a significant result.
The M-index quantifies the probability of the actual outcome (10 out of 10 significant results) given the expected value (six out of 10 significant results) using binomial
probability theory. From the perspective of binomial probability theory, the scenario
is analogous to an urn problem with replacement with six green balls (significant) and four red balls (nonsignificant). The binomial probability to draw at least one red ball in 10 independent draws is 99.4%. (Stat Trek, 2012).
That is, 994 out of 1,000 multiple-study articles with 10 studies and 60% average power
should have produced at least one nonsignificant result in one of the 10 studies. It is therefore incredible if an article reports 10 significant results because only six out of 1,000 attempts would have produced this outcome simply due to chance alone.
[I now realize that observed power of 60% would imply that the null-hypothesis is true because observed power is also inflated by selecting for significance. As 50% observed poewr is needed to achieve significance and chance cannot produce the same observed power each time, the minimum observed power is 62%!]
One of the main problems for power analysis in general and the computation of the IC-index in particular is that the true effect size is unknown and has to be estimated. There are three basic approaches to the estimation of true effect sizes. In rare cases, researchers provide explicit a priori assumptions about effect sizes (Bem, 2011). In this situation, it seems most appropriate to use an author’s stated assumptions about effect sizes to compute power with the sample sizes of each study. A second approach is to average reported effect sizes either by simply computing the mean value or by weighting effect sizes by their sample sizes. Averaging of effect sizes has the advantage that post hoc effect size estimates of single studies tend to have large confidence intervals. The confidence intervals shrink when effect sizes are aggregated across
studies. However, this approach has two drawbacks. First, averaging of effect sizes makes strong assumptions about the sampling of studies and the distribution of effect sizes (Bonett, 2009). Second, this approach assumes that all studies have the same effect
size, which is unlikely if a set of studies used different manipulations and dependent variables to demonstrate the generalizability of an effect. Ioannidis and Trikalinos (2007) were careful to warn readers that “genuine heterogeneity may be mistaken for bias” (p.
[I did not know about Ioannidis and Trikalinos’s (2007) article when I wrote the first draft. Maybe that is a good thing because I might have followed their approach. However, my approach is different from their approach and solves the problem of pooling effect sizes. Claiming that my method is the same as Trikalinos’s method is like confusing random effects meta-analysis with fixed-effect meta-analysis]
To avoid the problems of average effect sizes, it is promising to consider a third option. Rather than pooling effect sizes, it is possible to conduct post hoc power analysis for each study. Although each post hoc power estimate is associated with considerable sampling error, sampling errors tend to cancel each other out, and the M-index for a set of studies becomes more accurate without having to assume equal effect sizes in all studies.
Unfortunately, this does not guarantee that the M-index is unbiased because power is a nonlinear function of effect sizes. Yuan and Maxwell (2005) examined the implications of this nonlinear relationship. They found that the M-index may provide inflated estimates of average power, especially in small samples where observed effect sizes vary widely around the true effect size. Thus, the M-index is conservative when power is low and magic had to be used to create significant results.
In sum, it is possible to use reported effect sizes to compute post hoc power and to use post hoc power estimates to determine the probability of obtaining a significant result. The post hoc power values can be averaged and used as the probability for a successful
outcome. It is then possible to use binomial probability theory to determine the probability that a set of studies would have produced equal or more nonsignificant results than were actually reported. This probability is [now] called the M-index.
[Meanwhile, I have learned that it is much easier to compute observed power based on reported test statistics like t, F, and chi-square values because observed power is determined by these statistics.]
Example 1: Extrasensory Perception (Bem, 2011)
I use Bem’s (2011) article as an example because it may have been a tipping point for the current scientific paradigm in psychology (Wagenmakers et al., 2011).
[I am still waiting for EJ to return the favor and cite my work.]
The editors explicitly justified the publication of Bem’s article on the grounds that it was subjected to a rigorous review process, suggesting that it met current standards of scientific practice (Judd & Gawronski, 2011). In addition, the editors hoped that the publication of Bem’s article and Wagenmakers et al.’s (2011) critique would stimulate “critical further thoughts about appropriate methods in research on social cognition and attitudes” (Judd & Gawronski, 2011, p. 406).
A first step in the computation of the M-index is to define the set of effects that are being examined. This may seem trivial when the M-index is used to evaluate the credibility of results in a single article, but multiple-study articles contain many results and it is not always obvious that all results should be included in the analysis (Maxwell, 2004).
[Same here. Maxwell accepted my article, but apparently doesn’t think it is useful to cite when he writes about the replication crisis.]
[deleted minute details about Bem’s study here.]
Another decision concerns the number of hypotheses that should be examined. Just as multiple studies reduce total power, tests of multiple hypotheses within a single study also reduce total power (Maxwell, 2004). Francis (2012b) decided to focus only on the
hypothesis that ESP exists, that is, that the average individual can foresee the future. However, Bem (2011) also made predictions about individual differences in ESP. Therefore, I used all 19 effects reported in Table 7 (11 ESP effects and eight personality effects).
[I deleted the section that explains alternative approaches that rely on effect sizes rather than observed power here.]
I used G*Power 3.1.2 to obtain post hoc power on the basis of effect sizes and sample sizes (Faul, Erdfelder, Buchner, & Lang, 2009).
The M-index is more powerful when a set of studies contains only significant results. In this special case, the M-index is the inverse probability of total power.
[An article by Fabrigar and Wegener misrepresents my article and confuses the M-Index with total power. When articles do report non-significant result and honestly report them as failures to reject the null-hypothesis (not marginal significance), it is necessary to compute the binomial probability to get the M-Index.]
[Again, I deleted minute computations for Bem’s results.]
Using the highest magic estimates produces a total Magic-Index of 99.97% for Bem’s 17 results. Thus, it is unlikely that Bem (2011) conducted 10 studies, ran 19 statistical tests of planned hypotheses, and obtained 14 statisstically significant results.
Yet the editors felt compelled to publish the manuscript because “we can only take the author at his word that his data are in fact genuine and that the reported findings have not been taken from a larger set of unpublished studies showing null effects” (Judd & Gawronski, 2011, p. 406).
[It is well known that authors excluded disconfirming evidence and that editors sometimes even asked authors to engage in this questionable research practice. However, this quote implies that the editors asked Bem about failed studies and that he assured them that there are no failed studies, which may have been necessary to publish these magical results in JPSP. If Bem did not disclose failed studies on request and these studies exist, it would violate even the lax ethical standards of the time that mostly operated on a “don’t ask don’t tell” basis. ]
The M-index provides quantitative information about the credibility of this assumption and would have provided the editors with objective information to guide their decision. More importantly, awareness about total power could have helped Bem to plan fewer studies with higher total power to provide more credible evidence for his hypotheses.
Example 2: Sugar High—When Rewards Undermine Self-Control
Bem’s (2011) article is exceptional in that it examined a controversial phenomenon. I used another nine-study article that was published in the prestigious Journal of Personality and Social Psychology to demonstrate that low total power is also a problem
for articles that elicit less skepticism because they investigate less controversial hypotheses. Gailliot et al. (2007) examined the relation between blood glucose levels and self-regulation. I chose this article because it has attracted a lot of attention (142 citations in Web of Science as of May 2012; an average of 24 citations per year) and it is possible to evaluate the replicability of the original findings on the basis of subsequent studies by other researchers (Dvorak & Simons, 2009; Kurzban, 2010).
[If anybody needs evidence that citation counts are a silly indicator of quality, here it is: the article has been cited 80 times in 2014, 64 times in 2015, 63 times in 2016, and 61 times in 2017. A good reason to retract it, if JPSP and APA cares about science and not just impact factors.]
Sample sizes were modest, ranging from N = 12 to 102. Four studies had sample sizes of N < 20, which Simmons et al. (2011) considered to require special justification. The total N is 359 participants. Table 1 shows that this total sample
size is sufficient to have 80% total power for four large effects or two moderate effects and is insufficient to demonstrate a [single] small effect. Notably, Table 4 shows that all nine reported studies produced significant results.
The M-Index for these 9 studies was greater than 99%. This indicates that from a statistical point of view, Bem’s (2011) evidence for ESP is more credible than Gailliot et al.’s (2007) evidence for a role of blood glucose in self-regulation.
A more powerful replication study with N = 180 participants provides more conclusive evidence (Dvorak & Simons, 2009). This study actually replicated Gailliot et al.’s (1997) findings in Study 1. At the same time, the study failed to replicate the results for Studies 3–6 in the original article. Dvorak and Simons (2009) did not report the correlation, but the authors were kind enough to provide this information. The correlation was not significant in the experimental group, r(90) = .10, and the control group, r(90) =
.03. Even in the total sample, it did not reach significance, r(180) = .11. It is therefore extremely likely that the original correlations were inflated because a study with a sample of N = 90 has 99.9% power to produce a significant effect if the true effect
size is r = .5. Thus, Dvorak and Simons’s results confirm the prediction of the M-index that the strong correlations in the original article are incredible.
In conclusion, Gailliot et al. (2007) had limited resources to examine the role of blood glucose in self-regulation. By attempting replications in nine studies, they did not provide strong evidence for their theory. Rather, the results are incredible and difficult to replicate, presumably because the original studies yielded inflated effect sizes. A better solution would have been to test the three hypotheses in a single study with a large sample. This approach also makes it possible to test additional hypotheses, such as mediation (Dvorak & Simons, 2009). Thus, Example 2 illustrates that
a single powerful study is more informative than several small studies.
Fifty years ago, Cohen (1962) made a fundamental contribution to psychology by emphasizing the importance of statistical power to produce strong evidence for theoretically predicted effects. He also noted that most studies at that time had only sufficient power to provide evidence for strong effects. Fifty years later, power
analysis remains neglected. The prevalence of studies with insufficient power hampers scientific progress in two ways. First, there are too many Type II errors that are often falsely interpreted as evidence for the null hypothesis (Maxwell, 2004). Second, there
are too many false-positive results (Sterling, 1959; Sterling et al., 1995). Replication across multiple studies within a single article has been considered a solution to these problems (Ledgerwood & Sherman, 2012). The main contribution of this article is to point out that multiple-study articles do not provide more credible evidence simply because they report more statistically significant results. Given the modest power of individual studies, it is even less credible that researchers were able to replicate results repeatedly in a series of studies than that they obtained a significant effect in a single study.
