Category Archives: Replication Crisis

Once a p-hacker, always a p-hacker?

The 2010s have seen a replication crisis in social psychology (Schimmack, 2020). The main reason why it is difficult to replicate results from social psychology is that researchers used questionable research practices (QRPs, John et al., 2012) to produce more significant results than their low-powered designs warranted. A catchy term for these practices is p-hacking (Simonsohn, 2014).

New statistical techniques made it possible to examine whether published results were obtained with QRPs. In 2012, I used the incredibility index to show that Bem (2011) used QRPs to provide evidence for extrasensory perception (Schimmack, 2012). In the same article, I also suggested that Gailliot, Baumeister, DeWall, Maner, Plant, Tice, and Schmeichel, (2007) used QRPs to present evidence that suggested will-power relies on blood glucose levels. During the review process of my manuscript, Baumeister confirmed that QRPs were used (cf. Schimmack, 2014). Baumeister defended the use of these practices with a statement that the use of these practices was the norm in social psychology and that the use of these practices was not considered unethical.

The revelation that research practices were questionable casts a shadow on the history of social psychology. However, many also saw it as an opportunity to change and improve these practices (Świątkowski and Dompnier, 2017). Over the past decades, the evaluation of QRPs has changed. Many researchers now recognize that these practices inflate error rates, make published results difficult to replicate, and undermine the credibility of psychological science (Lindsay, 2019).

However, there are no general norms regarding these practices and some researchers continue to use them (e.g., Adam D. Galinsky, cf. Schimmack, 2019). This makes it difficult for readers of the social psychological literature to identify research that can be trusted or not, and the answer to this question has to be examined on a case by case basis. In this blog post, I examine the responses of Baumeister, Vohs, DeWall, and Schmeichel to the replication crisis and concerns that their results provide false evidence about the causes of will-power (Friese, Loschelder , Gieseler , Frankenbach & Inzlicht, 2019; Inzlicht, 2016).

To examine this question scientifically, I use test-statistics that are automatically extracted from psychology journals. I divide the test-statistics into those that were obtained until 2012, when awareness about QRPs emerged, and those published after 2012. The test-statistics are examined using z-curve (Brunner & Schimmack, 2019; Bartos & Schimmack, 2020). Results provide information about the expected replication rate and discovery rate. The use of QRPs is examined by comparing the observed discovery rate (how many published results are significant) to the expected discovery rate (how many tests that were conducted produced significant results).

Roy F. Baumeister’s replication rate was 60% (53% to 67%) before 2012 and 65% (57% to 74%) after 2012. The overlap of the 95% confidence intervals indicates that this small increase is not statistically reliable. Before 2012, the observed discovery rate was 70% and it dropped to 68% after 2012. Thus, there is no indication that non-significant results are reported more after 2012. The expected discovery rate was 32% before 2012 and 25% after 2012. Thus, there is also no change in the expected discovery rate and the expected discovery rate is much lower than the observed discovery rate. This discrepancy shows that QRPs were used before 2012 and after 2012. The 95%CI do not overlap before and after 2012, indicating that this discrepancy is statistically significant. Figure 1 shows the influence of QRPs when the observed non-significant results (histogram of z-scores below 1.96 in blue) is compared to the model prediction (grey curve). The discrepancy suggests a large file drawer of unreported statistical tests.

An old saying is that you can’t teach an old dog new tricks. So, the more interesting question is whether the younger contributors to the glucose paper changed their research practices.

The results for C. Nathan DeWall show no notable response to the replication crisis (Figure 2). The expected replication rate increased slightly from 61% to 65%, but the difference is not significant and visual inspection of the plots suggests that it is mostly due to a decrease in reporting p-values just below .05. One reason for this might be a new goal to p-hack at least to the level of .025 to avoid detection of p-hacking by p-curve analysis. The observed discovery rate is practically unchanged from 68% to 69%. The expected discovery rate increased only slightly from 28% to 35%, but the difference is not significant. More important, the expected discovery rates are significantly lower than the observed discovery rates before and after 2012. Thus, there is evidence that DeWall used questionable research practices before and after 2012, and there is no evidence that he changed his research practices.

The results for Brandon J. Schmeichel are even more discouraging (Figure 3). Here the expected replication rate decreased from 70% to 56%, although this decrease is not statistically significant. The observed discovery rate decreased significantly from 74% to 63%, which shows that more non-significant results are reported. Visual inspection shows that this is particularly the case for test-statistics close to zero. Further inspection of the article would be needed to see how these results are interpreted. More important, The expected discovery rates are significantly lower than the observed discovery rates before 2012 and after 2012. Thus, there is evidence that QRPs were used before and after 2012 to produce significant results. Overall, there is no evidence that research practices changed in response to the replication crisis.

The results for Kathleen D. Vohs also show no response to the replication crisis (Figure 4). The expected replication rate dropped slightly from 62% to 58%; the difference is not significant. The observed discovery rate dropped slightly from 69% to 66%, and the expected discovery rate decreased from 43% to 31%, although this difference is also not significant. Most important, the observed discovery rates are significantly higher than the expected discovery rates before 2012 and after 2012. Thus, there is clear evidence that questionable research practices were used before and after 2012 to inflate the discovery rate.


