All posts by Ulrich Schimmack

About Ulrich Schimmack

Since Cohen (1962) published his famous article on statistical power in psychological journals, statistical power has not increased. The R-Index makes it possible f to distinguish studies with high power (good science) and studies with low power (bad science). Protect yourself from bad science and check the R-Index before you believe statistical results.

Gaslighting about Replication Failures

This blog post is a review of a manuscript that hopefully will never be published, but it probably will be. In that case, it is a draft for a PubPeer comment. As the ms. is under review, I cannot share the actual ms., but the review makes clear what the authors are trying to do.


I assume that I was selected as a reviewer for this manuscript because the editor recognized my expertise in this research area.  While most of my work on replicability has been published in the form of blog posts, I have also published a few peer-reviewed publications that are relevant to this topic. Most important, I have provided estimates of replicability for social psychology using the most advanced method to do so, z-curve (Bartos & Schimmack, 2020; Brunner & Schimmack, 2020), using the extensive coding by Motyl et al. (2017) (see Schimmack, 2020).  I was surprised that this work was not mentioned.

In contrast, Yeager et al.’s (2019) replication study of 12 experiments is cited and as I recall 11 of the 12 studies replicated successfully. So, it is not clear why this study is cited as evidence that replication attempts often “producing pessimistic results”

While I agree that there are many explanations that have been offered for replication failures, I do not agree that listing all of these explanations is impossible and that it is reasonable to focus on some of these explanations, especially if the main reason is left out. Namely, the main reason for replication failures is that original studies are conducted with low statistical power and only those that achieve significance are published (Sterling et al., 1995; Schimmack, 2020).  Omitting this explanation undermines the contribution of this article.

The listed explanations are

(1) original articles making use of questionable research practices that result in Type I errors

This explanation conflates two problems. QRPs are used to get significance when power to do so is low, but we do not know whether the population effect size is zero (type-I error) or above zero (type-II error).

(2) original research’s pursuit of counterintuitive findings that may have lower a priori probabilities and thus poor chances at replication

This explanations assumes that there are a lot of type-I errors, but we don’t really know whether the population effect size is zero or not. So, this is not a separate explanation, but rather an explanation why we might have many type-I errors assuming that we do have many type-I errors, which we do not know.

(3) the presence of unexamined moderators that produce differences between original and replication research (Dijksterhuis, 2014; Simons et al., 2017),

This citation ignores that empirical tests of this hypothesis have failed to provide evidence for it (van Bavel et al., 2016).

4) specific design choices in original or replication research that produce different conclusions (Bouwmeester et al., 2017; Luttrell et al., 2017; Noah et al., 2018).

This argument is not different from (3). Replication failures are attributed to moderating factors that are always possible because exact replications are impossible.

To date, discussions of possible explanations for poor replication have generally been presented as distinct accounts for poor replication, with little attempt being made to organize them into a coherent conceptual framework. 

This claim ignores my detailed discussion of the various explanations including some not discussed by the authors (Schooler decline effect; Fiedler, regression to the mean; Schimmack, 2020).

The selection of journals is questionable. Psychological Science is not a general (meta)-psychological journal. Instead there are two journals, The Journal of General Psychology and Meta-Psychology that contain relevant articles.

The authors then introduce Cook and Campbell’s typology of validity and try to relate it to accounts of replication failures based on some work by Fabrigar et al. (2020). This attempt is flawed because validity is a broader construct than replicability or reliability.  Measures can be reliable and correlations can be replicable even if the conclusions drawn from these findings are invalid. This is Intro Psych level stuff.

Statistical conclusion validity is concerned with the question of “whether or not two or more variables are related.”  This is of course nothing else than the distinction between true and false conclusions based on significant or non-significant results.  As noted above, even statistical conclusion validity is not directly related to replication failures because replication failures do not tell us whether the population effect size is zero or not.  Yet, we might argue that there is a risk of false positive conclusions when statistical significance is achieved with QRPs and these results do not replicate. So, in some sense statistical conclusion validity is tied to the replication crisis in experimental social psychology.

Internal validity is about the problem of inferring causality from correlations. This issue has nothing to do with the replication crisis because replication failures can occur in experiments and correlational studies. The only indirect link to internal validity is that experimental social psychology prided itself on the use of between-subject experiments to maximize internal validity and minimize demand effects, but often used ineffective manipulations (priming) that required QRPs to get significance especially in the tiny samples that were used because experiments are more time-consuming and labor intensive. In contrast, survey studies often are more replicable because they have larger samples.  But the key point remains, it would be absurd to explain replication failures directly as a function of low internal validity.

Construct validity is falsely described as “the degree to which the operationalizations used in the research effectively capture their intended constructs.”  The problem here is the term operationalization. Once a construct is operationalized with some procedure, it is defined by the procedure (intelligence is what the IQ test measures) and there is no way to challenge the validity of the construct. In contrast, measurement implies that constructs exist independent of one specific procedure and it is possible to examine how well a measure reflects variation in the construct (Cronbach & Meehl, 1955).  That said, there is no relationship between construct validity and replicability because systematic measurement error can produce spurious correlations between measures in correlational studies that are highly replicable (e.g., social desirable responding). In experiments, systematic measurement error will attenuate effect sizes, but it will do so equally in original studies and replication studies. Thus, low construct validity also provides no explanation for replication failures.

External validity is defined as “the degree to which an effect generalizes to different populations and contexts”  This validation criterion is also only slightly related to replication failures when there are concerns about contextual sensitivity or hidden moderators. A replication study in a different population or context might fail because the population effect size varies across populations or contexts. While this is possible, there is little evidence that contextual sensitivity is a major factor.

In short, it is a red herring in explanations for replication failures or the replication crisis to talk about validity. Replicability is necessary but not sufficient for good science.

It is therefore not surprising that the authors found most discussions of replication failures focus on statistical conclusion validity. Any other finding would make no sense. It is just not clear why we needed a text analysis to reveal this.

However, the authors seem to be unable to realize that the other types of validity are not related to replication failures when they write “What does this study add? Identifies that statistical conclusion validity is over-emphasized in replication analysis”

Over-emphasized???  This is an absurd conclusion based on a failure to make a clear distinction between replicability/reliability and validity.  

Ulrich Schimmack

Replicability of Research in Frontiers of Psychology


The z-curve analysis of results in this journal shows (a) that many published results are based on studies with low to modest power, (b) selection for significance inflates effect size estimates and the discovery rate of reported results, and (c) there is no evidence that research practices have changed over the past decade. Readers should be careful when they interpret results and recognize that reported effect sizes are likely to overestimate real effect sizes, and that replication studies with the same sample size may fail to produce a significant result again. To avoid misleading inferences, I suggest using alpha = .005 as a criterion for valid rejections of the null-hypothesis. Using this criterion, the risk of a false positive result is below 2%. I also recommend computing a 99% confidence interval rather than the traditional 95% confidence interval for the interpretation of effect size estimates.

Given the low power of many studies, readers also need to avoid the fallacy to report non-significant results as evidence for the absence of an effect. With 50% power, the results can easily switch in a replication study so that a significant result becomes non-significant and a non-significant result becomes significant. However, selection for significance will make it more likely that significant results become non-significant than observing a change in the opposite direction.

The average power of studies in a heterogeneous journal like Frontiers of Psychology provides only circumstantial evidence for the evaluation of results. When other information is available (e.g., z-curve analysis of a discipline, author, or topic, it may be more appropriate to use this information).


Frontiers of Psychology was created in 2010 as a new online-only journal for psychology. It covers many different areas of psychology, although some areas have specialized Frontiers journals like Frontiers in Behavioral Neuroscience.

The business model of Frontiers journals relies on publishing fees of authors, while published articles are freely available to readers.

The number of articles in Frontiers of Psychology has increased quickly from 131 articles in 2010 to 8,072 articles in 2022 (source Web of Science). With over 8,000 published articles Frontiers of Psychology is an important outlet for psychological researchers to publish their work. Many specialized, print-journals publish fewer than 100 articles a year. Thus, Frontiers of Psychology offers a broad and large sample of psychological research that is equivalent to a composite of 80 or more specialized journals.

Another advantage of Frontiers of Psychology is that it has a relatively low rejection rate compared to specialized journals that have limited journal space. While high rejection rates may allow journals to prioritize exceptionally good research, articles published in Frontiers of Psychology are more likely to reflect the common research practices of psychologists.

To examine the replicability of research published in Frontiers of Psychology, I downloaded all published articles as PDF files, converted PDF files to text files, and extracted test-statistics (F, t, and z-tests) from published articles. Although this method does not capture all published results, there is no a priori reason that results reported in this format differ from other results. More importantly, changes in research practices such as higher power due to larger samples would be reflected in all statistical tests.

As Frontiers of Psychology only started shortly before the replication crisis in psychology increased awareness about the problem of low statistical power and selection for significance (publication bias), I was not able to examine replicability before 2011. I also found little evidence of changes in the years from 2010 to 2015. Therefore, I use this time period as the starting point and benchmark for future years.

Figure 1 shows a z-curve plot of results published from 2010 to 2014. All test-statistics are converted into z-scores. Z-scores greater than 1.96 (the solid red line) are statistically significant at alpha = .05 (two-sided) and typically used to claim a discovery (rejection of the null-hypothesis). Sometimes even z-scores between 1.65 (the dotted red line) and 1.96 are used to reject the null-hypothesis either as a one-sided test or as marginal significance. Using alpha = .05, the plot shows 71% significant results, which is called the observed discovery rate (ODR).

Visual inspection of the plot shows a peak of the distribution right at the significance criterion. It also shows that z-scores drop sharply on the left side of the peak when the results do not reach the criterion for significance. This wonky distribution cannot be explained with sampling error. Rather it shows a selective bias to publish significant results by means of questionable practices such as not reporting failed replication studies or inflating effect sizes by means of statistical tricks. To quantify the amount of selection bias, z-curve fits a model to the distribution of significant results and estimates the distribution of non-significant (i.e., the grey curve in the range of non-significant results). The discrepancy between the observed distribution and the expected distribution shows the file-drawer of missing non-significant results. Z-curve estimates that the reported significant results are only 31% of the estimated distribution. This is called the expected discovery rate (EDR). Thus, there are more than twice as many significant results as the statistical power of studies justifies (71% vs. 31%). Confidence intervals around these estimates show that the discrepancy is not just due to chance, but active selection for significance.

Using a formula developed by Soric (1989), it is possible to estimate the false discovery risk (FDR). That is, the probability that a significant result was obtained without a real effect (a type-I error). The estimated FDR is 12%. This may not be alarming, but the risk varies as a function of the strength of evidence (the magnitude of the z-score). Z-scores that correspond to p-values close to p =.05 have a higher false positive risk and large z-scores have a smaller false positive risk. Moreover, even true results are unlikely to replicate when significance was obtained with inflated effect sizes. The most optimistic estimate of replicability is the expected replication rate (ERR) of 69%. This estimate, however, assumes that a study can be replicated exactly, including the same sample size. Actual replication rates are often lower than the ERR and tend to fall between the EDR and ERR. Thus, the predicted replication rate is around 50%. This is slightly higher than the replication rate in the Open Science Collaboration replication of 100 studies which was 37%.

Figure 2 examines how things have changed in the next five years.

The observed discovery rate decreased slightly, but statistically significantly, from 71% to 66%. This shows that researchers reported more non-significant results. The expected discovery rate increased from 31% to 40%, but the overlapping confidence intervals imply that this is not a statistically significant increase at the alpha = .01 level. (if two 95%CI do not overlap, the difference is significant at around alpha = .01). Although smaller, the difference between the ODR of 60% and the EDR of 40% is statistically significant and shows that selection for significance continues. The ERR estimate did not change, indicating that significant results are not obtained with more power. Overall, these results show only modest improvements, suggesting that most researchers who publish in Frontiers in Psychology continue to conduct research in the same way as they did before, despite ample discussions about the need for methodological reforms such as a priori power analysis and reporting of non-significant results.

The results for 2020 show that the increase in the EDR was a statistical fluke rather than a trend. The EDR returned to the level of 2010-2015 (29% vs. 31), but the ODR remained lower than in the beginning, showing slightly more reporting of non-significant results. The size of the file drawer remains large with an ODR of 66% and an EDR of 72%.

The EDR results for 2021 look again better, but the difference to 2020 is not statistically significant. Moreover, the results in 2022 show a lower EDR that matches the EDR in the beginning.

Overall, these results show that results published in Frontiers in Psychology are selected for significance. While the observed discovery rate is in the upper 60%s, the expected discovery rate is around 35%. Thus, the ODR is nearly twice the rate of the power of studies to produce these results. Most concerning is that a decade of meta-psychological discussions about research practices has not produced any notable changes in the amount of selection bias or the power of studies to produce replicable results.

How should readers of Frontiers in Psychology articles deal with this evidence that some published results were obtained with low power and inflated effect sizes that will not replicate? One solution is to retrospectively change the significance criterion. Comparisons of the evidence in original studies and replication outcomes suggest that studies with a p-value below .005 tend to replicate at a rate of 80%, whereas studies with just significant p-values (.050 to .005) replicate at a much lower rate (Schimmack, 2022). Demanding stronger evidence also reduces the false positive risk. This is illustrated in the last figure that uses results from all years, given the lack of any time trend.

In the Figure the red solid line moved to z = 2.8; the value that corresponds to p = .005, two-sided. Using this more stringent criterion for significance, only 45% of the z-scores are significant. Another 25% were significant with alpha = .05, but are no longer significant with alpha = .005. As power decreases when alpha is set to more stringent, lower, levels, the EDR is also reduced to only 21%. Thus, there is still selection for significance. However, the more effective significance filter also selects for more studies with high power and the ERR remains at 72%, even with alpha = .005 for the replication study. If the replication study used the traditional alpha level of .05, the ERR would be even higher, which explains the finding that the actual replication rate for studies with p < .005 is about 80%.

The lower alpha also reduces the risk of false positive results, even though the EDR is reduced. The FDR is only 2%. Thus, the null-hypothesis is unlikely to be true. The caveat is that the standard null-hypothesis in psychology is the nil-hypothesis and that the population effect size might be too small to be of practical significance. Thus, readers who interpret results with p-values below .005 should also evaluate the confidence interval around the reported effect size, using the more conservative 99% confidence interval that correspondence to alpha = .005 rather than the traditional 95% confidence interval. In many cases, this confidence interval is likely to be wide and provide insufficient information about the strength of an effect.

Which Social Psychologists Can you Trust?

Social psychology has an open secret. For decades, social psychologists conducted experiments with low statistical power (i.e., even if the predicted effect is real, their study could not detect it with p < .05), but their journals were filled with significant (p < .05) results. To achieve significant results, social psychologists used so-called questionable research practices that most lay people or undergraduate students consider to be unethical. The consequences of these shady practices became apparent in the past decade when influential results could not be replicated. The famous reproducibility project estimated that only 25% of published significant results are replicable. Most undergraduate students who learn about this fact are shocked and worry about the credibility of results in their social psychology textbooks.

Today, there are two types of social psychologists. Some are actively trying to improve the credibility of social psychology by adopting open science practices such as preregistration of hypothesis, sharing open data, and publishing non-significant results rather than hiding these findings. However, other social psychologists are actively trying to deflect criticism. Unfortunately, it can be difficult for lay people, journalists, or undergraduate students to make sense of articles that make seemingly valid arguments, but only serve the purpose to protect the image of social psychology as a science.

As somebody who has followed the replication crisis in social psychology for the past decade, I can provide some helpful information. In the blog post , I want to point out that Duane T. Wegener and Leandre R. Fabrigar have made numerous false arguments against critics of social psychology, and that their latest article “Evaluating Research in Personality and Social Psychology: Considerations of Statistical Power and Concerns About False Findings” ignores the replication crisis in social psychology and the core problem of selectively publishing significant results from underpowered studies.

The key point of their article is that “statistical power should be de-emphasized in
comparison to current uses in research evaluation
” (p. 1105).

To understand why this is a strange recommendation, it is important to understand that power is simply the probability of producing evidence for an effect, when an effect exists. When the criterion for evidence is a p-value below .05, it means the probability of obtaining this desired outcome. One advantage of high power is that researchers get the correct result. In contrast, a study with low power is likely to produce the wrong result called a type-II error. While the study tested a correct hypothesis, the results fail to provide sufficient support for it. As these failures can be due to many reasons (low power or the theory is wrong), they are difficult to interpret and to publish. Often these studies remain unpublished, the published record is biased, and resources were wasted. Thus, high power is a researcher’s friend. To make a comparison, if you could gamble on a slot machine with a 20% chance of winning or an 80% chance of winning, which machine would you pick? The answer is simple. Everybody would rather want to win. The problem is only that researchers have to invest more resources in a single study to increase power. They may not have enough money or time to do so. So, they are more like desperate gamblers. You need a publication, you don’t have enough resources for a well-powered study, so you do a low powered study and hope for the best. Of course, many desperate gamblers lose and are then even more desperate. That is where the analogy ends. Unlike gamblers in a casino, researchers are their own dealers and can use a number of tricks to get the desired outcome (Simmons et al., 2011). Suddenly, a study with only 20% power (chance of winning honestly) can have a chance of winning of 80% or more.

This brings us to the second advantage of high-powered studies. Power determines the outcome of a close replication study. If a researcher conducted a study with 20% power and found some tricks to get significance, the probability of replicating the result honestly is again only 20%. Many unsuspecting graduate students have wasted precious years trying to build on studies that they were not able to replicate. Unless they quickly learned the dark art of obtaining significant results with low power, they did not have a competitive CV to get a job. Thus, selective publishing of underpowered studies is demoralizing and rewards cheating.

None of this is a concern for Wegener and Fabrigar, who do not cite influential articles about the use of questionable research practices (John et al., 2012) or my own work that uses estimates of observed power to reveal those practices (Schimmack, 2012; see also Francis, 2012). Instead, they suggest that “problems with the overuse of power arise when the pre-study concept of power is used retrospectively to evaluate completed research” (p. 1115). The only problem that arises from estimating actual power of completed studies, however, is the detection of questionable practices that produce more reported significant results (often 100%) than one would expect given the low power to do so. Of course, for researchers who want to use QRPs to produce inflated evidence for their theories, this is a a problem However, for consumers of research, the detection of questionable results is desirable so that they can ignore this evidence in favor of honestly reported results based on properly powered studies.

The bulk of Wegener and Fabrigar’s article discusses the relationship between power and the probability of false positive results. A false positive result occurs when a statistically significant result is obtained in the absence of a real effect. The standard criterion of statistical significance, p < .05, states that a researcher that tests 100 false hypothesis without a real effect is expected to obtain 95 non-significant results and 5 false positive results. This may sound sufficient to keep false positive results at a low level. However, the false positive risk is a conditional probability based on a significant result. If a researcher conducts 100 studies, obtains 5 significant results, and interprets these results as real effects, the researcher has a false positive rate of 100% because 5 significant results are expected by chance along. An honest researcher would conclude from a series of studies with only 5 out of 100 significant results that they found no evidence for a real effect.

Now let’s consider a researcher that conducted 100 studies and obtained 24 significant results. As 24 is a lot more than the expected 5 studies by chance along, the researcher can conclude that at least some of the 24 significant results are caused by real effects. However, it is also possible that some of these results are false positives. Soric (1989 – not cited by Wegener and Fabrigar – derived a simple formula to estimate the false discover risk. The formula makes the assumption that studies of real effects have 100% power to detect a real effect. As a result, there are zero studies that fail to provide evidence for a real effect. This assumption makes it possible to estimate the maximum percentage of false positive results.

In this simple example, we have 4 false positive results and 20 studies with evidence for a real effect. Thus, the false positive risk is 4 / 24 = 17%. While 17% is a lot more than 5%, it is still pretty low and doesn’t warrant claims that “most published results are false” (Ioannidis, 2005). Yet, it is also not very reassuring if 17% of published results might be false positives (e.g., 17% of cancer treatments actually do not work). Moreover, based on a single study, we do not know which of the 24 results are true results and false results. With a probability of 17% (1/6), trusting a result is like playing Russian roulette. The solution to this problem is to conduct a replication study. In our example, the 20 true effects will produce significant results again because they were obtained with 100% power to do so. However, the chance to replicate one of the 4 false positive results is only 5/100 * 5 / 100 = 25 / 10,000 = 0.25%. So, with high-powered studies, a single replication study can separate true and false original findings.

