Category Archives: Replicability

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

Greg Francis, Questionable Research Practices, Replicability, Replication Crisis

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

Introduction

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.

Conclusion

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 Diminishing Utility of Replication Studies In Social Psychology

Replicability, Replication, Replication Crisis, 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

Baumeister, Fact-Hchecking, Flair, Fraud, Replicability, Replicability Report, Replication Crisis

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.

https://replicationindex.com/wp-content/uploads/2019/09/ego-depletion-and-replication-crisis.docx

Comments are welcome.

Estimating the Replicability of Psychological Science

Estimating Reproducibility, Hand-Coding, Replicability, Z-Curve, Zcurve

Over the past years, psychologists have become increasingly concerned about the credibility of published results. The credibility crisis started in 2011, when Bem published incredible results that seemed to suggest that humans can foresee random future events. Bem’s article revealed fundamental flaws in the way psychologists conduct research. The main problem is that psychology journals only publish statistically significant results (Sterling, 1959). If only significant results are published, all hypotheses will receive empirical support as long as they are tested. This is akin to saying that everybody has a 100% free throw average or nobody ever makes a mistake if we do not count failures.

The main problem of selection for significance is that we do not know the real strength of evidence that empirical studies provide. Maybe the selection effect is small and most studies would replicate. However, it is also possible that many studies might fail a replication test. Thus, the crisis of confidence is a crisis of uncertainty.

The Open Science Collaboration conducted actual replication studies to estimate the replicability of psychological science. They replicated 97 studies with statistically significant results and were able to reproduce 35 significant results (a 36% success rate). This is a shockingly low success rate. Based on this finding, most published results cannot be trusted, especially because there is heterogeneity across studies. Some studies would have an even lower chance of replication and several studies might even be outright false positives (there is actually no real effect).

As important as this project was to reveal major problems with the research culture in psychological science, there are also some limitations that cast doubt about the 36% estimate as a valid estimate of the replicability of psychological science. First, the sample size is small and sampling error alone might have lead to an underestimation of the replicability in the population of studies. However, sampling error could also have produced a positive bias. Another problem is that most of the studies focused on social psychology and that replicability in social psychology could be lower than in other fields. In fact, a moderator analysis suggested that the replication rate in cognitive psychology is 50%, while the replication rate in social psychology is only 25%. The replicated studies were also limited to a single year (2008) and three journals. It is possible that the replication rate has increased since 2008 or could be higher in other journals. Finally, there have been concerns about the quality of some of the replication studies. These limitations do not undermine the importance of the project, but they do imply that the 36% estimate is an estimate and that it may underestimate the replicability of psychological science.

Over the past years, I have been working on an alternative approach to estimate the replicability of psychological science. This approach starts with the simple fact that replicabiliity is tightly connected to the statistical power of a study because statistical power determines the long-run probability of producing significant results (Cohen, 1988). Thus, estimating statistical power provides valuable information about replicability. Cohen (1962) conducted a seminal study of statistical power in social psychology. He found that the average power to detect an average effect size was around 50%. This is the first estimate of replicability of psychological science, although it was only based on one journal and limited to social psychology. However, subsequent studies replicated Cohen’s findings and found similar results over time and across journals (Sedlmeier & Gigerenzer, 1989). It is noteworthy that the 36% estimate from the OSC project is not statistically different from Cohen’s estimate of 50%. Thus, there is convergent evidence that replicability in social psychology is around 50%.

In collaboration with Jerry Brunner, I have developed a new method that can estimate mean power for a set of studies that are selected for significance and that vary in effect sizes and samples sizes, which produces heterogeneity in power (Brunner & Schimmack, 2018). The input for this method are the actual test statistics of significance tests (e.g., t-tests, F-tests). These test-statistics are first converted into two-tailed p-values and then converted into absolute z-scores. The magnitude of these absolute z-scores provides information about the strength of evidence against the null-hypotheses. The histogram of these z-scores, called a z-curve, is then used to fit a finite mixture model to the data that estimates mean power, while taking selection for significance intro account. Extensive simulation studies demonstrate that z-curve performs well and provides better estimates than alternative methods. Thus, z-curve is the method of choice for estimating the replicability of psychological science on the basis of the test statistics that are reported in original articles.

For this blog post, I am reporting results based on preliminary results from a large project that extracts focal hypothesis from a broad range of journals that cover all areas of psychology for the years 2010 to 2017. The hand-coding of these articles complements a similar project that relies on automatic extraction of test statistics (Schimmack, 2018).