After concerns about research practices and replicability emerged in the 2010s, social psychologists have debated this issue. Some social psychologists changed their research practices to increase statistical power and replicability. However, other social psychologists have denied that there is a crisis and attributed replication failures to a number of other causes. Not surprisingly, some social psychologists also did not change their research practices. This blog post shows that Baumeister and his students have not changed research practices. They are able to publish questionable research because there has been no collective effort to define good research practices and to ban questionable practices and to treat the hiding of non-significant results as a breach of research ethics. Thus, Baumeister and his students are simply exerting their right to use questionable research practices, whereas others voluntarily implemented good, open science, practices. Given the freedom of social psychologists to decide which practices they use, social psychology as a field continuous to have a credibility problem. Editors who accept questionable research in their journals are undermining the credibility of their journal. Authors are well advised to publish in journals that emphasis replicability and credibility with open science badges and with a high replicability ranking (Schimmack, 2019).

An Honorable Response to the Credibility Crisis by D.S. Lindsay: Fare Well

We all know what psychologists did before 2012. The name of the game was to get significant results that could be sold to a journal for publication. Some did it with more power and some did it with less power, but everybody did it.

In the beginning of the 2010s it became obvious that this was a flawed way to do science. Bem (2011) used this anything-goes to get significance approach to publish 9 significant demonstration of a phenomenon that does not exist: mental time-travel. The cat was out of the bag. There were only two questions. How many other findings were unreal and how would psychologists respond to the credibility crisis.

D. Steve Lindsay responded to the crisis by helping to implement tighter standards and to enforce these standards as editor of Psychological Science. As a result, Psychological Science has published more credible results over the past five years. At the end of his editorial term, Linday published a gutsy and honest account of his journey towards a better and more open psychological science. It starts with his own realization that his research practices were suboptimal.

Early in 2012, Geoff Cumming blew my mind with a talk that led me to realize that I had been conducting underpowered experiments for decades. In some lines of research in my lab, a predicted effect would come booming through in one experiment but melt away in the next.
My students and I kept trying to find conditions that yielded consistent statistical significance—tweaking items, instructions, exclusion rules—but we sometimes eventually threw in the towel
because results were maddeningly inconsistent. For example, a chapter by Lindsay
and Kantner (2011) reported 16 experiments with an on-again/off-again effect of feedback on recognition memory. Cumming’s talk explained that p values are very noisy. Moreover, when between-subjects designs are used to study small- to medium-sized effects, statistical
tests often yield nonsignificant outcomes (sometimes with huge p values) unless samples are very large.

Hard on the heels of Cumming’s talk, I read Simmons, Nelson, and Simonsohn’s (2011) “False-Positive Psychology” article, published in Psychological Science. Then I gobbled up several articles and blog posts on misuses of null-hypothesis significance testing (NHST). The
authors of these works make a convincing case that hypothesizing after the results are known (HARKing; Kerr, 1998) and other forms of “p hacking” (post hoc exclusions, transformations, addition of moderators, optional stopping, publication bias, etc.) are deeply problematic. Such practices are common in some areas of scientific psychology, as well as in some other life
sciences. These practices sometimes give rise to mistaken beliefs in effects that really do not exist. Combined with publication bias, they often lead to exaggerated estimates
of the sizes of real but small effects.

This quote is exceptional because few psychologists have openly talked about their research practices before (or after) 2012. It is an open secrete that questionable research practices were widely used and anonymous surveys support this (John et al., 2012), but nobody likes to talk about it. Lindsay’s frank account is an honorable exception in the spirit of true leaders who confront mistakes head on, just like a Nobel laureate who recently retracted a Science article (Frances Arnold).

1. Acknowledge your mistakes.

2. Learn from your mistakes.

3. Teach others from your mistakes.

4. Move beyond your mistakes.

Lindsay’s acknowledgement also makes it possible to examine what these research practices look like when we examine published results, and to see whether this pattern changes in response to awareness that certain practices were questionable.

So, I z-curved Lindsay’s published results from 1998 to 2012. The graph shows some evidence of QRPs, in that the model assumes more non-significant results (grey line from 0 to 1.96) than are actually observed (histogram of non-significant results). This is confirmed by a comparison of the observed discovery rate (70% of published results are significant) and the expected discovery rate (44%). However, the confidence intervals overlap. So this test of bias is not significant.

The replication rate is estimated to be 77%. This means that there is a 77% probability that repeating a test with a new sample (of equal size) would produce a significant result again. Even for just significant results (z = 2 to 2.5), the estimated replicability is still 45%. I have seen much worse results.

Nevertheless, it is interesting to see whether things improved. First of all, being editor of Psychological Science is full-time job. Thus, output has decreased. Maybe research also slowed down because studies were conducted with more care. I don’t know. I just know that there are very few statistics to examine.

Although the small sample size of tests makes results somewhat uncertain, the graph shows some changes in research practices. Replicability increased further to 88% and there is no loner a discrepancy between observed and expected discovery rate.