The demonstration that multiple-study articles often report incredible results might help to reduce the allure of multiple-study articles (Francis, 2012a, 2012b). This is not to say that multiple-study articles are intrinsically flawed or that single-study articles are superior. However, more studies are only superior if total power is held constant, yet limited resources create a trade-off between the number of studies and total power of a set of studies.
To maintain credibility, it is better to maximize total power rather than number of studies. In this regard, it is encouraging that some editors no longer consider number ofstudies as a selection criterion for publication (Smith, 2012).
[Over the past years, I have been disappointed by many psychologists that I admired or respected. I loved ER Smith’s work on exemplar models that influenced my dissertation work on frequency estimation of emotion. In 2012, I was hopeful that he would make real changes, but my replicability rankings show that nothing changed during his term as editor of the JPSP section that published Bem’s article. Five wasted years and nobody can say he couldn’t have known better.]
Subsequently, I first discuss the puzzling question of why power continues to be ignored despite the crucial importance of power to obtain significant results without the help of questionable research methods. I then discuss the importance of paying more attention to total power to increase the credibility of psychology as a science. Due to space limitations, I will not repeat many other valuable suggestions that have been made to improve the current scientific model (Schooler, 2011; Simmons et al., 2011; Spellman, 2012; Wagenmakers et al., 2011).
In my discussion, I will refer to Bem’s (2011) and Gailliot et al.’s (2007) articles, but it should be clear that these articles merely exemplify flaws of the current scientific
paradigm in psychology.
Why Do Researchers Continue to Ignore Power?
Maxwell (2004) proposed that researchers ignore power because they can use a shotgun approach. That is, if Joe sprays the barn with bullets, he is likely to hit the bull’s-eye at least once. For example, experimental psychologists may use complex factorial
designs that test multiple main effects and interactions to obtain at
least one significant effect (Maxwell, 2004).
Psychologists who work with many variables can test a large number of correlations
to find a significant one (Kerr, 1998). Although studies with small samples have modest power to detect all significant effects (low total power), they have high power to detect at least one significant effect (Maxwell, 2004).
The shotgun model is unlikely to explain incredible results in multiple-study articles because the pattern of results in a set of studies has to be consistent. This has been seen as the main strength of multiple-study articles (Ledgerwood & Sherman, 2012).
However, low total power in multiple-study articles makes it improbable that all studies produce significant results and increases the pressure on researchers to use questionable research methods to comply with the questionable selection criterion that
manuscripts should report only significant results.
A simple solution to this problem would be to increase total power to avoid
having to use questionable research methods. It is therefore even more puzzling why the requirement of multiple studies has not resulted in an increase in power.
One possible explanation is that researchers do not care about effect sizes. Researchers may not consider it unethical to use questionable research methods that inflate effect sizes as long as they are convinced that the sign of the reported effect is consistent
with the sign of the true effect. For example, the theory that implicit attitudes are malleable is supported by a positive effect of experimental manipulations on the implicit association test, no matter whether the effect size is d = .8 (Dasgupta & Greenwald,
2001) or d = .08 (Joy-Gaba & Nosek, 2010), and the influence of blood glucose levels on self-control is supported by a strong correlation of r = .6 (Gailliot et al., 2007) and a weak correlation of r = .1 (Dvorak & Simons, 2009).
The problem is that in the real world, effect sizes matter. For example, it matters whether exercising for 20 minutes twice a week leads to a weight loss of one
pound or 10 pounds. Unbiased estimates of effect sizes are also important for the integrity of the field. Initial publications with stunning and inflated effect sizes produce underpowered replication studies even if subsequent researchers use a priori power analysis.
As failed replications are difficult to publish, inflated effect sizes are persistent and can bias estimates of true effect sizes in meta-analyses. Failed replication studies in file drawers also waste valuable resources (Spellman, 2012).
In comparison to one small (N = 40) published study with an inflated effect size and
nine replication studies with nonsignificant replications in file drawers (N = 360), it would have been better to pool the resources of all 10 studies for one strong test of an important hypothesis (N = 400).
A related explanation is that true effect sizes are often likely to be small to moderate and that researchers may not have sufficient resources for unbiased tests of their hypotheses. As a result, they have to rely on fortune (Wegner, 1992) or questionable research
methods (Simmons et al., 2011; Vul et al., 2009) to report inflated observed effect sizes that reach statistical significance in small samples.
Another explanation is that researchers prefer small samples to large samples because small samples have less power. When publications do not report effect sizes, sample sizes become an imperfect indicator of effect sizes because only strong effects
reach significance in small samples. This has led to the flawed perception that effect sizes in large samples have no practical significance because even effects without practical significance can reach statistical significance (cf. Royall, 1986). This line of
reasoning is fundamentally flawed and confounds credibility of scientific evidence with effect sizes.
The most probable and banal explanation for ignoring power is poor statistical training at the undergraduate and graduate levels. Discussions with colleagues and graduate students suggest that power analysis is mentioned, but without a sense of importance.
[I have been preaching about power for years in my department and it became a running joke for students to mention power in their presentation without having any effect on research practices until 2011. Fortunately, Bem unintentionally made it able to convince some colleagues that power is important.]
Research articles also reinforce the impression that power analysis is not important as sample sizes vary seemingly at random from study to study or article to article. As a result, most researchers probably do not know how risky their studies are and how lucky they are when they do get significant and inflated effects.
I hope that this article will change this and that readers take total power into account when they read the next article with five or more studies and 10 or more significant results and wonder whether they have witnessed a sharpshooter or have seen a magic show.
Finally, it is possible that researchers ignore power simply because they follow current practices in the field. Few scientists are surprised that published findings are too good to be true. Indeed, a common response to presentations of this work has been that the M-index only shows the obvious. Everybody knows that researchers use a number of questionable research practices to increase their chances of reporting significant results, and a high percentage of researchers admit to using these practices, presumably
because they do not consider them to be questionable (John et al., 2012).
[Even in 2014, Stroebe and Strack claim that it is not clear which practices should be considered questionable, whereas my undergraduate students have no problem realizing that hiding failed studies undermines the purpose of doing an empirical study in the first place.]
The benign view of current practices is that successful studies provide all of the relevant information. Nobody wants to know about all the failed attempts of alchemists to turn base metals into gold, but everybody would want to know about a process that
actually achieves this goal. However, this logic rests on the assumption that successful studies were really successful and that unsuccessful studies were really flawed. Given the modest power of studies, this conclusion is rarely justified (Maxwell, 2004).
To improve the status of psychological science, it will be important to elevate the scientific standards of the field. Rather than pointing to limited resources as an excuse,
researchers should allocate resources more wisely (spend less money on underpowered studies) and conduct more relevant research that can attract more funding. I think it would be a mistake to excuse the use of questionable research practices by pointing out that false discoveries in psychological research have less dramatic consequences than drugs with little benefits, huge costs, and potential side effects.
Therefore, I disagree with Bem’s (2000) view that psychologists should “err on the side of discovery” (p. 5).
[Yup, he wrote that in a chapter that was used to train graduate students in social psychology in the art of magic.]
Recommendations for Improvement
Use Power in the Evaluation of Manuscripts
Granting agencies often ask that researchers plan studies with adequate power (Fritz & MacKinnon, 2007). However, power analysis is ignored when researchers report their results. The reason is probably that (a priori) power analysis is only seen as a way to ensure that a study produces a significant result. Once a significant finding has been found, low power no longer seems to be a problem. After all, a significant effect was found (in one condition, for male participants, after excluding two outliers, p =
One way to improve psychological science is to require researchers to justify sample sizes in the method section. For multiple-study articles, researchers should be asked to compute total power.
[This is something nobody has even started to discuss. Although there are more and more (often questionable) a priori power calculations in articles, they tend to aim for 80% power for a single hypothesis test, but these articles often report multiple studies or multiple hypothesis tests in a single article. The power to get two significant results with 80-% for each test is only 64%. ]
If a study has 80% total power, researchers should also explain how they would deal with the possible outcome of a nonsignificant result. Maybe it would change the perception of research contributions when a research article reports 10 significant
results, although power was only sufficient to obtain six. Implementing this policy would be simple. Thus, it is up to editors to realize the importance of statistical power and to make power an evaluation criterion in the review process (Cohen, 1992).
Implementing this policy could change the hierarchy of psychological
journals. Top journals would no longer be the journals with the most inflated effect sizes but, rather, the journals with the most powerful studies and the most credible scientific evidence.
[Based on this idea, I started developing my replicability rankings of journals. And they show that impact factors still do not take replicability into account.]
Reward Effort Rather Than Number of Significant Results
Another recommendation is to pay more attention to the total effort that went into an empirical study rather than the number of significant p values. The requirement to have multiple studies with no guidelines about power encourages a frantic empiricism in
which researchers will conduct as many cheap and easy studies as possible to find a set of significant results.
[And if power is taken into account, researchers now do six cheap Mturk studies. Although this is better than six questionable studies, it does not correct the problem that good research often requires a lot of resources.]
It is simply too costly for researchers to invest in studies with observation of real behaviors, high ecological validity, or longitudinal assessments that take
time and may produce a nonsignificant result.
Given the current environmental pressures, a low-quality/high-quantity strategy is
more adaptive and will ensure survival (publish or perish) and reproductive success (more graduate students who pursue a lowquality/ high-quantity strategy).
[It doesn’t help to become a meta-psychologists. Which smart undergraduate student would risk the prospect of a career by becoming a meta-psychologist?]
A common misperception is that multiple-study articles should be rewarded because they required more effort than a single study. However, the number of studies is often a function of the difficulty of conducting research. It is therefore extremely problematic to
assume that multiple studies are more valuable than single studies.
A single longitudinal study can be costly but can answer questions that multiple cross-sectional studies cannot answer. For example, one of the most important developments in psychological measurement has been the development of the implicit association test
(Greenwald, McGhee, & Schwartz, 1998). A widespread belief about the implicit association test is that it measures implicit attitudes that are more stable than explicit attitudes (Gawronski, 2009), but there exist hardly any longitudinal studies of the stability of implicit attitudes.