Things look different in a world with low powered studies. Let’s assume that studies have only 25% power to produce a significant result, which is in accordance with the success rate in replication studies in social psychology (Open Science Collaboration, 2005).

In this scenario, there is only 1 false positive result and the false positive risk is only 1 out of 21, ~ 5%. Of course, researchers do not know this and have to wonder whether some of 21 significant results are false positives. When they conduct a replication study, only 6 (25/100 * 25/100) of their 20 significant results replicate. Thus, a single replication study does not help to distinguish true and false findings. This leads to confusion and the need for additional studies to separate true and false findings, but low power will produce inconsistent results again and again. The consequences can be seen in the actual literature in social psychology. Many literatures are a selected set of inconsistent results that do not advance theories.

In sum, high powered studies quickly separate true and false findings, whereas low powered studies produce inconsistent results that make it difficult to separate true and false findings (Maxwell, 2004, not cited by Wegener & Fabrigar).

Actions speak louder than Words

Over the past decade, my collaborators and I I have developed powerful statistical tools to estimate the power of studies that were conducted (Bartos & Schimmack, 2021; Brunner & Schimmack, 2022; Schimmack, 2012). In combination with Soric’s (1989) formula, estimates of actual power can also be used to estimate the real false positive risk. Below, I show some results when this method is applied to social psychology. I focus on the journal Personality and Social Psychological Bulletin for two reasons. First, Wegener and Fabrigar were co-editors of this journal right after concerns about questionable research practices and low power became a highly discussed topic and some journal editors changed policies to increase replicability of published results (e.g., Steven Lindsay at Psychological Science). Examining the power of studies published in PSPB when Wegener and Fabrigar were editors provides objective evidence about their actions in response to concerns about replication failures in social psychology. Another reason to focus on PSPB is that Wegener and Fabrigar published their defense of low powered research in this journal, suggesting a favorable attitude towards their position by the current editors. We can therefore examine whether the current editors changed standards or not. Finally, PSPB was edited from 2017 to 2021 by Chris Crandall, who has been a vocal defender of results obtained with questionable research practices on social media.

Let’s start with the years before concerns about replication failures became openly discussed. I focus on the years 2000 to 2012.

Figure 1 shows a z-curve plot of automatically extracted statistical results published in PSPB from 2000 to 2012. All statistical results are converted into z-scores. A z-curve plot is a histogram that shows the distribution of z-scores. One important aspect of a z-curve plot is the percentage of significant results. All z-scores greater than 1.96 (the solid vertical red line) are statistically significant with p < .05 (two-sided). Visual inspection shows a lot more significant results than non-significant results. More precisely, the percentage of significant results (i.e., the Observed Discovery Rate, EDR) is 71%.

Visual inspection of the histogram also shows a strange shape to the distribution of z-scores. While the peak of the distribution is at the point of significance, the shape of the distribution shows a rather steep drop of z-scores just below z = 1.96. Moreover, some of these z-scores are still used to claim support for a hypothesis often called marginally significant. Only z-scores below 1.65 (p < .10, two-sided or .0 5 one-sided, the dotted red line) are usually interpreted as non-significant results. The distribution shows that these results are less likely to be reported. This wonky distribution of z-scores suggests that questionable research practices were used.

Z-curve analysis makes it possible to estimate statistical power based on the distribution of statistically significant results only. Without going into the details of this validated method, the results suggest that the power of studies (i.e., the expected discovery rate, EDR) would only produce 23% significant results. Thus, the actual percentage of 71% significant results is inflated by questionable practices. Moreover, the 23% estimate is consistent with the fact that only 25% of unbiased replication studies produce a significant result (Open Science Collaboration, 2005). With 23% significant results, Soric’s formula yields a false positive risk of 18%. That means, roughly 1 out of 5 published results could be a false positive result.

In sum, while Wegener and Fabrigar do not mention replication failures and questionable research practices, the present results confirm the explanation of replication failures in social psychology as a consequence of using questionable research practices to inflate the success rate of studies with low power (Schimmack, 2020).

Figure 2 shows the z-curve plot for results published during Wegener and Fabrigar’s reign as editors. The results are easily summarized. There is no significant change. Social psychologists continued to publish ~70% significant results with only 20% power to do so. Wegener and Fabrigar might argue that there was not enough time to change practices in response to concerns about questionable practices. However, their 2022 article provides an alternative explanation. They do not consider it a problem when researchers conduct underpowered studies. Rather, the problem is when researchers like me estimate the actual power of studies and reveal that massive use of questionable practices.

The next figure shows the results for Chris Chrandall’s years as editor. While the percentage of significant results remained at 70%, power to produce these results increased to 32%. However, there is uncertainty about this increase and the lower limit of the 95%CI is still only 21%. Even if there was an increase, it would not imply that Chris Crandall caused this increase. A more plausible explanation is that some social psychologists changed their research practices and some of this research was published in PSPB. In other words, Chris Crandall and his editorial team did not discriminate against studies with improved power.

It is too early to evaluate the new editorial team lead by Michael D. Robinson, but for the sake of completeness, I am also posting the results for the last two years. The results show a further increase in power to 48%. Even the lower limit of the confidence interval is now 36%. Thus, even articles published in PSPB are becoming more powerful, much to the dismay of Wegener and Fabrigar, who believe that “the recent overemphasis on statistical
should be replaced by a broader approach in which statistical and conceptual forms of validity are considered together” (p. 1114). In contrast, I would argue that even an average power of 48% is ridiculously low. An average power of 48% implies that many studies have even less than 48% power.


More than 50 years ago, famous psychologists Amos Tversky and Daniel Kahneman (1971) wrote “we refuse to believe that a serious investigator will knowingly accept a .50 risk of failing
to confirm a valid research hypothesis” (p. 110). Wegener and Fabrigar prove them wrong. Not only are they willing to conduct these studies, they even propose that doing so is scientific and that demanding more power can have many negative side-effects. Similar arguments have been made by other social psychologists (Finkel, Eastwick, Reis, 2017).

I am siding with Kahneman, who realized too late that he placed too much trust in questionable results produced by social psychologists and compared some of this research to a train wreck (Kahneman, 2017). However, there is no consensus among psychologists and readers of social psychological research have to make up their own mind. This blog post only points out that social psychology lacks clear scientific standards and no proper mechanism to ensure that theoretical claims rest on solid empirical foundations. Researchers are still allowed to use questionable research practices to present overly positive results. At this point, the credibility of results depends on researchers’ willingness to embrace open science practices. While many young social psychologists are motivated to do so, Wegener and Fabrigar’s article shows that they are facing resistance from older social psychologists who are trying to defend the status quo of underpowered research.

Publication Politics: When Your Invited Submission is Disinvited

I am not the first and I will not be the last to point out that the traditional peer-review process is biased. After all, who would take on the thankless job of editing a journal if it would not come with the influence and power to select articles you like and to reject articles you don’t like. Authors can only hope that they find an editor who favors their story during the process of shopping around a paper. This is a long and frustrating process. My friend Rickard Carlsson created a new journal that operates differently with a transparent review process and virtually no rejection rate. Check out Meta-Psychology. I published two articles there that reported results based on math and computer simulations. Nobody challenged the validity, but other journals rejected the work based on politics (AMMPS rejection).

The biggest event in psychology, especially social psychology, in the past decade (2011-2020) was the growing awareness of the damage caused by selective publishing of significant results. It has long been known that psychology journals nearly exclusively publish statistically significant results (Sterling, 1959). This made it impossible to publish studies with non-significant results that could correct false positive results. It was long assumed that this was not a problem because false positive results are rare. What changed over the past decade was that researchers published replication failures that cast doubt on numerous classic findings in social psychology such as unconscious priming or ego-depletion.

Many, if not most, senior social psychologists have responded to the replication crisis in their field with a variety of defense mechanisms, such as repression or denial. Some have responded with intellectualization/rationalization and were able to publish their false arguments to dismiss replication failures in peer-reviewed journals (Bargh, Baumeister, Gilbert, Fiedler, Fiske, Nisbett, Stroebe, Strack, Wilson, etc., to name the most prominent ones). In contrast, critics had a harder time to make their voices heard. Most of my work on this topic has been published in blog posts in part because I don’t have the patience and frustration tolerance to deal with reviewer comments. However, this is not the only reason and in this blog post I want to share what happened when Moritz Heene and I were invited by Christiph Klauer to write an article on this topic for the German journal “Psychological Rundschau”.

For readers who do not know Christipher; he is a very smart social psychologists who worked as an assistant professor with Hubert Feger when I was an undergraduate student. I respect his intelligence and his work such as his work on the Implicit Association Test.

Maybe he invited us to write a commentary because he knew me personally. Maybe he respected what we had to say. In any case, we were invited to write an article and I was motivated to get an easy ‘peer-reviewed’ publication, even if nobody outside of Germany cares about a publication in this journal.

After submitting our manuscript, I received the following response in German.
I used (free version) to share an English version.

Thu 2016-04-14 3:50 AM

Dear Uli,

Thank you very much for the interesting and readable manuscript. I enjoyed reading it and can agree with most of the points and arguments. I think this whole debate will be good for psychology (and hopefully social psychology as well), even if some are struggling at the moment. In any case, the awareness of the harmfulness of some previously widespread habits and the realization of the importance of replication has, in my impression, increased significantly among very many colleagues in the last two to three years.

Unfortunately, for formal reasons, the manusrkipt does not fit so well into the planned special issue. As I said, the aim of the special issue is to discuss topics around the replication question in a more fundamental way than is possible in the current discussions and forums, with some distance from the current debates. The article fits very well into the ongoing discussions, with which you and Mr. Heene are explicitly dealing with, but it misses the goal of the special issue. I’m sorry if there was a misunderstanding.

That in itself would not be a reason for rejection, but there is also the fact that a number of people and their contributions to the ongoing debates are critically discussed. According to the tradition of the Psychologische Rundschau, each of them would have to be given the opportunity to respond in the issue. Such a discussion, however, would go far beyond the intended scope of the thematic issue. It would also pose great practical difficulties, because of the German language, to realize this with the English-speaking authors (Ledgerwood; Feldman Barrett; Hewstone, however, I think can speak German; Gilbert). For example, you would have to submit the paper in an English version as well, so that these authors would have a chance to read the criticisms of their statements. Their comments would then have to be translated back into German for the readers of Psychologische Rundschau.

All this, I am afraid, is not feasible within the scope of the special issue in terms of the amount of space and time available. Personally, as I said, I find most of your arguments in the manuscript apt and correct. From experience, however, it is to be expected that the persons criticized will have counter-arguments, and the planned special issue cannot and should not provide such a continuation of the ongoing debates in the Psychologische Rundschau. We currently have too many discussion forums in the Psychologische Rundschau, and I do not want to open yet another one.

I ask for your understanding and apologize once again for apparently not having communicated the objective of the special issue clearly enough. I hope you and Mr. Heene will not hold this against me, even though I realize that you will be disappointed with this decision. However, perhaps the manuscript would fit well in one of the Internet discussion forums on these issues or in a similar setting, of which there are several and which are also emerging all the time. For example, I think the Fachgruppe Allgemeine Psychologie is currently in the process of setting up a new discussion forum on the replicability question (although there was also a deadline at the end of March, but perhaps the person responsible, Ms. Bermeitinger from the University of Hildesheim, is still open for contributions).

I am posting this letter now because the forced resignation of Fiedler as editor of Perspectives on Psychological Science made it salient how political publishing in psychology journals is. While many right-wing media commented on this event to support their anti-woke, pro-doze culture wars. They want to maintain the illusion that current science, I focus on psychology here, is free of ideology and only interested in searching for the truth. This is BS. Psychologists are human beings and show in-group bias. When most psychologists in power are old, White, men, they will favor old, White, men that are like them. Like all systems that work for the people in power, they want to maintain the status quo. Fiedler abused his power to defend the status quo against criticisms of a lack in diversity. He also published several articles to defend (social) psychology against accusations of shoddy practices (questionable research practices).

I am also posting it here because a very smart psychologists stated in private that he agreed with many of our critical comments that we made about replication-crisis deniers. As science is a social game, it is understandable that he never commented on this topic in public (If he doesn’t like that I am making them public, he can say that he was just polite and didn’t really mean what he wrote).

I published a peer-reviewed article on the replication crisis and the shameful response by many social psychologists several years later (Schimmack, 2020). A new generation of social psychologists is trying to correct the mistakes of the previous generation, but as so often, they do so without the support or even against the efforts of the old guard that cannot accept that many of their cherished findings may die with them. But that is life.

Klaus Fiedler is a Victim – of His Own Arrogance

One of the bigger stories in Psychological (WannaBe) Science was the forced resignation of Klaus Fiedler from his post as editor-in-chief at the prestigious journal “Perspectives on Psychological Science.” In response to his humiliating eviction, Klaus Fiedler declared “I am the victim.

In an interview, he claimed that the his actions that led to the vote of no confidence by the Board of Directors of the Association of Psychological Science (APS) were “completely fair, respectful, and in line with all journal standards.” In contrast, the Board of Directors listed several violations of editorial policies and standards.

The APS board listed the following complaints.

  • accept an article criticizing the original article based on three reviews that were also critical of the original article and did not reflect a representative range of views on the topic of the original article; 
  • invite the three reviewers who reviewed the critique favorably to themselves submit commentaries on the critique; 
  • accept those commentaries without submitting them to peer review; and, 
  • inform the author of the original article that his invited reply would also not be sent out for peer review. The EIC then sent that reply to be reviewed by the author of the critical article to solicit further comments.

As bystanders, we have to decide whether these accusations by several board members are accurate or whether these are trumped up charges that misrepresent the facts and Fiedler is an innocent victim. Even without specific knowledge about this incidence and the people involved, bystanders are probably forming an impression about Fiedler and his accusers. First, it is a natural human response to avoid embarrassment after a public humiliation. Thus, Fiedler’s claims of no wrong-doing have to be taken with a grain of salt. On the other hand, APS board members could also have motives to distort the facts, although they are less obvious.

To understand the APS board’s responses to Fiedler’s actions, it is necessary to take into account that Fiedler’s questionable editorial decisions affected Steven Roberts, an African American scholar, who had published an article about systemic racism in psychology in the same journal under a previous editor (Roberts et al., 2020). Fiedler’s decision to invite three White critical reviewers to submit their criticisms as additional commentaries was perceived by Roberts’ as racially biased. When he made his concerns public, over 1,000 bystanders agreed and signed an open letter asking for Fiedler’s resignation. In contrast, an opposing open letter received much fewer signatures. While some of the signatures on both sides have their own biases because they know Fiedler as a friend or foe, most of the signatures did not know anything about Fiedler, but reacted to Roberts’ description of his treatment. Fiedler never denied that this account was an accurate description of events. He merely claims that his actions were “completely fair, respectful, and in line with journal standards.” Yet, nobody else has supported Fiedler’s claim that it is entirely fair and acceptable to invite three White-ish reviewers to submit their reviews as commentaries and to accept these commentaries without peer-review.

I conducted an informal and unrepresentative poll that confirmed my belief that inviting reviewers to submit a commentary is rare.

What is even more questionable is that all the three reviews support with Hommel’s critical commentary of Robert’s target article. It is not clear why reviews of a commentary were needed to be published as additional commentaries if these reviews agreed with Hommel’s commentary. The main point of reviews is to determine whether a submission is suitable for publication. If Hommel’s commentary was so deficient that all three reviewers were able to make additional points that were missing from his commentary, his submission should have been rejected with or without a chance of resubmission. In short, Fiedler’s actions were highly unusual and questionable, even if they were not racially motivated.

Even if Fiedler thought that his actions were fair and unbiased when he was acting, the response by Roberts, over 1,000 signatories, and the APS board of directors could have made him realize that others viewed his behaviors differently and maybe recognize that his actions were not as fair as he assumed. He could even have apologized for his actions or at least the harm they caused however unintentional. Yet, he chose to blame others for his resignation – “I am the victim”. I believe that Fiedler is indeed a victim, but not in the way he perceives the situation. Rather than blaming others for his disgraceful resignation, he should blame himself. To support my argument, I will propose a mediation model and provide a case-study of Fiedler’s response to criticism as empirical support.

From Arrogance to Humiliation

A well-known biblical proverb states that arrogance is the cause of humiliation (“Hochmut kommt vor dem Fall). I am proposing a median model of this assumed relationship. Fiedler is very familiar with mediation models (Fiedler, Harris, & Schott, 2018). A mediation model is basically a causal chain. I propose that arrogance may lead to humiliation because it breeds ignorance. Figure 1 shows ignorance as the mediator. That is, arrogance makes it more likely that somebody is discounting valid criticism. In turn, individuals may act in ways that are not adaptive or socially acceptable. This leads to either personal harm or a damage to a person’s reputation. Arrogance and ignorance will also shape the response to social rejection. Rather than making an internal attribution that elicits feelings of embarrassed, an emotion that repairs social relationships, arrogant and ignorant individuals will make an external attribution (blame) that leads to anger, an emotion that further harms social relationships.

Fiedler’s claim that his actions were fair and that he is the victim makes it clear that he made an external attribution. He blames others, but the real problem is that Fiedler is unable to recognize when he is wrong and criticism is justified. This attributional bias is well known in psychology and called a self-serving attribution. To enhance one’s self-esteem, some individuals attribute successes to their own abilities and blame others for their failures. I present a case-study of Fiedler’s response to the replication crisis as evidence that his arrogance blinds him to valid criticism.

Replicability and Regression to the Mean

In 2011, social psychology was faced with emerging evidence that many findings, including fundamental findings like unconscious priming, cannot be replicated. A major replication project found that only 25% of social psychology studies produced a significant result again in an attempt to replicate the original study. These findings have triggered numerous explanations for the low replication rate in social psychology (OSC, 2015; Schimmack, 2020; Wiggins & Christopherson, 2019).

Explanations for the replication crisis in social psychology can be divided into two camps. One camp believes that replication failures reveal major problems with the studies that social psychologists conducted for decades. The other camp argues that replication failures are a normal part of science and that published results can be trusted even if they failed to replicate in recent replication studies. A notable difference between these two camps is that defenders of the credibility of social psychology tend to be established and prominent figures in social psychology. As a result, they also tend to be old, men, and White. However, these surface characteristics are only correlated with views about the replication crisis. The main causal factor is likely to be the threat to eminent social psychologists concerns about their reputation and legacy. Rather than becoming famous names along with Allport, their names may be used to warn future generations about the dark days when social psychologists invented theories based on unreliable results.

Consistent with the stereotype of old, White, male social psychologists, Fiedler has become an outspoken critic of the replication movement and tried to normalize replication failures. After the credibility of psychology was challenged in news outlets, the board of the German Psychological Society (DGPs) issued a reassuring (whitewashing) statement that tried to reassure the public that psychology is a science. The web page has been deleted, but a copy of the statement is preserved here (Stellungnahme). This official statement triggered outrage among some members and DGPs created a discussion forum (also deleted now). Fiedler participated in this discussion with the claim that replication failures can be explained by a statistical phenomenon known as regression to the mean. He repeated this argument in an email with a reporter that was shared by Mickey Inzlicht in the International Social Cognition Network group (ISCON) on Facebook. This post elicited many commentaries that were mostly critical of Fiedler’s attempt to cast doubt about the scientific validity of the replication project. The ISCON post and the comments were deleted (when Mickey left Facebook), but they were preserved in my Google inbox. Here is the post and the most notable comments.

Michael Inzlicht shares Fiedler’s response to the outcome of the Reproducibility Project that only 25% of significant results in social psychology could be replicated (i.e., produced a p-value below .05).


August 31 at 9:46am

Klaus Fiedler has granted me permission to share a letter that he wrote to a reported (Bruce Bowers) in response to the replication project. This letter contains Klaus’s words only and the only part I edited was to remove his phone number. I thought this would be of interest to the group.

Dear Bruce:

Thanks for your email. You can call me tomorrow but I guess what I have to say is summarized in this email.

Before I try to tell it like it is, I ask you to please attend to my arguments, not just the final evaluations, which may appear unbalanced. So if you want to include my statement in your article, maybe along with my name, I would be happy not to detach my evaluative judgment from the arguments that in my opinion inevitably lead to my critical evaluation.

First of all I want to make it clear that I have been a big fan of properly conducted replication and validation studies for many years – long before the current hype of what one might call a shallow replication research program. Please note also that one of my own studies has been included in the present replication project; the original findings have been borne out more clearly than in the original study. So there is no self-referent motive for me to be overly critical.