If psychology as a whole had responded like D.S. Lindsay it would be in a good position to start the new decade. The problem is that this response is an exception rather than the rule and some areas of psychology and some individual researchers have not changed at all since 2012. This is unfortunate because questionable research practices hurt psychology, especially when undergraduates and the wider public learn more and more how untrustworthy psychological science has been and often still us. Hopefully, reforms will come sooner than later or we may have to sing a swan song for psychological science.

Francis’s Audit of Multiple-Study Articles in Psychological Science in 2009-2012

Citation: Francis G., (2014). The frequency of excess success for articles
in Psychological Science. Psychon Bull Rev (2014) 21:1180–1187
DOI 10.3758/s13423-014-0601-x


The Open Science Collaboration article in Science has over 1,000 articles (OSC, 2015). It showed that attempting to replicate results published in 2008 in three journals, including Psychological Science, produced more failures than successes (37% success rate). It also showed that failures outnumbered successes 3:1 in social psychology. It did not show or explain why most social psychological studies failed to replicate.

Since 2015 numerous explanations have been offered for the discovery that most published results in social psychology cannot be replicated: decline effect (Schooler), regression to the mean (Fiedler), incompetent replicators (Gilbert), sabotaging replication studies (Strack), contextual sensitivity (vanBavel). Although these explanations are different, they share two common elements, (a) they are not supported by evidence, and (b) they are false.

A number of articles have proposed that the low replicability of results in social psychology are caused by questionable research practices (John et al., 2012). Accordingly, social psychologists often investigate small effects in between-subject experiments with small samples that have large sampling error. A low signal to noise ratio (effect size/sampling error) implies that these studies have a low probability of producing a significant result (i.e., low power and high type-II error probability). To boost power, researchers use a number of questionable research practices that inflate effect sizes. Thus, the published results provide the false impression that effect sizes are large and results are replicated, but actual replication attempts show that the effect sizes were inflated. The replicability projected suggested that effect sizes are inflated by 100% (OSC, 2015).

In an important article, Francis (2014) provided clear evidence for the widespread use of questionable research practices for articles published from 2009-2012 (pre crisis) in the journal Psychological Science. However, because this evidence does not fit the narrative that social psychology was a normal and honest science, this article is often omitted from review articles, like Nelson et al’s (2018) ‘Psychology’s Renaissance’ that claims social psychologists never omitted non-significant results from publications (cf. Schimmack, 2019). Omitting disconfirming evidence from literature reviews is just another sign of questionable research practices that priorities self-interest over truth. Given the influence that Annual Review articles hold, many readers maybe unfamiliar with Francis’s important article that shows why replication attempts of articles published in Psychological Science often fail.

Francis (2014) “The frequency of excess success for articles in Psychological Science”

Francis (2014) used a statistical test to examine whether researchers used questionable research practices (QRPs). The test relies on the observation that the success rate (percentage of significant results) should match the mean power of studies in the long run (Brunner & Schimmack, 2019; Ioannidis, J. P. A., & Trikalinos, T. A., 2007; Schimmack, 2012; Sterling et al., 1995). Statistical tests rely on the observed or post-hoc power as an estimate of true power. Thus, mean observed power is an estimate of the expected number of successes that can be compared to the actual success rate in an article.

It has been known for a long time that the actual success rate in psychology articles is surprisingly high (Sterling, 1995). The success rate for multiple-study articles is often 100%. That is, psychologists rarely report studies where they made a prediction and the study returns a non-significant results. Some social psychologists even explicitly stated that it is common practice not to report these ‘uninformative’ studies (cf. Schimmack, 2019).

A success rate of 100% implies that studies required 99.9999% power (power is never 100%) to produce this result. It is unlikely that many studies published in psychological science have the high signal-to-noise ratios to justify these success rates. Indeed, when Francis applied his bias detection method to 44 studies that had sufficient results to use it, he found that 82 % (36 out of 44) of these articles showed positive signs that questionable research practices were used with a 10% error rate. That is, his method could at most produce 5 significant results by chance alone, but he found 36 significant results, indicating the use of questionable research practices. Moreover, this does not mean that the remaining 8 articles did not use questionable research practices. With only four studies, the test has modest power to detect questionable research practices when the bias is relatively small. Thus, the main conclusion is that most if not all multiple-study articles published in Psychological Science used questionable research practices to inflate effect sizes. As these inflated effect sizes cannot be reproduced, the effect sizes in replication studies will be lower and the signal-to-noise ratio will be smaller, producing non-significant results. It was known that this could happen since 1959 (Sterling, 1959). However, the replicability project showed that it does happen (OSC, 2015) and Francis (2014) showed that excessive use of questionable research practices provides a plausible explanation for these replication failures. No review of the replication crisis is complete and honest, without mentioning this fact.

Limitations and Extension

One limitation of Francis’s approach and similar approaches like my incredibility Index (Schimmack, 2012) is that p-values are based on two pieces of information, the effect size and sampling error (signal/noise ratio). This means that these tests can provide evidence for the use of questionable research practices, when the number of studies is large, and the effect size is small. It is well-known that p-values are more informative when they are accompanied by information about effect sizes. That is, it is not only important to know that questionable research practices were used, but also how much these questionable practices inflated effect sizes. Knowledge about the amount of inflation would also make it possible to estimate the true power of studies and use it as a predictor of the success rate in actual replication studies. Jerry Brunner and I have been working on a statistical method that is able to to this, called z-curve, and we validated the method with simulation studies (Brunner & Schimmack, 2019).

