Category Archives: Psychological Science

Ethical Challenges for Psychological Scientists

Psychological scientists are human and like all humans they can be tempted to violate social norms (Fiske, 2015).  To help psychologists to conduct ethical research, professional organizations have developed codes of conduct (APA).  These rules are designed to help researchers to resist temptations to engage in unethical practices such as fabricate or falsify of data (Pain, Science, 2008).

Psychological science has ignored the problem of research integrity for a long time. The Association for Psychological Science (APS) still does not have formal guidelines about research misconduct (APS, 2016).

Two eminent psychologists recently edited a book with case studies that examine ethical dilemmas for psychological scientists (Sternberg & Fiske, 2015).  Unfortunately, this book lacks moral fiber and fails to discuss recent initiatives to address the lax ethical standards in psychology.

Many of the brief chapters in this book are concerned with unethical behaviors of students, in clinical settings, or ethics of conducting research with animals or human participants.  These chapters have no relevance for the current debates about improving psychological science.  Nevertheless, a few chapter do address these issues and these chapters show how little eminent psychologists are prepared to address an ethical crisis that threatens the foundation of psychological science.

Chapter 29
Desperate Data Analysis by a Desperate Job Candidate Jonathan Haidt

Pursuing a career in science is risky and getting an academic job is hard. After a two-year funded post-doc, I didn’t have a job for one year and I worked hard to get more publications.  Jonathan Haidt was in a similar situation.  He didn’t get an academic job after his first post-doc and was lucky to get a second post-doc,but he needed more publications.

He was interested in the link between feelings of disgust and moral judgments.  A common way to demonstrate causality in experimental social psychology is to use an incidental manipulation of the cause (disgust) and to show that the manipulation has an effect on a measure of the effect (moral judgments).

“I was looking for carry-over effects of disgust”

In the chapter, JH tells readers about the moral dilemma when he collected data and the data analysis showed the predicted pattern, but it was not statistically significant. This means the evidence was not strong enough to be publishable.  He carefully looked at the data and saw several outliers.  He came up with various reasons to exclude some. Many researchers have been in the same situation, but few have told their story in a book.

I knew I was doing this post hoc, and that it was wrong to do so. But I was so confident that the effect was real, and I had defensible justifications! I made a deal with myself: I would go ahead and write up the manuscript now, without the outliers, and while it was under review I would collect more data, which would allow me to get the result cleanly, including all outliers.

This account contradicts various assertions by psychological scientists that they did not know better or that questionable research practices just happen without intent. JH story is much more plausible. He needed publications to get a job. He had a promising dataset and all he was doing was eliminating a few outliers to bet an arbitrary criterion of statistical significance.  So what, if the p-value was .11 with the three cases included. The difference between p = .04 and p = .11 is not statistically significant.  Plus, he was not going to rely on these results. He would collect more data.  Surely, there was a good reason to bend the rules slightly or as Sternberg (2015) calls it going a couple of miles over the speed limit.  Everybody does it.  JH realized that his behavior was unethical, it just was not significantly unethical (Sternberg, 2015).

Decide That the Ethical Dimension Is Significant. If one observes a driver going one mile per hour over the speed limit on a highway, one is unlikely to become perturbed about the unethical behavior of the driver, especially if the driver is oneself.” (Sternberg, 2015). 

So what if JH was speeding a little bit to get an academic job. He wasn’t driving 80 miles in front of an elementary school like Diedrik Stapel, who just made up data.  But that is not how this chapter ends.  JH tells us that he never published the results of this study.

Fortunately, I ended up recruiting more participants before finishing the manuscript, and the new data showed no trend whatsoever. So I dropped the whole study and felt an enormous sense of relief. I also felt a mix of horror and shame that I had so blatantly massaged my data to make it comply with my hopes.

What vexes me about this story is that Jonathan Haidt is known for his work on morality and disgust and published a highly cited (> 2,000 citations in WebofScience) article that suggested disgust does influence moral judgments.

Wheatley and Haidt (2001) manipulated somatic markers even more directly. Highly hypnotizable participants were given the suggestion, under hypnosis, that they would feel a pang of disgust when they saw either the word take or the word often.  Participants were then asked to read and make moral judgments about six stories that were designed to elicit mild to moderate disgust, each of which contained either the word take or the word often. Participants made higher ratings of both disgust and moral condemnation about the stories containing their hypnotic disgust word. This study was designed to directly manipulate the intuitive judgment link (Link 1), and it demonstrates that artificially increasing the strength of a gut feeling increases the strength of the resulting moral judgment (Haidt, 2001, Psychological Review). 

A more detailed report of these studies was published in a few years later (Wheatley & Haidt, 2005).  Study 1 reported a significant difference between the disgust-hypnosis group and the control group, t(44) = 2.41, p = .020.  Study 2 produced a marginally significant result that was significant in a non-parametric test.

For the morality ratings, there were substantially more outliers (in both directions) than in Experiment 1 or for the other ratings in this experiment. As the paired-samples
t test loses power in the presence of outliers, we used its non-parametric analogue, the Wilcoxon signed-rank test, as well (Hollander&Wolfe, 1999). Participants judged the actions to be more morally wrong when their hypnotic word was present (M = 
73.4) than when it was absent (M = 69.6), t(62) = 1.74, p = .09, Wilcoxon Z = 2.18, p < .05. 