[I haven’t checked but I don’t think this has changed much. Cross-sectional Mturk studies can still produce sexier results than a study that simply estimates the stability of the same measure over time. Social psychologists tend to be impatient creatures (e.g., Bem)]
A simple way to change the incentive structure in the field is to undermine the false belief that multiple-study articles are better than single-study articles. Often multiple studies are better combined into a single study. For example, one article published four studies that were identical “except that the exposure duration—suboptimal (4 ms)
or optimal (1 s)—of both the initial exposure phase and the subsequent priming phase was orthogonally varied” (Murphy, Zajonc, & Monahan, 1995, p. 589). In other words, the four studies were four conditions of a 2 x 2 design. It would have been more efficient and
informative to combine the information of all studies in a single study. In fact, after reporting each study individually, the authors reported the results of a combined analysis. “When all four studies are entered into a single analysis, a clear pattern emerges” (Murphy et al., 1995, p. 600). Although this article may be the most extreme example of unnecessary multiplicity, other multiple-study articles could also be more informative by reducing the number of studies in a single article.
Apparently, readers of scientific articles are aware of the limited information gain provided by multiple-study articles because citation counts show that multiple-study articles do not have more impact than single-study articles (Haslam et al., 2008). Thus, editors should avoid using number of studies as a criterion for accepting articles.
Allow Publication of Nonsignificant Results
The main point of the M-index is to alert researchers, reviewers, editors, and readers of scientific articles that a series of studies that produced only significant results is neither a cause for celebration nor strong evidence for the demonstration of a scientific discovery; at least not without a power analysis that shows the results are credible.
Given the typical power of psychological studies, nonsignificant findings should be obtained regularly, and the absence of nonsignificant results raises concerns about the credibility of published research findings.
Most of the time, biases may be benign and simply produce inflated effect sizes, but occasionally, it is possible that biases may have more serious consequences (e.g.,
demonstrate phenomena that do not exist).
A perfectly planned set of five studies, where each study has 80% power, is expected to produce one nonsignificant result. It is not clear why editors sometimes ask researchers to remove studies with nonsignificant results. Science is not a beauty contest, and a
nonsignificant result is not a blemish.
This wisdom is captured in the Japanese concept of wabi-sabi, in which beautiful objects are designed to have a superficial imperfection as a reminder that nothing is perfect. On the basis of this conception of beauty, a truly perfect set of studies is one that echoes the imperfection of reality by including failed studies or studies that did not produce significant results.
Even if these studies are not reported in great detail, it might be useful to describe failed studies and explain how they informed the development of studies that produced significant results. Another possibility is to honestly report that a study failed to produce a significant result with a sample size that provided 80% power and that the researcher then added more participants to increase power to 95%. This is different from snooping (looking at the data until a significant result has been found), especially if it is stated clearly that the sample size was increased because the effect was not significant with the originally planned sample size and the significance test has been adjusted to take into account that two significance tests were performed.
The M-index rewards honest reporting of results because reporting of null findings renders the number of significant results more consistent with the total power of the studies. In contrast, a high M-index can undermine the allure of articles that report more significant results than the power of the studies warrants. In this
way, post-hoc power analysis could have the beneficial effect that researchers finally start paying more attention to a priori power.
Limited resources may make it difficult to achieve high total power. When total power is modest, it becomes important to report nonsignificant results. One way to report nonsignificant results would be to limit detailed discussion to successful studies but to
include studies with nonsignificant results in a meta-analysis. For example, Bem (2011) reported a meta-analysis of all studies covered in the article. However, he also mentioned several pilot studies and a smaller study that failed to produce a significant
result. To reduce bias and increase credibility, pilot studies or other failed studies could be included in a meta-analysis at the end of a multiple-study article. The meta-analysis could show that the effect is significant across an unbiased sample of studies that produced significant and nonsignificant results.
This overall effect is functionally equivalent to the test of the hypothesis in a single
study with high power. Importantly, the meta-analysis is only credible if it includes nonsignificant results.
[Since then, several articles have proposed meta-analyses and given tutorials on mini-meta-analysis without citing my article and without clarifying that these meta-analysis are only useful if all evidence is included and without clarifying that bias tests like the M-Index can reveal whether all relevant evidence was included.]
It is also important that top journals publish failed replication studies. The reason is that top journals are partially responsible for the contribution of questionable research practices to published research findings. These journals look for novel and groundbreaking studies that will garner many citations to solidify their position
as top journals. As everywhere else (e.g., investing), the higher payoff comes with a higher risk. In this case, the risk is publishing false results. Moreover, the incentives for researchers to get published in top journals or get tenure at Ivy League universities
increases the probability that questionable research practices contribute
to articles in the top journals (Ledford, 2010). Stapel faked data to get a publication in Science, not to get a publication in Psychological Reports.
There are positive signs that some journal editors are recognizing their responsibility for publication bias (Dirnagl & Lauritzen, 2010). The medical journal Journal of Cerebral Blood Flow and Metabolism created a section that allows researchers to publish studies with disconfirmatory evidence so that this evidence is published in the same journal. One major advantage of having this section in top journals is that it may change the evaluation criteria of journal editors toward a more careful assessment of Type I error when they accept a manuscript for publication. After all, it would be quite embarrassing to publish numerous articles that erred on the side of discovery if subsequent issues reveal that these discoveries were illusory.
[After some pressure from social media, JPSP did publish failed replications of Bem, and it now has a replication section (online only). Maybe somebody can dig up some failed replications of glucose studies, I know they exist, or do one more study to publish in JPSP that, just like ESP, glucose is a myth.]
It could also reduce the use of questionable research practices by researchers eager to publish in prestigious journals if there was a higher likelihood that the same journal will publish failed replications by independent researchers.It might also motivate more researchers to conduct rigorous replication studies if they can bet against a finding and hope to get a publication in a prestigious journal.
The M-index can be helpful in putting pressure on editors and journals to curb the proliferation of false-positive results because it can be used to evaluate editors and journals in terms of the credibility of the results that are published in these journals.
As everybody knows, the value of a brand rests on trust, and it is easy to destroy this value when consumers lose that trust. Journals that continue to publish incredible results and suppress contradictory replication studies are not going to survive, especially given the fact that the Internet provides an opportunity for authors of repressed replication studies to get their findings out (Spellman, 2012).
[I wrote this in the third revision when I thought the editor would not want to see the manuscript again.]
[I deleted the section where I pick on Ritchie’s failed replications of Bem because three studies with small studies of N = 50 are underpowered and can be dismissed as false positives. Replication studies should have at least the sample size of original studies which was N = 100 for most of Bem’s studies.]
Another solution would be to ignore p values altogether and to focus more on effect sizes and confidence intervals (Cumming & Finch, 2001). Although it is impossible to demonstrate that the true effect size is exactly zero, it is possible to estimate
true effect sizes with very narrow confidence intervals. For example, a sample of N = 1,100 participants would be sufficient to demonstrate that the true effect size of ESP is zero with a narrow confidence interval of plus or minus .05.
If an even more stringent criterion is required to claim a null effect, sample sizes would have to increase further, but there is no theoretical limit to the precision of effect size estimates. No matter whether the focus is on p values or confidence intervals, Cohen’s recommendation that bigger is better, at least for sample sizes, remains true because large samples are needed to obtain narrow confidence intervals (Goodman & Berlin, 1994).
Changing paradigms is a slow process. It took decades to unsettle the stronghold of behaviorism as the main paradigm in psychology. Despite Cohen’s (1962) important contribution to the field 50 years ago and repeated warnings about the problems of underpowered studies, power analysis remains neglected (Maxwell, 2004; Rossi, 1990; Sedlmeier & Gigerenzer, 1989). I hope the M-index can make a small contribution toward the goal of improving the scientific standards of psychology as a science.
Bem’s (2011) article is not going to be a dagger in the heart of questionable research practices, but it may become the historic marker of a paradigm shift.
There are positive signs in the literature on meta-analysis (Sutton & Higgins, 2008), the search for better statistical methods (Wagenmakers, 2007)*, the call for more
open access to data (Schooler, 2011), changes in publication practices of journals (Dirnagl & Lauritzen, 2010), and increasing awareness of the damage caused by questionable research practices (Francis, 2012a, 2012b; John et al., 2012; Kerr, 1998; Simmons
et al., 2011) to be hopeful that a paradigm shift may be underway.
[Another sad story. I did not understand Wagenmaker’s use of Bayesian methods at the time and I honestly thought this work might make a positive contribution. However, in retrospect I realize that Wagenmakers is more interested in selling his statistical approach at any cost and disregards criticisms of his approach that have become evident in recent years. And, yes, I do understand how the method works and why it will not solve the replication crisis (see commentary by Carlsson et al., 2017, in Psychological Science).]
Even the Stapel debacle (Heatherton, 2010), where a prominent psychologist admitted to faking data, may have a healthy effect on the field.
[Heaterton emailed me and I thought he was going to congratulate me on my nice article or thank me for citing him, but he was mainly concerned that quoting him in the context of Stapel might give the impression that he committed fraud.]
After all, faking increases Type I error by 100% and is clearly considered unethical. If questionable research practices can increase Type I error by up to 60% (Simmons et al., 2011), it becomes difficult to maintain that these widely used practices are questionable but not unethical.
[I guess I was a bit optimistic here. Apparently, you can hide as many studies as you want, but you cannot change one data point because that is fraud.]
During the reign of a paradigm, it is hard to imagine that things will ever change. However, for most contemporary psychologists, it is also hard to imagine that there was a time when psychology was dominated by animal research and reinforcement schedules. Older psychologists may have learned that the only constant in life is change.
[Again, too optimistic. Apparently, many old social psychologists still believe things will remain the same as they always were. Insert head in the sand cartoon here.]
I have been fortunate enough to witness historic moments of change such as the falling of the Berlin Wall in 1989 and the end of behaviorism when Skinner gave his last speech at the convention of the American Psychological Association in 1990. In front of a packed auditorium, Skinner compared cognitivism to creationism. There was dead silence, made more audible by a handful of grey-haired members in the audience who applauded
[Only I didn’t realize that research in 1990 had other problems. Nowadays I still think that Skinner was just another professor with a big ego and some published #me_too allegations to his name, but he was right in his concerns about (social) cognitivism as not much more scientific than creationism.]
I can only hope to live long enough to see the time when Cohen’s valuable contribution to psychological science will gain the prominence that it deserves. A better understanding of the need for power will not solve all problems, but it will go a long way toward improving the quality of empirical studies and the credibility of results published in psychological journals. Learning about power not only empowers researchers to conduct studies that can show real effects without the help of questionable research practices but also empowers them to be critical consumers of published research findings.