I coded the 195 studies in the 44 articles analyzed by Francis and subjected the results to a z-curve analysis. The results are shocking and much worse than the results for the studies in the replicability project that produced an expected replication rate of 61%. In contrast, the expected replication rate for multiple-study articles in Psychological Science is only 16%. Moreover, given the fairly large number of studies, the 95% confidence interval around this estimate is relatively narrow and includes 5% (chance level) and a maximum of 25%.

There is also clear evidence that QRPs were used in many, if not all, articles. Visual inspection shows a steep drop at the level of significance, and the only results that are not significant with p < .05 are results that are marginally significant with p < .10. Thus, the observed discovery rate of 93% is an underestimation and the articles claimed an amazing success rate of 100%.

Correcting for bias, the expected discovery rate is only 6%, which is just shy of 5%, which would imply that all published results are false positives. The upper limit for the 95% confidence interval around this estimate is 14, which would imply that for every published significant result there are 6 studies with non-significant results if file-drawring were the only QRP that was used. Thus, we see not only that most article reported results that were obtained with QRPs, we also see that massive use of QRPs was needed because many studies had very low power to produce significant results without QRPs.


Social psychologists have used QRPs to produce impressive results that suggest all studies that tested a theory confirmed predictions. These results are not real. Like a magic show they give the impression that something amazing happened, when it is all smoke and mirrors. In reality, social psychologists never tested their theories because they simply failed to report results when the data did not support their predictions. This is not science. The 2010s have revealed that social psychological results in journals and text books cannot be trusted and that influential results cannot be replicated when the data are allowed to speak. Thus, for the most part, social psychology has not been an empirical science that used the scientific method to test and refine theories based on empirical evidence. The major discovery in the 2010s was to reveal this fact, and Francis’s analysis provided valuable evidence to reveal this fact. However, most social psychologists preferred to ignore this evidence. As Popper pointed out, this makes them truly ignorant, which he defined as “the unwillingness to acquire knowledge.” Unfortunately, even social psychologists who are trying to improve it wilfully ignore Francis’s evidence that makes replication failures predictable and undermines the value of actual replication studies. Given the extent of QRPs, a more rational approach would be to dismiss all evidence that was published before 2012 and to invest resources in new research with open science practices. Actual replication failures were needed to confirm predictions made by bias tests that old studies cannot be trusted. The next decade should focus on using open science practices to produce robust and replicable findings that can provide the foundation for theories.

The Demise of the Solo Experiment

Wegner’s article “The Premature Demise of the Solo Experiment” in PSPB (1992) is an interesting document for meta-psychologists. It provides some insight into the thinking of leading social psychologists at the time; not only the author, but reviewers and the editor who found this article worthy of publishing, and numerous colleagues who emailed Wegner with approving comments.

The article starts with the observation that in the 1990s social psychology journals increasingly demanded that articles contain more than one study. Wegner thinks that the preference of multiple-study articles is a bias rather than a preference in favour of stronger evidence.

it has become evident that a tremendous bias against the “solo” experiment exists that guides both editors and reviewers” (p. 504).

The idea of bias is based on the assumption that rejection a null-hypothesis with a long-run error-probability of 5% is good enough to publish exciting new ideas and give birth to wonderful novel theories. Demanding even just one replication of this finding would create a lot more burden without any novel insights just to lower this probability to 0.25%.

But let us just think a moment about the demise of the solo experiment. Here we have a case in which skepticism has so overcome the love of ideas that we seem to have squared the probability of error we are willing to allow. Once, p < .05 was enough. Now, however, we must prove things twice. The multiple experiment ethic has surreptitiously changed alpha to .0025 or below.

That’s right. The move from solo-experiment to multiple-study articles shifted the type-I error probability. Even a pair of studies reduced the type-I error probability more than the highly cited and controversial call to move alpha from .05 to .005. A pair of studies with p < .05 reduces the .005 probability by 50%!

Wegner also explains why journals started demanding multiple studies.

After all, the statistical reasons for multiple experiments are obvious-what better protection of the truth than that each article contain its own replication? (p. 505)

Thus, concerns about replicabilty in social psychology were prominent in the early 1990s, twenty years before the replication crisis. And demanding replication studies was considered to be a solution to this problem. If researchers were able to replicate their findings, ideally with different methods, stimuli, and dependent variables, the results are robust and generalizable. So much for the claim that psychologists did not value or conduct replication studies before the open science movement was born in the early 2010.

Wegner also reports about his experience with attempting to replicate his perfectly good first study.

Sometimes it works wonderfully….more often than not, however, we find the second
experiment is harder to do than the first
Even if we do the exact same experiment again” (p. 506).

He even cheerfully acknowledge that the first results are difficult to replicate because the first results were obtained with some good fortune.