Although JH account of his failed study suggests he acted ethically, the same story also reveals that he did have at least one study that failed to provide support for the moral disgust hypothesis that was not mentioned in his Psychological Review article.  Disregarding an entire study that ultimately did not support a hypothesis is a questionable research practice, just as removing some outliers is (John et al., 2012; see also next section about Chapter 35).  However, JH seems to believe that he acted morally.

However, in 2015 social psychologists were well aware that hiding failed studies and other questionable practices undermine the credibility of published findings.  It is therefore particularly troubling that JH was a co-author of another article that failed to mention this study. Schnall, Haidt, Core, and Jordan (2015) responded to a meta-analysis that suggested the effect of incidental disgust on moral judgments is not reliable and that there was evidence for publication bias (e..g, not reporting the failed study JH mentions in his contribution to the book on ethical challenges).  This would have been a good opportunity to admit that some studies failed to show the effect and that these studies were not reported.  However, the response is rather different.

With failed replications on various topics getting published these days, we were pleased that Landy and Goodwin’s (2015) meta-analysis supported most of the findings we reported in Schnall, Haidt, Clore, and Jordan (2008). They focused on what Pizarro, Inbar 
and Helion (2011) had termed the amplification hypothesis of Haidt’s (2001) social intuitionist model of moral judgment, namely that “disgust amplifies moral evaluations—it makes wrong things seem even more wrong (Pizarro et al., 2011, p. 267, emphasis in original).” Like us, Landy and Goodwin (2015) found that the overall effect of incidental disgust on moral judgment is usually small or zero when ignoring relevant moderator variables.”   

Somebody needs to go back in time and correct JH’s Psychological Review article and the hypnosis studies that reported main effects with moderated effect sizes and no moderator effects.  Apparently, even JH doesn’t believe in these effects anymore in 2015 and so it was not important to mention failed studies. However, it might have been relevant to point out that the studies that did report main effects were false positives and what theoretical implications this would have.

More troubling is that the moderator effects are also not robust.  The moderator effects were shown in studies by Schnall and may be inflated by the use of questionable research practices.  In support of this interpretation of her results, a large replication study failed to replicate the results of Schnall et al.’s (2008) Study 3.  Neither the main effect of the disgust manipulation nor the interaction with the personality measure were significant (Johnson et al., 2016).

The fact that JH openly admits to hiding disconfirming evidence, while he would have considered selective deletion of outliers a moral violation, and was ashamed of even thinking about it, suggests that he does not consider hiding failed studies a violation of ethics (but see APA Guidelines, 6th edition, 2010).  This confirms Sternberg’s (2015) first observation about moral behavior.  A researcher needs to define an event as having an ethical dimension to act ethically.  As long as social psychologists do not consider hiding failed studies unethical, reported results cannot be trusted to be objective fact. Maybe it is time to teach social psychologists that hiding failed studies is a questionable research practice that violates scientific standards of research integrity.

Chapter 35
“Getting it Right” Can also be Wrong by Ronnie Janoff-Bulman 

This chapter provides the clearest introduction to the ethical dilemma that researchers face when they report the results of their research.  JB starts with a typical example that all empirical psychologists encountered.  A study showed a promising result, but a second study failed to show the desired and expected result (p > .10).  She then did what many researchers do. She changed the design of the study (a different outcome measure) and collected new data.  There is nothing wrong with trying again because there are many reasons why a study may produce an unexpected result.  However, JB also makes it clear that the article would not include the non-significant results.

“The null-result of the intermediary experiment will not be discussed or mentioned, but will be ignored and forgotten.” 

The suppression of the failed study is called a questionable research practice (John et al., 2012).  The Publication Manual of APA considers this unethical reporting of research results.

JP makes it clear that hiding failed studies undermines the credibility of published results.

“Running multiple versions of studies and ignoring the ones that “didn’t work” can have far-reaching negative effects by contributing to the false positives that pervade our field and now pass for psychological knowledge. I plead guilty.”

JP also explains why it is wrong to neglect failed studies. Running study after study to get a successful outcome, “is likely capitalize on chance, noise, or situational factors and increase the likelihood of finding a significant (but unreliable) effect.” 

This observation is by no means new. Sterling (1959) pointed out that publication bias (publishing only p-values below .05), essentially increases the risk of a false positive result from the nominal level of 5% to an actual level of 100%.  Even evidently false results will produce only significant results in the published literature if failures are not reported (Bem, 2011).

JP asked what can be done about this.  Apparently, JP is not aware of recent developments in psychological science that range from statistical tests that reveal missing studies (like an X-ray for looked file-drawers) to preregistration of studies that will be published without a significance filter.

Although utterly unlikely given current norms, reporting that we didn’t find the effect in a previous study (and describing the measures and manipulations used) would be broadly informative for the field and would benefit individual researchers conducting related studies. Certainly publication of replications by others would serve as a corrective as well.

It is not clear why publishing non-significant results is considered utterly unlikely in 2015, if the 2010 APA Publication Manual mandates publication of these studies.

Despite her pessimism about the future of Psychological Science, JP has a clear vision how psychologists could improve their science.