Table 1 shows the journals that have been coded so far. It also shows the estimates based on the automated method and for hand-coding of focal hypotheses.

JournalHandAutomated
Psychophysiology8475
Journal of Abnormal Psychology7668
Journal of Cross-Cultural Psychology7377
Journal of Research in Personality6875
J. Exp. Psych: Learning, Memory, & Cognition5877
Journal of Experimental Social Psychology5562
Infancy5368
Behavioral Neuroscience5368
Psychological Science5266
JPSP-Interpersonal Relations & Group Processes3363
JPSP-Attitudes and Social Cognition3065
Mean5869

Hand coding of focal hypothesis produces lower estimates than the automated method because the automated analysis also codes manipulation checks and other highly significant results that are not theoretically important. The correlation between the two methods shows consistency across the two methods, r = .67. Finally, the mean for the automated method, 69%, is close to the mean for over 100 journals, 72%, suggesting that the sample of journals is an unbiased sample.

The hand coding results also confirm results found with the automated method that social psychology has a lower replicability than some other disciplines. Thus, the OSC reproducibility results that are largely based on social psychology should not be used to make claims about psychological science in general.

The figure below shows the output of the latest version of z-curve. The first finding is that the replicability estimate for all 1,671 focal tests is 56% with a relatively tight confidence interval ranging from 45% to 56%. ZZZ The next finding is that the discovery rate or success rate is 92%, using p < .05 as the criterion. This confirms that psychology journals continue to published results are selected for significance (Sterling, 1959). The histogram further shows that even more results would be significant if p-values below .10 are included as evidence for “marginal significance.”

Z-Curve.19.1 also provides an estimate of the size of the file drawer. It does so by projecting the distribution of observed significant results into the range of non-significant results (grey curve). The file drawer ratio shows that for every published result, we would expect roughly two unpublished studies with non-significant results. However, z-curve cannot distinguish between different questionable research practices. Rather than not disclosing failed studies researchers may not disclose other statistical analyses within a published study to report significant results.

Z-Curve.19.1 also provides an estimate of the false positive rate (FDR). FDR is the percentage of significant results that may arise from testing a true nil-hypothesis, where the population effect size is zero. For a long time, the consensus has been that false positives are rare because the nil-hypothesis is rarely true (Cohen, 1994). Consistent with this view, Soric’s estimate of the maximum false discovery rate is only 10% with a tight CI ranging from 8% to 16%.

However, the focus on the nil-hypothesis is misguided because it treats tiny deviations from zero as true hypotheses even if the effect size has no practical or theoretical significance. These effect sizes also lead to low power and replication failures. Therefore, Z-Curve 19.1 also provides an estimate of the FDR that treats studies with very low power as false positives. This broader definition of false positives raises the FDR estimate slightly, but 15% is still a low percentage. Thus, the modest replicability of results in psychological science is mostly due to low statistical power to detect true effects rather than a high number of false positive discoveries.

The reproducibility project showed that studies with low p-values were more likely to replicate. This relationship follows from the influence of statistical power on p-values and replication rates. To achieve a replication rate of 80%, p-values had to be less than .00005 or the z-score had to exceed 4 standard deviations. However, this estimate was based on a very small sample of studies. Z-Curve.19.1 also provides estimates of replicability for different levels of evidence. These values are shown below the x-axis. Consistent with the OSC results, a replication rate over 80% is only expected once z-scores are greater than 4.

The results also provide information about the choice of the alpha criterion to draw inferences from significance tests in psychology. To do so, it is important to distinguish observed p-values and type-I probabilities. For a single unbiased tests, we can infer from an observed p-value less than .05 that the risk of a false positive result is less than 5%. However, when multiple comparisons are made or results are selected for significance, an observed p-values less than .05 does not imply that the type-I error risk is below .05. To claim a type-I error risk of 5% or less, we have to correct the observed p-values, just like a Bonferroni correction. As 50% power corresponds to statistical significance, we see that z-scores between 2 and 3 are not statistically significant; that is, the type-I error risk is greater than 5%. Thus, the standard criterion to claim significance with alpha = .05 is a p-value of .003. Given the popularity of .005, I suggest to use p = .005 as a criterion for statistical significance. However, this claim is not based on lowering the criterion for statistical significance because p < .005 still only allows to claim that the type-I error probability is less than 5%. The need for a lower criterion value stems from the inflation of the type-I error rate due to selection for significance. This is a novel argument that has been overlooked in the significance wars, which ignored the influence of publication bias on false positive risks.