However, I have to say that I am more than disappointed by the present report. In my view, such an expensive, time-consuming, and resource-intensive replication study, which can be expected to receive so much attention and to have such a strong impact on the field and on its public image, should live up (at least) to the same standards of scientific scrutiny as the studies that it evaluates. I’m afraid this is not the case, for the following reasons …

The rationale is to plot the effect size of replication results as a function of original results. Such a plot is necessarily subject to regression toward the mean. On a-priori-grounds, to the extent that the reliability of the original results is less than perfect, it can be expected that replication studies regress toward weaker effect sizes. This is very common knowledge. In a scholarly article one would try to compare the obtained effects to what can be expected from regression alone. The rule is simple and straightforward. Multiply the effect size of the original study (as a deviation score) with the reliability of the original test, and you get the expected replication results (in deviation scores) – as expected from regression alone. The informative question is to what extent the obtained results are weaker than the to-be-expected regressive results.

To be sure, the article’s muteness regarding regression is related to the fact that the reliability was not assessed. This is a huge source of weakness. It has been shown (in a nice recent article by Stanley & Spence, 2014, in PPS) that measurement error and sampling error alone will greatly reduce the replicability of empirical results, even when the hypothesis is completely correct. In order not to be fooled by statistical data, it is therefore of utmost importance to control for measurement error and sampling error. This is the lesson we took from Frank Schmidt (2010). It is also very common wisdom.

The failure to assess the reliability of the dependent measures greatly reduces the interpretation of the results. Some studies may use single measures to assess an effect whereas others may use multiple measures and thereby enhance the reliability, according to a principle well-known since Spearman & Brown. Thus, some of the replication failures may simply reflect the naïve reliance on single-item dependent measures. This is of course a weakness of the original studies, but a weakness different from non-replicability of the theoretically important effect. Indeed, contrary to the notion that researchers perfectly exploit their degrees of freedom and always come up with results that overestimate their true effect size, they often make naïve mistakes.

By the way, this failure to control for reliability might explain the apparent replication advantage of cognitive over social psychology. Social psychologists may simply often rely on singular measure, whereas cognitive psychologists use multi-trial designs resulting in much higher reliability.

The failure to consider reliability refers to the dependent measure. A similar failure to systematically include manipulation checks renders the independent variables equivocal. The so-called Duhem-Quine problem refers to the unwarranted assumption that some experimental manipulation can be equated with the theoretical variable. An independent variable can be operationalized in multiple ways. A manipulation that worked a few years ago need to work now, simply because no manipulation provides a plain manipulation of the theoretical variable proper. It is therefore essential to include a manipulation check, to make sure that the very premise of a study is met, namely a successful manipulation of the theoretical variable. Simply running the same operational procedure as years before is not sufficient, logically.

Last but not least, the sampling rule that underlies the selection of the 100 studies strikes me as hard to tolerate. Replication teams could select their studies from the first 20 articles published in a journal in a year (if I correctly understand this sentence). What might have motivated the replication teams’ choices? Could this procedure be sensitive to their attitude towards particular authors or their research? Could they have selected simply studies with a single dependent measure (implying low reliability)? – I do not want to be too suspicious here but, given the costs of the replication project and the human resources, does this sampling procedure represent the kind of high-quality science the whole project is striving for?

Across all replication studies, power is presupposed to be a pure function of the size of participant samples. The notion of a truly representative design in which tasks and stimuli and context conditions and a number of other boundary conditions are taken into account is not even mentioned (cf. Westfall & Judd).


Brent W. Roberts, 10:02am Sep 4
This comment just killed me “What might have motivated the replication teams’ choices? Could this procedure be sensitive to Their attitude towards Particular authors or Their research?” Once again, we have an eminent, high powered scientist impugning the integrity of, in this case, close to 300, mostly young researchers. What a great example to set.

Daniel Lakens, 12:32pm Sep 4
I think the regression to the mean comment just means: if you start from an extreme initial observation, there will be regression to the mean. He will agree there is publication bias – but just argues the reduction in effect sizes is nothing unexpected – we all agree with that, I think. I find his other points less convincing – there is data about researchers expectencies about whether a study would replicate. Don’t blabla, look at data. The problem with moderators is not big – original researchers OKéd the studies – if they can not think of moderators, we cannot be blamed for not including others checks. Finally, it looks like our power was good, if you examine the p-curve. Not in line with the idea we messed up. I wonder why, with all commentaries I’ve seen, no one takes the effort to pre-register their criticisms, and then just look at the studies and data, and let us know how much it really matters?

Felix Cheung, ,2:11pm Sep 4
I don’t understand why the regression to mean cannot be understood in a more positive light when the “mean” in regression to the mean refers to the effect sizes of interests. If that’s the case, then regressing to mean would mean that we are providing more accurate estimates of the effect sizes.

Joachim Vandekerckhove, 2:15pm Aug 31
The dismissive “regression to the mean” argument either simply takes publication bias as given or assumes that all effect sizes are truly zero. Either of those assumptions make for an interesting message to broadcast, I feel.

Michael Inzlicht, 2:54pm Aug 31
I think we all agree with this, Jeff, but as Simine suggested, if the study in question is a product of all the multifarious biases we’ve discussed and cannot be replicated (in an honest attempt), what basis do we have to change our beliefs at all? To me the RP–plus lots of other stuff that has come to light in the past few years–make me doubt the evidentiary basis of many findings, and by extension, many theories/models. Theories are based on data…and it turns out that data might not be as solid as we thought.

Jeff Sherman, 2:58pm Aug 31
Michael, I don’t disagree. I think RP–plus was an important endeavor. I am sympathetic to Klaus’s lament that the operationalizations of the constructs weren’t directly validated in the replications.

Uli Schimmack, 11:15am Sep 1
This is another example that many psychologists are still trying to maintain the illusion that psychology doesn’t have a replicabiltiy problem.
A recurrent argument is that human behavior is complex and influenced by many factors that will produce variation in results across seemingly similar studies.
Even if this were true, it would not explain why all original studies find significant effects. If moderators can make effects appear or disappear, there would be an equal number of non-significant results in original and replication studies. If psychologists were really serious about moderating factors, non-significant results would be highly important to understand under what conditions an effect does not occur. The publication of only significant results in psychology (since 1959 Sterling) shows that psychologists are not really serious about moderating factors and that moderators are only invoked post-hoc to explain away failed replications of significant results.
Just like Klaus Fiedler’s illusory regression to the mean, these arguments are hollow and only reveal the motivated biases of their proponents to deny a fundamental problem in the way psychologists collect, analyze, and report their research findings.
If a 25% replication rate for social psychology is not enough to declare a crisis then psychology is really in a crisis and psychologists provide the best evidence for the validity of Freud’s theory of repression. Has Daniel Kahneman commented on the reproducibility-project results?

Garriy Shteynberg, 10:33pm Sep 7
Again, I agree that there is publication bias and its importance even in a world where all H0 are false (as you show in your last comment). Now, do you see that in that very world, regression to the mean will still occur? Also, in the spirit of the dialogue, try to refrain from claiming what others do not know. I am sure you realize that making such truth claims on very little data is at best severely underpowered.

Uli Schimmack, 10:38pm Sep 7
Garriy Shteynberg Sorry, but I always said that regression to the mean occurs when there is selection bias, but without selection bias it will not occur. That is really the issue here and I am not sure what point you are trying to make. We agree that studies were selected and that low replication rate is a result of this selection and regression to the mean. If you have any other point to make, you have to make it clearer.

Malte Elson, 3:38am Sep 8
Garriy Shteynberg would you maybe try me instead? I followed your example of the perfect discipline with great predictions and without publication bias. What I haven’t figured out is what would cause regression to the mean to only occur in one direction (decreased effect size at replication level). The predictions are equally great at both levels since they are exactly the same. Why would antecedent effect sizes in publications be systematically larger if there was no selection at that level?

Marc Halusic, 12:53pm Sep 1
Even if untold moderators affect the replicability of a study that describes a real effect, it would follow that any researcher who cannot specify the conditions under which an effect will replicate does not understand that effect well enough to interpret it in the discussion section.

Maxim Milyavsky, 11:16am Sep 3
I am not sure whether Klaus meant that regression to mean by itself can explain the failure of replication or regression to mean given a selection bias. I think that without selection bias regression to mean cannot count as an alternative explanation. If it could, every subsequent experiment would yield a smaller effect than the previous one, which sounds like absurd. I assume that Klaus knows that. So, probably he admits that there was a selection bias. Maybe he just wanted to say – it’s nobody’s fault. Nobody played with data, people were just publishing effects that “worked”. Yet, what is sounds puzzling to me is that he does not see any problem in this process.

– Mickey shared some of the responses with Klaus and posted Klaus’s responses to the comment. Several commentators tried to defend Klaus by stating that he would agree with the claim that selection for significance is necessary to see an overall decrease in effect sizes. However, Klaus Fiedler doubles down on the claim that this is not necessary even though the implication would be that effect sizes shrink every time a study is replicated which is “absurd” (Maxim Milyavsk), although even this absurd claim has been made (Schooler, 2011).

Michael Inzlicht, September 2 at 1:08pm

More from Klaus Fiedler. He has asked me to post a response to a sample of the replies I sent him. Again, this is unedited, directly copying and pasting from a note Klaus sent me. (Also not sure if I should post it here or the other, much longer, conversation).

Having read the echo to my earlier comment on the Nosek report, I got the feeling that I should add some more clarifying remarks.

(1) With respect to my complaints about the complete failure to take regressiveness into account, some folks seem to suggest that this problem can be handled simply by increasing the power of the replication study and that power is a sole function of N, the number of participants. Both beliefs are mistaken. Statistical power is not just a function of N, but also depends on treating stimuli as a random factor (cf. recent papers by Westfall & Judd). Power is 1 minus β, the probability that a theoretical hypothesis, which is true, will be actually borne out in a study. This probability not only depends on N. It also depends on the appropriateness of selected stimuli, task parameters, instructions, boundary conditions etc. Even with 1000 participant per cell, measurement and sampling error can be high, for instance, when a test includes weakly selected items, or not enough items. It is a cardinal mistake to reduce power to N.

(2) The only necessary and sufficient condition for regression (to the mean or toward less pronounced values) is a correlation less than zero. This was nicely explained and proven by Furby (1973). We all “learned” that lesson in the first semester, but regression remains a counter-intuitive thing. When you plot effect sizes in the replication studies as a function of effect sizes in the original studies and the correlation between corresponding pairs is < 1, then there will be regression. The replication findings will be weaker than the original ones. One can refrain from assuming that the original findings have been over-estimations. One might represent the data the other way around, plotting the original results as a function of given effects in the replication studies, and one will also see regression. (Note in this connection that Etz’ Bayesian analysis of the replication project also identified quite a few replications that were “too strong”). For a nice illustration of this puzzling phenomenon, you may also want to read the Erev, Wallsten & Budescu (1994) paper, which shows both overconfidence and underconfidence in the same data array.

(3) I’m not saying that regression is easy to understand intuitively (Galton took many years to solve the puzzle). The very fact that people are easily fooled by regression is the reason why controlling for expected regression effects is standard in the kind of research published here. It is almost a prototypical example of what Don Campbell (1996) had in mind when he tried to warn the community from drawing erroneous inferences.

(4) I hope it is needless to repeat that controlling for the reliability of the original studies is essential, because variation in reliability affects the degree of regressiveness. It is particularly important to avoid premature interpretations of seemingly different replication results (e.g., for cognitive and social psychology) that could reflect nothing but unequal reliability.

(5) My critical remark that the replication studies did not include manipulation checks was also met with some spontaneous defensive reactions. Please note that the goal to run so-called “exact” replications (I refrain from discussing this notion here) does not prevent replication researchers from including additional groups supposed to estimate the effectiveness of a manipulation under the current conditions. (Needless to add that a manipulation check must be more than a compliant repetition of the instruction).

(6) Most importantly perhaps, I would like to reinforce my sincere opinion that methodological and ethical norms have to be applied to such an expensive, pretentious and potentially very consequential project even more carefully and strictly than they are applied to ordinary studies. Hardly any one of the 100 target studies could have a similarly strong impact, and call for a similar degree of responsibility, as the present replication project.

Kind regards, Klaus

This response elicited an even more heated discussion. Unfortunately, only some of these comments were mailed to my inbox. I must have made a very negative comment about Klaus Fiedler that elicited a response by Jeff Sherman, the moderator of the group. Eventually, I was banned from the group and created the Psychological Methods Discussion Group. that became the main group for critical discussion of psychological science.

Uli Schimmack, 2:36pm Sep 2
Jeff Sherman The comparison extends to the (in German) official statement regarding the results of the OSF-replication project. It does not mention that publication bias is at least a factor that contributed to the outcome or mentions any initiatives to improve the way psychologists conduct their research. It would be ironic if a social psychologists objects to a comparison that is based on general principles of social behavior.
I think I don’t have to mention that the United States of America pride themselves on freedom of expression that even allows Nazis to publish their propaganda which German law does not allow. In contrast, censorship was used by socialist Germany to maintain in power. So, please feel free to censor my post. and send me into Psychological Method exile.

Jeff Sherman, 2:49pm Sep 2
Uli Schimmack I am not censoring the ideas you wish to express. I am saying that opinions expressed on this page must be expressed respectfully.
Calling this a freedom of speech issue is a red herring. Ironic, too, given that one impact of trolling and bullying is to cause others to self-censor.
I am working on a policy statement. If you find the burden unbearable, you can choose to not participate.

Uli Schimmack, 2:53pm Sep 2
Jeff Sherman Klaus is not even part of this. So, how am I bullying him? Plus, I don’t think Klaus is easily intimidated by my comment. And, as a social psychologist how do you explain that Klaus doubled down when every comment pointed out that he ignores the fact that regression to the mean can only produce a decrease in the average if the original sample was selected to be above the mean?

This discussion led to a letter to the DGPs board by Moritz Heene that expressed outrage about the whitewashing of the replication results in their official statement.

From: Moritz Heene
To: Andrea Abele-Brehm, Mario Gollwitzer, & Fritz Strack
Subject: DGPS-Stellungnahme zu Replikationsprojekt
Date: Wed, 02 Sep 2015

[I suggest to copy and past the German text into DeepL, a powerful translation program]

Sehr geehrte Mitglieder des Vorstandes der DGPS,

Zunächst Dank an Sie für das Bemühen, die Ergebnisse des OSF-Replikationsprojektes der Öffentlichkeit klarer zu machen. Angesichts dieser Stellungnahme der DGPS möchte ich jedoch persönlich meinen Widerspruch dazu ausdrücken, da ich als Mitglied der DGPS durch diese Stellungnahmen in keiner Weise eine ausgewogene Sichtweise ausgedrückt sehe, sie im Gegenteil als sehr einseitig empfinde. Ich sehe diese Stellungnahme vielmehr als einen Euphemismus der Replikationsproblematik in der Psychologie an, um es milde auszudrücken, bin davon enttäuscht und hatte mir mehr erwartet.
Meine Kritikpunkte an ihrer Stellungnahme:

1. Zum Argument 68% der Studien seien repliziert worden: Der Test dazu prüft, ob der replizierte Effekte im Konfidenzintervall um den originalen Effekt liegt, ob diese also signifikant voneinander verschieden sind, so die Logik der Autoren. Lassen wir mal großzügig beiseite, dass dies kein Test über die Differenz der Effektgrößen ist, da das Konfidenzintervall um den originalen beobachteten Effekt gelegt wird, nicht um die Differenz. Wesentlicher ist, dass dies ein schlechtes Maß für Replizierbarkeit ist, denn die originalen Effekte sind upward biased (sieht man in dem originalen paper auch), und vergessen wir den publication bias nicht (siehe density distribution der p-Werte im originalen paper). Anzunehmen, dass die originalen Effektgrößen die Populationseffektgrößen sind, ist wirklich eine heroische Annahme, gerade angesichts des positiven bias der originalen Effekte. Nebenbei: In einem offenen Brief von Klaus Fiedler auf Facebook dazu publiziert wurde, wird argumentiert, die Regression zur Mitte habe die im Schnitt geringeren Effektgrößen im OSF-Projekt produziert, könne diesen Effekt erklären. Dieses Argument mag teilweise stimmen, impliziert aber, dass die originalen Effekte extrem (also biased, weil selektiv publiziert wurde) waren, denn genau das ist ja das Charakteristikum dieses Regressionseffektes: Ergebnisse, die in einer ersten Messung extrem waren, “tendieren” in einer zweiten Messung zum Mittelwert. Die Tatsache, dass die originalen Effekte einen deutlichen positiven bias aufweisen, wird in Ihrer Stellungnahme ignoriert, bzw. gar nicht erst erwähnt.

Das Argument der 68%-Replizierbarkeit wird im übrigen auch vom Hauptautor in Antwort auf ihre Stellungnahme ganz offen in ähnlicher Weise kritisiert:

Kurzum: Sich genau diese Statistik als Unterstützung dafür aus der OSF-Studie herauszusuchen, um der Öffentlichkeit zu erklären, dass in der Psychologie im Grunde alles in Ordnung ist, sehe ich als “cherry picking” von Ergebnissen an.

2. Das Moderatoren-Argument ist letztlich unhaltbar, denn erstens > wurde dies insbesondere im OSF-Projekt 3 intensiv getestet. Das Ergebnis ist u.a. hier zusammengefasst:

Siehe u.a.:
In Many Labs 1 and Many Labs 3 (which I reviewed here), different labs followed standardized replication protocols for a series of experiments. In principle, different experimenters, different lab settings, and different subject populations could have led to differences between lab sites. But in analyses of heterogeneity across sites, that was not the result. In ML1, some of the very large and obvious effects (like anchoring) varied a bit in just how large they were (from “kinda big” to “holy shit”). Across both projects, more modest effects were quite consistent. Nowhere was there evidence that interesting effects wink in and out of detectability for substantive reasons linked to sample or setting. Länger findet man es hier zusammengefasst:

The authors put the interpretation so well that I’ll quote them at length here [emphasis added]:
A common explanation for the challenges of replicating results across samples and settings is that there are many seen and unseen moderators that qualify the detectability of effects (Cesario, 2014). As such, when differences are observed across study administrations, it is easy to default to the assumption that it must be due to features differing between the samples and settings. Besides time of semester, we tested whether the site of data collection, and the order of administration during the study session moderated the effects. None of these had a substantial impact on any of the investigated effects. This observation is consistent with the first “Many Labs” study (Klein et al., 2014) and is the focus of the second (Klein et al., 2015). The present study provides further evidence against sample and setting differences being a default explanation for variation in replicability. That is not to deny that such variation occurs, just that direct evidence for a given effect is needed to demonstrate that it is a viable explanation.
Zweitens schreiben Sie In ihrer Stellungnahme: Solche Befunde zeigen vielmehr, dass psychologische Prozesse oft kontextabhängig sind und ihre Generalisierbarkeit weiter erforscht werden muss. Die Replikation einer amerikanischen Studie erbringt möglicherweise andere Ergebnisse, wenn diese in Deutschland oder in Italien durchgeführt wird (oder umgekehrt). In ähnlicher Weise können sich unterschiedliche Merkmale der Stichprobe (Geschlechteranteil, Alter, Bildungsstand, etc.) auf das Ergebnis auswirken. Diese Kontextabhängigkeit ist kein Zeichen von fehlender Replizierbarkeit, sondern vielmehr ein Zeichen für die Komplexität psychologischer Phänomene und Prozesse.
Nein, das zeigen diese neuen Befunde eben nicht, denn dies ist eine (Post-hoc-)Interpretation die durch die im neuen OSF-Projekt erhobenen Moderatoren nicht unterstützt wird, da diese Moderatorenanalysen gar nicht durchgeführt wurden. Die postulierte Kontextabhängigkeit wurde zudem im OSF-Projekt #3 nicht gefunden. Was man zwischen den labs als Variationsquelle fand war schlicht und einfach Stichprobenvariation, wie man sie nun mal in der Statistik erwarten muss. Ich sehe für Ihre Behauptung also gar keine empirische Basis, wie sie doch in einer sich empirisch nennenden Wissenschaft doch vorhanden sein sollte.
Was mir als abschließende Aussage in der Stellungnahme deutlich fehlt ist, dass die Psychologie (und gerade die Sozialpsychologie) in Zukunft keine selektiv publizierten und “underpowered studies” mehr akzeptieren sollte. Das hätte den Kern des Problems etwas besser getroffen.
Mit freundlichen Grüßen,
Moritz Heene

Moritz Heene received the following response from one of the DGPs board members.