A major, needed shift in research and publication norms is likely to be greatly facilitated by an embrace of open access publishing, where immediate feedback, open evaluations and peer reviews, and greater communication among researchers (including replications and null results) hold the promise of opening debate and discussion of findings. Such changes would help preclude false-positive effects from becoming prematurely reified as facts; but such changes, if they are to occur, will clearly take time.

The main message of this chapter is that researchers in psychology have been trained to chase significance because obtaining statistical significance by all means was considered a form of creativity and good research (Sternberg, 2018).  Unfortunately, this is wrong. Statistical significance is only meaningful if it is obtained the right way and in an open and transparent manner.

33 Commentary to Part V Susan T. Fiske

It was surprising to read Fiske’s (2015) statement that “contrary to human nature, we as scientists should welcome humiliation, because it shows that the science is working.”

In marked contrast to this quote, Fiske has attacked psychologists who are trying to correct some of the errors in published articles as “method terrorists

I personally find both statements problematic. Nobody should welcome humiliation and nobody who points out errors in published articles is a terrorist.  Researchers should simply realize that publications in peer-reviewed journals can still contain errors and that it is part of the scientific process to correct these errors.  The biggest problem in the past seven years was not that psychologists made mistakes, but that they resisted efforts to correct them that arise from a flawed understanding of the scientific method.

36 Commentary to Part VI Susan T. Fiske

Social psychologists have justified not reporting failed study (cf. Jonathan Haidt example) by calling these studies pilot studies (Bem, 2011).  Bem pointed out that social psychologists have a lot of these pilot studies.  But a pilot study is not a study that tests the cause effect relationship. A pilot study tests either whether a manipulation is effective or whether a measure is reliable and valid.  It is simply wrong to treat studies that test the effect of a manipulation on an outcome a pilot study, if the study did not work.

“However, few of the current proposals for greater transparency recommend describingeach and every failed pilot study.”

The next statement makes it clear that Fiske conflates pilot studies with failed studies.

As noted, the reasons for failures to produce a given result are multiple, and supporting the null hypothesis is only one explanation. 

Yes, but it is one plausible explanation and not disclosing the failure renders the whole purpose of empirical hypothesis testing irrelevant (Sterling, 1959).

“Deciding when one has failed to replicate is a matter of persistence and judgment.”

No it is not. Preregister the study and if you are willing to use a significant result if you obtain it, you have to report the non-significant result if you do not. Everything else is not science and Susan Fiske seems to lack an understanding of the most basic reason for conducting an experiment.

What is an ethical scientist to do? One resolution is to treat a given result – even if it required fine-tuning to produce – as an existence proof: This result demonstrably can occur, at least under some circumstances. Over time, attempts to replicate will test generalizability.

This statement ignores that the observed pattern of results is heavily influenced by sampling error, especially in the typical between-subject design with small samples that is so popular in experimental social psychology.  A mean difference between two groups does not mean that anything happened in this study. It could just be sampling error.  But maybe the thought that most of the published results in experimental social psychology are just errors is too much to bear for somebody at the end of her career.

I have followed the replication crisis unfold over the past seven years since Bem (2011) published the eye-opening, ridiculous claims about feeling the future location of randomly displayed erotica. I cannot predict random events in the future, but I can notice trends and I do have a feeling that the future will not look kindly on those who tried to stand in the way of progress in psychological science. A new generation of psychologists is learning everyday about replication failures and how to conduct better studies.  For old people there are only two choices. Step aside or help them to learn from the mistakes of the older generation.

P.S. I think there is a connection between morality and disgust but it (mainly) goes from immoral behaviors to disgust.  So let me tell you, psychological science, Uranus stinks.

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A critique of Stroebe and Strack’s Article “The Alleged Crisis and the Illusion of Exact Replication”

The article by Stroebe and Strack (2014) [henceforth S&S] illustrates how experimental social psychologists responded to replication failures in the beginning of the replicability revolution.  The response is a classic example of repressive coping: Houston, we do not have a problem. Even in 2014,  problems with the way experimental social psychologists had conducted research for decades were obvious (Bem, 2011; Wagenmakers et al., 2011; John et al., 2012; Francis, 2012; Schimmack, 2012; Hasher & Wagenmakers, 2012).  S&S article is an attempt to dismiss these concerns as misunderstandings and empirically unsupported criticism.

“In contrast to the prevalent sentiment, we will argue that the claim of a replicability crisis is greatly exaggerated” (p. 59).  

Although the article was well received by prominent experimental social psychologists (see citations in appendix), future events proved S&S wrong and vindicated critics of research methods in experimental social psychology. Only a year later, the Open Science Collaboration (2015) reported that only 25% of studies in social psychology could be replicated successfully.  A statistical analysis of focal hypothesis tests in social psychology suggests that roughly 50% of original studies could be replicated successfully if these studies were replicated exactly (Motyl et al., 2017).  Ironically, one of S&S’s point is that exact replication studies are impossible. As a result, the 50% estimate is an optimistic estimate of the success rate for actual replication studies, suggesting that the actual replicability of published results in social psychology is less than 50%.