Finally, z-curve.19.1 makes it possible to examine the robustness of the estimates by using different selection criteria. One problem with selection models is that p-values just below .05, say in the .01 to .05 range, can arise from various questionable research practices that have different effects on replicability estimates. To address this problem, it is possible to estimate the density with a different selection criterion, while still estimating the replicability with alpha = .05 as the criterion. Figure 2 shows the results by using only z-scores greater than 2.5, p = .012) to fit the observed z-curve for z-scores greater than 2.5.

The blue dashed line at z = 2.5 shows the selection criterion. The grey curve between 1.96 and 2.5 is projected form the distribution for z-scores greater than 2.5. Results show a close fit with the observed distribution. A s a result, the parameter estimates are also very similar. Thus, the results are robust and the selection model seems to be reasonable.

Conclusion

Psychology is in a crisis of confidence about the credibility of published results. The fundamental problems are as old as psychology itself. Psychologists have conducted low powered studies and selected only studies that worked for decades (Cohen, 1962; Sterling, 1959). However, awareness of these problems has increased in recent years. Like many crises, the confidence crisis in psychology has created confusion. Psychologists are aware that there is a problem, but they do not know how large the problem is. Some psychologists believe that there is no crisis and pretend that most published results can be trusted. Others are worried that most published results are false positives. Meta-psychologists aim to reduce the confusion among psychologists by applying the scientific method to psychological science itself.

This blog post provided the most comprehensive assessment of the replicability of psychological science so far. The evidence is largely consistent with previous meta-psychological investigations. First, replicability is estimated to be slightly above 50%. However, replicability varies across discipline and the replicability of social psychology is below 50%. The fear that most published results are false positives is not supported by the data. Replicability increases with the strength of evidence against the null-hypothesis. If the p-value is below .00001, studies are likely to replicate. However, significant results with p-values above .005 should not be considered statistically significant with an alpha level of 5%, because selection for significance inflates the type-I error. Only studies with p < .005 can claim statistical significance with alpha = .05.

The correction for publication bias implies that researchers have to increase sample sizes to meet the more stringent p < .005 criterion. However, a better strategy is to preregister studies to ensure that reported results can be trusted. In this case, p-values below .05 are sufficient to demonstrate statistical significance with alpha = .05. Given the low prevalence of false positives in psychology, I do see no need to lower the alpha criterion.

Future Directions

This blog post is just an interim report. The final project requires hand-coding of a broader range of journals. Readers who think that estimating the replicability of psychological science is beneficial and who want information about a particular journal are invited to collaborate on this project and can obtain authorship if their contribution is substantial enough to warrant authorship. Please consider taking part in this project. Although it is a substantial time commitment, it doesn’t require participants or materials that are needed for actual replication studies. Please consider taking part in this project. Contact me, if you are interested and want to know how you can get involved.

Replicability Audit of John A. Bargh

Bargh, Priming, Questionable Research Practices, Replicability, Replicability Audit, Replication Crisis, , , , ,

“Trust is good, but control is better”  

INTRODUCTION

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.

Data

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).

Results

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).

Conclusion

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.

Disclaimer

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.

Postscript

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.



An Introduction to Z-Curve: A method for estimating mean power after selection for significance (replicability)

Observed Power, Post-Hoc Power, Posteriori Power Analysis, Power, Replicability, Z-Curve, Zcurve

UPDATE 5/13/2019   Our manuscript on the z-curve method for estimation of mean power after selection for significance has been accepted for publication in Meta-Psychology. As estimation of actual power is an important tool for meta-psychologists, we are happy that z-curve found its home in Meta-Psychology.  We also enjoyed the open and constructive review process at Meta-Psychology.  Definitely will try Meta-Psychology again for future work (look out for z-curve.2.0 with many new features).

Z.Curve.1.0.Meta.Psychology.In.Press

Since 2015, Jerry Brunner and I have been working on a statistical tool that can estimate mean (statitical) power for a set of studies with heterogeneous sample sizes and effect sizes (heterogeneity in non-centrality parameters and true power).   This method corrects for the inflation in mean observed power that is introduced by the selection for statistical significance.   Knowledge about mean power makes it possible to predict the success rate of exact replication studies.   For example, if a set of studies with mean power of 60% were replicated exactly (including sample sizes), we would expect that 60% of the replication studies produce a significant result again.

Our latest manuscript is a revision of an earlier manuscript that received a revise and resubmit decision from the free, open-peer-review journal Meta-Psychology.  We consider it the most authoritative introduction to z-curve that should be used to learn about z-curve, critic z-curve, or as a citation for studies that use z-curve.