From: Mario Gollwitzer
To: Moritz Heene
Subject: Re: DGPS-Stellungnahme zu Replikationsprojekt
Date: Thu, 03 Sep 2015 10:19:28 +0200

Lieber Moritz,  

vielen Dank für deine Mail — sie ist eine von vielen Rückmeldungen, die uns auf unsere Pressemitteilung vom Montag hin erreicht hat, und wir finden es sehr gut, dass in der DGPs-Mitgliedschaft dadurchoffenbar eine Diskussion angestoßen wurde. Wir glauben, dass diese Diskussion offen geführt werden sollte; daher haben wir uns entschlossen, zu unserer Pressemitteilung (und der Science-Studie bzw. dem ganzen Replikations-Projekt) eine Art Diskussionsforum auf unserer DGPs-Homepage einzurichten. Wir arbeiten gerade daran, die Seite aufzubauen. Ich fände es gut, wenn auch du dich hier beteiligen würdest, gerne mit deiner kritischen Haltung gegenüber unserer Pressemitteilung.

Deine Argumente kann ich gut nachvollziehen — und ich stimme dir zu, dass die Zahl “68%” nicht einen “Replikationsanteil” wiederspiegelt. Das war eine missverständliche Äußerung.

Aber abgesehen davon war unser Ziel, mit dieser Pressemitteilung den negativen, teilweise hämischen und destruktiven Reaktionen vieler Medien auf die Science-Studie etwas Konstruktives hinzuzufügen bzw. entgegenzusetzen. Keineswegs wollten wir die Ergebnisse der Studie”schönreden” oder eine Botschaft im Sinne von “alles gut, business as usual” verbreiten! Vielmehr wollten wir argumentieren, dass Replikationsversuche wie diese die Chance auf einen Erkenntnisgewinn bieten, die man nutzen sollte. Das ist die konstruktive Botschaft, die wir gerne auch ein bisschen stärker in den Medien vertreten sehen wollen.

Anders als du bin ich allerdings der Überzeugung, dass es durchaus möglich ist, dass die Unterschiede zwischen einer Originalstudie undihren Replikationen durchaus durch eine (unbekannte) Menge (teilweise bekannter, teilweise unbekannter) Moderatorvariablen (und deren Interaktionen) zustande kommen. Auch “Stichprobenvariation” ist nicht anderes als ein Sammelbegriff für solche Moderatoreffekte. Einige dieser Effekte sind für den Erkenntnisgewinn über ein psychologisches Phänomen zentral, andere nicht. Es gilt, die zentralen Effekte besser zu beschreiben und zu erklären. Darin sehe ich auch einen Wert von Replikationen, insbesondere von konzeptuellen Replikationen.  

Abgesehen davon bin ich aber mit dir völlig einer Meinung, dass man nicht ausschließen kann, dass einige der nicht-replizierbaren, aber publizierten Effekte — übrigens nicht bloß in der Sozialpsychologie, sondern in allen Disziplinen — falsch Positive sind, für die es eine Reihe von Gründen gibt (selektives Publizieren, fragwürdige Auswertungspraktiken etc.), die hoch problematisch sind. Über diese Dinge wird ja andernorts auch heftig diskutiert. Diese Diskussionwollten wir aber in unserer Pressemitteilung erst einmal beseite lassen und stattdessen speziell auf die neue Science-Studiefokussieren.

Nochmals vielen Dank für deine Email. Solche Reaktionen sind für uns ein wichtiger Spiegel unserer Arbeit.

Herzliche Grüße, Mario

After the DGPs created a discussion forum, Klaus Fiedler, Moritz Heene and I shared our exchange of views openly on this site. The website is no longer available, but Moritz Heene saved a copy. He also shared our contribution on The Winnower.

We would like to address the two main arguments in Dr. Fiedler’s post on

1), that the notably lower average effect size in the OSF-project are a statistical artifact of regression to the mean,

2) that low reliability contributed to the lower effect sizes in the replication studies.

Response to 1) as noted in Heene’s previous post, Fiedler’s regression to the mean argument (results that were extreme in a first assessment tend to be closer to the mean in a second assessment) implicitly assumes that the original effects were biased; that is, they are extreme estimates of population effect sizes because they were selected for publication. However, Fiedler does not mention the selection of original effects, which leads to a false interpretation of the OSF-results in Fiedler’s commentary:

“(2) The only necessary and sufficient condition for regression (to the mean or toward less pronounced values) is a correlation less than zero. … One can refrain from assuming that the original findings have been over-estimations.” (Fiedler)

It is NOT possible to avoid the assumption that original results are inflated estimates because selective publication of results is necessary to account for the notable reduction in observed effect sizes.

a) Fiedler is mistaken when he cites Furby (1973) as evidence that regression to the mean can occur without selection. “The only necessary and sufficient condition for regression (to the mean or toward less pronounced values) is a correlation less than zero. This was nicely explained and proven by Furby (1973)” (Fiedler). It is noteworthy that Furby (1973) explicitly mentions a selection above or below the population mean in his example, when Furby (1973) writes: “Now let us choose a certain aggression level at Time 1 (any level other than the mean)”.

The math behind regression to the mean further illustrates this point. The expected amount of regression to the mean is defined as (1 – r)(mu – M), where r = correlation between first and second measurement, mu: population mean, and M = mean of the selected group (sample at time 1). For example, if r = .80 (thus, less than 1 as assumed by Fiedler) and the observed mean in the selected group (M) equals the population mean (mu) (e.g., M = .40, mu = .40, and M – mu = .40 – .40 = 0), no regression to the mean will occur because (1 – .80)(.40-.40) = .20*0 = 0. Consequently, a correlation less than 1 is not a necessary and sufficient condition for regression to the mean. The effect occurs only if the correlation is less than 1 and the sample mean differs from the population mean. [Actually the mean will decrease even if the correlation is 1, but individual scores will maintain their position relative to other scores]

b) The regression to the mean effect can be positive or negative. If M < mu and r < 1, the second observations would be higher than the first observations, and the trend towards the mean would be positive. On the other hand, if M > mu and r < 1, the regression effect is negative. In the OSF-project, the regression effect was negative, because the average effect size in the replication studies was lower than the average effect size in the original studies. This implies that the observed effects in the original studies overestimated the population effect size (M > mu), which is consistent with publication bias (and possibly p-hacking).

Thus, the lower effect sizes in the replication studies can be explained as a result of publication bias and regression to the mean. The OSF-results make it possible to estimate, how much publication bias inflates observed effect sizes in original studies. We calculated that for social psychology the average effect size fell from Cohen’s d = .6 to d = .2. This shows inflation by 200%. It is therefore not surprising that the replication studies produced so few significant results because the increase in sample size did not compensate for the large decrease in effect sizes.

Regarding Fiedler’s second point 2)

In a regression analysis, the observed regression coefficient (b) for an observed measure with measurement error is a function of the true relationship (bT) and an inverse function of the amount of measurement error (1 – error = reliability; Rel(X)):


(Interested readers can obtain the mathematical proof from Dr. Heene).

The formula implies that an observed regression coefficient (and other observed effect sizes) is always smaller than the true coefficient that could have been obtained with a perfectly reliable measure, when the reliability of the measure is less than 1. As noted by Dr. Fiedler, unreliability of measures will reduce the statistical power to obtain a statistically significant result. This statistical argument cannot explain the reduction in effect sizes in the replication studies because unreliability has the same influence on the outcome in the original studies and the replication studies. In short, the unreliability argument does not provide a valid explanation for the low success rate in the OSF-replication project.

Furby, L. (1973). Interpreting regression toward the mean in developmental research. Developmental Psychology, 8(2), 172-179. doi:10.1037/h0034145

On September 5, Klaus Fiedler emailed me to start a personal discussion over email.

From: klaus.fiedler []
Sent: September-05-15 7:17 AM
To: Uli Schimmack;
Subject: iscon gossip

Dear Uli … auf Deutsch … lieber Uli,

Du weisst vielleicht, dass ich nicht fuer Facebook registriert bin, aber ich kriege gelegentlich von anderen Notizen aus dem Chat geschickt. Du bist der Einzige, dem ich mal kurz schreibe. Du hattest geschrieben, dass meine Kommentare falsch waren und ich deshalb keinerlei Repsekt mehr verdiene.

Du bist ein methodisch motivierter und versierter Kollege, und ich waere daher sehr dankbar, wenn Du mir sagen koenntest, inwiefern meine Punkte nicht zutreffen. Was ist falsch:

— dass es die regression trap gibt?
— dass eine state-of-the art Studie der Art Retest = f(Test) für Regression kontrollieren muss?
— dass Regression eine Funktion der Reliabilitaet ist?
— dass allein ein hohes participant N keineswegs dieses Problem behebt?
— dass ein fehlender manipulation check die zentral Praemisse unterminiert, dass die UV ueberhaupt hergestellt wurde?
— dass fehlende Kontrolle von measurement + sampling error die Interpretation der Ergebnisse unterminiert?

Oder ist der Punkt, dass scientific scrutiny nicht mehr zaehlt, wenn “junge Leute” fuer eine “gute Sache” kaempfen?

Sorry, die letzte Frage driftet ein bisschen ab ins Polemische. Das war nicht so gemeint. Ich moechte wirklich wissen, warum ich falsch liege, dann wuerde ich das auch gern richtigstellen. Ich habe doch nicht behauptet, dass ich empirische Daten habe, die den Vergleich von kognitiver und sozialer Psychologie erhellen (obwohl es stimmt, dass man den Vergleich nur machen kann, wenn man Reliabilitaet und Effektivitaet der Manipulationen kontrolliert). Was mich motiviert, ist lediglich das Ziel, dass auch Meta-Science (und gerade Meta-Science) denselben strengen Standards unterliegt wie jene Forschung, die sie bewertet (und oft leichtfertig schaedigt).

Was die Sozialpsychologie angeht, so hast Du sicher schon gemerkt, dass ich auch ihr Kritiker bin … Vielleicht koennen wir uns ja mal darueber unterhalten …

Schoene Gruesse aus Heidelberg, Klaus

I responded to this email and asked him directly to comment on selection bias as a reasonable explanation for the low replicability of social psychology results.

Dear Klaus Fiedler,

Moritz Heene and I have written a response to your comments posted on the DGPS website, which is waiting for moderation.
I cc Moritz so that he can send you the response (in German), but I will try to answer your question myself.

First, I don’t think it was good that Mickey posted your comments. I think it would have been better to communicate directly with you and have a chance
to discuss these issues in an exchange of arguments. It is also
unfortunate that I mixed my response to the official DGPSs statement with your comments. I see some similarities, but you expressed a personal opinion and did not use the authority of an official position to speak for all psychologists when many psychologists disagree with the statement, which led to the post-hoc creation of a discussion forum to find out about members’ opinions on this issue.

Now let me answer your question. First, I would like to clarify that we are trying to answer the same question. To me the most important question is why the reproducibility of published results in psychology journals is so low (it is only 8% for social psychology, see my post
ion-success-in-osf-reproducibility-project/ )?

One answer to this question is publication bias. This argument has been made since Sterling (1959). Cohen (1962) estimated the replication rate at 60% based on his analysis of typical effect sizes and sample sizes in Journal of Abnormal and Social Psychology (now JPSP). The 60% estimate has been replicated by Sedlmeier and Giegerenzer (1989). So, with this figure in
mind we could have expected that 60 out of 100 randomly selected results in JPSP would replicate. However, the actual success rate for JPSP is much lower. How can we explain this?

For the past five years I have been working on a better method to estimate post-hoc power, starting with my Schimmack (2012) Psych Method paper, followed by publications on my R-Index website. Similar work has been conducted by Simonsohn (p-curve) and Wicherts
(puniform) approach. The problem with the 60% estimate is that it uses reported effect sizes which are inflated. After correcting for information, the estimated power for social psychology studies in the OSF-project is only 35%. This still does not explain why only 8% were replicated and I think it is an interesting question how much moderators or mistakes in the replication study explain this discrepancy. However, a low replication rate of 35% is entirely predicted based on the published result after taking power and publication bias into account.

In sum, it is well established and known that selectin of significant results distorts the evidence in the published literature and that this creates a discrepancy between the posted success rate (95%) and the replication rate (let’s say less than 50% to be conservative). I would be surprised if you would disagree with my argument that (a) publication bias is present and (b) that publication bias at least partially contributes to the low rate of successful replications in the OSF-project.

A few days later, I sent a reminder email.

Dear Klaus Fiedler,

I hope you received my email from Saturday in reply to your email “iscon gossip”. It would be nice if you could confirm that you received it and let me know whether you are planning to respond to it.

Best regards,
Uli Schimmack

Klaus Fiedler responds without answering my question about the fact that regression to the mean can only explain a decrease in the mean effect sizes if the original values were inflated by selection for significance.


as soon as my time permits, I will have a look. Just a general remark in response to your email, I do not undersatand what argument applies to my critical evaluation of the Nosek report. What you are telling me in the email does not apply to my critique.

Or do you contest that

  • a state-of the art study of retest = f(original test) has to tackle the regression beast
  • reliability of the dependent measure has to be controlled
  • manipulation check is crucial to assess the effective variation of the independent variable
  • the sampling of studies was suboptimal

If you disagree, I wonder if there is any common ground in scientific methodology.

I am not sure if I want to contribute to Facebook debates … As you can see, the distance from a scientitic argument to personal attacks is so short that I do not believe in the value of such a forum

Kind regards, Klaus

P.S. If I have a chance to read what you have posted, I may send a reply to the DPGs. By the way, I just sent my comments to Andrea Abele Brehm.
I did not ask her to publicize it. But that’s OK

As in a chess game, I am pressing my advantage – Klaus Fiedler is clearly alone and wrong with his immaculate regression argument – in a follow up email.

Dear Klaus Fiedler,

I am waiting for a longer response from you, but to answer your question I find it hard to see how my comments are irrelevant as they are challenge direct quotes from your response.

My main concern is that you appear to neglect the fact that regression to the mean can only occur when selection occurred in the original set of studies.

Moritz Heene and I responded to this claim and find that it is invalid.  If the original studies were not a selection of studies, the average mean should be an estimate of the average population mean and there would be no reason to expect a dramatic decrease in effect size in the OSF replication studies.  Let’s just focus on this crucial point.

You can either maintain that selection is not necessary and try to explain how regression to the mean can occur without selection or you can concede that selection is necessary and explain how the OSF replication study should have taken selection into account.  At a minimum, it would be interesting to hear your response to our quote of Furby (1973) that shows he assumed selection, while you cite Furby as evidence that selection is not necessary.

Although we may not be able to settle all disputes, we should be able to determine whether Furby assumed selection or not.

Here are my specific responses to your questions. 

– a state-of the art study of retest = f(original test) has to tackle the regression beast   [we can say that it tackeled it by examining how much selection contributed to the original results by seeing how much means regressed towards a lower mean of population effect sizes. 

Result:  there was a lot of selection and a lot of regression.

– reliability of the dependent measure has to be controlled

in a project that aims to replicate original studies exactly, reliability is determined by the methods of the original study

– manipulation check is crucial to assess the effective variation of the independent variable

sure, we can question how good the replication studies were, but adding additional manipulation checks might also introduce concerns that the study is not an exact replication.  Nobody is claiming that the replication studies are conclusive, but no study can assure that it was a perfect study.

– the sampling of studies was suboptimal

how so?  The year was selected at random.  To take the first studies in a year was also random.  Moreover it is possible to examine whether the results are representative of other studies in the same journals and they are; see my blog

You may decide that my responses are not satisfactory, but I would hope that you answer at least one of my questions: Do you maintain that the OSF-results could have been obtained without selection of results that overestimate the true population effect sizes (a lot)?


Uli Schimmack

Moritz Heene comments.

Thanks, Uli! Don’t let them get away by tactically ignoring these facts.
BTW, since we share the same scientific rigor, as far as I can see, we could ponder about a possible collaboration study. Just an idea. [This led to the statistical examination of Kahneman’s book Thinking: Fast and Slow]

Regards, Moritz

Too busy to really think about the possibility that he might have been wrong, Fiedler sends a terse response.

Klaus Fiedler

Very briefly … in a mad rush this morning: This is not true. A necessary and sufficient condition for regression is r < 1. So if the correlation between the original results and the replications is less than unity, there will be regression. Draw a scatter plot and you will easily see. An appropriate reference is Furby (1973 or 1974).

I try to clarify the issue in another attempt.

Dear Klaus Fiedler,

The question is what you mean by regression. We are talking about the mean at time 1 and time 2.

Of course, there will be regression of individual scores, but we are interested in the mean effect size in social psychology (which also determines power and percentage of significant results given equal N).

It is simply NOT true that the mean will change systematically unless there
is systematic selection of observations.

As regression to the mean is defined by (1- r) * (mu – M), the formula implies that a selection effect (mu – M unequal 0) is necessary. Otherwise the whole term becomes 0.

There are three ways to explain mean differences between two sets of exact replication studies.
The original set was selected to produce significant results. The replication studies are crappy and failed to reproduce the same conditions. Random sampling error (which can be excluded because the difference in OSF is highly significant).

In the case of the OSF replication studies, selection occurred because the published results were selected to be significant from a larger set of results with non-significant results.

If you see another explanation, it would be really helpful if you would elaborate on your theory.

Uli Schimmack

Moritz Heene joins the email exchange and makes a clear case that Fiedler’s claims are statistically wrong.

Dear Klaus Fiedler, dear Uli,

Just to add another clarification:

Once again, Furby (1973, p.173, see attached file) explicitly mentioned selection: “Now let us choose a certain aggression level at Time 1 (any level other than the mean) and call it x’ “.

Furthermore, regression to the mean is defined by (1- r)*(mu – M). See Shepard and Finison (1983, p.308, eq. [1]): “The term in square brackets, the product of two factors, is the estimated reduction in BP [blood pressure] due to regression.”

Now let us fix terms:

Definition of necessity and sufficiency

~p –> ~q , with “~” denoting negation

So, if r is not smaller than 1 than regression to the mean does not occur.

This is true as can be verified by the formula.

p –> q

So, if r is smaller than 1 than regression to the mean does occur. This is not true as can be verified by the formula as explained in our reply on and in Ulrich’s previous email.


Moritz Heene

I sent another email to Klaus to see whether he is going to respond.

Lieber Dr. Fiedler,

Kann ich noch auf eine Antwort von Ihnen warten oder soll ich annehmen dass Sie sich entschieden haben nicht auf meine Anfrage zu antworten?

LG, Uli Schimmack

Klaus Fiedler does respond.

Dear Ullrich:

Yes, I was indeed very, very busy over two weeks, working for the Humboldt foundation, for two conferences where I had to play leading roles, the Leopoldina Academy, and many other urgent jobs. Sorry but this is simply so.
I now received your email reminder to send you my comments to what you and Moritz Heene have written. However, it looks like you have already committed yourself publicly (I was sent this by colleagues who are busy on facebook):
Fiedler was quick to criticize the OSF-project and Brian Nosek for making the mistake to ignore the well-known regression to the mean effect. This silly argument ignores that regression to the mean requires that the initial scores are selected, which is exactly the point of the OSF-replication studies.

Look, this passage shows that there is apparently a deep misunderstanding about the “silly argument”. Let me briefly try to explain once more what my critique of the Science article (not Brian Nosek personally – this is not my style) referred to.
At the statistical level, I was simply presupposing that there is common ground on the premise that regressiveness is ubiquitous; it is not contingent on selected initial scores. Take a scatter plot of 100 bi-variate points (jointly distributed in X and Y). If r(X,Y) < 1(disregarding sign), regressing Y on X will result in a regression slope less than 1. The variance of predicted Y scores will be reduced. I very much hope we all agree that this holds for every correlation, not just those in which X is selected. If you don’t believe, I can easily demonstrate it with random (i.e., non-selective vectors x and y).
Across the entire set of data pairs, large values of X will be underestimated in Y, and small values of X will be overestimated. By analogy, large original findings can be expected to be much smaller in the replication. However, when we regress X on Y, we can also expect to see that large Y scores (i.e., i.e., strong replication effects) have been weaker in the original. The Bayes factors reported by Alexander Etz in his “Bayesian reproducibility project”, although not explicit about reverse regression, strongly suggest that there are indeed quite a few cases in which replication results have been stronger than the original ones. Etz’ analysis, which nicely illustrates how a much more informative and scientifically better analysis than the one provided by Nosek might look like, also reinforces my point that the report published in Science is very weak. By the way, the conclusions are markedly different from Nosek, showing that most replication studies were equivocal. The link (that you have certainly found yourself) is provided below.