Thus, even if S&S had reasons to be skeptical about the extent of the replicability crisis in experimental social psychology, it is now clear that experimental social psychology has a serious replication problem. Many published findings in social psychology textbooks may not replicate and many theoretical claims in social psychology rest on shaky empirical foundations.

What explains the replication problem in experimental social psychology?  The main reason for replication failures is that social psychology journals mostly published significant results.  The selective publishing of significant results is called publication bias. Sterling pointed out that publication bias in psychology is rampant.  He found that psychology journals publish over 90% significant results (Sterling, 1959; Sterling et al., 1995).  Given new estimates that the actual success rate of studies in experimental social psychology is less than 50%, only publication bias can explain why journals publish over 90% results that confirm theoretical predictions.

It is not difficult to see that reporting only studies that confirm predictions undermines the purpose of empirical tests of theoretical predictions.  If studies that do not confirm predictions are hidden, it is impossible to obtain empirical evidence that a theory is wrong.  In short, for decades experimental social psychologists have engaged in a charade that pretends that theories are empirically tested, but publication bias ensured that theories would never fail.  This is rather similar to Volkswagen’s emission tests that were rigged to pass because emissions were never subjected to a real test.

In 2014, there were ample warning signs that publication bias and other dubious practices inflated the success rate in social psychology journals.  However, S&S claim that (a) there is no evidence for the use of questionable research practices and (b) that it is unclear which practices are questionable or not.

“Thus far, however, no solid data exist on the prevalence of such research practices in either social or any other area of psychology. In fact, the discipline still needs to reach an agreement about the conditions under which these practices are unacceptable” (p. 60).

Scientists like to hedge their statements so that they are immune to criticism. S&S may argue that the evidence in 2014 was not “solid” and surely there was and still is no agreement about good research practices. However, this is irrelevant. What is important is that success rates in social psychology journals were and still are inflated by suppressing disconfirming evidence and biasing empirical tests of theories in favor of positive outcomes.

Although S&S’s main claims are not based on empirical evidence, it is instructive to examine how they tried to shield published results and established theories from the harsh light of open replication studies that report results without selection for significance and subject social psychological theories to real empirical tests for the first time.

Failed Replication of Between-Subject Priming Studies

S&S discuss failed replications of two famous priming studies in social psychology: Bargh’s elderly priming study and Dijksterhuis’s professor priming studies.  Both seminal articles reported several successful tests of the prediction that a subtle priming manipulation would influence behavior without participants even noticing the priming effect.  In 2012, Doyen et al., failed to replicate elderly priming. Schanks et al. (2013) failed to replicate professor priming effects and more recently a large registered replication report also provided no evidence for professor priming.  For naïve readers it is surprising that original studies had a 100% success rate and replication studies had a 0% success rate.  However, S&S are not surprised at all.

“as in most sciences, empirical findings cannot always be replicated” (p. 60). 

Apparently, S&S knows something that naïve readers do not know.  The difference between naïve readers and experts in the field is that experts have access to unpublished information about failed replications in their own labs and in the labs of their colleagues. Only they know how hard it sometimes was to get the successful outcomes that were published. With the added advantage of insider knowledge, it makes perfect sense to expect replication failures, although may be not 0%.

The problem is that S&S give the impression that replication failures are too be expected, but that this expectation cannot be based on the objective scientific record that hardly ever reports results that contradict theoretical predictions.  Replication failures occur all the time, but they remained unpublished. Doyen et al. and Schanks et al.’s articles only violated the code to publish only supportive evidence.

Kahneman’s Train Wreck Letter

S&S also comment on Kahneman’s letter to Bargh that compared priming research to a train wreck.  In response S&S claim that

“priming is an entirely undisputed method that is widely used to test hypotheses about associative memory (e.g., Higgins, Rholes, & Jones, 1977; Meyer & Schvaneveldt, 1971; Tulving & Schacter, 1990).” (p. 60).  

This argument does not stand the test of time.  Since S&S published their article researchers have distinguished more clearly between highly replicable priming effects in cognitive psychology with repeated measures and within-subject designs and difficult to replicate between-subject social priming studies with subtle priming manipulations and a single outcome measure (BS social priming).  With regards to BS social priming, it is unclear which of these effects can be replicated and leading social psychologists have been reluctant to demonstrate replicability of their famous studies by conducting self-replications as they were encouraged to do in Kahneman’s letter.

S&S also point to empirical evidence for robust priming effects.

“A meta-analysis of studies that investigated how trait primes influence impression formation identified 47 articles based on 6,833 participants and found overall effects to be statistically highly significant (DeCoster & Claypool, 2004).” (p. 60). 

The problem with this evidence is that this meta-analysis did not take publication bias into account; in fact, it does not even mention publication bias as a possible problem.  A meta-analysis of studies that were selected for significance produces is also biased by selection for significance.

Several years after Kahneman’s letter, it is widely agreed that past research on social priming is a train wreck.  Kahneman published a popular book that celebrated social priming effects as a major scientific discovery in psychology.  Nowadays, he agrees with critiques that the existing evidence is not credible.  It is also noteworthy that none of the researchers in this area have followed Kahneman’s advice to replicate their own findings to show the world that these effects are real.

It is all a big misunderstanding

S&S suggest that “the claim of a replicability crisis in psychology is based on a major misunderstanding.” (p. 60). 