Knowledge about power is power.
Bem, D. J. (2000). Writing an empirical article. In R. J. Sternberg (Ed.), Guide
to publishing in psychological journals (pp. 3–16). Cambridge, England:
Cambridge University Press. doi:10.1017/CBO9780511807862.002
Bem, D. J. (2011). Feeling the future: Experimental evidence for anomalous
retroactive influences on cognition and affect. Journal of Personality
and Social Psychology, 100, 407–425. doi:10.1037/a0021524
Bonett, D. G. (2009). Meta-analytic interval estimation for standardized
and unstandardized mean differences. Psychological Methods, 14, 225–
Cohen, J. (1962). Statistical power of abnormal–social psychological research:
A review. Journal of Abnormal and Social Psychology, 65,
Cohen, J. (1990). Things I have learned (so far). American Psychologist,
45, 1304–1312. doi:10.1037/0003-066X.45.12.1304
Cohen, J. (1992). A power primer. Psychological Bulletin, 112, 155–159.
Dasgupta, N., & Greenwald, A. G. (2001). On the malleability of automatic
attitudes: Combating automatic prejudice with images of admired and
disliked individuals. Journal of Personality and Social Psychology, 81,
Diener, E. (1998). Editorial. Journal of Personality and Social Psychology,
74, 5–6. doi:10.1037/h0092824
Dirnagl, U., & Lauritzen, M. (2010). Fighting publication bias: Introducing
the Negative Results section. Journal of Cerebral Blood Flow and
Metabolism, 30, 1263–1264. doi:10.1038/jcbfm.2010.51
Dvorak, R. D., & Simons, J. S. (2009). Moderation of resource depletion
in the self-control strength model: Differing effects of two modes of
self-control. Personality and Social Psychology Bulletin, 35, 572–583.
Erdfelder, E., Faul, F., & Buchner, A. (1996). GPOWER: A general power
analysis program. Behavior Research Methods, 28, 1–11. doi:10.3758/
Fanelli, D. (2010). “Positive” results increase down the hierarchy of the
sciences. PLoS One, 5, Article e10068. doi:10.1371/journal.pone
Faul, F., Erdfelder, E., Buchner, A., & Lang, A. G. (2009). Statistical
power analyses using G*Power 3.1: Tests for correlation and regression
analyses. Behavior Research Methods, 41, 1149–1160. doi:10.3758/
Faul, F., Erdfelder, E., Lang, A. G., & Buchner, A. (2007). G*Power 3: A
flexible statistical power analysis program for the social, behavioral, and
biomedical sciences. Behavior Research Methods, 39, 175–191. doi:
Fiedler, K. (2011). Voodoo correlations are everywhere—not only in
neuroscience. Perspectives on Psychological Science, 6, 163–171. doi:
Francis, G. (2012a). The same old New Look: Publication bias in a study
of wishful seeing. i-Perception, 3, 176–178. doi:10.1068/i0519ic
Francis, G. (2012b). Too good to be true: Publication bias in two prominent
studies from experimental psychology. Psychonomic Bulletin & Review,
19, 151–156. doi:10.3758/s13423-012-0227-9
Fritz, M. S., & MacKinnon, D. P. (2007). Required sample size to detect
the mediated effect. Psychological Science, 18, 233–239. doi:10.1111/
Gailliot, M. T., Baumeister, R. F., DeWall, C. N., Maner, J. K., Plant,
E. A., Tice, D. M., & Schmeichel, B. J. (2007). Self-control relies on
glucose as a limited energy source: Willpower is more than a metaphor.
Journal of Personality and Social Psychology, 92, 325–336. doi:
Gawronski, B. (2009). Ten frequently asked questions about implicit
measures and their frequently supposed, but not entirely correct answers.
Canadian Psychology/Psychologie canadienne, 50, 141–150. doi:
Goodman, S. N., & Berlin, J. A. (1994). The use of predicted confidence
intervals when planning experiments and the misuse of power when
interpreting results. Annals of Internal Medicine, 121, 200–206.
Greenwald, A. G., McGhee, D. E., & Schwartz, J. L. K. (1998). Measuring
individual differences in implicit cognition: The implicit association test.
Journal of Personality and Social Psychology, 74, 1464–1480. doi:
Haslam, N., Ban, L., Kaufmann, L., Loughnan, S., Peters, K., Whelan, J.,
& Wilson, S. (2008). What makes an article influential? Predicting
impact in social and personality psychology. Scientometrics, 76, 169–
Henrich, J., Heine, S. J., & Norenzayan, A. (2010). The weirdest people in
the world? Behavioral and Brain Sciences, 33, 61–83. doi:10.1017/
Ioannidis, J. P. A. (2005). Why most published research findings are false.
PLoS Medicine, 2(8), Article e124. doi:10.1371/journal.pmed.0020124
Ioannidis, J. P. A., & Trikali nos, T. A. (2007). An exploratory test for an
excess of significant findings. Clinical Trials, 4, 245–253. doi:10.1177/
John, L. K., Loewenstein, G., & Prelec, D. (2012). Measuring the prevalence
of questionable research practices with incentives for truth telling.
Psychological Science, 23, 524–532. doi:10.1177/0956797611430953
Joy-Gaba, J. A., & Nosek, B. A. (2010). The surprisingly limited malleability
of implicit racial evaluations. Social Psychology, 41, 137–146.
Judd, C. M., & Gawronski, B. (2011). Editorial comment. Journal of
Personality and Social Psychology, 100, 406. doi:10.1037/0022789
Kerr, N. L. (1998). HARKing: Hypothezising after the results are known.
Personality and Social Psychology Review, 2, 196–217. doi:10.1207/
Kurzban, R. (2010). Does the brain consume additional glucose during
self-control tasks? Evolutionary Psychology, 8, 244–259.
Ledford, H. (2010, August 17). Harvard probe kept under wraps. Nature,
466, 908–909. doi:10.1038/466908a
Ledgerwood, A., & Sherman, J. W. (2012). Short, sweet, and problematic?
The rise of the short report in psychological science. Perspectives on Psychological Science, 7, 60–66. doi:10.1177/1745691611427304
Maxwell, S. E. (2004). The persistence of underpowered studies in psychological
research: Causes, consequences, and remedies. Psychological Methods, 9, 147–163. doi:10.1037/1082-989X.9.2.147
Milloy, J. S. (1995). Science without sense: The risky business of public
health research. Washington, DC: Cato Institute.
Mudge, J. F., Baker, L. F., Edge, C. B., & Houlahan, J. E. (2012). Setting
an optimal that minimizes errors in null hypothesis significance tests.
PLoS One, 7(2), Article e32734. doi:10.1371/journal.pone.0032734
Murphy, S. T., Zajonc, R. B., & Monahan, J. L. (1995). Additivity of
nonconscious affect: Combined effects of priming and exposure. Journal
of Personality and Social Psychology, 69, 589–602. doi:10.1037/0022-
Ritchie, S. J., Wiseman, R., & French, C. C. (2012a). Failing the future:
Three unsuccessful attempts to replicate Bem’s “retroactive facilitation
of recall” effect. PLoS One, 7(3), Article e33423. doi:10.1371/
Rossi, J. S. (1990). Statistical power of psychological research: What have
we gained in 20 years? Journal of Consulting and Clinical Psychology,
58, 646–656. doi:10.1037/0022-006X.58.5.646
Royall, R. M. (1986). The effect of sample size on the meaning of
significance tests. American Statistician, 40, 313–315. doi:10.2307/
Schmidt, F. (2010). Detecting and correcting the lies that data tell. Perspectives
on Psychological Science, 5, 233–242. doi:10.1177/
Schooler, J. (2011, February 23). Unpublished results hide the decline
effect. Nature, 470, 437. doi:10.1038/470437a
Sedlmeier, P., & Gigerenzer, G. (1989). Do studies of statistical power
have an effect on the power of studies? Psychological Bulletin, 105,
Simmons, J. P., Nelson, L. D., & Simonsohn, U. (2011). False-positive
psychology: Undisclosed flexibility in data collection and analysis allows
presenting anything as significant. Psychological Science, 22,
Smith, E. R. (2012). Editorial. Journal of Personality and Social Psychology,
102, 1–3. doi:10.1037/a0026676
Spellman, B. A. (2012). Introduction to the special section: Data, data,
everywhere . . . especially in my file drawer. Perspectives on Psychological
Science, 7, 58–59. doi:10.1177/1745691611432124
Steen, R. G. (2011a). Retractions in the scientific literature: Do authors
deliberately commit research fraud? Journal of Medical Ethics, 37,
Steen, R. G. (2011b). Retractions in the scientific literature: Is the incidence
of research fraud increasing? Journal of Medical Ethics, 37,
Sterling, T. D. (1959). Publication decisions and their possible effects on inferences drawn from tests of significance— or vice versa. Journal of the American Statistical Association, 54(285), 30–34. doi:10.2307/ 2282137
Sterling, T. D., Rosenbaum, W. L., & Weinkam, J. J. (1995). Publication decisions revisited: The effect of the outcome of statistical tests on the decision to publish and vice-versa. American Statistician, 49, 108–112. doi:10.2307/2684823
Strube, M. J. (2006). SNOOP: A program for demonstrating the consequences
of premature and repeated null hypothesis testing. Behavior
Research Methods, 38, 24–27. doi:10.3758/BF03192746
Sutton, A. J., & Higgins, J. P. I. (2008). Recent developments in metaanalysis.
Statistics in Medicine, 27, 625–650. doi:10.1002/sim.2934
Vul, E., Harris, C., Winkielman, P., & Pashler, H. (2009). Puzzlingly high
correlations in fMRI studies of emotion, personality, and social cognition.
Perspectives on Psychological Science, 4, 274–290. doi:10.1111/
Wagenmakers, E. J. (2007). A practical solution to the pervasive problems
of p values. Psychonomic Bulletin & Review, 14, 779–804. doi:10.3758/
Wagenmakers, E. J., Wetzels, R., Borsboom, D., & van der Maas, H. L. J.
(2011). Why psychologists must change the way they analyze their data:
The case of psi: Comment on Bem (2011). Journal of Personality and
Social Psychology, 100, 426–432. doi:10.1037/a0022790
Wegner, D. M. (1992). The premature demise of the solo experiment.