We know since Rulon (1941 or so) and even since Galton (1986 or so) that regression is a tricky thing, and here I get to the normative (as opposed to the statistical, tautological) point of my critique, which is based on the recommendation of such people as Don Campbell, Daniel Kahneman & Amos Tversky, Ido Erev, Tom Wallsten & David Budescu and many others, who have made it clear that the interpretation of retesting or replication studies will be premature and often mistaken, if one does not take the vicissitudes of regression into account. A very nice historical example is Erev, Wallsten & Budescu’s 1994 Psych. Review article on overconfidence. They make it clear you find very strong evidence for both overconfidence and underconfidence in the same data array, when you regress either accuracy on confidence or confidence on accuracy, respectively. Another wonderful demonstration is Moore and Small’s 2008 Psych. Review analysis of several types of self-serving biases.

So, while my statistical point is analytically true (because regression slope with a single predictor is always < 1; I know there can be suppressor effects with slopes > 1 in multiple regression), my normative point is also well motivated. I wonder if the audience of your Internet allusion to my “silly argument” has a sufficient understanding of the “regression trap” so that, as you write:

Everybody can make up their own mind and decide where they want to stand, but the choices are pretty clear. You can follow Fiedler, Strack, Baumeister, Gilbert, Bargh and continue with business as usual or you can change. History will tell what the right choice will be.

By the way, why you put me in the same pigeon hole as Fritz, Roy, Dan, and John. The role I am playing is completely different and it definitely not aims at business as usual. My very comment on the Nosek article is driven my deep concerns about the lack of scientific scrutiny in such a prominent journal, in which there is apparently no state-of-the-art quality control. A replication project is the canonical case of a scientific interpretation that strongly calls for awareness of the regression trap. That is, the results are only informative if one takes into account what shrinkage of strong effects could be expected by regression alone. Regressiveness imposes an upper limit on the possible replication success, which ought to be considered as a baseline for the presentation of the replication results.

To do that, it is essential to control for reliability. (I know that the reliability of individual scores within a study is not the same as the reliability of the aggregate study results, but they are of course related). I also continue to believe, strongly, that a good replication project ought to control for the successful induction of the independent variable, as evident in a manipulation check (maybe in an extra group), and that the sampling of the 100 studies itself was suboptimal. If Brian Nosek (or others) come up with a convincing interpretation of this replication project, then it is fine. However, the present analysis is definitely not convincing. It is rather a symptom of shallow science.

So, as you can see, the comments that you and Moritz Heene have sent me do not really affect these considerations. And, because there is obviously no common ground between the two of us, not even about the simplest statistical constraints, I have decided not to engage in a public debate with you. I’m afraid hardly anybody in this Facebook cycle will really invest time and work to read the literature necessary to judge the consequences of the regression trap, in order to make an informed judgment. And I do not want to nourish the malicious joy of an audience that apparently likes personal insults and attacks, detached from scientific arguments.

Kind regards, Klaus

P.S. As you can see, I CC this email to myself and to Joachim Krueger, who spontaneously sent me a similar note on the Nosek article and the regression trap.! thwester

Am 9/18/2015 um 3:21 PM schrieb Ulrich Schimmack:
Lieber Dr. Fiedler,

Kann ich noch auf eine Antwort von Ihnen warten oder soll ich annehmen dass Sie sich entschieden haben nicht auf meine Anfrage zu antworten?

LG, Uli Schimmack

Klaus Fiedler responds

Dear Ullrich:

Yes, I was indeed very, very busy over two weeks, working for the Humboldt foundation, for two conferences where I had to play leading roles, the Leopoldina Academy, and many other urgent jobs. Sorry but this is simply so.

I now received your email reminder to send you my comments to what you and Moritz Heene have written. However, it looks like you have already committed yourself publicly (I was sent this by colleagues who are busy on facebook):

Fiedler was quick to criticize the OSF-project and Brian Nosek for making the mistake to ignore the well-known regression to the mean effect. This silly argument ignores that regression to the mean requires that the initial scores are selected, which is exactly the point of the OSF-replication studies.

Look, this passage shows that there is apparently a deep misunderstanding about the “silly argument”. Let me briefly try to explain once more what my critique of the Science article (not Brian Nosek personally – this is not my style) referred to.

At the statistical level, I was simply presupposing that there is common ground on the premise that regressiveness is ubiquitous; it is not contingent on selected initial scores. Take a scatter plot of 100 bi-variate points (jointly distributed in X and Y). If r(X,Y) < 1(disregarding sign), regressing Y on X will result in a regression slope less than 1. The variance of predicted Y scores will be reduced. I very much hope we all agree that this holds for every correlation, not just those in which X is selected. If you don’t believe, I can easily demonstrate it with random (i.e., non-selective vectors x and y).

Across the entire set of data pairs, large values of X will be underestimated in Y, and small values of X will be overestimated. By analogy, large original findings can be expected to be much smaller in the replication. However, when we regress X on Y, we can also expect to see that large Y scores (i.e., i.e., strong replication effects) have been weaker in the original. The Bayes factors reported by Alexander Etz in his “Bayesian reproducibility project”, although not explicit about reverse regression, strongly suggest that there are indeed quite a few cases in which replication results have been stronger than the original ones. Etz’ analysis, which nicely illustrates how a much more informative and scientifically better analysis than the one provided by Nosek might look like, also reinforces my point that the report published in Science is very weak. By the way, the conclusions are markedly different from Nosek, showing that most replication studies were equivocal. The link (that you have certainly found yourself) is provided below.

We know since Rulon (1941 or so) and even since Galton (1986 or so) that regression is a tricky thing, and here I get to the normative (as opposed to the statistical, tautological) point of my critique, which is based on the recommendation of such people as Don Campbell, Daniel Kahneman & Amos Tversky, Ido Erev, Tom Wallsten & David Budescu and many others, who have made it clear that the interpretation of retesting or replication studies will be premature and often mistaken, if one does not take the vicissitudes of regression into account. A very nice historical example is Erev, Wallsten & Budescu’s 1994 Psych. Review article on overconfidence. They make it clear you find very strong evidence for both overconfidence and underconfidence in the same data array, when you regress either accuracy on confidence or confidence on accuracy, respectively. Another wonderful demonstration is Moore and Small’s 2008 Psych. Review analysis of several types of self-serving biases.

So, while my statistical point is analytically true (because regression slope with a single predictor is always < 1; I know there can be suppressor effects with slopes > 1 in multiple regression), my normative point is also well motivated. I wonder if the audience of your Internet allusion to my “silly argument” has a sufficient understanding of the “regression trap” so that, as you write:

Everybody can make up their own mind and decide where they want to stand, but the choices are pretty clear. You can follow Fiedler, Strack, Baumeister, Gilbert, Bargh and continue with business as usual or you can change. History will tell what the right choice will be.

By the way, why you put me in the same pigeon hole as Fritz, Roy, Dan, and John. The role I am playing is completely different and it definitely not aims at business as usual. My very comment on the Nosek article is driven my deep concerns about the lack of scientific scrutiny in such a prominent journal, in which there is apparently no state-of-the-art quality control. A replication project is the canonical case of a scientific interpretation that strongly calls for awareness of the regression trap. That is, the results are only informative if one takes into account what shrinkage of strong effects could be expected by regression alone. Regressiveness imposes an upper limit on the possible replication success, which ought to be considered as a baseline for the presentation of the replication results.

To do that, it is essential to control for reliability. (I know that the reliability of individual scores within a study is not the same as the reliability of the aggregate study results, but they are of course related). I also continue to believe, strongly, that a good replication project ought to control for the successful induction of the independent variable, as evident in a manipulation check (maybe in an extra group), and that the sampling of the 100 studies itself was suboptimal. If Brian Nosek (or others) come up with a convincing interpretation of this replication project, then it is fine. However, the present analysis is definitely not convincing. It is rather a symptom of shallow science.

So, as you can see, the comments that you and Moritz Heene have sent me do not really affect these considerations. And, because there is obviously no common ground between the two of us, not even about the simplest statistical constraints, I have decided not to engage in a public debate with you. I’m afraid hardly anybody in this Facebook cycle will really invest time and work to read the literature necessary to judge the consequences of the regression trap, in order to make an informed judgment. And I do not want to nourish the malicious joy of an audience that apparently likes personal insults and attacks, detached from scientific arguments.

Kind regards, Klaus

P.S. As you can see, I CC this email to myself and to Joachim Krueger, who spontaneously sent me a similar note on the Nosek article and the regression trap.

I made another attempt to talk about selection bias and ended pretty much with a simple yes/no question as a prosecutor asking a hostile witness.

Dear Klaus,

I don’t understand why we cannot even agree about the question that regression to the mean is supposed to answer.  

Moritz Heene and I are talking about the mean difference in effect sizes (the intercept, not the slope, in a regression).  According to the Science article, the effect sizes in the replication studies were, on average, 50% lower than the effect sizes in the original studies. My own analysis for social psychology show a difference of d = .6 and d = .2, which suggests results published in original articles are inflated by 200%.   Do you believe that regression to the mean can explain this finding?  Again, this is not a question about the slope, so please try to provide an explanation that can account for mean differences in effect sizes.  

Of course, you can just say that we know that a published significant result is inflated by publication bias.  After all, power is never 100% so if you select 100% significant results for publication, you cannot expect 100% successful replications.  The percentage that you can expect is determined by the true power of the set of studies (this has nothing to do with regression to the mean, it is simply power + publication bias.   However, the  OSF-reproducibility project did take power into account and increased sample sizes to account for the problem. They are also aware that the replication studies will not produce 100% successes if the replication studies were planned with 90% power. 

The problem that I see with the OSF-project is that they were naïve to use the observed effect sizes to conduct their power analyses. As these effect sizes were strongly inflated by publication bias, the true power was much lower than they thought it would be.  For social psychology, I calculated the true power of the original studies to be only 35%.  Increasing sample sizes from 90 to 120 does not make much of a difference with power this low.   If your point is simply to say that the replication studies were underpowered to reject the null-hypothesis, I agree with you.  But the reason for the low power is that reported results in the literature are not credible and strongly influenced by bias.  Published effect sizes in social psychology are, on average, 1/3 real and 2/3 bias.  Good luck finding the false positive results with evidence like this.

Do you disagree with any of my arguments about power,  publication bias, and the implication that social psychological results lack credibility?  

Best regards,


Klaus Fiedler’s response continues to evade the topic of selection bias that undermines the credibility of published results with a replication rate of 25%, but he acknowledges for the first time that regression works in both directions and cannot explain mean changes without selection bias..

Dear Uli, Moritz and Krueger:

I’m afraid it’s getting very basic now … we are talking about problems which are not really there … very briefly, just for the sake of politeness

First, as already clarified in my letter to Uli yesterday, nobody will come to doubt that every correlation < 1 will produce regression in both directions. The scatter plot does not have to be somehow selected. Let’s talk about (or simulate) a bi-variate random sample. Given r < 1, if you plot Y as a function of X (i.e., “given” X values), the regression curve will have a slope < 1, that is, Y values corresponding to high X values will be smaller and Y values corresponding to low X values will be higher. In one word, the variance in Y predictions (in what can be expected in Y) will shrink. If you regress X on Y, the opposite will be the case in the same data set. That’s the truism that I am referring to.

Of course, regression is always a conditional phenomenon. Assuming a regression of Y on X: If X is (very) high, the predicted Y analogue is (much) lower. If X is (very) low, the predicted Y analogue is (much) higher. But this conditional IF phrase does not imply any selectivity. The entire sample is drawn randomly. By plotting Y as a function of given X levels (contaminated with error and unreliability), you conditionalize Y values on (too) high or (too) low X values. But this is always the case with regression.

If I correctly understand the point, you simply equate the term “selective” with “conditional on” or “given”. But all this is common sense, or isn’t it. If you believe you have found a mathematical or Monte-Carlo proof that a correlation (in a bivariate distribution) is 1 and there is no regression (in the scatter plot), then you can probably make a very surprising contribution to statistics and numerical mathematics.

Of course, regression a multiplicative function of unreliability and extremity. So points have to be extreme to be regressive. But I am talking about the entire distribution …

Best, Klaus

… who is now going back to work, sorry.

At this point, Moritz Heene is willing to let it go. There is really no point in arguing with a dickhead – a slightly wrong translation of the German term “Dickkopf” (bull-headed, stubborn).

Lieber Uli,

Sorry, schnell auf Deutsch:
Angesichts der Email unten von Fiedler sehe ich es als “fruitless endeavour” an, da noch weiter zu diskutieren. Er geht auf unsere -formal korrekten!- Argumente überhaupt nicht ein und mittlerweile ist er schon bei “Ihr seid es gar nicht wert, dass ich mit Euch diskutiere”
angekommen. Auch, dass er Ferby (1973) nachweislich falsch zitiert, ist ihm keine Erwähnung wert. Ich diskutiere das nun nicht mehr mit ihm, weil er es einfach nicht einsehen will und daher unsere mathematisch korrekten Argumente einfach nicht mehr erwähnt (tactical ignorance).

Eines der großen Probleme der Psychologie ist, dass die Probleme grauenhaft basal zu widerlegen sind. Bspw. ist das “hidden-moderatorArgument” am Stammtisch mit 1.3 Promille noch zu widerlegen. Taucht aber leider in Artikeln von Strack und Stroebe und anderen immer wieder auf.

I agreed with him and decided to write a blog post about this fruitless discussion. I didn’t until now, when the PoPS scandal reminded me of Fiedler’s “I am never wrong” attitude.

Hallo Moritz,

Ja Diskussion ist zu Ende.
Nun werde ich ein blog mit den emails schreiben um zu zeigen mit welchen schadenfeinigen (? Ist das wirklich ein Wort) Argumenten gearbeitet wird.

Null Respekt fuer Klaus Fiedler.

LG, Uli

I communicated our decision to end the discussion to Klaus Fiedler in a final email.

Dear Klaus,

Last email  from me to you. 

It is sad that you are not even trying to answer my questions about the results of the reproducibility project.

I also going back to work now, where my work is to save psychology from psychologists like you who continue to deny that psychology has been facing a crisis for 50 years, make some quick bogus statistical arguments to undermine the credibility of the OSF-reproducibility project, and then go back to work as usual.

History will decide who wins this argument.

Disappointed (which implies that I had expected more for you when I started this attempt at a scientific discussion), Uli

Klaus Fiedler replied with his last email.

Dear Uli:

no, sorry that is not my intention … and not my position. I would like to share with you my thoughts about reproducibility … and I am not at all happy with the (kernel of truth) of the Nosek report. However, I believe the problems are quite different from those focused in the current debate, and in the premature consequences drawn by Nosek, Simonsohn, an others. You may have noticed that I have published a number of relevant articles, arguing that what we are lacking is not better statistics and larger subject samples but a better methodology more broader. Why should we two (including Moritz and Joachim and
others) not share our thoughts, and I would also be willing to read your papers. Sure. For the moment, we have been only debating about my critique of the Nosek report. My point was that in such a report of replications plotted against originals,

  • an informed interpretation is not possible unless one takes regression into acount
  • one has to control for reliability as a crucial moderator
  • one has to consider manipulation checks
  • one has to contemplate sampling of studies

Our “debate” about 2+2=4 (I agree that’s what it was) does not affect this critique. I do not believe that I am at variance with your mathematical sketch, but it does not undo the fact that in a bivariate distribution of 100 bivariate points, the devil is lurking in the regression trap.

So please distinguish between the two points: (a) Nosek’s report does not live up to appropriate standards; but (b) I am not unwilling to share with you my thoughts about replicability. (By the way, I met Ioannidis some weeks ago and I never saw as clearly as now that he, like Fanelli, whom I also met, believe that all behavioral science is unreliable and invalid)

Kind regards, Klaus

More Gaslighting about the Replication Crisis by Klaus Fiedler

Klaus Fiedler and Norbert Schwarz are both German-born influential social psychologists. Norbert Schwarz migrated to the United States but continued to collaborate with German social psychologists like Fritz Strack. Klaus Fiedler and Norbert Schwarz have only one peer-reviewed joined publication titled “Questionable Research Practices Revisited” This article is based on John, Loewenstein, & Prelec’s (2012) influential article that coined the term “questionable research practices” In the original article, John et al. (2012) conducted a survey and found that many researchers admit that they used QRPs and also found these practices were acceptable (i.e., not a violation of ethical norms about scientific integrity). John et al.’s (2012) results provide a simple explanation for the outcome of the reproducibility project. Researchers use QRPs to get statistically significant results in studies with low statistical power. This leads to an inflation of effect sizes. When these studies are replicated WITHOUT QRPs, effect sizes are closer to the real effect sizes and lower than the inflated estimates in replications. As a result, the average effect size shrinks and the percentage of significant results decreases. All of this was clear, when Moritz Heene and I debated with Fiedler.

Fiedler and Schwarz’s article had one purpose, namely to argue that John et al.’s (2012) article did not provide credible evidence for the use of QRPs. The article does not make any connection between the use of QRPs and the outcome of the reproducibility project.

The resulting prevalence estimates are lower by order of magnitudes. We conclude that inflated prevalence estimates, due to problematic interpretation of survey data, can create a descriptive norm (QRP is normal) that can counteract the injunctive norm to minimize QRPs and unwantedly damage the image of behavioral sciences, which are essential to dealing with many societal problems” (Fiedler & Schwarz, 2016, p. 45).

Indeed, the article has been cited to claim that “questionable research practices” are not always questionable and that “QRPs may be perfectly acceptable given a suitable context and verifiable justification (Fiedler & Schwarz, 2016; …) (Rubin & Dunkin, 2022).

To be clear what this means. Rubin and Dunkin claim that it is perfectly acceptable to run multiple studies and publish only those that worked, drop observations to increase effect sizes, and to switch outcome variables after looking at the results. No student will agree that these practices are scientific or trust results based on such practices. However, Fiedler and other social psychologists want to believe that they did nothing wrong when they engaged in these practices to publish.

Fiedler triples down on Immaculate Regression

I assumed everybody had moved on from the heated debates in the wake of the reproducibility project, but I was wrong. Only a week ago, I discovered an article by Klaus Fiedler – with a co-author with one of his students that repeats the regression trap claims in an English-language peer-reviewed journal with the title “The Regression Trap and Other Pitfalls of Replication Science—Illustrated by the Report of the Open Science Collaboration” (Fiedler & Prager, 2018).

The Open Science Collaboration’s 2015 report suggests that replication effect sizes in psychology are modest. However, closer inspection reveals serious problems.

A more general aim of our critical note, beyond the evaluation of the OSC report, is to emphasize the need to enhance the methodology of the current wave of simplistic replication science.

Moreover, there is little evidence for an interpretation in terms of insufficient statistical power.

Again, it is sufficient to assume a random variable of positive and negative deviations (from the overall mean) in different study domains or ecologies, analogous to deviations of high and low individual IQ scores. One need not attribute such deviations to “biased” or unfair measurement procedures, questionable practices, or researcher expectancies.

Yet, when concentrating on a domain with positive deviation scores (like gifted students), it is permissible—though misleading and unfortunate—to refer to a “positive bias” in a technical sense, to denote the domain-specific enhancement.

Depending on the selectivity and one- sided distribution of deviation scores in all these domains, domain-specific regression effects can be expected.

How about the domain of replication science? Just as psychopathology research produces overall upward regression, such that patients starting in a crisis or a period of severe suffering (typically a necessity for psychiatric diagnoses) are better off in a retest, even without therapy (Campbell, 1996), research on scientific findings must be subject to an opposite, downward regression effect. Unlike patients representing negative deviations from normality, scientific studies published in highly selective journals constitute a domain of positive deviations, of well-done empirical demonstrations that have undergone multiple checks on validity and a very strict review process. In other words, the domain of replication science, major empirical findings, is inherently selective. It represents a selection of the most convincing demonstrations of obtained effect sizes that should exceed most everyday empirical observations. Note once more that the emphasis here is not on invalid effects or outliers but on valid and impressive effects, which are, however, naturally contaminated with overestimation error (cf. Figure 2).

The domain-specific overestimation that characterizes all science is by no means caused by publication bias alone. [!!!!! the addition of alone here is the first implicit acknowledgement that publication bias contributes to the regression effect!!!!]

To summarize, it is a moot point to speculate about the reasons for more or less successful replications as long as no evidence is available about the reliability of measures and the effectiveness of manipulations.