Cite as “submitted for publication”.

Final.Revision.874-Manuscript in PDF-2236-1-4-20180425 mva final (002)

Feel free to ask questions, provide comments, and critic our manuscript in the comments section.  We are proud to be an open science lab, and consider criticism an opportunity to improve z-curve and our understanding of power estimation.

R-CODE
Latest R-Code to run Z.Curve (Z.Curve.Public.18.10.28).
[updated 18/11/17]   [35 lines of code]
call function  mean.power = zcurve(pvalues,Plot=FALSE,alpha=.05,bw=.05)[1]

Z-Curve related Talks
Presentation on Z-curve and application to BS Experimental Social Psychology and (Mostly) WS-Cognitive Psychology at U Waterloo (November 2, 2018)
[Powerpoint Slides]

Charles Stangor’s Failed Attempt to Predict the Future

Charles Stangor, Replicability, Replication Crisis, Stangor, Zcurve

Background

It is 2018, and 2012 is a faint memory.  So much has happened in the word and in
psychology over the past six years.

Two events rocked Experimental Social Psychology (ESP) in the year 2011 and everybody was talking about the implications of these events for the future of ESP.

First, Daryl Bem had published an incredible article that seemed to suggest humans, or at least extraverts, have the ability to anticipate random future events (e.g., where an erotic picture would be displayed).

Second, it was discovered that Diederik Stapel had fabricated data for several articles. Several years later, over 50 articles have been retracted.

Opinions were divided about the significance of these two events for experimental social psychology.  Some psychologists suggested that these events are symptomatic of a bigger crisis in social psychology.  Others considered these events as exceptions with little consequences for the future of experimental social psychology.

In February 2012, Charles Stangor tried to predict how these events will shape the future of experimental social psychology in an essay titled “Rethinking my Science”

How will social and personality psychologists look back on 2011? With pride at having continued the hard work of unraveling the mysteries of human behavior, or with concern that the only thing that is unraveling is their discipline?

Stangor’s answer is clear.

“Although these two events are significant and certainly deserve our attention, they are flukes rather than game-changers.”

He describes Bem’s article as a “freak event” and Stapel’s behavior as a “fluke.”

“Some of us probably do fabricate data, but I imagine the numbers are relatively few.”

Stangor is confident that experimental social psychology is not really affected by these two events.

As shocking as they are, neither of these events create real problems for social psychologists

In a radical turn, Stangor then suggests that experimental social psychology will change, but not in response to these events, but in response to three other articles.

But three other papers published over the past two years must completely change how we think about our field and how we must conduct our research within it. And each is particularly important for me, personally, because each has challenged a fundamental assumption that was part of my training as a social psychologist.

Student Samples

The first article is a criticism of experimental social psychology for relying too much on first-year college students as participants (Heinrich, Heine, & Norenzayan, 2010).  Looking back, there is no evidence that US American psychologists have become more global in their research interests. One reason is that social phenomena are sensitive to the cultural context and for Americans it is more interesting to study how online dating is changing relationships than to study arranged marriages in more traditional cultures. There is nothing wrong with a focus on a particular culture.  It is not even clear that research article on prejudice against African Americans were supposed to generalize to the world (how would this research apply to African countries where the vast majority of citizens are black?).

The only change that occurred was not in response to Heinrich et al.’s (2010) article, but in response to technological changes that made it easier to conduct research and pay participants online.  Many social psychologists now use the online service Mturk to recruit participants.

Thus, I don’t think this article significantly changed experimental social psychology.

Decline Effect 

The second article with the title (“The Truth Wears Off“) was published in the weekly magazine the New Yorker.  It made the ridiculous claim that true effects become weaker or may even disappear over time.

The basic phenomenon is that observed findings in the social and biological sciences weaken with time. Effects that are easily replicable at first become less so every day. Drugs stop working over time the same way that social psychological phenomena become more and more elusive. The “the decline effect” or “the truth wears off effect,” is not easy to dismiss, although perhaps the strength of the decline effect will itself decline over time.

The assumption that the decline effect applies to real effects is no more credible than Bem’s claims of time-reversed causality.   I am still waiting for the effect of eating cheesecake on my weight (a biological effect) to wear off. My bathroom scale tells me it is not.

Why would Stangor believe in such a ridiculous idea?  The answer is that he observed it many times in his own work.