Apparently, lay people, trained psychologists, and a Noble laureate are mistaken in their interpretation of replication failures.  S&S suggest that failed replications are unimportant.

“the myopic focus on “exact” replications neglects basic epistemological principles” (p. 60).  

To make their argument, they introduce the notion of exact replications and suggest that exact replication studies are uninformative.

 “a finding may be eminently reproducible and yet constitute a poor test of a theory.” (p. 60).

The problem with this line of argument is that we are supposed to assume that a finding is eminently reproducible, which probably means it has been successfully replicate many times.  It seems sensible that further studies of gender differences in height are unnecessary to convince us that there is a gender difference in height. However, results in social psychology are not like gender differences in height.  According to S&S own accord earlier, “empirical findings cannot always be replicated” (p. 60). And if journals only publish significant results, it remains unknown which results are eminently reproducible and which results are not.  S&S ignore publication bias and pretend that the published record suggests that all findings in social psychology are eminently reproducible. Apparently, they would suggest that even Bem’s findings that people have supernatural abilities is eminently reproducible.  These days, few social psychologists are willing to endorse this naïve interpretation of the scientific record as a credible body of empirical facts.   

Exact Replication Studies are Meaningful if they are Successful

Ironically, S&S next suggest that exact replication studies can be useful.

Exact replications are also important when studies produce findings that are unexpected and only loosely connected to a theoretical framework. Thus, the fact that priming individuals with the stereotype of the elderly resulted in a reduction of walking speed was a finding that was unexpected. Furthermore, even though it was consistent with existing theoretical knowledge, there was no consensus about the processes that mediate the impact of the prime on walking speed. It was therefore important that Bargh et al. (1996) published an exact replication of their experiment in the same paper.

Similarly, Dijksterhuis and van Knippenberg (1998) conducted four studies in which they replicated the priming effects. Three of these studies contained conditions that were exact replications.

Because it is standard practice in publications of new effects, especially of effects that are surprising, to publish one or two exact replications, it is clearly more conducive to the advancement of psychological knowledge to conduct conceptual replications rather than attempting further duplications of the original study.

Given these citations it is problematic that S&S article is often cited to claim that exact replications are impossible or unnecessary.  The argument that S&S are making here is rather different.  They are suggesting that original articles already provide sufficient evidence that results in social psychology are eminently reproducible because original articles report multiple studies and some of these studies are often exact replication studies.  At face value, S&S have a point.  An honest series of statistically significant results makes it practically impossible that an effect is a false positive result (Schimmack, 2012).  The problem is that multiple study articles are not honest reports of all replication attempts.  Francis (2014) found that at least 80% of multiple study articles showed statistical evidence of questionable research practices.  Given the pervasive influence of selection for significance, exact replication studies in original articles provide no information about the replicability of these results.

What made the failed replications by Doyen et al. and Shank et al. so powerful was that these studies were the first real empirical tests of BS social priming effects because the authors were willing to report successes or failures.  The problem for social psychology is that many textbook findings that were obtained with selection for significance cannot be reproduced in honest empirical tests of the predicted effects.  This means that the original effects were either dramatically inflated or may not exist at all.

Replication Studies are a Waste of Resources

S&S want readers to believe that replication studies are a waste of resources.

Given that both research time and money are scarce resources, the large scale attempts at duplicating previous studies seem to us misguided” (p. 61).

This statement sounds a bit like a plea to spare social psychology from the embarrassment of actual empirical tests that reveal the true replicability of textbook findings. After all, according to S&S it is impossible to duplicate original studies (i.e., conduct exact replication studies) because replication studies differ in some way from original studies and may not reproduce the original results.  So, none of the failed replication studies is an exact replication.  Doyen et al. replicate Bargh’s study that was conducted in New York city in Belgium and Shanks et al. replicated Dijksterhuis’s studies from the Netherlands in the United States.  The finding that the original results could not be replicate the original results does not imply that the original findings were false positives, but they do imply that these findings may be unique to some unspecified specifics of the original studies.  This is noteworthy when original results are used in textbook as evidence for general theories and not as historical accounts of what happened in one specific socio-cultural context during a specific historic period. As social situations and human behavior are never exact replications of the past, social psychological results need to be permanently replicated and doing so is not a waste of resources.  Suggesting that replications is a waste of resources is like suggesting that measuring GDP or unemployment every year is a waste of resources because we can just use last-year’s numbers.

As S&S ignore publication bias and selection for significance, they are also ignoring that publication bias leads to a massive waste of resources.  First, running empirical tests of theories that are not reported is a waste of resources.  Second, publishing only significant results is also a waste of resources because researchers design new studies based on the published record. When the published record is biased, many new studies will fail, just like airplanes who are designed based on flawed science would drop from the sky.  Thus, a biased literature creates a massive waste of resources.

Ultimately, a science that publishes only significant result wastes all resources because the outcome of the published studies is a foregone conclusion: the prediction was supported, p < .05. Social psychologists might as well publish purely theoretical article, just like philosophers in the old days used “thought experiments” to support their claims. An empirical science is only a real science if theoretical predictions are subjected to tests that can fail.  By this simple criterion, experimental social psychology is not (yet) a science.

Should Psychologists Conduct Exact Replications or Conceptual Replications?