Doing it again, we will be less likely to find the same thing even if it is true, because the
error variance regresses our effects to the mean. So we must add more subjects right off the bat. The joy of discovery we felt on bumbling into the first study is soon replaced by the strain of collecting an all new and expanded set of data to fend off the pointers
[pointers = method-terrorists]” (p. 506).

Wegner even thinks that publishing these replication studies is pointless because readers expect the replication study to work. Sure, if the first study worked, so will the second.

This is something of a nuisance in light of the reception that our second experiment will likely get Readers who see us replicate our own findings roll their eyes and say “Sure,” and we wonder why we’ve even gone to the trouble.

However, he fails to examine more carefully why a successful replication study receives only a shoulder-shrug from readers. After all, his own experience was that it was quite difficult to get these replication studies to work. Doesn’t this mean readers should be at the edge of their seats and wonder whether the original result was a false positive or whether it can actually be replicated? Isn’t the second study the real confirmatory test where the rubber hits the road? Insiders of course know that this is not the case. The second study works because it would not have been included in the multiple-study article if it hadn’t worked. That is after all how the field operated. Everybody had the same problems to get studies to work that Wegner describes, but many found a way to get enough studies to work to meet the demands of the editor. The number of studies was just a test of the persistence of a researcher, not a test of a theory. And that is what Wegner rightfully criticized. What is the point of producing a set of studies with p < .05, if more studies do not strengthen the evidence for a claim. We might as well publish a single finding and then move on to find more interesting ideas and publish them with p-values less than .05. Even 9 studies with p < .05 don’t mean that people can foresee the future (Bem, 2011), but it is surely an interesting idea.

Wegner also comments on the nature of replication studies that are now known as conceptual replication studies. The justification for conceptual replication studies is that they address limitations that are unavoidable in a single study. For example, including a manipulation check may introduce biases, but without one, it is not clear whether a manipulation worked. So, ideally the effect could be demonstrated with and without a manipulation check. However, this is not how conceptual replication studies are conducted.

We must engage in a very delicate “tuning” process to dial in a second experiment that is both sufficiently distant from and sufficiently similar to the original. This tuning requires a whole set of considerations and skills that have nothing to do with conducting an experiment. We are not trained in multi experiment design, only experimental design, and this enterprise is therefore largely one of imitation, inspiration, and luck.

So, to replicate original results that were obtained with a healthy dose of luck, more luck is needed in finding a condition that works, or simply to try often enough until luck strikes again.

Given the negative attitude towards rigor, Wegner and colleagues also used a number of tricks to make replication studies work.

Some of us use tricks to disguise our solos. We run “two experiments” in the same session with the same subjects and write them up separately. Or we run what should rightfully be one experiment as several parts, analyzing each separately and writing it up in bite-sized pieces as a multi experiment Many times, we even hobble the first experiment as a way of making sure there will be something useful to do when we run another.” (p. 506).

If you think this sounds like some charlatans who enjoy pretending to be scientists, your impression is rather accurate because the past decade has shown that many of these internal replications in multiple study articles were obtained with tricks and provide no empirical test of empirical hypotheses; p-values are just for show so that it looks like science, but it isn’t.

My own views on this issue are that the multiple study format was a bad fix for a real problem. The real problem was that it was all to easy to get p < .05 in a single study to make grand claims about the causes of human behavior. Multiple-study articles didn’t solve this problem because researchers found ways to get significant results again and again even when their claims were false.

The failure of multiple-study articles to fix psychology has some interesting lessons for the current attempts to improve psychology. Badges for data sharing and preregistration will not improve psychology, if they are being gamed like psychologists gamed the multiple-study format. Ultimately, science can only advance if results are reported honestly and if results are finally able to falsify theoretical predictions. Psychology will only become a science when brilliant novel ideas can be proven false and scientific rigor is prized as much as the creation of interesting ideas. Coming up with interesting ideas is philosophy. Psychology emerged as a distinct discipline in order to subject those theories to empirical tests. After a century of pretending to do so, it is high time to do so for real.

The Diminishing Utility of Replication Studies In Social Psychology

Dorthy Bishop writes on her blog.

“As was evident from my questions after the talk, I was less enthused by the idea of doing a large, replication of Darryl Bem’s studies on extra-sensory perception. Zoltán Kekecs and his team have put in a huge amount of work to ensure that this study meets the highest standards of rigour, and it is a model of collaborative planning, ensuring input into the research questions and design from those with very different prior beliefs. I just wondered what the point was. If you want to put in all that time, money and effort, wouldn’t it be better to investigate a hypothesis about something that doesn’t contradict the laws of physics?”

I think she makes a valid and important point. Bem’s (2011) article highlighted everything that was wrong with the research practices in social psychology. Other articles in JPSP are equally incredible, but this was ignored because naive readers found the claims more plausible (e.g., blood glucose is the energy for will power). We know now that none of these published results provide empirical evidence because the results were obtained with questionable research practices (Schimmack, 2014; Schimmack, 2018). It is also clear that these were not isolated incidents, but that hiding results that do not support a theory was (and still is) a common practice in social psychology (John et al., 2012; Schimmack, 2019).