Frankly I have difficulty getting my head around this idea (I’m guessing others do too) but it is nevertheless exceedingly troubling. I know that I need to replicate my effects, but am often unable to do it. And perhaps this is part of the reason. Given the difficulty of replication, will we continue to even bother? And what becomes of our research if we do even less replicating than we do now? This is indeed a problem that does not seem likely to go away soon. 

In hindsight, it is puzzling that Stangor misses the connection between Bem’s (2011) article and the decline effect.   Bem published 9 successful results with p < .05.  This is not a fluke. The probability to get lucky 9 times in a row with a probability of just 5% for a single event is very very small (less than 1 in a billion attempts).  It is not a fluke. Bem also did not fabricate data like Stapel, but he falsified data to present results that are too good to be true (Definitions of Research Misconduct).  Not surprisingly, neither he nor others can replicate these results in transparent studies that prevent the use of QRPs (just like paranormal phenomena like spoon bending can not be replicated in transparent experiments that prevent fraud).

The decline effect is real, but it is wrong to misattribute it to a decline in the strength of a true phenomenon.  The decline effect occurs when researchers use questionable research practices (John et al., 2012) to fabricate statistically significant results.  Questionable research practices inflate “observed effect sizes” [a misnomer because effects cannot be observed]; that is, the observed mean differences between groups in an experiment.  Unfortunately, social psychologists do not distinguish between “observed effects sizes” and true or population effect sizes. As a result, they believe in a mysterious force that can reduce true effect sizes when sampling error moves mean differences in small samples around.

In conclusion, the truth does not wear off because there was no truth to begin with. Bem’s (2011) results did not show a real effect that wore off in replication studies. The effect was never there to begin with.

P-Hacking

The third article mentioned by Stangor did change experimental social psychology.  In this article, Simmons, Nelson, and Simonsohn (2011) demonstrate the statistical tricks experimental social psychologists have used to produce statistically significant results.  They call these tricks, p-hacking.  All methods of p-hacking have one common feature. Researchers conduct mulitple statistical analysis and check the results. When they find a statistically significant result, they stop analyzing the data and report the significant result.  There is nothing wrong with this practice so far, but it essentially constitutes research misconduct when the result is reported without fully disclosing how many attempts were made to get it.  The failure to disclose all attempts is deceptive because the reported result (p < .05) is only valid if a researcher collected data and then conducted a single test of a hypothesis (it does not matter whether this hypothesis was made before or after data collection).  The point is that at the moment a researcher presses a mouse button or a key on a keyboard to see a p-value,  a statistical test occurred.  If this p-value is not significant and another test is run to look at another p-value, two tests are conducted and the risk of a type-I error is greater than 5%. It is no longer valid to claim p < .05, if more than one test was conducted.  With extreme abuse of the statistical method (p-hacking), it is possible to get a significant result even with randomly generated data.

In 2010, the Publication Manual of the American Psychological Association advised researchers that “omitting troublesome observations from reports to present a more convincing story is also prohibited” (APA).  It is telling that Stangor does not mention this section as a game-changer, because it has been widely ignored by experimental psychologists until this day.  Even Bem’s (2011) article that was published in an APA journal violated this rule, but it has not been retracted or corrected so far.

The p-hacking article had a strong effect on many social psychologists, including Stangor.

Its fundamental assertions are deep and long-lasting, and they have substantially affected me. 

Apparently, social psychologists were not aware that some of their research practices undermined the credibility of their published results.

Although there are many ways that I take the comments to heart, perhaps most important to me is the realization that some of the basic techniques that I have long used to collect and analyze data – techniques that were taught to me by my mentors and which I have shared with my students – are simply wrong.

I don’t know about you, but I’ve frequently “looked early” at my data, and I think my students do too. And I certainly bury studies that don’t work, let alone fail to report dependent variables that have been uncooperative. And I have always argued that the researcher has the obligation to write the best story possible, even if may mean substantially “rewriting the research hypothesis.” Over the years my students have asked me about these practices (“What do you recommend, Herr Professor?”) and I have
routinely, but potentially wrongly, reassured them that in the end, truth will win out. 

Although it is widely recognized that many social psychologists p-hacked and buried studies that did not work out,  Stangor’s essay remains one of the few open admissions that these practices were used, which were not considered unethical, at least until 2010. In fact, social psychologists were trained that telling a good story was essential for social psychologists (Bem, 2001).

In short, this important paper will – must – completely change the field. It has shined a light on the elephant in the room, which is that we are publishing too many Type-1 errors, and we all know it.

Whew! What a year 2011 was – let’s hope that we come back with some good answers to these troubling issues in 2012.