Strobe and Strack’s next cite Pashler and Harris (2012) to claim that critiques of experimental social psychology have dismissed the value of so-called conceptual replications and generalize.

The main criticism of conceptual replications is that they are less informative than exact replications (e.g., Pashler & Harris, 2012).” 

Before I examine S&S’s counterargument, it is important to realize that S&S misrepresented, and maybe misunderstood, Pashler and Harris’s main point. Here is the relevant quote from Pashler and Harris’s article.

We speculate that the harmful interaction of publication bias and a focus on conceptual rather than direct replications may even shed light on some of the famous and puzzling “pathological science” cases that embarrassed the natural sciences at several points in the 20th century (e.g., Polywater; Rousseau & Porto, 1970; and cold fusion; Taubes, 1993).

The problem for S&S is that they cannot address the problem of publication bias and therefore carefully avoid talking about it.  As a result, they misrepresent Pashler and Harris’s critique of conceptual replications in combination with publication bias as a criticism of conceptual replication studies, which is absurd and not what Pashler and Harris’s intended to say or actually said. The following quote from their article makes this crystal clear.

However, what kept faith in cold fusion alive for some time (at least in the eyes of some onlookers) was a trickle of positive results achieved using very different designs than the originals (i.e., what psychologists would call conceptual replications). This suggests that one important hint that a controversial finding is pathological may arise when defenders of a controversial effect disavow the initial methods used to obtain an effect and rest their case entirely upon later studies conducted using other methods. Of course, productive research into real phenomena often yields more refined and better ways of producing effects. But what should inspire doubt is any situation where defenders present a phenomenon as a “moving target” in terms of where and how it is elicited (cf. Langmuir, 1953/1989). When this happens, it would seem sensible to ask, “If the finding is real and yet the methods used by the original investigators are not reproducible, then how were these investigators able to uncover a valid phenomenon with methods that do not work?” Again, the unavoidable conclusion is that a sound assessment of a controversial phenomenon should focus first and foremost on direct replications of the original reports and not on novel variations, each of which may introduce independent ambiguities.

I am confident that unbiased readers will recognize that Pashler and Harris did not suggest that conceptual replication studies are bad.  Their main point is that a few successful conceptual replication studies can be used to keep theories alive in the face of a string of many replication failures. The problem is not that researchers conduct successful conceptual replication studies. The problem is dismissing or outright hiding of disconfirming evidence in replication studies. S&S misconstrue Pashler and Harris’s claim to avoid addressing this real problem of ignoring and suppressing failed studies to support an attractive but false theory.

The illusion of exact replications.

S&S next argument is that replication studies are never exact.

If one accepts that the true purpose of replications is a (repeated) test of a theoretical hypothesis rather than an assessment of the reliability of a particular experimental procedure, a major problem of exact replications becomes apparent: Repeating a specific operationalization of a theoretical construct at a different point in time and/or with a different population of participants might not reflect the same theoretical construct that the same procedure operationalized in the original study.

The most important word in this quote is “might.”   Ebbinghaus’s memory curve MIGHT not replicate today because he was his own subject.  Bargh’s elderly priming study MIGHT not work today because Florida is no longer associated with the elderly, and Disjterhuis’s priming study MIGHT no longer works because students no longer think that professors are smart or that Hooligans are dumb.

Just because there is no certainty in inductive inferences doesn’t mean we can just dismiss replication failures because something MIGHT have changed.  It is also possible that the published results MIGHT be false positives because significant results were obtained by chance, with QRPs, or outright fraud.  Most people think that outright fraud is unlikely, but the Stapel debacle showed that we cannot rule it out.  So, we can argue forever about hypothetical reasons why a particular study was successful or a failure. These arguments are futile and have nothing to do with scientific arguments and objective evaluation of facts.

This means that every study, whether it is a groundbreaking success or a replication failure needs to be evaluate in terms of the objective scientific facts. There is no blanket immunity for seminal studies that protects them from disconfirming evidence.  No study is an exact replication of another study. That is a truism and S&S article is often cited for this simple fact.  It is as true as it is irrelevant to understand the replication crisis in social psychology.

Exact Replications Are Often Uninformative

S&S contradict themselves in the use of the term exact replication.  First it is impossible to do exact replications, but then they are uninformative.  I agree with S&S that exact replication studies are impossible. So, we can simply drop the term “exact” and examine why S&S believe that some replication studies are uninformative.

First they give an elaborate, long and hypothetical explanation for Doyen et al.’s failure to replicate Bargh’s pair of elderly priming studies. After considering some possible explanations, they conclude

It is therefore possible that the priming procedure used in the Doyen et al. (2012) study failed in this respect, even though Doyen et al. faithfully replicated the priming procedure of Bargh et al. (1996).  

Once more the realm of hypothetical conjectures has to rescue seminal findings. Just as it is possible that S&S are right it is also possible that Bargh faked his data. To be sure, I do not believe that he faked his data and I apologized for a Facebook comment that gave the wrong impression that I did. I am only raising this possibility here to make the point that everything is possible. Maybe Bargh just got lucky.  The probability of this is 1 out of 1,600 attempts (the probability to get the predicted effect with .05 two-tailed (!) twice is .025^2). Not very likely, but also not impossible.