A large attempt at estimating the replicability of social psychology revealed that only 25% of published significant results could be replicated (OSC). The rate for between-subject experiments was even lower. Thus, the a-priori probability (base rate) that a randomly drawn study from social psychology will produce a significant result in a replication attempt is well below 50%. In other words, a replication failure is the more likely outcome.

The low success rate of these replication studies was a shock. However, it is sometimes falsely implied that the low replicability of results in social psychology was not recognized earlier because nobody conducted replication studies. This is simply wrong. In fact, social psychology is one of the disciplines in psychology that required researchers to conduct multiple studies that showed the same effect to ensure that a result was not a false positive result. Bem had to present 9 studies with significant results to publish his crazy claims about extrasensory perception (Schimmack, 2012). Most of the studies that failed to replicate in the OSC replication project were taken from multiple-study articles that reported several successful demonstrations of an effect. Thus, the problem in social psychology was not that nobody conducted replication studies. The problem was that social psychologists only reported replication studies that were successful.

The proper analyses of the problem also suggests a different solution to the problem. If we pretend that nobody did replication studies, it may seem useful to starting doing replication studies. However, if social psychologists conducted replication studies, but did not report replication failures, the solution is simply to demand that social psychologists report all of their results honestly. This demand is so obvious that undergraduate students are surprised when I tell them that this is not the way social psychologists conduct their research.

In sum, it has become apparent that questionable research practices undermine the credibility of the empirical results in social psychology journals, and that the majority of published results cannot be replicated. Thus, social psychology lacks a solid empirical foundation.

What Next?

It is implied by information theory that little information is gained by conducting actual replication studies in social psychology because a failure to replicate the original result is likely and uninformative. In fact, social psychologists have responded to replication failures by claiming that these studies were poorly conducted and do not invalidate the original claims. Thus, replication studies are both costly and have not advanced theory development in social psychology. More replication studies are unlikely to change this.

A better solution to the replication crisis in social psychology is to characterize research in social psychology from Festinger’s classic small-sample, between-subject study in 1957 to research in 2017 as exploratory and hypotheses generating research. As Bem suggested to his colleagues, this was a period of adventure and exploration where it was ok to “err on the side of discovery” (i.e., publish false positive results, like Bem’s precognition for erotica). Lot’s of interesting discoveries were made during this period; it is just not clear which of these findings can be replicated and what they tell us about social behavior.

Thus, new studies in social psychology should not try to replicate old studies. For example, nobody should try to replicate Devine’s subliminal priming study with racial primes with computers and software from the 1980s (Devine, 1989). Instead, prominent theoretical predictions should be tested with the best research methods that are currently available. Thus, the way forward is not to do more replication studies, but rather to use open science (a.k.a. honest science) that uses experiments to subject theories to empirical tests that may also falsify a theory (e.g., subliminal racial stimuli have no influence on behavior). The main shift that is required is to get away from research that can only confirm theories and to allow for empirical data to falsify theories.

This was exactly the intent of Danny Kahneman’s letter, when he challenged social priming researchers to respond to criticism of their work by going into their labs and to demonstrate that these effects can be replicated across many labs.

Kahneman makes it clear that the onus of replication is on the original researchers who want others to believe their claims. The response to this letter speaks volumes. Not only did social psychologists fail to provide new and credible evidence that their results can be replicated, they also demonstrated defiant denial in the face of replication failures by others. The defiant denial by prominent social psychologists (e.g., Baumeister, 2019) make it clear that they will not be convinced by empirical evidence, while others who can look at the evidence objectively do not need more evidence to realize that the social psychological literature is a train-wreck (Schimmack, 2017; Kahneman, 2017). Thus, I suggest that young social psychologists search the train wreck for survivors, but do not waste their time and resources on replication studies that are likely to fail.

A simple guide through the wreckage of social psychology is to distrust any significant result with a p-value greater than .01 (Schimmack, 2019). Prediction markets also suggest that readers are able to distinguish credible and incredible results (Atlantic). Thus, I recommend to build on studies that are credible and to stay clear of sexy findings that are unlikely to replicate. As Danny Kahneman pointed out, young social psychologists who work in questionable areas face a dilemma. Either they have to replicate the questionable methods that were used to get the original results, which is increasingly considered unethical, or they end up with results that are not very informative. On the positive side, the replication crisis implies that there are many important topics in social psychology that need to be studied properly with the scientific method. Addressing these important questions may be the best way to rescue social psychology.

Fact-Checking Roy Baumeister

Roy Baumeister wrote a book chapter with the title “Self-Control, Ego Depletion, and Social Psychology’s Replication CrisisRoy” (preprint). I think this chapter will make a valuable contribution to the history of psychology and provides valuable insights into the minds of social psychologists.

I fact-checked the chapter and comment on 31 misleading or false statements.

Comments are welcome.

Replicability Audit of John A. Bargh

“Trust is good, but control is better”  


Information about the replicability of published results is important because empirical results can only be used as evidence if the results can be replicated.  However, the replicability of published results in social psychology is doubtful. Brunner and Schimmack (2020) developed a statistical method called z-curve to estimate how replicable a set of significant results are, if the studies were replicated exactly.  In a replicability audit, I am applying z-curve to the most cited articles of psychologists to estimate  the replicability of their studies.