In the absence of any information about the internal and external validity (Campbell, 1957) of both studies, there is no logical justification to attribute failed replications to the weakness of scientific hypotheses or to engage in speculations about predictors of replication success.

A recent simulation study by Stanley and Spence (2014) highlights this point, showing that measurement error and sampling error alone (Schmidt, 2010) can greatly reduce the replication success of empirical tests of correct hypotheses in studies that are not underpowered.

Our critical comments on the OSC report highlight the conclusion that the development of such a methodology is sorely needed.

Final Conclusion

Fiedler’s illusory regression account of the replication crisis was known to me since 2015. It was not part of the official record. However, his articles with Schwarz in 2016 and Prager in 2018 are part of his official CV. The articles show a clear motivated bias against Open Science and the reforms initiated by social psychologists to fix their science. He was fired because he demonstrated the same arrogant dickheadedness in interactions with a Black scholar. Does this mean he is a racist? No, he also treats White colleagues with the same arrogance, yet when he treated Roberts like this he abused his position as gate-keeper at an influential journal. I think APS made the right decision to fire him, but they were wrong to hire him in the first place. The past editors of PoPS have shown that old White eminent psychologists are unable to navigate the paradigm shift in psychology towards credibility, transparency, and inclusivity. I hope APS will learn a lesson from the reputational damage caused by Fiedler’s actions and search for a better editor that represents the values of contemporary psychologists.

P.S. This blog post is about Klaus Fiedler, the public figure and his role in psychological science. It has nothing to do with the human being.

P.P.S I also share the experience of being forced from an editorial position with Klaus. I was co-founding editor of Meta-Psychology and made some controversial comments about another journal that led to a negative response. To save the new journal, I resigned. It was for the better and Rickard Carlsson is doing a much better job alone than we could have done together. It hurt a little, but live goes on. Reputations are not made by a single incidence, especially if you can admit to mistakes.

Implicit Bias ≠ Unconscious Bias


The journal Psychological Inquire publishes theoretical articles that are accompanied by commentaries. In a recent issue, prominent implicit cognition researchers discussed the meaning of the term implicit. This blog post differs from the commentaries by researchers in the field, by providing an outsider perspective and by focusing on the importance of communicating research findings clearly to the general public. This purpose of definitions was largely ignored by researchers who are more focused on communicating with each other than with the general public. I will show that this unique outsider perspective favors a definition of implicit bias in terms of the actual research that has been conducted under the umbrella of implicit social cognition research rather than proposing a definition that renders 30 years of research useless with a simple stroke of a pen. If social cognition researchers want to communicate about implicit bias as empirical scientists they have to define implicit bias as effects of automatically activated information (associations, stereotypes, attitudes) on behavior. This is what they have studied for 30 years. Defining implicit bias as unconscious bias is not helpful because 30 years of research have failed to provide any evidence that people can act in a biased way without awareness. Although unconscious biases may occur, there is currently no scientific evidence to inform the public about unconscious biases. While the existing research on automatically activated stereotypes and attitudes has problems, the topic remains important. As the term implicit bias has caught on, it can be used in communications with the public about, but it should be made clear that implicit does not mean unconscious.


Psychologists are notoriously sloppy with language. This leads to misunderstandings and unnecessary conflicts among scientists. However, the bigger problem is a break-down in communication with the general public. This is particularly problematic in social psychology because research on social issues can influence public discourse and ultimately policy decisions.

One of the biggest case-studies of conceptual confusion that had serious real-world consequences is the research on implicit cognition that created the popular concept of implicit bias. Although the term implicit bias is widely used to talk about racism, the term lacks clear meaning.

The Stanford Encyclopedia of Philosophy defines implicit bias as a tendency to “act on the basis of prejudice and stereotypes without intending to do so.” However, lack of intention (not wanting to) is only one of several meanings of the term implicit. Another meaning of the word implicit is automatic activation of thoughts. For example, a Scientific American article describes implicit bias as a “tendency for stereotype-confirming thoughts to pass spontaneously through our minds.” Notably, this definition of implicit bias clearly implies that people are aware of the activated stereotype. The stereotype-confirming thought is in people’s mind and not activated in some other area of the brain that is not accessible to consciousness. This definition also does not imply that implicit bias results in biased behavior because awareness makes it possible to control the influence of activated stereotypes on behavior.

Merriam Webster Dictionary offers another definition of implicit bias as “a bias or prejudice that is present but not consciously held or recognized.” In contrast to the first two meanings of implicit bias, this definition suggests that implicit bias may occur without awareness; that is implicit bias = unconscious bias.

The different definitions of implicit bias lead to very different explanations of biased behavior. One explanation assumes that implicit biases can be activated and guide behavior without awareness and individuals who act in a biased way may either fail to recognize their biases or make up some false explanation for their biased behaviors after the fact. This idea is akin to Freud’s notion of a powerful, autonomous unconscious (the Id) that can have subversive effects on behavior that contradict the values of a conscious, moral self (Super-Ego). Given the persistent influence of Freud on contemporary culture, this idea of implicit bias is popular and reinforced by the Project Implicit website that offers visitors tests to explore their hidden (hidden = unconscious) biases.

The alternative interpretation of implicit bias is less mysterious and more mundane. It means that our brain constantly retrieves information from memory that is related to the situation we are in. This process does not have a filter to retrieve only information that we want. As a result, we sometimes have unwanted thoughts. For example, even individuals who do not want to be prejudice will sometimes have unwanted stereotypes and associated negative feelings pop into their mind (Scientific American). No psychoanalysis or implicit test is needed to notice that our memory has stored stereotypes. In safe contexts, we may even laugh about them (Family Guy). In theory, awareness that a stereotype was activated also makes it possible to make sure that it does not influence behavior. This may even be the main reason for our ability to notice what our brain is doing. Rather than acting in a reflexive way to a situation, awareness makes it possible to respond more flexible to a situation. When implicit is defined as automatic activation of a thought, the distinction between implicit and explicit bias becomes minor and academic because the processes that retrieve information information from memory are automatic. The only difference between implicit and explicit retrieval of information is that the process may be triggered spontaneously by something in our environment or by a deliberate search for information.

After more than 30 years of research on implicit cognitions (Fazio, Sanbonmatsu, Powell, Kardes, 1986), implicit social cognition researchers increasingly recognize the need for clearer definitions of the term implicit (Gawronski, Ledgerwood, & Eastwick, 20222a), but there is little evidence that they can agree on a definition (Gawronski, Ledgerwood, & Eastwick, 20222b). Gawronski et al. (2022a, 2022b) propose to limit the meaning of implicit bias to unconscious biases; that is, individuals are unaware that their behavior was influenced by activation of negative stereotypes or affects/attitudes. “instances of bias can be described as implicit if respondents are unaware of the effect of social category cues on their behavioral response” (p. 140). I argue that this definition is problematic because there is no scientific evidence to support the hypothesis that prejudice is unconscious. Thus, the term cannot be used to communicate scientific results that have been obtained by implicit cognition researchers over the past three decades because these studies did not study unconscious bias.

Implicit Bias Is Not Unconscious Bias

Gawronski et al. note that their decision to limit the term implicit to mean unconscious is arbitrary. “A potential objection against our arguments might be that they are based on a particular interpretation of implicit in IB that treats the term as synonymous with unconscious” (p. 145). Gawronski et al. argue in favor of their definition because “unconscious biases have the potential to cause social harm in ways that are fundamentally different from conscious biases that are unintentional and hard-to-control” (p. 146). The key words in this argument is “have the potential,” which means that there is no scientific evidence that shows different effects of biases with and without awareness of bias. Thus, the distinction is merely a theoretical, academic one without actual real-world implications. Gawronski et al. agree with this assessment when they point out that existing implicit cognition research “provides no information about IB [implicit bias] if IB is understood as an unconscious effect of social category cues on behavioral responses. It seems bizarre to define the term implicit bias in a way that makes all of the existing implicit cognition research irrelevant. A more reasonable approach would be to define implicit bias in a way that is more consistent with the work of implicit bias researchers. As several commentators pointed out, the most widely used meaning of implicit is automatic activation of information stored in memory about social groups. In fact, Gawronski himself used the term implicit in this sense and repeatedly pointed out that implicit does not mean unconscious (i.e., without awareness) (Appendix 1).

Defining the term implicit as automatic activation makes sense because the standard experimental procedure to study implicit cognition is based on presenting stimuli (words, faces, names) related to a specific group and to examine how these stimuli influence behaviors such as the speed of pressing a button on a keyboard. The activation of stereotypic information is automatic because participants are not told to attend to these stimuli or even to ignore them. Sometimes the stimuli are also presented in subtle ways to make it less likely that participants consciously attend to them. The question is always whether these stimuli activate stereotypes and attitudes stored in memory and how activation of this information influences behavior. If behavior is influenced by the stimuli, it suggests that stereotypic information was activated – with or without awareness. The evidence from studies like these provides the scientific basis for claims about implicit bias. Thus, implicit bias is basically operationally defined as systematic effects of automatically activated information about groups on behavior.

The aim of implicit bias research is to study real-word incidences of prejudice under controlled laboratory conditions. A recent incidence at racism shows how activation of stereotypes can have harmful consequences for victims and perpetrators of racist behavior .

University of Kentucky student who repeatedly hurled racist slur at Black student permanently banned from campus

The question of consciousness is secondary. What is important is how individuals can prevent harmful consequences of prejudice. What can individuals do to avoid storing negative stereotypes and attitudes in the first place? What can individuals do to weaken stored memories and attitudes? What can individuals do to make it less likely that stereotypes are activated? What can individuals do to control the influence of attitudes when they are activated? All of these questions are important and are related to the concept of implicit as automatic activation of attitudes. The only reason to emphasize unconscious process would be a scenario where individuals are unable to control the influence of information that influences behavior without awareness. However, given the lack of evidence that unconscious biases exist, it is currently unnecessary to focus on this scenario. Clearly, many instances of biases occur with awareness (“White teacher in Texas fired after telling students his race is ‘the superior one’”).

Unfortunately, it may be surprising for some readers to learn that implicit does not mean unconscious because the term implicit bias has been popularized in part to make a distinction between well-known forms of bias and prejudice and a new form of bias that can influence behavior even when individuals are consciously trying to be unbiased. These hidden biases occur against individuals’ best intentions because they exist in a blind spot of consciousness. This meaning of implicit bias was popularized by Banaji and Greenwald (2013), who also founded the Project Implicit website that provides individuals with feedback about their hidden biases; akin to psychoanalysts who can recover repressed memories.

Gawronski et al. (2022b) point out that Greenwald and Banaji’s theory of unconscious bias evolved independently of research by other implicit bias researchers who focused on automaticity and were less concerned about the distinction between conscious and unconscious biases. Gawronski’s definition of implicit bias as unconscious bias favors Banaji and Greenwald’s school of thought (hidden bias) over other research programs (automatically activated biases). The problem with this decision is that Greenwald and Banaji recently walked back their claims about unconscious biases and no longer maintain that the effects they studies were obtained without awareness (Implicit = Indirect & Indirect ≠ Unconscious, Greenwald & Banaji, 2017). The reversal of their theoretical position is evident in their statement that “even though the present authors find themselves occasionally lapsing to use implicit and explicit as if they had conceptual meaning [unconscious vs. conscious], they strongly endorse the empirical understanding of the implicit– explicit distinction” (p. 892). It is puzzling to see Gawronski arguing for a definition that is based on a theory that the authors no longer endorse. Given the lack of scientific evidence that stereotypes regularly lead to biases without awareness, this might be the time to agree on a definition that matches the actual research by implicit cognition researchers, and the most fitting definition would be automatic activation of stereotypes and attitudes, not unconscious causes of behavior.

Gawronski et al. (2022a) also falsely imply that implicit cognition researchers have ignored the distinction between conscious and unconscious biases. In reality, numerous studies have tried to demonstrate that implicit biases can occur without awareness. To study unconscious biases, social cognition researchers have relied heavily on an experimental procedure known as subliminal priming. In a subliminal priming study, a stimulus (prime) is presented very briefly, outside of the focus of attention, and/or with a masking stimuli. If a manipulation check shows that individuals have no awareness of the prime and the prime influences behavior, the effect appears to occur without awareness. Several studies suggested that racial primes can influence behavior without awareness (Bargh et al., 1996; Davis, 1989).

However, the credibility of these results has been demolished by the replication crisis in social psychology (Open Science Collaboration, 2015; Schimmack, 2020). Priming research has been singled out as the field with the biggest replication problems (Kahneman, 2012). When asked to replicate their own findings, leading priming researchers like Bargh refused to do so. Thus, while subliminal priming studies started the implicit revolution (Greenwald & Banaji, 2017), the revolution imploded over the past decade when doubts about the credibility of the original findings increased.

Unfortunately, researchers within the field of implicit bias research often ignore the replication crisis and cite questionable evidence as if it provided solid evidence for unconscious biases. For example, Gawronski et al. (2022b) suggest that unconscious biases may contribute to racial disparities in use-of-force errors such as the high-profile killing of Philando Castile. To make this case, they use a (single) study of 58 White undergraduate students (Correll, Wittenbrink, Crawford, & Sadler, 2015, Study 3). The study asked participants to make shoot vs. no-shoot decisions in a computer task (game) that presented pictures of White or Black men holding a gun or another object. Participants were instructed to make one quick decision within 630 milliseconds and another decision without time restriction. Gawronski et al. suggest that failures to correct an impulsive error given ample time to do so constitutes evidence of unconscious bias. They summarized the results as evidence that “unconscious effects on basic perceptual processes play a major role in tasks that more closely resemble real-world settings” (p. 226).

Fact checking reveals that this characterization of the study and its results is at least misleading, if not outright false. First, it is important to realize that the critical picture was presented for only 175ms and immediately replaced by another picture to wipe out visual memory. Although this is not a strictly subliminal presentation of stimuli, it is clearly a suboptimal presentation of stimuli. As a result, participants sometimes had to guess what the object was. They also had no other information to know whether their initial perception was correct or incorrect. The fact that participants’ performance improved without time pressure may be due to response errors under time pressure and this improvement was evident independent of the race of the men in the picture.

Without time pressure, participants shot 85% of armed Black men and 83% of armed White men. For unarmed men, participants shot 28% Black men and 25% White men. The statistical comparison of these differences showed weak effect of a systematic bias. The comparison for unarmed men produced a p-value that was just significant with the standard criterion of alpha = .05 criterion, F(1,53) = 6.65, p = .013, but not the more stringent criterion of alpha = .005 that is used to predict a high chance of replication. The same is true for the comparison of responses to pictures of unarmed men, F(1,53) = 4.96, p =.031. To my knowledge, this study has not been replicated and Gawronski et al.’s claim rests entirely on this single study.

Even if these effects could be replicated in the laboratory, they do not provide any information about unconscious biases in the real world because the study lacks ecological validity. To make claims about the real world, it is necessary to study police officers in simulations of real world scenarios (Andersen, Di Nota, Boychuk, Schimmack, & Collins, 2021). This research is rare, difficult, and has not yet produced conclusive results. Andersen et al. (2021) found a small racial bias, but the sample was too small to provide meaningful information about the amount of racial bias in the real world. Most important, however, real-word scenarios provide ample information to see whether a suspect is Black or White and is armed or not. The real decision is often whether use of force is warranted or not. Racial biases in these shooting errors are important, but they are not unconscious biases.

Contrary to Gawronski et al., I do not believe that social cognition researchers focus on automatic biases rather than unconscious biases was a mistake. The real mistake was the focus on reaction times in artificial computer tasks rather than studying racial biases in the real world. As a result, thirty years of research on automatic biases has produced little insights into racial biases in the real world. To move the field towards the study of unconscious biases would be a mistake. Instead, social cognition researchers need to focus on outcome variables that matter.


The term implicit bias can have different meanings. Gawronski et al. (2022a) proposed to limit the meaning of the term to unconscious bias. I argue that this definition of implicit bias is not useful because most studies of implicit cognition are studies in which racial stereotypes and attitudes toward stigmatized groups are automatically activated. In contrast, priming studies that tried to distinguish between conscious and unconscious activation of this information have been discredited during the replication crisis and there exists no credible empirical evidence to suggest that unconscious biases exist or contribute to real-world behavior. Thus, funding a new research agenda focusing on unconscious biases may waste resources that are better spent on real-world studies of racial biases. Evidently, this conclusion diverges from the conclusion of implicit cognition researchers who are interested in continuing their laboratory studies, but they have failed to demonstrate that their work makes a meaningful contribution to society. To make research on automatic biases more meaningful, implicit bias research needs to move from artificial outcomes like reaction times on computer tasks to actual behaviors.

Appendix 1

Implicit Cognition Research Focusses on Automatic (Not Unconscious) Processes

Gawronski & Bodenhausen (2006), WOS/11/22 1,537

“If eras of psychological research can be characterized in terms of general ideas, a major theme of the current era is probably the notion of automaticity” (p. 692)

This perspective is also dominant in contemporary research on attitudes, in which deliberate, “explicit” attitudes are often contrasted with automatic, “implicit” attitudes (Greenwald & Banaji, 1995; Petty, Fazio, & Brin˜ol, in press; Wilson, Lindsey, &
Schooler, 2000; Wittenbrink & Schwarz, in press).

“We assume that people generally do have some degree of conscious access to their automatic affective reactions and that they tend to rely on these affective reactions in making evaluative judgments (Gawronski, Hofmann, & Wilbur, in press; Schimmack & Crites, 2005) (p. 696).

Conrey, Sherman, Gawronski, Hugenberg, & Groom (2005) , WOS/11/22

“The distinction between automatic and controlled processes now occupies a central role in many areas of social psychology and is reflected in contemporary dual-process theories of prejudice and stereotyping (e.g., Devine, 1989)” (p. 469)

“Specifically, we argued that performance on implicit measures is influenced by at least four different processes: the automatic activation of an association (association activation), the ability to determine a correct response (discriminability), the success at overcoming automatically activated associations (overcoming bias), and the influence of response biases
that may influence responses in the absence of other available guides to response (guessing)” (p. 482)

Gawronski & DeHouwer (2014), WOS 11/22 240

” other researchers assume that the two kinds of 11lL’asurcs tap into distinct memory representations, such that explicit measures tap into conscious representations whereas implicit measures tap into unconscious representations (e.g., Greenwald &
Banaji, 1995). Although the conceptualizations arc relatively common in the literature on implicit measures, we believe that it is concecptually more appropriate to classify different measures in terms of whether the tobe-measured psychological attribute influences participants’ responses on the task in an automatic fashion (De Houwer, Teige-Mocigemba, Spruyt, & Moors, 2009).” (p. 283)

Hofmann, Gawronski, Le, & Schmitt, PSPB, 2005, WoS/11/22

“These [implicit] measures—most of them based on reaction times in response compatibility tasks (cf. De Houwer, 2003)—are intended to assess relatively automatic mental associations that are difficult to gauge with explicit self-report measures”. (p. 1369)

Gawronski, Hofmann, & Wilbur (2006), WoS/11/22 200

“A common explanation for these findings is that the spontaneous behavior assessed in these
studies is difficult to control, and thus more likely to be influenced by automatic evaluations, such as they are reflected in indirect attitude measures” (p. 492)

“there is no empirical evidence that people lack conscious awareness of indirectly assessed attitudes per se” (p. 496)

Gawronski, LeBel, & Peters, PoPS (2007) WOS/11/22 187

“The central assumption in this model is that indirect measures provide a proxy for the activation of associations in memory” (p. 187)

Gawronski & LeBel, JESP (2008) WOS/11/22

“We argue that implicit measures provide a proxy for automatic associations in memory,
which may or may not influence verbal judgments reflected in self-report measures” (p. 1356)

Deutsch, Gawronski, & Strack, JPSP (2006), WOS/11/22 122

“Phenomena such as stereotype and attitude activation can be readily reconstructed as instance-based automaticity. For example, perceiving a person of a stereotyped group or an
attitude object may be sufficient to activate well-practiced stereotypic or evaluative associations in memory” (p. 386)

Implicit measures are important even if they do not assess unconscious processes.