No matter what the reason for the discrepancy between Bargh and Doyen’s findings is, the example does not support S&S’s claim that replication studies are uninformative. The failed replication raised concerns about the robustness of BS social priming studies and stimulated further investigation of the robustness of social priming effects. In the short span of six years, the scientific consensus about these effects has shifted dramatically, and the first publication of a failed replication is an important event in the history of social psychology.

S&S’s critique of Shank et al.’s replication studies is even weaker.  First, they have to admit that professor probably still primes intelligence more than soccer hooligans. To rescue the original finding S&S propose

“the priming manipulation might have failed to increase the cognitive representation of the concept “intelligence.” 

S&S also think that

another LIKELY reason for their failure could be their selection of knowledge items.

Meanwhile a registered replication report with a design that was approved by Dijksterhuis failed to replicate the effect.  Although it is possible to come up with more possible reasons for these failures, real scientific creativity is revealed in creating experimental paradigms that produce replicable results, not in coming up with many post-hoc explanations for replication failures.

Ironically, S&S even agree with my criticism of their argument.

 “To be sure, these possibilities are speculative”  (p. 62). 

In contrast, S&S fail to consider the possibility that published significant results are false positives, even though there is actual evidence for publication bias. The strong bias against published failures may be rooted in a long history of dismissing unpublished failures that social psychologists routinely encounter in their own laboratory.  To avoid the self-awareness that hiding disconfirming evidence is unscientific, social psychologists made themselves believe that minute changes in experimental procedures can ruin a study (Stapel).  Unfortunately, a science that dismisses replication failures as procedural hiccups is fated to fail because it removed the mechanism that makes science self-correcting.

Failed Replications are Uninformative

S&S next suggest that “nonreplications are uninformative unless one can demonstrate that the theoretically relevant conditions were met” (p. 62).

This reverses the burden of proof.  Original researchers pride themselves on innovative ideas and groundbreaking discoveries.  Like famous rock stars, they are often not the best musicians, nor is it impossible for other musicians to play their songs. They get rewarded because they came up with something original. Take the Implicit Association Test as an example. The idea to use cognitive switching tasks to measure attitudes was original and Greenwald deserves recognition for inventing this task. The IAT did not revolutionize attitude research because only Tony Greenwald could get the effects. It did so because everybody, including my undergraduate students, could replicate the basic IAT effect.

However, let’s assume that the IAT effect could not have been replicated. Is it really the job of researchers who merely duplicated a study to figure out why it did not work and develop a theory under which circumstances an effect may occur or not?  I do not think so. Failed replications are informative even if there is no immediate explanation why the replication failed.  As Pashler and Harris’s cold fusion example shows there may not even be a satisfactory explanation after decades of research. Most probably, cold fusion never really worked and the successful outcome of the original study was a fluke or a problem of the experimental design.  Nevertheless, it was important to demonstrate that the original cold fusion study could not be replicated.  To ask for an explanation why replication studies fail is simply a way to make replication studies unattractive and to dismiss the results of studies that fail to produce the desired outcome.

Finally, S&S ignore that there is a simple explanation for replication failures in experimental social psychology: publication bias.  If original studies have low statistical power (e.g., Bargh’s studies with N = 30) to detect small effects, only vastly inflated effect sizes reach significance.  An open replication study without inflated effect sizes is unlikely to produce a successful outcome. Statistical analysis of original studies show that this explanation accounts for a large proportion of replication failures. Thus, publication bias provides one explanation for replication failures.

Conceptual Replication Studies are Informative

S&S cite Schmidt (2009) to argue that conceptual replication studies are informative.

With every difference that is introduced the confirmatory power of the replication increases, because we have shown that the phenomenon does not hinge on a particular operationalization but “generalizes to a larger area of application” (p. 93).

S&S continue

“An even more effective strategy to increase our trust in a theory is to test it using completely different manipulations.”

This is of course true as long as conceptual replication studies are successful. However, it is not clear why conceptual replication studies that for the first time try a completely different manipulation should be successful.  As I pointed out in my 2012 article, reading multiple-study articles with only successful conceptual replication studies is a bit like watching a magic show.

Multiple-study articles are most common in experimental psychology to demonstrate the robustness of a phenomenon using slightly different experimental manipulations. For example, Bem (2011) used a variety of paradigms to examine ESP. Demonstrating a phenomenon in several different ways can show that a finding is not limited to very specific experimental conditions. Analogously, if Joe can hit the bull’s-eye nine times from different angles, with different guns, and in different light conditions, Joe truly must be a sharpshooter. However, the variation of experimental procedures also introduces more opportunities for biases (Ioannidis, 2005). The reason is that variation of experimental procedures allows researchers to discount null findings. Namely, it is possible to attribute nonsignificant results to problems with the experimental procedure rather than to the absence of an effect.

I don’t know whether S&S are impressed by Bem’s article with 9 conceptual replication studies that successfully demonstrated supernatural abilities.  According to their line of arguments, they should be.  However, even most social psychologists found it impossible to accept that time-reversed subliminal priming works. Unfortunately, this also means that successful conceptual replication studies are meaningless if only successful results are published.  Once more, S&S cannot address this problem because they ignore the simple fact that selection for significance undermines the purpose of empirical research to test theoretical predictions.