In hindsight Stangor was right about the p-hacking article. It has been cited over 1,000 times so far and the term p-hacking is widely used for methods that essentially constitute a violation of research ethics.  P-values are only meaningful if all analyses are reported and failures to disclose analyses that produced inconvenient non-significant results to tell a more convincing story constitutes research misconduct according to the guidelines of APA and the HHS.

Charles Stangor’s Z-Curve

Stangor’s essay is valuable in many ways.  One important contribution is the open admission to the use of QRPs before the p-hacking article made Stangor realize that doing so was wrong.   I have been working on statistical methods to reveal the use of QRPs.  It is therefore interesting to see the results of this method when it is applied to data by a researcher who used QRPs.

stangor.png

This figure (see detailed explanation here) shows the strength of evidence (based on test statistics like t and F-values converted into z-scores in Stangor’s articles. The histogram shows a mode at 2, which is just significant (z = 1.96 ~ p = .05, two-tailed).  The steep drop on the left shows that Stangor rarely reported marginally significant results (p = .05 to .10).  It also shows the use of questionable research practices because sampling error should produce a larger number of non-significant results than are actually observed. The grey line provides a vague estimate of the expected proportion of non-significant results. The so called file-drawer (non-significant results that are not reported) is very large.  It is unlikely that so many studies were attempted and not reported. As Stangor mentions, he also used p-hacking to get significant results.  P-hacking can produce just significant results without conducting many studies.

In short, the graph is consistent with Stangor’s account that he used QRPs in his research, which was common practice and even encouraged, and did not violate any research ethics code of the times (Bem, 2001).

The graph also shows that the significant studies have an estimated average power of 71%.  This means any randomly drawn statistically significant result from Stangor’s articles has a 71% chance of producing a significant result again, if the study and the statistical test were replicated exactly (see Brunner & Schimmack, 2018, for details about the method).  This average is not much below the 80% value that is considered good power.

There are two caveats with the 71% estimate. One caveat is that this graph uses all statistical tests that are reported, but not all of these tests are interesting. Other datasets suggest that the average for focal hypothesis tests is about 20-30 percentage points lower than the estimate for all tests. Nevertheless, an average of 71% is above average for social psychology.

The second caveat is that there is heterogeneity in power across studies. Studies with high power are more likely to produce really small p-values and larger z-scores. This is reflected in the estimates below the x-axis for different segments of studies.  The average for studies with just significant results (z = 2 to 2.5) is only 49%.  It is possible to use the information from this graph to reexamine Stangor’s articles and to adjust nominal p-values.  According to this graph p-values in the range between .05 and .01 would not be significant because 50% power corresponds to a p-value of .05. Thus, all of the studies with a z-score of 2.5 or less (~ p > .01) would not be significant after correcting for the use of questionable research practices.

The main conclusion that can be drawn from this analysis is that the statistical analysis of Stangor’s reported results shows convergent validity with the description of his research practices.  If test statistics by other researchers show a similar (or worse) distribution, it is likely that they also used questionable research practices.

Charles Stangor’s Response to the Replication Crisis 

Stangor was no longer an active researcher when the replication crisis started. Thus, it is impossible to see changes in actual research practices.  However, Stangor co-edited a special issue for the Journal of Experimental Social Psychology on the replication crisis.

The Introduction mentions the p-hacking article.

At the same time, the empirical approaches adopted by social psychologists leave room for practices that distort or obscure the truth (Hales, 2016-in this issue; John, Loewenstein, & Prelec, 2012; Simmons, Nelson, & Simonsohn, 2011)

and that

social psychologists need to do some serious housekeeping in order to progress
as a scientific enterprise.

It quotes, Dovidio to claim that social psychologists are

lucky to have the problem. Because social psychologists are rapidly developing new approaches and techniques, our publications will unavoidably contain conclusions that are uncertain, because the potential limitations of these procedures are not yet known. The trick then is to try to balance “new” with “careful.

It also mentions the problem of fabricating stories by hiding unruly non-significant results.

The availability of cheap data has a downside, however,which is that there is little cost in omitting data that contradict our hypotheses from our manuscripts (John et al., 2012). We may bury unruly data because it is so cheap and plentiful. Social psychologists justify this behavior, in part, because we think conceptually. When a manipulation fails, researchers may simply argue that the conceptual variable was not created by that particular manipulation and continue to seek out others that will work. But when a study is eventually successful,we don’t know if it is really better than the others or if it is instead a Type I error. Manipulation checks may help in this regard, but they are not definitive (Sigall &Mills, 1998).