Personality and Social Psychology Bulletin, 18, 504–508. doi:10.1177/
Yarkoni, T. (2009). Big correlations in little studies: Inflated fMRI correlations
reflect low statistical power—Commentary on Vul et al. (2009).
Perspectives on Psychological Science, 4, 294–298. doi:10.1111/j.1745-
Yong, E. (2012, May 16). Bad copy. Nature, 485, 298–300. doi:10.1038/
Yuan, K. H., & Maxwell, S. (2005). On the post hoc power in testing mean
differences. Journal of Educational and Behavioral Statistics, 30, 141–
Received May 30, 2011
Revision received June 18, 2012
Accepted June 25, 2012
Further Revised February 18, 2018
Thanks to social media, geography is no longer a barrier for scientific discourse. However, language is still a barrier. Fortunately, I understand German and I can respond to the official statement of the board of the German Psychological Association (DGPs), which was posted on the DGPs website (in German).
On September 1, 2015, Prof. Dr. Andrea Abele-Brehm, Prof. Dr. Mario Gollwitzer, and Prof. Dr. Fritz Strack published an official response to the results of the OSF-Replication Project – Psychology (in German) that was distributed to public media in order to correct potentially negative impressions about psychology as a science.
Numerous members of DGPs felt that this official statement did not express their views and noticed that members were not consulted about the official response of their organization. In response to this criticism, DGfP opened a moderated discussion page, where members could post their personal views (mostly in German).
On October 6, 2015, the board closed the discussion page and posted some final words (Schlussbeitrag). In this blog, I provide a critical commentary on these final words.
BOARD’S RESPONSE TO COMMENTS
The board members provide a summary of the core insights and arguments of the discussion from their (personal/official) perspective.
„Wir möchten nun die aus unserer Sicht zentralen Erkenntnisse und Argumente der unterschiedlichen Forumsbeiträge im Folgenden zusammenfassen und deutlich machen, welche vorläufigen Erkenntnisse wir im Vorstand aus ihnen ziehen.“
1. 68% success rate?
The first official statement suggested that the replication project showed that 68% of studies. This number is based on significance in a meta-analysis of the original and replication study. Critics pointed out that this approach is problematic because the replication project showed clearly that the original effect sizes were inflated (on average by 100%). Thus, the meta-analysis is biased and the 68% number is inflated.
In response to this criticism, the DGPs board states that “68% is the maximum [größtmöglich] optimistic estimate.” I think the term “biased and statistically flawed estimate” is a more accurate description of this estimate. It is common practice to consider fail-safe-N or to correct meta-analysis for publication bias. When there is clear evidence of bias, it is unscientific to report the biased estimate. This would be like saying that the maximum optimistic estimate of global warming is that global warming does not exist. This is probably a true statement about the most optimistic estimate, but not a scientific estimate of the actual global warming that has been taking place. There is no place for optimism in science. Optimism is a bias and the aim of science is to remove bias. If DGPs wants to represent scientific psychology, the board should post what they consider the most accurate estimate of replicability in the OSF-project.
2. The widely cited 36% estimate is negative.
The board members then justify the publication of the maximally optimistic estimate as a strategy to counteract negative perceptions of psychology as a science in response to the finding that only 36% of results were replicated. The board members felt that these negative responses misrepresent the OSF-project and psychology as a scientific discipline.
„Dies wird weder dem Projekt der Open Science Collaboration noch unserer Disziplin insgesamt gerecht. Wir sollten jedoch bei der konstruktiven Bewältigung der Krise Vorreiter innerhalb der betroffenen Wissenschaften sein.“
However, reporting the dismal 36% replication rate of the OSF-replication project is not a criticism of the OSF-project. Rather, it assumes that the OSF-replication project was a rigorous and successful attempt to provide an estimate of the typical replicability of results published in top psychology journals. The outcome could have been 70% or 35%. The quality of the project does not depend on the result. The result is also not a negatively biased perception of psychology as a science. It is an objective scientific estimate of the probability that a reported significant result in a journal would produce a significant result again in a replication study. Whether 36% is acceptable or not can be debated, but it seems problematic to post a maximally optimistic estimate to counteract negative implications of an objective estimate.
3. Is 36% replicability good or bad?
Next, the board ponders the implications of the 36% success rate. “How should we evaluate this number?” The board members do not know. According to their official conclusion, this question is complex as divergent contributions on the discussion page suggest.
„Im Science-Artikel wurde die relative Häufigkeit der in den Replikationsstudien statistisch bedeutsamen Effekte mit 36% angegeben. Wie ist diese Zahl zu bewerten? Wie komplex die Antwort auf diese Frage ist, machen die Forumsbeiträge von Roland Deutsch, Klaus Fiedler, Moritz Heene (s.a. Heene & Schimmack) und Frank Renkewitz deutlich.“
To help the board members to understand the number, I can give a brief explanation of replicability. Although there are several ways to define replicability, one plausible definition of replicability is to equate it with statistical power. Statistical power is the probability that a study will produce a significant result. A study with 80% power has an 80% probability to produce a significant result. For a set of 100 studies, one would expect roughly 80 significant results and 20 non-significant results. For 100 studies with 36% power, one would expect roughly 36 significant results and 64 non-significant results. If researchers would publish all studies, the percentage of published significant results would provide an unbiased estimate of the typical power of studies. However, it is well known that significant results are more likely to be written up, submitted for publication, and accepted for publication. These reporting biases explain why psychology journals report over 90% significant results, although the actual power of studies is less than 90%.
In 1962, Jacob Cohen provided the first attempt to estimate replicability of psychological results. His analysis suggested that psychological studies have approximately 50% power. He suggested that psychologists should increase power to 80% to provide robust evidence for effects and to avoid wasting resources on studies that cannot detect small, but practically important effects. For the next 50 years, psychologists have ignored Cohen’s warning that most studies are underpowered, despite repeated reminders that there are no signs of improvement, including reminders by prominent German psychologists like Gerg Giegerenzer, director of a Max Planck Institute (Sedlmeier & Giegerenzer, 1989; Maxwell, 2004; Schimmack, 2012).
The 36% success rate for an unbiased set of 100 replication studies, suggest that the actual power of published studies in psychology journals is 36%. The power of all studies conducted is even lower because the p < .05 selection criterion favors studies with higher power. Does the board think 36% power is an acceptable amount of power?
4. Psychologists should improve replicability in the future
On a positive note, the board members suggest that, after careful deliberation, psychologists need to improve replicability so that it can be demonstrated in a few years that replicability has increased.
„Wir müssen nach sorgfältiger Diskussion unter unseren Mitgliedern Maßnahmen ergreifen (bei Zeitschriften, in den Instituten, bei Förderorganisationen, etc.), die die Replikationsquote im temporalen Vergleich erhöhen können.“
The board members do not mention a simple solution to the replicabilty problem that was advocated over 50 years ago by Jacob Cohen. To increase replicability, psychologists have to think about the strength of the effects that they are investigating and they have to conduct studies that have a realistic chance to distinguish these effects from variation due to random error. This often means investing more resources (larger samples, repeated trials, etc.) in a single study. Unfortunately, the leaders of German psychologists appear to be unaware of this important and simple solution to the replication crisis. They neither mention power as a cause of the problem, nor do they recommend increasing power to increase replicability in the future.
5. Do the Results Reveal Fraud?
The DGPs board members then discuss the possibility that the OSF-reproducibilty results reveal fraud, like the fraud committed by Stapel. The board points out that the OSF-results do not imply that psychologists commit fraud because failed replications can occur for various reasons.
„Viele Medien (und auch einige Kolleginnen und Kollegen aus unserem Fach) nennen die Befunde der Science-Studie im gleichen Atemzug mit den Betrugsskandalen, die unser Fach in den letzten Jahren erschüttert haben. Diese Assoziation ist unserer Meinung nach problematisch: sie suggeriert, die geringe Replikationsrate sei auf methodisch fragwürdiges Verhalten der Autor(inn)en der Originalstudien zurückzuführen.“
It is true that the OSF-results do not reveal fraud. However, the board members confuse fraud with questionable research practices. Fraud is defined as fabricating data that were never collected. Only one of the 100 studies in the OSF-replication project (by Jens Förster, a former student of Fritz Strack, one of the board members) is currently being investigated for fraud by the University of Amsterdam. Despite very strong results in the original study, it failed to replicate.
The more relevant question is how much questionable research practices contributed to the results. Questionable research practices are practices where data are being collected, but statistical results are only being reported if they produce a significant result (studies, conditions, dependent variables, data points that do not produce significant results are excluded from the results that are being submitted for publication. It has been known for over 50 years that these practices produce a discrepancy between the actual power of studies and the rate of significant results that are published in psychology journals (Sterling, 1959).
Recent statistical developments have made it possible to estimate the true power of studies after correcting for publication bias. Based on these calculations, the true power of the original studies in the OSF-project was only 50%. Thus a large portion of the discrepancy between nearly 100% reported significant results and a replication success rate of 36% is explained by publication bias (see R-Index blogs for social psychology and cognitive psychology).
Other factors may contribute to the discrepancy between the statistical prediction that the replication success rate would be 50% and the actual success rate of 36%. Nevertheless, the lion share of the discrepancy can be explained by the questionable practice to report only evidence that supports a hypothesis that a researcher wants to support. This motivated bias undermines the very foundations of science. Unfortunately, the board ignores this implication of the OSF results.
6. What can we do?
The board members have no answer to this important question. In the past four years, numerous articles have been published that have made suggestions how psychology can improve its credibility as a science. Yet, the DPfP board seems to be unaware of these suggestions or unable to comment on these proposals.
„Damit wären wir bei der Frage, die uns als Fachgesellschaft am stärksten beschäftigt und weiter beschäftigen wird. Zum einen brauchen wir eine sorgfältige Selbstreflexion über die Bedeutung von Replikationen in unserem Fach, über die Bedeutung der neuesten Science-Studie sowie der weiteren, zurzeit noch im Druck oder in der Phase der Auswertung befindlichen Projekte des Center for Open Science (wie etwa die Many Labs-Studien) und über die Grenzen unserer Methoden und Paradigmen“
The time for more discussion has passed. After 50 years of ignoring Jacob Cohen’s recommendation to increase statistical power it is time for action. If psychologists are serious about replicability, they have to increase the power of their studies.