Hofmann, Gawronski, Le, & Schmitt, PSPB, 2005, WoS/11/22

” Arguably one of the most important contributions in social cognition research within the last decade was the development of implicit measures of attitudes, stereotypes, self-concept, and self-esteem (e.g., Fazio, Jackson, Dunton, & Williams, 1995; Greenwald, McGhee, & Schwartz, 1998; Nosek & Banaji, 2001; Wittenbrink, Judd, & Park, 1997).” (p. 1369)

Gawronski & DeHouwer (2014), WOS 11/22 240

“For the decade to come, we believe that the field would benefit from a stronger focus on underlying mechanisms with regard to the measures themselves as well as their capability to predict behavior (see also Nosek, Hawkins, & Frazier, 2011).” (p. 303)

Lost in Latent Variable Space

Post-war American Psychology is rooted in behaviorism. The key assumption of behaviorism is that psychology (i.e., the science of the mind) should only study phenomena that are directly observable. As a result, the science of the mind became the science of behavior. While behaviorism is long dead (see the 1990 funeral here), it’s (harmful) effect on psychology is still noticeable today. One lasting effect is psychologists aversion to make causal attributions to the mind (cognitive processes). While cognitive processes cannot be directly observed with the human senses (we cannot see, touch, smell, or hear what goes on in somebody’s mind), we can indirectly observe these processes on the basis of observable behaviors. A whole different discipline that is called psychometrics has developed elaborate theories and statistical models to relate observed behaviors to unobserved processes in the mind. Unfortunately, psychometrics is often not covered in the education of psychologists. As a result, psychologists often make simple mistakes when they apply psychometric tools to psychological questions.

In the language of psychometrics, observed behaviors are observed variables and unobserved mental processes are unobserved variables that are also often called latent (i.e., of a quality or state) existing but not yet developed or manifest; hidden or concealed) variables. The goal of psychometrics is to find systematic relationships between observed and latent variables that make it possible to study mental processes. We can compare this process to the task of early astronomers to make sense of the lights in the night sky. Bright stars are like observable indicators and the task of astronomers is to explain the behavior of these observable variables with unobserved forces. Astronomy has come a long way from seeing astrological signs in the sky, but psychology is pretty much at this early stage of science, where most of the unknown cognitive processes that cause observable behaviors are unknown. In fact, some psychologists still resist the idea that observable behavior can be explained by latent variables (Borsboom et al., 2021). Others, however, have used psychometric tools, but fail to understand the basic properties of psychometric models (e.g., Digman, 1997; DeYoung & Peterson, 2002; Musek, 2007). Here, I give a simple introduction to the basic logic of psychometric models and illustrate how applied psychologists can get lost in latent variable space.

Figure 2 shows the most basic psychometric model that relates an observed variable to an unobserved cause. I am using a widely used measure of life-satisfaction as an example. Please rate your life on a scale from 0 = worst possible life to 10 = best possible life. Thousands of studies with millions of respondents have used this question to study “the secret of happiness.” Behaviorists would treat this item as a stimulus and participants responses on the 11-point rating scales as behaviors. One problem for behaviorists is that participants will respond differently to the same question. Responses vary from 0 (very rarely) all the way to 10 (more often, but still rare). The modal response in affluent Western countries is 7. Behaviorism has no answer to the question why participants respond differently to the same situation (i.e., question). Some researchers have tried to provide a behavioristic answers by demonstrating that responses can be manipulated (e.g., responses are different in a good or bad mood; Schwarz & Strack, 1999; Kahneman, 2011). However, these effects are small and do not explain why responses are highly stable over time and across different situations (Schimmack & Oishi, 2005). To explain why some people report higher levels of life-satisfaction than others, we have to invoke unobserved causes within respondents’ minds. Just like forces that creates the universe, these causes are not directly observable, but we know they must exist because we observe variation in responses that cannot be explained by variation in the situation (i.e., same situation and different behaviors imply internal causes).

Psychologists have tried to understand the mental processes that produce variation in Cantril ladder scores for nearly 100 years (Andrews & Whitey, 1976; Cantril, 1965; Diener, 1984; Hartmann, 1936). In the 1980s, focus shifted from thoughts about one’s life (e.g., I hate my work, I love my spouse, etc.) to the influence of personality traits (Costa & McCrae, 1980). Just like life-satisfaction, personality is a latent variable that can only be measured indirectly by observing differences in behaviors in the same situation. The most widely used observed variables to do so are self-ratings of personality.

The key problem for the measurement of unobserved mental processes is that variation in observed scores can be caused by many different mental processes. To go beyond the level of observed variation in behaviors, it is necessary to separate the different causes that contribute to the variance in observed scores. The first step is to separate causes that produce measurement error. The most widely used approach to do so is to ask the same or similar questions repeatedly and to consider variability in responses as measurement error. The next figure shows a model for responses to two similar items.

When two or more observed variables are available, it is possible to examine the correlation between two variables. if two observed variables share a common cause, they are going to be correlated. The strength of the correlation depends on the relative strength of the shared mental process and the unique mental processes. Psychometrics works in reverse and makes inferences about the unobserved causes by examining the observed correlations. To do so, it is necessary to make some assumptions, and this is where things can go wrong, when researchers do not understand these assumptions.

A common assumption is that the shared causal processes are important and meaningful, whereas the unique mental processes are unimportant, irrelevant, and error variance. Based on this assumption, the model is often drawn differently. Sometimes, the shared unobserved variable is drawn on top, and the unshared unobserved variables are drawn at the bottom (top = important, bottom = unimportant).

Sometimes, the unique mental processes are drawn smaller and without a name.

And sometimes, they are simply omitted because they are considered unimportant and irrelevant.

The omission of the unshared causes makes sense when psychometricians communicate with each other because they are trained in understanding psychometric models and use figures merely as a short-hand to communicate with each other. However, when psychometricians communicate with psychologists things can go horribly wrong because psychologists may not realize that the omission of residuals is based on assumptions that can be right or wrong. They may simply assume that the unique variances are never important and can always be omitted. However, this is a big mistake with undesirable consequences. To demonstrate this, I am always going to show the unique causes of all variables in the following models.

When psychologists ask similar questions repeatedly, they are assuming that the unique causes of the responses are measurement error. In the present example, individuals may interpret the words “worry” and “nervous” somewhat differently and this may elicit different mental processes that result in slightly different responses. However, the two terms are sufficiently similar that they also elicit similar cognitive processes that produce a correlation between responses to the two items. Under this assumption, the common causes reflect the causes that are of interest and the unique causes produce error variance. Under the assumption that unique causes produce error variance, it is possible to average responses to similar items. These averages are called scales. Averaging amplifies the variance that is produced by shared causes.

This is illustrated in the next figure where the average is fully determined by the two observed variables “I often worry” and “I am often nervous.” To make this a measurement model, we have to relate the average scores to the unobserved variables. Now we see that the shared mental process variable has two ways to influence the average scores, whereas each of the unique causes has only one way to contribute to the average. As the number of variables increases the ratio (2:1) becomes even bigger for the shared variable (3 variables, 3:1). This implies that the shared mental processes more and more determine the average scores. This is the only part of measurement theory that psychologists are taught and understand as reflected in the common practice to report Cronbach’s alpha (a measure of the shared variance in the average scored) as evidence that a measure is a good measure (Flake & Fried, 2020). However, the real measurement problems are not addressed by averaging across similarly-worded items. This is revealed in the next figure.

To use the average of responses to similarly worded items as an observed measure of an unobserved personality trait, we have to assume that the shared mental processes that produce most of the variance in the average scores are caused by the personality trait that we are trying to measure. In the present example, personality psychologists use items like “worry” and “nervous” to measure a trait called Neuroticism. Despite 100 years of research, it is still not clear what Neuroticism is and some psychologists still doubt that Neuroticism even exists. Those who do believe in Neuroticism assume it reflects a general disposition to have more negative thoughts (e.g., low self-esteem, pessimism) and feelings (anxiety, anger, sadness, guilt). The main problem in current personality research is that item-averages are often treated as if they are perfect observed indicators of an unobserved personality trait (see next figure).

Ample research suggests that average scores of neuroticism items are also influenced by other factors such as socially desirable responding. Thus, it is a simplification to assume that item-averages are identical or isomorphous to the personality trait that they are designed to measure. Nevertheless, it is common for personality psychologists to study the influence of unobserved causes like Neuroticism by means of item averages. As we see later, even when psychologists use latent variable models, Neuroticism is just a label for an item-average. The problem with this practice is that it gives the illusion that we can study the causal effects of unobservable personality traits by examining the correlations of observable item-averages.

In this way, measurement problems are treated as unimportant, just like behaviorists considered mental processes as unimportant and relegated them to a black box that should not be examined. The same attitude prevails today with regards to personality measurement, when boxes (observed variables) are given names without checking that the labels actually match the content of the box (i.e., the unobserved causes that a measure is supposed to reflect). Often psychological constructs are merely labels for item-averages. Accordingly, neuroticism is ‘operationalized’ with an item-average and neuroticism can be defined as “whatever a neuroticism scale measures.”

When Things Go from Bad to Worse

In the 1980s, personality psychologists came to a broad consensus that the diversity of human traits (e.g., anxious, bold, curious, determined, energetic, frank, gentle, helpful, etc.) can be organized into a taxonomy with five broad traits, known as the Big Five. The basic idea is illustrate in the next Figure with Neuroticism. According to Big Five theory, Neuroticism is a general disposition to experience more anxiety, anger, and sadness. However, each emotion also has its one dispositions. Thus, variation in scales that measure anxiety, anger, and sadness is influenced by both Neuroticism (i.e., the general disposition) and specific causes. In addition, scales can also be influenced by general and specific measurement errors. The figure makes it clear that the scores in the item-averages can reflect many different causes aside from the intended broader personality trait called Neuroticism. This makes it risky to rely on these item averages to draw inferences about the unobserved variable Neuroticism.

A true science of personality would try to separate these different causes and to examine how they relate to other variables. However, personality psychologists often hide the complexity of personality measurement by treating personality scales as if they directly reflect a single cause). While this is bad enough, things get even worse when personality psychologists speculate about even broader personality traits.

The General Personality Factor (Musek, 2007)

The Big Five were considered to be roughly independent from each other. In fact, they were found with a method that looked for independent factors (another name for unobserved variables) more commonly used in personality research. However, when Digman (1997) examined correlations among item-averages, he found some systematic patterns in these correlations. This led him to postulate even broader factors than the Big Five that might explain these patterns. The problem with these theories is that they are no longer trying to relate observed variables to unobserved variables. Rather, Digman started to speculate about causal relationships among unobserved variables on the basis of imperfect indicators of the Big Five.

The first problem with Digman’s attempt to explain correlations among unobserved variables was that he lacked expertise in the use of psychometric models. As a result, he made some mistakes and his results could not be replicated (Anusic et al., 2009). A few years later, a study that controlled for some of the measurement problems by using self-ratings and informant ratings suggested that the Big Five are more or less independent and that correlations reflect measurement error (Biesanz & West, 2004; see also Anusic et al., 2009). However, other studies suggested that higher-order factors exists and may have powerful effects on people’s lives, including their well-being. Subsequently, I am going to show that these claims are based on a simple misunderstanding of measurement models that treat unique variance in the Big Five scales as error variance.

Musek (2007) proposed that correlations among Big Five scales can be explained with a single higher-order factor. This model is illustrated in his Figure 1.

First, it is notable that the unique mental processes that contribute to each of the Big Five scales are called e1 to e5 and the legend of the figure explains that e stands for error variances. This terminology can be justified if we treat Big Five scales only as observed variables that help us to observe the unobserved variable GFP. As GFP is not directly observable, we have to infer its presence from the correlations among the observed variables, namely the Big Five scales. However, labeling the unique causes that produce variation in Neuroticism scores error variance is dangerous because we may think that the unique variance in Neuroticism is no longer important; just error. Of course, this variance is not error variance in some absolute sense. After all, Neuroticism scales exists only because personality psychologists assume that Neuroticism is a real personality trait that is related to even more specific traits like anxiety, anger, and sadness. Thus, all of the variance in a neuroticism scale is assumed to be important and it would be wrong to assume that only the variance shared with other Big Five scales is important. To avoid this misinterpretation, it would be better to keep the unique causes in the model.

Another problem of this model is that the model itself provides no information about the actual causes of the correlations among the Big Five scales. This is different when items are written for the explicit purpose of measuring something that they have in common. In contrast, the correlations among the Big Five traits are an empirical phenomenon that requires further investigation to understand the nature of the causal processes that produce correlations. In other words, GFP is just a name for “shared cognitive processes;” it does not tell us what these shared cognitive processes are. To examine this question, it is necessary to see how the GFP is related to other things. This is where things go horribly wrong. Rather than relating the unobserved variable in Figure 1 to other measures, Musek (2007) averages all Big Five items to create an item average that is supposed to represent the unobserved variable. He then uses correlations of the GFP scale to make inferences about the GFP factor. The problems of this approach are illustrated with the next figure.

The figure illustrates that the general personality scale is not a good indicator of the general personality factor. The main problem is that the scale scores are also influenced by the unique causes that contribute to variation in the Big Five scales (on top of measurement error that is not shown in the picture to avoid clutter, but should not be forgotten). The problem is hidden when the unique causes are represented as errors, but unique variance in neuroticism is not error variance. It reflects a disposition to have more negative thoughts and this disposition could have a negative influence on life-satisfaction. This contribution of unique causes is hidden when Big Fife scale scores are averaged and labeled General Personality.

Musek (2007) reports a correlation of r = .5 (Study 1) between the general personality scale and a life-satisfaction scale. Musek claims that this high correlation must reveal a true relationship between the general factor of personality and life-satisfaction and cannot reflect a method artifact like social desirable responding. It is unclear why Musek (2007) relied on an average of Big Five scale scores to examine the relationship of the general factor with life-satisfaction. Latent variable modeling makes it possible to examine the relationship of the general factor directly without the need for scale scores. Fortunately, it is possible to conduct this analysis post-hoc based on the reported correlations in Table 1.

The first model created a general personality scale and used the scale as a predictor of life-satisfaction. The only difference to a simple correlation is that the model also includes the implied measurement model. This makes the model testable because it imposes restrictions on the correlations of the Big Five scales with the life-satisfaction scale. The fit of the model was acceptable, but not great, suggesting that alternative models might produce even better fit, RMSEA = .078, CFI = .958.

In this model, it is possible to trace the paths from the unobserved variables to life-satisfaction. The strongest relationship was the path from the general personality factor (h) to life-satisfaction, b = .42, se = .04, but the model also implied that unique variances of the Big Five scales contribute to life-satisfaction. These effects are hidden when the general personality scale is interpreted as if it is a pure measure of the general personality factor.

A direct test of the assumption that the general factor is the only predictor of life-satisfaction requires a simple modification of the model that links life-satisfaction directly to the general factor (h). This model actually fits the data better, RMSEA = .048, CFI = .984. This might suggest that the unique causes of variation in the Big Five are unrelated to life-satisfaction.

However, good fit is not sufficient to accept a model. It is also important to rule out plausible alternative models. An alternative model assumes that the Big Five factors are necessary and sufficient to explain variation in life-satisfaction. There is no reason to create a general scale and use it as a predictor. Instead, life-satisfaction can simply be regressed onto the Big Five scales as indicator of the Big Five factors. In fact, it is always possible to get good fit for a model that uses indicators as predictors of outcomes because the model does not impose any restrictions (i.e., the model is just identified). The only reason why this model fits worse than the other model is that fit indices like RMSEA and CFI reward parsimony and this model uses 5 predictors of life-satisfaction whereas the previous model had only one predictor. However, parsimony cannot be used to falsify a model.

In fact, it is possible to find an even better fitting model because only two of the five Big Five scales were significant predictors of life-satisfaction. This finding is consistent with many previous studies that these two Big Five traits are the strongest predictors of life-satisfaction. If the model is limited to these two predictors, it fits the data better than the model with a direct path from the general factor, CFI = .987, RMSEA = .045. Musek (2007) was unable to realize that the unique variances in neuroticism and extraversion make a unique contribution to life-satisfaction because the general personality scale does not separate shared and unique causes of variation in the Big Five scales.

The Correlated Big Two

In contrast to Musek (2007), DeYoung and Peterson favor a model with two correlated higher-order factors (DeYoung, Peterson, & Higgins, 2002; see Schimmack, 2022, for a detailed discussion).

As Musek (2007) they treat the unique causes of variation in Big Five traits as error (e1-e5) and assume that relationships of the higher-order factors with criterion variables are direct rather than being mediated by the Big Five factors. Here, I fitted this model to Musek’s (2007) data. Fit was excellent, CFI = .996, RMSEA = .030.

Based on this model, life-satisfaction would be mostly predicted by stability rather than neuroticism and extraversion or a general factor. However, just because this model has excellent fit doesn’t mean it is the best model. The model simply masks the presence of a general factor by modeling the shared variance between Plasticity and Stability as a correlated residual. It is also possible to model it with a general factor. In this model, Stability and Plasticity would be an additional level in a hierarchy between the Big Five and the General Factor. This model does not impose any additional restrictions and fits the data as well as the previous model, CFI = .996, RMSEA = .030. Thus, even though Stability and Plasticity can be identified, it does not mean that this distinction is important for the prediction of life-satisfaction. The general factor could still be the key predictor of life-satisfaction.

However, both models make the assumption that the unique causes of variation in Big Five scales are unrelated to life-satisfaction, and we already saw that this assumption is false. As a result, the model that relates life-satisfaction to neuroticism and extraversion fits the data, CFI = .994, RMSEA = .035, and the paths from extraversion and neuroticism to life-satisfaction were significant.

Musek (2007) and DeYoung et al. (2006) ignored the possibility that unique causes of variation in the Big Five contribute to the prediction of other variables because they made the mistake to equate unique variances with error variances. This interpretation is based on the basic examples that are used to illustrate latent variable models for beginners. However, the interpretation of all aspects of a latent variable model, including the residual or unique variances has to be guided by theory. To avoid these mistakes, psychometricians need to stop presenting their models as if they can be used without substantive theory and substantive researchers need to get better training in the use of psychometric tools.


Compared to other sciences like physics, astronomy, chemistry, or biology, psychology has made little progress over the past 40 years. While there are many reasons for this lack of progress, one problem is the legacy of behaviorism to focus on observable behaviors and to rely on experimentation as the only scientific approach to test causal theories. Another problem is an ideological bias against personality as a causal force that produces variation between individuals (Mischel, 1968). To make progress, personality science has to adopt a new scientific approach that uses observed behaviors to test causal theories of unobservable forces like personality. While personality scales can be used to predict behaviors and life-outcomes, they cannot explain behaviors and life-outcomes. Latent variable modeling provides a powerful tool to test causal theories. The biggest advantage of latent variable modeling is that model fit can be used to reject models. A cynic might think that this is the main reason why they are ot used more by psychologists because it is more fun to build a theory and confirm it rather than to find out that it was false, but fun doesn’t equal scientific progress.

P.S. What about Network Models?

Of course, it is also possible to reject the idea of unobserved variables altogether and draw pictures of the correlations (or partial correlations) among all the observed variables. The advantage of this approach is that it always produces results that can be used to tell an interesting story about the data. The disadvantage is that it always produces a result and therefore doesn’t test any theory. Thus, these models cannot be used to advance personality psychology towards a science that progresses by testing and rejecting false theories.

Princeton Talk About Z-Curve

Awards, Ivy League universities, or prestigious journals are suboptimal heuristics to evaluate people’s work, but in a world of information overflow, they influence the popularity of ideas. Therefore, I am caching in on Jason Geller’s invitation to present z-curve in the Advanced Research Methods seminar at Princeton.

The talk was recorded and Jason and Princeton University generously shared the recording with me (Video). The talk builds on previous talks, but incorporates the latest z-curve findings that demonstrate the power of z-curve to predict replication failures and to justify the use of alpha = .005 as a reasonable criterion for significance tests to keep the risk of false positive results in psychological journals at a reasonably low level.

You can find many other z-curve related articles and studies on my blog. Here I want to mention only the two peer-reviewed articles that introduced the method and provide more detailed information about the method.

Estimating Population Mean Power Under Conditions of Heterogeneity and Selection for Significance

Z-Curve 2.0: Estimating Replication Rates and Discovery Rates

To conduct your own z-curve analysis, you can use the z-curve package in R.

Racism and Traffic Stops

Recently, a team of German sociologists combined data about racial biases in police stops in the United States (Stanford Open Policing Project ; Pierson et al., 2020) and data about county-level average levels of racial biases collected by Project Implicit (Xu et al., 2022). The key finding was that various measures of racial bias were correlated with racial bias in traffic stops by police (published in the Supplement Table 2).