It also mentioned file-drawers with unsuccessful studies like the one shown in the Figure above.

Unpublished studies likely outnumber published studies by an order of magnitude. This is wasteful use of research participants and demoralizing for social psychologists and their students.

It also mentions that governing bodies have failed to crack down on the use of p-hacking and other questionable practices and the APA guidelines are not mentioned.

There is currently little or no cost to publishing questionable findings

It foreshadows calls for a more stringent criterion of statistical significance, known as the p-value wars (alpha  = .05 vs. alpha = .005 vs. justify your alpha vs. abandon alpha)

Researchers base statistical analyses on the standard normal distribution but the actual tails are probably bigger than this approach predicts. It is clear that p b .05 is not enough to establish the credibility of an effect. For example, in the Reproducibility Project (Open Science Collaboration, 2015), only 18% of studies with a p-value greater than .04 replicated whereas 63% of those with a p-value less than .001 replicated. Perhaps we should require, at minimum, p <  .01 

It is not clear, why we should settle for p < .01, if only 63% of results replicated with p < .001. Moreover, it ignores that a more stringent criterion for significance also increases the risk of type-II error (Cohen).  It also ignores that only two studies are required to reduce the risk of a type-I error from .05 to .05*.05 = .0025.  As many articles in experimental social psychology are based on multiple cheap studies, the nominal type-I error rate is well below .001.  The real problem is that the reported results are not credible because QRPs are used (Schimmack, 2012).  A simple and effective way to improve experimental social psychology would be to enforce the APA ethics guidelines and hold violators of these rules accountable for their actions.  However, although no new rules would need to be created, experimental social psychologists are unable to police themselves and continue to use QRPs.

The Introduction ignores this valid criticism of multiple study and continues to give the misleading impression that more studies translate into more replicable results.  However, the Open-Science Collaboration reproducibility project showed no evidence that long, multiple-study articles reported more replicable results than shorter articles in Psychological Science.

In addition, replication concerns have mounted with the editorial practice of publishing short papers involving a single, underpowered study demonstrating counterintuitive results (e.g., Journal of Experimental Social Psychology; Psychological Science; Social Psychological and Personality Science). Publishing newsworthy results quickly has benefits,
but also potential costs (Ledgerwood & Sherman, 2012), including increasing Type 1 error rates (Stroebe, 2016-in this issue). 

Once more, the problem is dishonest reporting of results.  A risky study can be published and a true type-I error rate of 20% informs readers that there is a high risk of a false positive result. In contrast, 9 studies with a misleading type-I error rate of 5% violate the implicit assumptions that readers can trust a scientific research article to report the results of an objective test of a scientific question.

But things get worse.

We do, of course, understand the value of replication, and publications in the premier social-personality psychology journals often feature multiple replications of the primary findings. This is appropriate, because as the number of successful replications increases, our confidence in the finding also increases dramatically. However, given the possibility
of p-hacking (Head, Holman, Lanfear, Kahn, & Jennions, 2015; Simmons et al., 2011) and the selective reporting of data, replication is a helpful but imperfect gauge of whether an effect is real. 

Just like Stangor dismissed Bem’s mulitple-study article in JPSP as a fluke that does not require further attention, he dismisses evidence that QRPs were used to p-hack other multiple study articles (Schimmack, 2012).  Ignoring this evidence is just another violation of research ethics. The data that are being omitted here are articles that contradict the story that an author wants to present.

And it gets worse.

Conceptual replications have been the field’s bread and butter, and some authors of the special issue argue for the superiority of conceptual over exact replications (e.g. Crandall & Sherman, 2016-in this issue; Fabrigar and Wegener, 2016–in this issue; Stroebe, 2016-in this issue).  The benefits of conceptual replications are many within social psychology, particularly because they assess the robustness of effects across variation in methods, populations, and contexts. Constructive replications are particularly convincing because they directly replicate an effect from a prior study as exactly as possible in some conditions but also add other new conditions to test for generality or limiting conditions (Hüffmeier, 2016-in this issue).

Conceptual replication is a euphemism for story telling or as Sternberg calls it creative HARKing (Sternberg, in press).  Stangor explained earlier how an article with several conceptual replication studies is constructed.

I certainly bury studies that don’t work, let alone fail to report dependent variables that have been uncooperative. And I have always argued that the researcher has the obligation to write the best story possible, even if may mean substantially “rewriting the research hypothesis.”

This is how Bem advised generations of social psychologists to write articles and that is how he wrote his 2011 article that triggered awareness of the replicability crisis in social psychology.