The board then discusses the possibility of measuring and publishing replication rates at the level of departments or individual scientists. They are not in favor of such initiatives, but they provide no argument for their position.
„Datenbanken über erfolgreiche und gescheiterte Replikationen lassen sich natürlich auch auf der Ebene von Instituten oder sogar Personen auswerten (wer hat die höchste Replikationsrate, wer die niedrigste?). Sinnvoller als solche Auswertungen sind Initiativen, wie sie zurzeit (unter anderem) an der LMU an der LMU München implementiert wurden (siehe den Beitrag von Schönbrodt und Kollegen).“
The question is why replicability should not be measured and used to evaluate researchers. If the board really valued replicability and wanted to increase replicability in a few years, wouldn’t it be helpful to have a measure of replicability and to reward departments or researchers who invest more resources in high powered studies that can produce significant results without the need to hide disconfirming evidence in file-drawers? A measure of replicability is also needed because current quantitative measures of scientific success are one of the reasons for the replicability crisis. The most successful researchers are those who publish the most significant results, no matter how these results were obtained (with the exception of fraud). To change this unscientific practice of significance chasing, it is necessary to have an alternative indicator of scientific quality that reflects how significant results were obtained.
The board makes some vague concluding remarks that are not worthwhile repeating here. So let me conclude with my own remarks.
The response of the DGPs board is superficial and does not engage with the actual arguments that were exchanged on the discussion page. Moreover, it ignores some solid scientific insights into the causes of the replicability crisis and it makes no concrete suggestions how German psychologists should change their behaviors to improve the credibility of psychology as a science. Not once do they point out that the results of the OSF-project were predictable based on the well-known fact that psychological studies are underpowered and that failed studies are hidden in file-drawers.
I received my education in Germany all the way to the Ph.D at the Free University in Berlin. I had several important professors and mentors that educated me about philosophy of science and research methods (Rainer Reisenzein, Hubert Feger, Hans Westmeyer, Wolfgang Schönpflug). I was a member of DGPs for many years. I do not believe that the opinion of the board members represent a general consensus among German psychologists. I hope that many German psychologists recognize the importance of replicability and are motivated to make changes to the way psychologists conduct research. As I am no longer a member of DGfP, I have no direct influence on it, but I hope that the next election will elect a candidate that will promote open science, transparency, and above all scientific integrity.
Abstract: I predicted the replicability of 38 social psychology results in the OSF-Reproducibility Project. Based on post-hoc-power analysis I predicted a success rate of 35%. The actual success rate was 8% (3 out of 38) and post-hoc-power was estimated to be 3% for 36 out of 38 studies (5% power = type-I error rate, meaning the null-hypothesis is true).
The OSF-Reproducibility Project aimed to replicate 100 results published in original research articles in three psychology journals in 2008. The selected journals focus on publishing results from experimental psychology. The main paradigm of experimental psychology is to recruit samples of participants and to study their behaviors in controlled laboratory conditions. The results are then generalized to the typical behavior of the average person.
An important methodological distinction in experimental psychology is the research design. In a within-subject design, participants are exposed to several (a minimum of two) situations and the question of interest is whether responses to one situation differ from behavior in other situations. The advantage of this design is that individuals serve as their own controls and variation due to unobserved causes (mood, personality, etc.) does not influence the results. This design can produce high statistical power to study even small effects. The design is often used by cognitive psychologists because the actual behaviors are often simple behaviors (e.g., pressing a button) that can be repeated many times (e.g., to demonstrate interference in the Stroop paradigm).
In a between-subject design, participants are randomly assigned to different conditions. A mean difference between conditions reveals that the experimental manipulation influenced behavior. The advantage of this design is that behavior is not influenced by previous behaviors in the experiment (carry over effects). The disadvantage is that many uncontrolled factors (e..g, mood, personality) also influence behavior. As a result, it can be difficult to detect small effects of an experimental manipulation among all of the other variance that is caused by uncontrolled factors. As a result, between-subject designs require large samples to study small effects or they can only be used to study large effects.
One of the main findings of the OSF-Reproducibility Project was that results from within-subject designs used by cognitive psychology were more likely to replicate than results from between-subject designs used by social psychologists. There were two few between-subject studies by cognitive psychologists or within-subject designs by social psychologists to separate these factors. This result of the OSF-reproducibility project was predicted by PHP-curves of the actual articles as well as PHP-curves of cognitive and social journals (Replicability-Rankings).
Given the reliable difference between disciplines within psychology, it seems problematic to generalize the results of the OSF-reproducibility project to all areas of psychology. The Replicability-Rankings suggest that social psychology has a lower replicability than other areas of psychology. For this reason, I conducted separate analyses for social psychology and for cognitive psychology. Other areas of psychology had two few studies to conduct a meaningful analysis. Thus, the OSF-reproducibility results should not be generalized to all areas of psychology.
The master data file of the OSF-reproducibilty project contained 167 studies with replication results for 99 studies. 57 studies were classified as social studies. However, this classification used a broad definition of social psychology that included personality psychology and developmental psychology. It included six articles published in the personality section of the Journal of Personality and Social Psychology. As each section functions essentially like an independent journal, I excluded all studies from this section. The file also contained two independent replications of two experiments (experiment 5 and 7) in Albarracín et al. (2008; DOI: 10.1037/a0012833). As the main sampling strategy was to select the last study of each article, I only included Study 7 in the analysis (Study 5 did not replicate, p = .77). Thus, my selection did not lower the rate of successful replications. There were also two independent replications of the same result in Bressan and Stranieri (2008). Both replications produced non-significant results (p = .63, p = .75). I selected the replication study with the larger sample (N = 318 vs. 259). I also excluded two studies that were not independent replications. Rule and Ambady (2008) examined the correlation between facial features and success of CEOs. The replication study had new raters to rate the faces, but used the same faces. Heine, Buchtel, and Norenzayan (2008) examined correlates of conscientiousness across nations and the replication study examined the same relationship across the same set of nations. I also excluded replications of non-significant results because non-significant results provide ambiguous information and cannot be interpreted as evidence for the null-hypothesis. For this reason, it is not clear how the results of a replication study should be interpreted. Two underpowered studies could easily produce consistent results that are both type-II errors. For this reason, I excluded Ranganath and Nosek (2008) and Eastwick and Finkel (2008). The final sample consisted of 38 articles.
I first conducted a post-hoc-power analysis of the reported original results. Test statistics were first converted into two-tailed p-values and two-tailed p-values were converted into absolute z-scores using the formula (1 – norm.inverse(1-p/2). Post-hoc power was estimated by fitting the observed z-scores to predicted z-scores with a mixed-power model with three parameters (Brunner & Schimmack, in preparation).
Estimated power was 35%. This finding reflects the typical finding that reported results are a biased sample of studies that produced significant results, whereas non-significant results are not submitted for publication. Based on this estimate, one would expect that only 35% of the 38 findings (k = 13) would produce a significant result in an exact replication study with the same design and sample size.
The Figure visualizes the discrepancy between observed z-scores and the success rate in the original studies. Evidently, the distribution is truncated and the mode of the curve (it’s highest point) is projected to be on the left side of the significance criterion (z = 1.96, p = .05 (two-tailed)). Given the absence of reliable data in the range from 0 to 1.96, the data make it impossible to estimate the exact distribution in this region, but the step decline of z-scores on the right side of the significance criterion suggests that many of the significant results achieved significance only with the help of inflated observed effect sizes. As sampling error is random, these results will not replicate again in a replication study.
The replication studies had different sample sizes than the original studies. This makes it difficult to compare the prediction to the actual success rate because the actual success rate could be much higher if the replication studies had much larger samples and more power to replicate effects. For example, if all replication studies had sample sizes of N = 1,000, we would expect a much higher replication rate than 35%. The median sample size of the original studies was N = 86. This is representative of studies in social psychology. The median sample size of the replication studies was N = 120. Given this increase in power, the predicted success rate would increase to 50%. However, the increase in power was not uniform across studies. Therefore, I used the p-values and sample size of the replication study to compute the z-score that would have been obtained with the original sample size and I used these results to compare the predicted success rate to the actual success rate in the OSF-reproducibility project.
The depressing finding was that the actual success rate was much lower than the predicted success rate. Only 3 out of 38 results (8%) produced a significant result (without the correction of sample size 5 findings would have been significant). Even more depressing is the fact that a 5% criterion, implies that every 20 studies are expected to produce a significant result just by chance. Thus, the actual success rate is close to the success rate that would be expected if all of the original results were false positives. A success rate of 8% would imply that the actual power of the replication studies was only 8%, compared to the predicted power of 35%.
The next figure shows the post-hoc-power curve for the sample-size corrected z-scores.
The PHP-Curve estimate of power for z-scores in the range from 0 to 4 is 3% for the homogeneous case. This finding means that the distribution of z-scores for 36 of the 38 results is consistent with the null-hypothesis that the true effect size for these effects is zero. Only two z-scores greater than 4 (one shown, the other greater than 6 not shown) appear to be replicable and robust effects.
One replicable finding was obtained in a study by Halevy, Bornstein, and Sagiv. The authors demonstrated that allocation of money to in-group and out-group members is influenced much more by favoring the in-group than by punishing the out-group. Given the strong effect in the original study (z > 4), I had predicted that this finding would replicate.
The other successful replication was a study by Lemay and Clark (DOI: 10.1037/0022-3522.214.171.1247). The replicated finding was that participants’ projected their own responsiveness in a romantic relationship onto their partners’ responsiveness while controlling for partners’ actual responsiveness. Given the strong effect in the original study (z > 4), I had predicted that this finding would replicate.
Based on weak statistical evidence in the original studies, I had predicted failures of replication for 25 studies. Given the low success rate, it is not surprising that my success rate was 100.
I made the wrong prediction for 11 results. In all cases, I predicted a successful replication when the outcome was a failed replication. Thus, my overall success rate was 27/38 = 71%. Unfortunately, this success rate is easily beaten by a simple prediction rule that nothing in social psychology replicates, which is wrong in only 3 out of 38 predictions (89% success rate).
Below I briefly comment on the 11 failed predictions.
1 Based on strong statistics (z > 4), I had predicted a successful replication for Förster, Liberman, and Kuschel (DOI: 10.1037/0022-35126.96.36.1999). However, even when I made this predictions based on the reported statistics, I had my doubts about this study because statisticians had discovered anomalies in Jens Förster’s studies that cast doubt on the validity of these reported results. Post-hoc power analysis can correct for publication bias, but it cannot correct for other sources of bias that lead to vastly inflated effect sizes.