John A. Bargh

Bargh is an eminent social psychologist (H-Index in WebofScience = 61). He is best known for his claim that unconscious processes have a strong influence on behavior. Some of his most cited article used subliminal or unobtrusive priming to provide evidence for this claim.

Bargh also played a significant role in the replication crisis in psychology. In 2012, a group of researchers failed to replicate his famous “elderly priming” study (Doyen et al., 2012). He responded with a personal attack that was covered in various news reports (Bartlett, 2013). It also triggered a response by psychologist and Nobel Laureate Daniel Kahneman, who wrote an open letter to Bargh (Young, 2012).

As all of you know, of course, questions have been raised about the robustness of priming results…. your field is now the poster child for doubts about the integrity of psychological research.

Kahneman also asked Bargh and other social priming researchers to conduct credible replication studies to demonstrate that the effects are real. However, seven years later neither Bargh nor other prominent social priming researchers have presented new evidence that their old findings can be replicated.

Instead other researchers have conducted replication studies and produced further replication failures. As a result, confidence in social priming is decreasing – but not as fast as it should gifen replication failures and lack of credibility – as reflected in Bargh’s citation counts (Figure 1)

Figure 1. John A. Bargh’s citation counts in Web of Science (updated 9/29/23)

In this blog post, I examine the replicability and credibility of John A. Bargh’s published results using z-curve. It is well known that psychology journals only published confirmatory evidence with statistically significant results, p < .05 (Sterling, 1959). This selection for significance is the main cause of the replication crisis in psychology because selection for significance makes it impossible to distinguish results that can be replicated from results that cannot be replicated because selection for significance ensures that all results will be replicated (we never see replication failures).

While selection for significance makes success rates uninformative, the strength of evidence against the null-hypothesis (signal/noise or effect size / sampling error) does provide information about replicability. Studies with higher signal to noise ratios are more likely to replicate. Z-curve uses z-scores as the common metric of signal-to-noise ratio for studies that used different test statistics. The distribution of observed z-scores provides valuable information about the replicability of a set of studies. If most z-scores are close to the criterion for statistical significance (z = 1.96), replicability is low.

Given the requirement to publish significant results, researches had two options how they could meet this goal. One option requires obtaining large samples to reduce sampling error and therewith increase the signal-to-noise ratio. The other solution is to conduct studies with small samples and conduct multiple statistical tests. Multiple testing increases the probability of obtaining a significant results with the help of chance. This strategy is more efficient in producing significant results, but these results are less replicable because a replication study will not be able to capitalize on chance again. The latter strategy is called a questionable research practice (John et al., 2012), and it produces questionable results because it is unknown how much chance contributed to the observed significant result. Z-curve reveals how much a researcher relied on questionable research practices to produce significant results.


I used WebofScience to identify the most cited articles by John A. Bargh (datafile).  I then selected empirical articles until the number of coded articles matched the number of citations, resulting in 43 empirical articles (H-Index = 41).  The 43 articles reported 111 studies (average 2.6 studies per article).  The total number of participants was 7,810 with a median of 56 participants per study.  For each study, I identified the most focal hypothesis test (MFHT).  The result of the test was converted into an exact p-value and the p-value was then converted into a z-score.  The z-scores were submitted to a z-curve analysis to estimate mean power of the 100 results that were significant at p < .05 (two-tailed). Four studies did not produce a significant result. The remaining 7 results were interpreted as evidence with lower standards of significance. Thus, the success rate for 111 reported hypothesis tests was 96%. This is a typical finding in psychology journals (Sterling, 1959).


The z-curve estimate of replicability is 29% with a 95%CI ranging from 15% to 38%.  Even at the upper end of the 95% confidence interval this is a low estimate. The average replicability is lower than for social psychology articles in general (44%, Schimmack, 2018) and for other social psychologists. At present, only one audit has produced an even lower estimate (Replicability Audits, 2019).

The histogram of z-values shows the distribution of observed z-scores (blue line) and the predicted density distribution (grey line). The predicted density distribution is also projected into the range of non-significant results.  The area under the grey curve is an estimate of the file drawer of studies that need to be conducted to achieve 100% successes if hiding replication failures were the only questionable research practice that is used. The ratio of the area of non-significant results to the area of all significant results (including z-scores greater than 6) is called the File Drawer Ratio.  Although this is just a projection, and other questionable practices may have been used, the file drawer ratio of 7.53 suggests that for every published significant result about 7 studies with non-significant results remained unpublished. Moreover, often the null-hypothesis may be false, but the effect size is very small and the result is still difficult to replicate. When the definition of a false positive includes studies with very low power, the false positive estimate increases to 50%. Thus, about half of the published studies are expected to produce replication failures.

Finally, z-curve examines heterogeneity in replicability. Studies with p-values close to .05 are less likely to replicate than studies with p-values less than .0001. This fact is reflected in the replicability estimates for segments of studies that are provided below the x-axis. Without selection for significance, z-scores of 1.96 correspond to 50% replicability. However, we see that selection for significance lowers this value to just 14% replicability. Thus, we would not expect that published results with p-values that are just significant would replicate in actual replication studies. Even z-scores in the range from 3 to 3.5 average only 32% replicability. Thus, only studies with z-scores greater than 3.5 can be considered to provide some empirical evidence for this claim.