There is nothing wrong with doing multiple studies and to examine conditions that make an effect stronger or weaker.  However, it is psuedo-science if such a program of research reports only successful results because reporting only successes renders statistical significance meaningless (Sterling, 1959).

The miraculous conceptual replications of Bem (2011) are even more puzzling in the context of social psychologists conviction that their effects can decrease over time (Stangor, 2012) or change dramatically from one situation to the next.

Small changes in social context make big differences in experimental settings, and the same experimental manipulations create different psychological states in different times, places, and research labs (Fabrigar andWegener, 2016–in this issue). Reviewers and editors would do well to keep this in mind when evaluating replications. 

How can effects be sensitive to context and the success rate in published articles is 95%?

And it gets worse.

Furthermore, we should remain cognizant of the fact that variability in scientists’ skills can produce variability in findings, particularly for studies with more complex protocols that require careful experimental control (Baumeister, 2016-in this issue). 

Baumeister is one of the few other social psychologists who has openly admitted not disclosing failed studies.  He also pointed out that in 2008 this practice did not violate APA standards.  However, in 2016 a major replication project failed to replicate the ego-depletion effect that he first “demonstrated” in 1998.  In response to this failure, Baumeister claimed that he had produced the effect many times, suggesting that he has some capabilities that researchers who fail to show the effect lack (in his contribution to the special issue in JESP he calls this ability “flair”).  However, he failed to mention that many of his attempts failed to show the effect and that his high success rate in dozens of articles can only be explained by the use of QRPs.

While there is ample evidence for the use of QRPs, there is no empirical evidence for the claim that research expertise matters.  Moreover, most of the research is carried out by undergraduate students supervised by graduate students and the expertise of professors is limited to designing studies and not to actually carrying out studies.

In the end, the Introduction also comments on the process of correcting mistakes in published articles.

Correctors serve an invaluable purpose, but they should avoid taking an adversarial tone. As Fiske (2016–this issue) insightfully notes, corrective articles should also
include their own relevant empirical results — themselves subject to
correction.

This makes no sense. If somebody writes an article and claims to find an interaction effect based on a significant result in one condition and a non-significant result in another condition, the article makes a statistical mistake (Gelman & Stern, 2005). If a pre-registration contains the statement that an interaction is predicted and a published article claims an interaction is not necessary, the article misrepresents the nature of the preregistration.  Correcting mistakes like this is necessary for science to be a science.  No additional data are needed to correct factual mistakes in original articles (see, e.g., Carlsson, Schimmack, Williams, & Bürkner, 2017).

Moreover, Fiske has been inconsistent in her assessment of psychologists who have been motivated by the events of 2011 to improve psychological science.  On the one hand, she has called these individuals “method terrorists” (2016 review).  On the other hand, she suggests that psychologists should welcome humiliation that may result from the public correction of a mistake in a published article.

Conclusion

In 2012, Stangor asked “How will social and personality psychologists look back on 2011?” Six years later, it is possible to provide at least a temporary answer. There is no unified response.

The main response by older experimental social psychologist has been denial along Stangor’s initial response to Stapel and Bem.  Despite massive replication failures and criticism, including criticism by Noble Laureate Daniel Kahneman, no eminent social psychologists has responded to the replication crisis with an admission of mistakes.  In contrast, the list of eminent social psychologists who stand by their original findings despite evidence for the use of QRPs and replication failures is long and is growing every day as replication failures accumulate.

The response by some younger social psychologists has been to nudge social psychologists slowly towards improving their research methods, mainly by handing out badges for preregistrations of new studies.  Although preregistration makes it more difficult to use questionable research practices, it is too early to see how effective preregistration is in making published results more credible.  Another initiative is to conduct replication studies. The problem with this approach is that the outcome of replication studies can be challenged and so far these studies have not resulted in a consensual correction in the scientific literature. Even articles that reported studies that failed to replicate continue to be cited at a high rate.

Finally, some extremists are asking for more radical changes in the way social psychologists conduct research, but these extremists are dismissed by most social psychologists.

It will be interesting to see how social psychologists, funding agencies, and the general public will look back on 2011 in 2021.  In the meantime, social psychologists have to ask themselves how they want to be remembered and new investigators have to examine carefully where they want to allocate their resources.  The published literature in social psychology is a mine field and nobody knows which studies can be trusted or not.

I don’t know about you, but I am looking forward to reading the special issues in 2021 in celebration of the 10-year anniversary of Bem’s groundbreaking or should I saw earth-shattering publication of “Feeling the Future.”