2 I predicted a successful replication of Payne, MA Burkley, MB Stokes. The replication study actually produced a significant result, but it was no longer significant after correcting for the larger sample size in the replication study (180 vs. 70, p = .045 vs. .21). Although the p-value in the replication study is not very reassuring, it is possible that this is a real effect. However, the original result was probably still inflated by sampling error to produce a z-score of 2.97.
3 I predicted a successful replication of McCrae (DOI: 10.1037/0022-35188.8.131.524). This prediction was based on a transcription error. Whereas the z-score for the target effect was 1.80, I posted a z-score of 3.5. Ironically, the study did successfully replicate with a larger sample size, but the effect was no longer significant after adjusting the result for sample size (N = 61 vs. N = 28). This study demonstrates that marginally significant effects can reveal real effects, but it also shows that larger samples are needed in replication studies to demonstrate this.
4 I predicted a successful replication for EP Lemay, MS Clark (DOI: 10.1037/0022-35184.108.40.2060). This prediction was based on a transcription error because EP Lemay and MS Clark had another study in the project. With the correct z-score of the original result (z = 2.27), I would have predicted correctly that the result would not replicate.
5 I predicted a successful replication of Monin, Sawyer, and Marquez (DOI: 10.1037/0022-35220.127.116.11) based on a strong result for the target effect (z = 3.8). The replication study produced a z-score of 1.45 with a sample size that was not much larger than the original study (N = 75 vs. 67).
6 I predicted a successful replication for Shnabel and Nadler (DOI: 10.1037/0022-3518.104.22.168). The replication study increased sample size by 50% (Ns = 141 vs. 94), but the effect in the replication study was modest (z = 1.19).
7 I predicted a successful replication for van Dijk, van Kleef, Steinel, van Beest (DOI: 10.1037/0022-3522.214.171.1240). The sample size in the replication study was slightly smaller than in the original study (N = 83 vs. 103), but even with adjustment the effect was close to zero (z = 0.28).
8 I predicted a successful replication of V Purdie-Vaughns, CM Steele, PG Davies, R Ditlmann, JR Crosby (DOI: 10.1037/0022-35126.96.36.1995). The original study had rather strong evidence (z = 3.35). In this case, the replication study had a much larger sample than the original study (N = 1,490 vs. 90) and still did not produce a significant result.
9 I predicted a successful replication of C Farris, TA Treat, RJ Viken, RM McFall (doi:10.1111/j.1467-9280.2008.02092.x). The replication study had a somewhat smaller sample (N = 144 vs. 280), but even with adjustment of sample size the effect in the replication study was close to zero (z = 0.03).
10 I predicted a successful replication of KD Vohs and JW Schooler (doi:10.1111/j.1467-9280.2008.02045.x)). I made this prediction of generally strong statistics, although the strength of the target effect was below 3 (z = 2.8) and the sample size was small (N = 30). The replication study doubled the sample size (N = 58), but produced weak evidence (z = 1.08). However, even the sample size of the replication study is modest and does not allow strong conclusions about the existence of the effect.
11 I predicted a successful replication of Blankenship and Wegener (DOI: 10.1037/0022-35188.8.131.52.2.196). The article reported strong statistics and the z-score for the target effect was greater than 3 (z = 3.36). The study also had a large sample size (N = 261). The replication study also had a similarly large sample size (N = 251), but the effect was much smaller than in the original study (z = 3.36 vs. 0.70).
In some of these failed predictions it is possible that the replication study failed to reproduce the same experimental conditions or that the population of the replication study differs from the population of the original study. However, there are twice as many studies where the failure of replication was predicted based on weak statistical evidence and the presence of publication bias in social psychology journals.
In conclusion, this set of results from a representative sample of articles in social psychology reported a 100% success rate. It is well known that this success rate can only be achieved with selective reporting of significant results. Even the inflated estimate of median observed power is only 71%, which shows that the success rate of 100% is inflated. A power estimate that corrects for inflation suggested that only 35% of results would replicate, and the actual success rate is only 8%. While mistakes by the replication experimenters may contribute to the discrepancy between the prediction of 35% and the actual success rate of 8%, it was predictable based on the results in the original studies that the majority of results would not replicate in replication studies with the same sample size as the original studies.
This low success rate is not characteristic of other sciences and other disciplines in psychology. As mentioned earlier, the success rate for cognitive psychology is higher and comparisons of psychological journals show that social psychology journals have lower replicability than other journals. Moreover, an analysis of time trends shows that replicability of social psychology journals has been low for decades and some journals even show a negative trend in the past decade.
The low replicability of social psychology has been known for over 50 years, when Cohen examined the replicability of results published in the Journal of Social and Abnormal Psychology (now Journal of Personality and Social Psychology), the flagship journal of social psychology. Cohen estimated a replicability of 60%. Social psychologists would rejoice if the reproducibility project had shown a replication rate of 60%. The depressing result is that the actual replication rate was 8%.
The main implication of this finding is that it is virtually impossible to trust any results that are being published in social psychology journals. Yes, two articles that posted strong statistics (z > 4) replicated, but several results with equally strong statistics did not replicate. Thus, it is reasonable to distrust all results with z-scores below 4 (4 sigma rule), but not all results with z-scores greater than 4 will replicate.
Given the low credibility of original research findings, it will be important to raise the quality of social psychology by increasing statistical power. It will also be important to allow publication of non-significant results to reduce the distortion that is created by a file-drawer filled with failed studies. Finally, it will be important to use stronger methods of bias-correction in meta-analysis because traditional meta-analysis seemed to show strong evidence even for incredible effects like premonition for erotic stimuli (Bem, 2011).
In conclusion, the OSF-project demonstrated convincingly that many published results in social psychology cannot be replicated. If social psychology wants to be taken seriously as a science, it has to change the way data are collected, analyzed, and reported and demonstrate replicability in a new test of reproducibility.
The silver lining is that a replication rate of 8% is likely to be an underestimation and that regression to the mean alone might lead to some improvement in the next evaluation of social psychology.
In 2008, Turner and colleagues (2008) examined the presence of publication bias in clinical trials of antidepressants. They found that out of 74 FDA-registered studies, 51% showed positive results. However, positive results were much more likely to be published, as 94% of the published results were positive. There were two reasons for the inflated percentage of positive results. First, negative results were not published. Second, negative results were published as positive results. Turner and colleagues’ (2008) results received a lot of attention and cast doubt on the effectiveness of anti-depressants.
A year after Turner and colleagues (2008) published their study, Moreno, Sutton, Turner, Abrams, Cooper and Palmer (2009) examined the influence of publication bias on the effect-size estimate in clinical trials of antidepressants. They found no evidence of publication bias in the FDA-registered trials, leading the researchers to conclude that the FDA data provide an unbiased gold standard to examine biases in the published literature.
The effect size for treatment with anti-depressants in the FDA data was g = 0.31, 95% confidence interval 0.27 to 0.35. In contrast, the uncorrected average effect size in the published studies was g = 0.41, 95% confidence interval 0.37 to 0.45. This finding shows that publication bias inflates effect size estimates by 32% ((0.41 – 0.31)/0.31).
Moreno et al. (2009) also used regression analysis to obtain a corrected effect size estimate based on the biased effect sizes in the published literature. In this method, effect sizes are regressed on sampling error under the assumption that studies with smaller samples (and larger sampling error) have more bias. The intercept is used as an estimate of the population effect size when sampling error is zero. This correction method yielded an effect size estimate of g = 0.29, 95% confidence interval 0.23 to 0.35, which is similar to the gold standard estimate (.31).
The main limitation of the regression method is that other factors can produce a correlation between sample size and effect size (e.g., higher quality studies are more costly and use smaller samples). To avoid this problem, we used an alternative correction method that does not make this assumption.
The method uses the R-Index to examine bias in a published data set. The R-Index increases as statistical power increases and it decreases when publication bias is present. To obtain an unbiased effect size estimate, studies are selected to maximize the R-Index.
Since the actual data files were not available, graphs A and B from Moreno et al.’s (2009) study were used to obtain information about effect size and sample error of all the FDA-registered and the published journal articles.
The FDA-registered studies had the success rate of 53% and the observed power of 56%, resulting in an inflation of close to 0. The close match between the success rate and observed confirms FDA studies are not biased. Given the lack of bias (inflation), the most accurate estimate of the effect size is obtained by using all studies.
The published journal articles had a success rate of 86% and the observed power of 73%, resulting in the inflation rate of 12%. The inflation rate of 12% confirms that the published data set is biased. The R-Index subtracts the inflation rate from observed power to correct for inflation. Thus, the R-Index for the published studies is 73-12 = 61. The weighted effect size estimate was d = .40.
The next step was to select sets of studies to maximize the R-Index. As most studies were significant, the success rate could not change much. As a result, most of the increase would be achieved by selecting studies with higher sample sizes in order to increase power. The maximum R-Index was obtained for a cut-off point of N = 225. This left 14 studies with a total sample size of 4,170 participants. The success rate was 100% with median observed power of 85%. The Inflation was still 15%, but the R-Index was higher than it was for the full set of studies (70 vs. 61). The weighted average effect size in the selected set of powerful studies was d = .34. This result is very similar to the gold standard in the FDA data. The small discrepancy can be attributed to the fact that even studies with 85% power still have a small bias in the estimation of the true effect size.
In conclusion, our alternative effect size estimation procedure confirms Moreno et al.’s (2009) results using an alternative bias-correction method and shows that the R-Index can be a valuable tool to detect and correct for publication bias in other meta-analyses.
These results have important practical implications. The R-Index confirms that published clinical trials are biased and can provide false information about the effectiveness of drugs. It is therefore important to ensure that clinical trials are preregistered and that all results of clinical trials are published. The R-Index can be used to detect violations of these practices that lead to biased evidence. Another important finding is that clinical trials of antidepressants do show effectiveness and that antidepressants can be used as effective treatments of depression. The presence of publication bias should not be used to claim that antidepressants lack effectiveness.
Moreno, S. G., Sutton, A. J., Turner, E. H., Abrams, K. R., Cooper, N. J., Palmer, T. M., & Ades, A. E. (2009). Novel methods to deal with publication biases: secondary analysis of antidepressant trials in the FDA trial registry database and related journal publications. Bmj, 339, b2981.