The authors missed an opportunity to examine the validity of different measures of racial attitudes under the assumption that all measures, implicit and explicit, reflect a common attitude rather than distinct attitudes (Schimmack, 2021). If implicit measures tapped some distinct form of unconscious bias, they should show incremental predictive validity. To examine this question, I used the correlations in Table 2 and fitted a structural equation model to the data. I found that a model with a single racial bias factor fitted the data reasonably well, chi2 (df = 9, N ~ 300) = 34.52, CFI = .975, RMSEA = .097. The effect size of b = .369 for bias implies that for every increase in bias by one standard deviation, there is a .369 increase in racial bias in traffic stops. This is considered a moderate effect size in comparison to other effect sizes in the social sciences.

,The more interesting result is that the race IAT and simple self-report measures of racial bias are equally valid measures of counties’ average level of racial bias. The effect sizes are .797 for the feeling thermometer, .784 for a simple preference rating, and .834 for the race Implicit Association Test; a computerized task that is less susceptible to socially desirable responding. The high validity coefficients of these measures can be explained by the aggregation of individuals’ scores. Aggregation reduces random measurement error as well as systematic biases that are unique to individuals. Thus, the present results show that race IAT scores are valid measures of racial biases at the aggregated level. The results also show that self-ratings provide as much valid information. This undermines claims by Greenwald, who developed the IAT, that the race IAT is a more valid measure of racial biases than self-ratings (see also Schimmack, 2021, for studies at the individual level).

The figure also shows an additional relationship between the race IAT and the weapons IAT. This relationship reveals that IAT tasks reflect some information that is not captured by self-reports. However, it is not clear whether this variance is method variance or valid variance of unconscious bias. In the latter case, the unique variance in the race IAT could predict police stops in addition to the bias factor (incremental predictive validity).

Adding this path did not improve model fit and the effect size estimate was not significantly different from zero, b = -.045, 95%CI = -.305 to .214. These results are consistent with many other results that the incremental predictive validity of the race IAT is elusive and even if it is not zero, it is likely to be negligible (Kurdi et al., 2019).

In short, the article could have made a nice contribution to the literature by demonstrating that implicit and explicit measures of racial bias show high convergent validity when they are aggregated to measure racial bias of US counties, and by demonstrating that racial bias predicts an important behavior, namely police officers’ decision to conduct a traffic stop.

However, the discussion of the results in the article is problematic and may reveal a sociological bias or the lack of lived experience of German researchers. The authors interpret the results as evidence that situational factors explain the results.

The observed relationships between regional-level bias and police traffic stops underscore the role of the context in which police officers operate. Our findings are consistent with theorizing by Payne et al. (2017), who argued that some contexts expose individuals more regularly to stereotypes and/or prejudice, increasing mental accessibility of biased thoughts and feelings, in turn influencing individual behavior. Consequently, behavioral expressions of prejudice and stereotypes often reflect properties of contexts rather than stable dispositions of people (but see Connor & Evers, 2020).”

The plausible alternative explanation is relegated to a “but see.” As a German who has lived in the United States and is constantly exposed to US media while living in Canada, I think the “but” deserves more attention and is actually a more plausible explanation of these findings. After all, police officers are not Robo-Cops or United Nations soldiers. They are typically born and raised in the county or in close proximity they are working in (Flint Town). As a result, their own racial biases are likely to be similar to the racial biases measured in the Project Implicit data (see Andersen et al., 2021, for race IAT scores of police officers). Thus, it is entirely possible that racial biases of police officers, rather than some mysterious unidentified social context, contribute to the racial biases in police stops. This does not mean that social factors are not at play. The fact that racial bias is not some involuntary, unconscious bias means that better training and incentives can be used to reduce bias in police officers’ behaviors without changing their attitudes and feelings. Traffic stops are clearly deliberate actions that are not made in a split second. Thus, officers can be trained in avoiding biases in their actions without the need to change their implicit or explicit attitudes. Although attitude change would be desirable, it is difficult and will take time. For now, Black citizens are likely to settle for equal treatment rather than waiting for changes in implicit attitudes that are difficult to measure and have no known effects on behavior.

In conclusion, it is well known that racism is a problem among US police officers. Often these officers are known and remain on the force. This study shows that these racial attitudes have clear consequences that sometimes lead to the death of innocent Black civilians. To attribute these incidences to some abstract contextual factors ignores the lived experiences of thousands of African Americans. The data are fully consistent with the common assumption of African Americans that racists cops are more likely to pull them over. The present study showed that this fear is more justified in counties with higher levels of racism.

Personality Misch-Masch-urement

Lew Goldberg has made important contributions to personality psychology. He contributed to the development of the Big Five model that is currently the most widely accepted model of the higher-order factors of personality that describe the relationship among the basic trait words used in everyday language.

He also pioneered open science when he made a large pool of personality items available to all researchers and created open and free measures that mimic proprietary measures like Costa and McCrae’s NEO scales. Because these measures were designed to measure the original scales as closely as possible, the validity of the scales is defined in terms of correlations with the existing scales. The goal of the IPIP project was not to examine validity or to improve on existing measures. As Lew pointed out in a personal correspondence to me, users of IPIP measures could have created new measures based on the initial 300 items. The fact that users of these items have failed to do so shows a lack of interested in construct validation. Thanks to Lew Goldberg, we have open items and open data to develop better measures of personality.

The extended 300-item IPIP measure has been used to provide thousands of internet users free feedback about their personality, and Johnson made his data from these surveys openly available (OSF-data).

The present critical examination of the psychometric properties of the IPIP scales would not be possible without these contributions. My main criticism of personality measurement is that personality psychologists have not used the statistical tools that are needed to validate a personality measure. A common and false belief among personality psychologists is that these tools are not suitable for personality measures. A misleading article by McCrae, Costa and colleagues in the esteemed Journal of Personality and Social Psychology did not help. The authors were unable to fit a Big Five model to their data. Rather than questioning the model, they decided that the method is wrong because “we know that the Big Five model is right”. This absurd conclusion has been ridiculed by psychometricians (Borsboom, 2006), but led only to a defensive response by personality psychologists (Clark, 2006). For the most part, personality psychologists today continue to create scales or use scales that lack proper validation. The IPIP-300 is no exception. This blog post is just illustrates with a simple example how bad measurement can derail science.

The IPIP-300 aims to measure 30 personality traits that are called facets. Facets are constructs that are more specific than the Big Five and closer to everyday trait concepts. Each facet is measured with 10 items. The 10 items are summed or averaged to give individuals a score for one of the 30 facets. Each facet has a name. There are two ways to interpret these names. One interpretation is that the name is just a short-hand for a scientific construct. For example, the term Depression is just a name for the sum-scores of 10-items from the IPIP. To know what this sum score actually measures, one might need to examine the item content, learn about the correlations of this sum-score with other sum-scores, or understand the scientific theory that let to the creation of the 10-items. Accordingly, the Depression scale measures whatever it is supposed to measure and what this is is called Depression. In this case, we could change the name of the scale without changing anything in our understanding of the scale. We could call it the D-scale or just facet number 3 of Neuroticism. Depression is just a name. The alternative view assumes that the 10-items were selected to measure a construct that is at least somewhat related to what we mean by depression in our everyday language. For example, we would be surprised to see the item “I like ginger” or “I often break the rules” in a list of items that are supposed to measure depression. The use of everyday trait worlds as labels for scales does usually imply that researchers are aiming to measure a construct that is at least similar to the everyday meaning of the label. Unfortunately, this is often not the case and interpreting scales based on their labels can lead to misunderstandings.

To illustrate the problem of misch-mesch-urement, I am using two facets scales from the IPIP-300 that are labeled Depression and Modesty. I used the first 10,000 observations in Johnson’s dataset and selected only US respondents with complete data (N = 6,786). The correlation between Depression and Modesty was r = .35, SE = .01. I replicated this finding with the next 10,000 observations, again selecting only US respondents with complete data (N = 5,864), r = .39, SE = .01. The results clearly show a moderate positive relationship between the two scale scores. A correlation of r = .35 implies that a respondent who is above average in Depression has about a 67.5% probability to be also above average in Modesty. We could now start speculating about the causal mechanism that produces this correlation. Maybe bragging (not being modest) reduces the risk of depression. Maybe being depressed lowers the probability of bragging. Maybe it is both and maybe there are third variables at play. However, before we even start down this path, we have to consider the possibility that the sum score labels are misleading and we are not even seeing the correlation between the constructs that we have in mind when we talk about depression and modesty. This question is examined by fitting a measurement model to the items that were used to create the sum scores.

Of course, the two scales were chosen because a simple measurement model does not fit the data. This is shown with a simplified figure of a measurement model that assumes the 10 items of a scale all reflect a common construct and some random measurement error. The items are summed to reduce the random measurement error so that the sum score mostly reflects the common construct. The main finding is that this simple model does not meet standard criteria of acceptable fit such as a Comparative Fit Index (CFI) greater than .95 or a Root Mean Square Error of Approximation (RMSEA) below .06. Another finding is that the correlation between the factors (i.e., unobserved variables that are assumed to cause the shared variance among items) is even stronger, r = .69, than the correlation among the scales. This would be interpreted as evidence that measurement error reduces the correlation with scales and the correlation among the factors shows the true correlation. However, the model does not fit and the correlation should not be interpreted.

Inspection of the items suggests some reasons why the simple model may not fit and why the positive correlation is at least inflated, if not totally an artifact. For example, the item “Have a low opinion of myself” is used as an item to measure Depression, while the item “Have a high opinion of myself ” is reversed and used to measure Modesty (reverse scoring means that low ratings on this item are scored as high modesty). Just looking at the items, we might suspect that they are both measures of low and high self-esteem, respectively. While it is plausible that Depression and Modesty are linked to low self-esteem, but it is a problem to use self-esteem items to measure both. This will produce an artificial positive correlation between the scales and lead to the false impression that Depression and Modesty are positively correlated when they are actually unrelated or even negatively related. This is what I call the misch-masch problem of personality measurement. Scales are foremost averages of items and it is not clear what these scales measure if the scales are not properly evaluated with a measurement model.

As items are closer to the level of everyday conversations about personality, it is not difficult to notice other similarities between items. For example, “often feel blue” and “rarely feel blue” are simply oppositely worded questions about the same feeling. These items should correlate more strongly (negatively) with each other than the item “rarely feel blue” and “feel comfortable with myself”. However, our interpretation of items may differ from the interpretation of the average survey respondent. Thus, we need to examine empirically the pattern of correlations. One reason why personality researchers do not do this is another confusion caused by a bad label. The best statistical tool to explore the pattern of correlations among items with called Confirmatory Factor Analysis. The label “Confirmatory” has led to the false impression that this method can only be used to confirm a theoretical model. But when a model like the simple model in Figure 1 does not fit, we do not have a theory to suggest a more complex model. We could of course explore the data, but the term confirmatory implies that this would be wrong or an abuse of a method that should not be used for exploration. This is pure nonsense. We can use CFA to explore the data, find a plausible model that fits the data, and then confirm this model with a new dataset. We can then also use this model to make new predictions, test them, and if the predictions fail, further revise the model. This is called science and fully in line with Cronbach and Meehl’s (1955) approach to construct validation. Why do I make such a big deal about this? Because my suggestion to use CFA to explore personality data has been met with a lot of resistance by veteran personality psychologists.

In response to a related blog post, William Revelle wrote me an email.

Inspired by your blog on how one needs to use CFA to do hierarchical models (which is in fact, incorrect), I prepared the enclosed slides.
I try to point out that EFA approaches can a) give goodness of fit tests and  b) do hierarchical models.
In a previous post you suggested that those of us in personality should know some psychometrics and not use simple sum scores.  I think you are correct with respect to the first part of your argument, but you might find my paper with Keith Widaman a useful response suggesting that sum scores are not as bad as you think.
Your comment about some people (i.e., our Dutch friend) refusing to understand the silliness of a general factor of personality was most accurate. 

Bill is right that EFA can sometimes produce the right results, but this is not a good argument to use an inferior method. The key problem of EFA is that it does not require any theory and as a result also does not test a theory. If a model does not fit, researchers cannot change the model because the model is based on a stringent set of mathematical principles that are not based on any substantive theory. In contrast, CFA requires that researchers think about their data and why the model does not fit.

In response to my CFA analysis of Costa and McCrae’s NEO-PI-R, Robert McCrae wrote this response:

I just read your blog on “what lurks beneath”. I must say that I find the blog format disconcerting, both for its informality and its lack of editing and references. But here are a few responses.
1. We certainly agree that people ought to measure facets as well as domains; that personality is not simple structured; that there is some degree of evaluative bias in any single source of data.
2. What we argued in the 1996 paper was that CFA “as it has typically been applied in investigating personality structure, is systematically flawed” (p. 552, italics added). I should think you would agree with that position; you have criticized others for failing to acknowledge secondary loadings and evaluative biases in their CFAs.
3. Why in the world do you think that “CFA is the only method that can be used to test structural theories”? If that were true, I would agree with your position. But the major point of our paper was to offer an alternative confirmatory approach using targeted rotation. There are a number of instances where this method has led to falsification of hypotheses—John’s study of personality in dogs and cats showed that the FFM doesn’t fit even after targeted rotation.
4. I would have liked a comparison with Marsh’s ESEM, which was developed in part in response to our 1996 paper.
5.”The evaluation of model fit was still evolving”. That, I would say, is an understatement. In my experience, most fit indices in SEM and other statistical approaches are essentially as arbitrary as p < .05. There are virtually no empirical tests of the utility of fit indices. And most are treated as dichotomies: A model fits or not. That is like deciding that coefficient alpha should be .70, and throwing out a scale because its alpha is only .69. I recall a paper on national levels of traits in which the authors were told by reviewers not to report the observed means because they could not demonstrate measurement invariance. This is statistically-mandated data suppression.
6. I am not quite convinced by your analysis of evaluative bias in the NEO data. It is really difficult to separate substance from style in mono-method data. One could argue that the factor you call EVB is really N, and vice-versa. I have attached a chapter in which we reported joint factor analyses of self-reports and observer ratings and included bias factors (pp. 280-283).

I was fortunate to take a CFA (SEM) course offered by Ralf Schwarzer at the Free University Berlin in the early 1990s. I have been using LISREL, EQS, and now MPLUS for 30 years. I thought, the older professors were just too old to learn this method, and that the attitudes would change. However, in 2006 Borsboom wrote his attack on bad practices in personality research and measurement is still considered a secondary topic in graduate education. This attitude towards measurement has been called a measurement-schmeasurement attitude (Flake & Fried, 2020). It is time to end this embarrassing status quo and to take measurement seriously.

After exploring the data and trying many different models, I settled on a model that fits the data. I then cross-validated this model in the second dataset. However, given the large sample sizes, the structure is very robust and the model had nearly identical fit in the second dataset. The model fit of the cross-validated model also met standard fit criteria, CFI = .983, RMSEA = .035. This does not mean that it is the best model. As the data are open, other researchers could try to find better models. Importantly, minor differences between models are not important, as long as the main results are consistent. The model also does not automatically tell us what the 10-item scales measure. This question can only be answered with additional data that relate the factors in the model to other variables. However, we can at least see how items are related to the factors that the scales aimed to measure.

Figure 2 shows that it is possible to describe the correlations among items from the same scale with three factors that are simply labeled Dep1, Dep2, and Dep3 for Depression and Mod1, Mod2, and Mod3 for Modesty. Dep1 is mainly related to feeling blue and depressed. Dep2 is related to low self-esteem. Dep 3 is related to two items that might be interpreted as pessimism. Mod1 is related to low self-esteem, Mod2 is about bragging, and Mod3 is about avoiding being the center of attention. As predicted by the similar wording, two self-esteem items of Mod2 are also related to the Dep2 factor. In addition, the Modesty factor is also related to Dep2, presumably because modest participants do not rate themselves lower on self-estem items. However, there is no relationship to Dep1, the feeling blue factor. Thus, Modesty is not related to feeling depressed, as implied by the Depression label of the scale. In fact, the correlation between the Depression and Modesty factors is now close to zero. Thus, the strong correlation in the bad fitting model and the moderate correlation based on scale scores misrepresents the relationship between Depression and Modesty.

Simple models of two facets are just a building block along the way to testing more complex models of personality. I hope you realize that this is an important step before personality scales can be used for research and before people are given feedback about their personality online. You might be surprised that not all personality psychologists agree. Some personality researchers rather publish pretty pictures of the models in their heads without checking that they actually fit real data. For example, Colin DeYoung has published this picture to illustrate his ideas about the structure of personality.

This model implies that there should be a negative correlation between the Depression facet of Neuroticism and the Modesty facet of Agreeableness because Stability has a negative relationship with Neuroticism and a positive relationship with Agreeableness (minus times plus = minus). I shared my initial results that showed a positive correlation which contradicts his model (see also our published results by Anusic et al., 2009, that showed problems with the Stability factor).

His final response was:

Uli, I think the problem is that the actual structure is too complex to make it easily represented in a single CFA model. The point of the pictures is to show only some important aspects of the actual structure. As long as one acknowledges it’s only part of the structure, I don’t see that as a problem.”

To my knowledge he has never attempted to specify his model in more detail to accommodate findings that are inconsistent with this simple model. He also does not seem very eager to explore this question using CFA.

I suppose I could try to create a more complete CFA model, starting from the 10 aspects, which would allow correlations between Enthusiasm and Compassion and between Politeness and Assertiveness, and also would include additional paths from Plasticity and Stability to certain aspects, but even then I’d be wary of claiming it was the complete structure. Whatever might be left out could still easily lead to misfit. It would take a lot of chutzpah to claim that one was confident in understanding all details of the covariance structure of personality traits.

To me this sounds like an excuse for bad fit. The picture gets it right, even if the model does not fit. This is the same argument that was ridiculed by Borsboom’s critique of Costa and McCrae. If models are immune to empirical tests, they are merely figments of researchers’ imagination. To make scientific claims one first needs to pass the first test: show that a model fits the data, and if a simple model does not fit the data, we need to reject the simple model and find a better one. As Revelle pointed out, nowadays EFA software can also show fit indices. What he doesn’t say is that the typical EFA models have bad fit and that there is not much EFA users can do when this is the case. In contrast, CFA can be used to explore the data, find plausible models with good fit, like the one in Figure 2, and then test these models with new data. Call me crazy, but I have the chutzpah and confidence that I can find a well-fitting model for the structure of personality. In fact, I have already done so (Schimmack, 2019), and now I am working on doing the same for the IPIP-300. Stay tuned for the complete results. I hope this post made it clear why it is important to examine this question even for measures that have been used for decades in hundreds of studies.

Post-Script: When a figure says less than zero words

In a further email exchange Colin DeYoung asked me to add the following clarification.


Uli, please add the following quote to your blog post. You are misrepresenting me inasmuch as you are claiming that my theoretical position requires that your model of modesty and depression should show a negative correlation between modesty and depression. This is not true. I would absolutely never predict that, and I think quoting the passage here makes it clear why that is:

“A final note on the hierarchy shown in Fig. 1: It is necessarily an oversimplification at the levels below the Big Five, because personality does not have simple structure (Costa & McCrae, 1992; Hofstee, de Raad, & Goldberg, 1992). Some facets and aspects have associations, not depicted in the figure, with factors in other domains. This is true even between some traits located under different metatraits, which could not be related if the diagram in Fig. 1 were complete. For example, Compassion is positively related to Enthusiasm, and Politeness is negatively related to Assertiveness (DeYoung et al., 2007, 2013).”


Happy to add this to the blog post, but I do have to ask.  Is there any finding that you would take seriously to revise your model or is this model basically unfalsifiable? 

After all, I also fitted a model without higher-order factors and aspects to the 30 facets.   It would be really interesting to do a multi-method study with facet-factors as starting point, but I don’t know a study that did that or any data to do it. 


Thanks, Uli. Please do add that text to your blog post as my explanation of the figure.

As that text points out, what you’re calling my “model” is in fact just a summary of various empirical results. It is not, and has never been, intended as a formal CFA model.

[Explanation: The figure uses the symbolic language of causal modeling that links factors (circles) to other factors (circles) with arrows pointing from one factor to another (implying a causal effect or at least a representation of shared variance among factors that are related to a common higher-order factor. It is not clear what this figure could tell readers unless we believe that factors are real and at some point explain a pattern of observed correlations. To say that the model is not a CFA model is to say that the model makes no empirical predictions and that factors like Stability or Plasticity only exit as constructs in Colin’s imagination. Not sure why we should print such imaginary models in a scientific article.]