Inspection of the datafile shows that z-scores greater than 3.5 were consistently obtained in 2 out of the 43 articles. Both articles used a more powerful within-subject design.

The automatic evaluation effect: Unconditional automatic attitude activation with a pronunciation task (JPSP, 1996)

Subjective aspects of cognitive control at different stages of processing (Attention, Perception, & Psychophysics, 2009).


John A. Bargh’s work on unconscious processes with unobtrusive priming task is at the center of the replication crisis in psychology. This replicability audit suggests that this is not an accident. The low replicability estimate and the large file-drawer estimate suggest that replication failures are to be expected. As a result, published results cannot be interpreted as evidence for these effects.

So far, John Bargh has ignored criticism of his work. In 2017, he published a popular book about his work on unconscious processes. The book did not mention doubts about the reported evidence, while a z-curve analysis showed low replicability of the cited studies (Schimmack, 2017).

Recently, another study by John Bargh failed to replicate (Chabris et al., in press), and Jessy Singal wrote a blog post about this replication failure (Research Digest) and John Bargh wrote a lengthy comment.

In the commentary, Bargh lists several studies that successfully replicated the effect. However, listing studies with significant results does not provide evidence for an effect unless we know how many studies failed to demonstrate the effect and often we do not know this because these studies are not published. Thus, Bargh continues to ignore the pervasive influence of publication bias.

Bargh then suggests that the replication failure was caused by a hidden moderator which invalidates the results of the replication study.

One potentially important difference in procedure is the temperature of the hot cup of coffee that participants held: was the coffee piping hot (so that it was somewhat uncomfortable to hold) or warm (so that it was pleasant to hold)? If the coffee was piping hot, then, according to the theory that motivated W&B, it should not activate the concept of social warmth – a positively valenced, pleasant concept. (“Hot” is not the same as just more “warm”, and actually participates in a quite different metaphor – hot vs. cool – having to do with emotionality.) If anything, an uncomfortably hot cup of coffee might be expected to activate the concept of anger (“hot-headedness”), which is antithetical to social warmth. With this in mind, there are good reasons to suspect that in C&S, the coffee was, for many participants, uncomfortably hot. Indeed, C&S purchased a hot or cold coffee at a coffee shop and then immediately handed that coffee to passersby who volunteered to take the study. Thus, the first few people to hold a hot coffee likely held a piping hot coffee (in contrast, W&B’s coffee shop was several blocks away from the site of the experiment, and they used a microwave for subsequent participants to keep the coffee at a pleasantly warm temperature). Importantly, C&S handed the same cup of coffee to as many as 7 participants before purchasing a new cup. Because of that feature of their procedure, we can check if the physical-to-social warmth effect emerged after the cups were held by the first few participants, at which point the hot coffee (presumably) had gone from piping hot to warm.

He overlooks that his original study produced only weak evidence for the effect with a p-value of .0503, that is technically not below the .05 value for significance. As shown in the z-curve plot, results with a p-value of .0503 have only an average replicability of 13%. Moreover, the 95%CI for the effect size touches 0. Thus, the original study did not rule out that the effect size is extremely small and has no practical significance. To make any claims that the effect of holding a warm cup on affection is theoretically relevant for our understanding of affection would require studies with larger samples and more convincing evidence.

At the end of his commentary, John A. Bargh assures readers that he is purely motivated by a search for the truth.

Let me close by affirming that I share your goal of presenting the public with accurate information as to the state of the scientific evidence on any finding I discuss publicly. I also in good faith seek to give my best advice to the public at all times, again based on the present state of evidence. Your and my assessments of that evidence might differ, but our motivations are the same.

Let me be crystal clear. I have no reasons to doubt that John A. Bargh believes what he says. His conscious mind sees himself as a scientist who employs the scientific method to provide objective evidence. However, Bargh himself would be the first to acknowledge that our conscious mind is not fully aware of the actual causes of human behavior. I submit that his response to criticism of his work shows that he is less capable of being objective than he thinks he his. I would be happy to be proven wrong in a response by John A. Bargh to my scientific criticism of his work. So far, eminent social psychologists have preferred to remain silent about the results of their replicability audits.


It is nearly certain that I made some mistakes in the coding of John A. Bargh’s articles. However, it is important to distinguish consequential and inconsequential mistakes. I am confident that I did not make consequential errors that would alter the main conclusions of this audit. However, control is better than trust and everybody can audit this audit.  The data are openly available and the data can be submitted to a z-curve analysis using a shinny app. Thus, this replicability audit is fully transparent and open to revision.


Many psychologists do not take this work seriously because it has not been peer-reviewed. However, nothing is stopping them from conducting a peer-review of this work and to publish the results of their review as a commentary here or elsewhere. Thus, the lack of peer-review is not a reflection of the quality of this work, but rather a reflection of the unwillingness of social psychologists to take criticism of their work seriously.

If you found this audit interesting, you might also be interested in other replicability audits of eminent social psychologists.