Turner, E. H., Matthews, A. M., Linardatos, E., Tell, R. A., & Rosenthal, R. (2008). Selective publication of antidepressant trials and its influence on apparent efficacy. New England Journal of Medicine, 358(3), 252-260.
Imagine an NBA player has an 80% chance to make one free throw. What is the chance that he makes both free throws? The correct answer is 64% (80% * 80%).
Now consider the possibility that it is possible to distinguish between two types of free throws. Some free throws are good; they don’t touch the rim and make a swishing sound when they go through the net (all net). The other free throws bounce of the rim and go in (rattling in).
What is the probability that an NBA player with an 80% free throw percentage makes a free throw that is all net or rattles in? It is more likely that an NBA player with an 80% free throw average makes a perfect free throw because a free throw that rattles in could easily have bounded the wrong way, which would lower the free throw percentage. To achieve an 80% free throw percentage, most free throws have to be close to perfect.
Let’s say the probability of hitting the rim and going in is 30%. With an 80% free throw average, this means that the majority of free throws are in the close-to-perfect category (20% misses, 30% rattle-in, 50% close-to-perfect).
What does this have to do with science? A lot!
The reason is that the outcome of a scientific study is a bit like throwing free throws. One factor that contributes to a successful study is skill (making correct predictions, avoiding experimenter errors, and conducting studies with high statistical power). However, another factor is random (a lucky or unlucky bounce).
The concept of statistical power is similar to an NBA players’ free throw percentage. A researcher who conducts studies with 80% statistical power is going to have an 80% success rate (that is, if all predictions are correct). In the remaining 20% of studies, a study will not produce a statistically significant result, which is equivalent to missing a free throw and not getting a point.
Many years ago, Jacob Cohen observed that researchers often conduct studies with relatively low power to produce a statistically significant result. Let’s just assume right now that a researcher conducts studies with 60% power. This means, researchers would be like NBA players with a 60% free-throw average.
Now imagine that researchers have to demonstrate an effect not only once, but also a second time in an exact replication study. That is researchers have to make two free throws in a row. With 60% power, the probability to get two significant results in a row is only 36% (60% * 60%). Moreover, many of the freethrows that are made rattle in rather than being all net. The percentages are about 40% misses, 30% rattling in and 30% all net.
One major difference between NBA players and scientists is that NBA players have to demonstrate their abilities in front of large crowds and TV cameras, whereas scientists conduct their studies in private.
Imagine an NBA player could just go into a private room, throw two free throws and then report back how many free throws he made and the outcome of these free throws determine who wins game 7 in the playoff finals. Would you trust the player to tell the truth?
If you would not trust the NBA player, why would you trust scientists to report failed studies? You should not.
It can be demonstrated statistically that scientists are reporting more successes than the power of their studies would justify (Sterling et al., 1995; Schimmack, 2012). Amongst scientists this fact is well known, but the general public may not fully appreciate the fact that a pair of exact replication studies with significant results is often just a selection of studies that included failed studies that were not reported.
Fortunately, it is possible to use statistics to examine whether the results of a pair of studies are likely to be honest or whether failed studies were excluded. The reason is that an amateur is not only more likely to miss a free throw. An amateur is also less likely to make a perfect free throw.
Based on the theory of statistical power developed by Nyman and Pearson and popularized by Jacob Cohen, it is possible to make predictions about the relative frequency of p-values in the non-significant (failure), just significant (rattling in), and highly significant (all net) ranges.
As for made-free-throws, the distinction between lucky and clear successes is somewhat arbitrary because power is continuous. A study with a p-value of .0499 is very lucky because p = .501 would have been not significant (rattled in after three bounces on the rim). A study with p = .000001 is a clear success. Lower p-values are better, but where to draw the line?
As it turns out, Jacob Cohen’s recommendation to conduct studies with 80% power provides a useful criterion to distinguish lucky outcomes and clear successes.
Imagine a scientist conducts studies with 80% power. The distribution of observed test-statistics (e.g. z-scores) shows that this researcher has a 20% chance to get a non-significant result, a 30% chance to get a lucky significant result (p-value between .050 and .005), and a 50% chance to get a clear significant result (p < .005). If the 20% failed studies are hidden, the percentage of results that rattled in versus studies with all-net results are 37 vs. 63%. However, if true power is just 20% (an amateur), 80% of studies fail, 15% rattle in, and 5% are clear successes. If the 80% failed studies are hidden, only 25% of the successful studies are all-net and 75% rattle in.
One problem with using this test to draw conclusions about the outcome of a pair of exact replication studies is that true power is unknown. To avoid this problem, it is possible to compute the maximum probability of a rattling-in result. As it turns out, the optimal true power to maximize the percentage of lucky outcomes is 66% power. With true power of 66%, one would expect 34% misses (p > .05), 32% lucky successes (.050 < p < .005), and 34% clear successes (p < .005).
For a pair of exact replication studies, this means that there is only a 10% chance (32% * 32%) to get two rattle-in successes in a row. In contrast, there is a 90% chance that misses were not reported or that an honest report of successful studies would have produced at least one all-net result (z > 2.8, p < .005).
Example: Unconscious Priming Influences Behavior
I used this test to examine a famous and controversial set of exact replication studies. In Bargh, Chen, and Burrows (1996), Dr. Bargh reported two exact replication studies (studies 2a and 2b) that showed an effect of a subtle priming manipulation on behavior. Undergraduate students were primed with words that are stereotypically associated with old age. The researchers then measured the walking speed of primed participants (n = 15) and participants in a control group (n = 15).
The two studies were not only exact replications of each other; they also produced very similar results. Most readers probably expected this outcome because similar studies should produce similar results, but this false belief ignores the influence of random factors that are not under the control of a researcher. We do not expect lotto winners to win the lottery again because it is an entirely random and unlikely event. Experiments are different because there could be a systematic effect that makes a replication more likely, but in studies with low power results should not replicate exactly because random sampling error influences results.
Study 1: t(28) = 2.86, p = .008 (two-tailed), z = 2.66, observed power = 76%
Study 2: t(28) = 2.16, p = .039 (two-tailed), z = 2.06, observed power = 54%
The median power of these two studies is 65%. However, even if median power were lower or higher, the maximum probability of obtaining two p-values in the range between .050 and .005 remains just 10%.
Although this study has been cited over 1,000 times, replication studies are rare.
One of the few published replication studies was reported by Cesario, Plaks, and Higgins (2006). Naïve readers might take the significant results in this replication study as evidence that the effect is real. However, this study produced yet another lucky success.
Study 3: t(62) = 2.41, p = .019, z = 2.35, observed power = 65%.
The chances of obtaining three lucky successes in a row is only 3% (32% *32% * 32*). Moreover, with a median power of 65% and a reported success rate of 100%, the success rate is inflated by 35%. This suggests that the true power of the reported studies is considerably lower than the observed power of 65% and that observed power is inflated because failed studies were not reported.
The R-Index corrects for inflation by subtracting the inflation rate from observed power (65% – 35%). This means the R-Index for this set of published studies is 30%.
This R-Index can be compared to several benchmarks.
An R-Index of 22% is consistent with the null-hypothesis being true and failed attempts are not reported.
An R-Index of 40% is consistent with 30% true power and all failed attempts are not reported.
It is therefore not surprising that other researchers were not able to replicate Bargh’s original results, even though they increased statistical power by using larger samples (Pashler et al. 2011, Doyen et al., 2011).
In conclusion, it is unlikely that Dr. Bargh’s original results were the only studies that they conducted. In an interview, Dr. Bargh revealed that the studies were conducted in 1990 and 1991 and that they conducted additional studies until the publication of the two studies in 1996. Dr. Bargh did not reveal how many studies they conducted over the span of 5 years and how many of these studies failed to produce significant evidence of priming. If Dr. Bargh himself conducted studies that failed, it would not be surprising that others also failed to replicate the published results. However, in a personal email, Dr. Bargh assured me that “we did not as skeptics might presume run many studies and only reported the significant ones. We ran it once, and then ran it again (exact replication) in order to make sure it was a real effect.” With a 10% probability, it is possible that Dr. Bargh was indeed lucky to get two rattling-in findings in a row. However, his aim to demonstrate the robustness of an effect by trying to show it again in a second small study is misguided. The reason is that it is highly likely that the effect will not replicate or that the first study was already a lucky finding after some failed pilot studies. Underpowered studies cannot provide strong evidence for the presence of an effect and conducting multiple underpowered studies reduces the credibility of successes because the probability of this outcome to occur even when an effect is present decreases with each study (Schimmack, 2012). Moreover, even if Bargh was lucky to get two rattling-in results in a row, others will not be so lucky and it is likely that many other researchers tried to replicate this sensational finding, but failed to do so. Thus, publishing lucky results hurts science nearly as much as the failure to report failed studies by the original author.
Dr. Bargh also failed to realize how lucky he was to obtain his results, in his response to a published failed-replication study by Doyen. Rather than acknowledging that failures of replication are to be expected, Dr. Bargh criticized the replication study on methodological grounds. There would be a simple solution to test Dr. Bargh’s hypothesis that he is a better researcher and that his results are replicable when the study is properly conducted. He should demonstrate that he can replicate the result himself.
In an interview, Tom Bartlett asked Dr. Bargh why he didn’t conduct another replication study to demonstrate that the effect is real. Dr. Bargh’s response was that “he is aware that some critics believe he’s been pulling tricks, that he has a “special touch” when it comes to priming, a comment that sounds like a compliment but isn’t. “I don’t think anyone would believe me,” he says.” The problem for Dr. Bargh is that there is no reason to believe his original results, either. Two rattling-in results alone do not constitute evidence for an effect, especially when this result could not be replicated in an independent study. NBA players have to make free-throws in front of a large audience for a free-throw to count. If Dr. Bargh wants his findings to count, he should demonstrate his famous effect in an open replication study. To avoid embarrassment, it would be necessary to increase the power of the replication study because it is highly unlikely that even Dr. Bargh can continuously produce significant results with samples of N = 30 participants. Even if the effect is real, sampling error is simply too large to demonstrate the effect consistently. Knowledge about statistical power is power. Knowledge about post-hoc power can be used to detect incredible results. Knowledge about a priori power can be used to produce credible results.