Exact Replications Contribute Little to Scientific Knowledge

Without providing much evidence for their claims, S&S conclude

one reason why exact replications are not very interesting is that they contribute little to scientific knowledge.

Ironically, one year later Science published 100 replication studies with the only goal of estimating the replicability of psychology, with a focus on social psychology.  The article has already been cited 640 times, while S&S’s criticism of replication studies has been cited (only) 114 times.

Although the article did nothing else then to report the outcome of replication studies, it made a tremendous empirical contribution to psychology because it reported results of studies without the filter of publication bias.  Suddenly the success rate plummeted from over 90% to 37% and for social psychology to 25%.  While S&S could claim in 2014 that “Thus far, however, no solid data exist on the prevalence of such [questionable] research practices in either social or any other area of psychology,” the reproducibility project revealed that these practices dramatically inflated the percentage of successful studies reported in psychology journals.

The article has been celebrated by scientists in many disciplines as a heroic effort and a sign that psychologists are trying to improve their research practices. S&S may disagree, but I consider the reproducibility project a big contribution to scientific knowledge.

Why null findings are not always that informative

To fully appreciate the absurdity of S&S’s argument, I let them speak for themselves.

One reason is that not all null findings are interesting.  For example, just before his downfall, Stapel published an article on how disordered contexts promote stereotyping and discrimination. In this publication, Stapel and Lindenberg (2011) reported findings showing that litter or a broken-up sidewalk and an abandoned bicycle can increase social discrimination. These findings, which were later retracted, were judged to be sufficiently important and interesting to be published in the highly prestigious journal Science. Let us assume that Stapel had actually conducted the research described in this paper and failed to support his hypothesis. Such a null finding would have hardly merited publication in the Journal of Articles in Support of the Null Hypothesis. It would have been uninteresting for the same reason that made the positive result interesting, namely, that (a) nobody expected a relationship between disordered environments and prejudice and (b) there was no previous empirical evidence for such a relationship. Similarly, if Bargh et al. (1996) had found that priming participants with the stereotype of the elderly did not influence walking speed or if Dijksterhuis and van Knippenberg (1998) had reported that priming participants with “professor” did not improve their performance on a task of trivial pursuit, nobody would have been interested in their findings.

Notably, all of the examples are null-findings in original studies. Thus, they have absolutely no relevance for the importance of replication studies. As noted by Strack and Stroebe earlier

Thus, null findings are interesting only if they contradict a central hypothesis derived from an established theory and/or are discrepant with a series of earlier studies.” (p. 65). 

Bem (2011) reported 9 significant results to support unbelievable claims about supernatural abilities.  However, several failed replication studies allowed psychologists to dismiss these findings and to ignore claims about time-reversed priming effects. So, while not all null-results are important, null-results in replication studies are important because they can correct false positive results in original articles. Without this correction mechanism, science looses its ability to correct itself.

Failed Replications Do Not Falsify Theories

S&S state that failed replications do not falsify theories

The nonreplications published by Shanks and colleagues (2013) cannot be taken as a falsification of that theory, because their study does not explain why previous research was successful in replicating the original findings of Dijksterhuis and van Knippenberg (1998).” (p. 64). 

I am unaware of any theory in psychology that has been falsified. The reason for this is not that failed replication studies are not informative. The reason is that theories have been protected by hiding failed replication studies until recently. Only in recent years have social psychologists started to contemplate the possibility that some theories in social psychology might be false.  The most prominent example is ego-depletion theory, which has been one of the first prominent theories that has been put under the microscope of open science without the protection of questionable research practices in recent years. While ego-depletion theory is not entirely dead, few people still believe in the simple theory that 20 Stroop trials deplete individuals’ will power.  Falsification is hard, but falsification without disconfirming evidence is impossible.

Inconsistent Evidence

S&S argue that replication failures have to be evaluated in the context of replication successes.

Even multiple failures to replicate an established finding would not result in a rejection of the original hypothesis, if there are also multiple studies that supported that hypothesis. 

Earlier S&S wrote

in social psychology, as in most sciences, empirical findings cannot always be replicated (this was one of the reasons for the development of meta-analytic methods). 

Indeed. Unless studies have very high statistical power, inconsistent results are inevitable; which is one reason why publishing only significant results is a sign of low credibility (Schimmack, 2012). Meta-analysis is the only way to make sense of these inconsistent findings.  However, it is well known that publication bias makes meta-analytic results meaningless (e.g., meta-analysis show very strong evidence for supernatural abilities).  Thus, it is important that all tests of a theoretical prediction are reported to produce meaningful meta-analyses.  If social psychologists would take S&S seriously and continue to suppress non-significant results because they are uninformative, meta-analysis would continue to provide biased results that support even false theories.

Failed Replications are Uninformative II

Sorry that this is getting really long. But S&S keep on making the same arguments and the editor of this article didn’t tell them to shorten the article. Here they repeat the argument that failed replications are uninformative.

One reason why null findings are not very interesting is because they tell us only that a finding could not be replicated but not why this was the case. This conflict can be resolved only if researchers develop a theory that could explain the inconsistency in findings.  

A related claim is that failed replications never demonstrate that original findings were false because the inconsistency is always due to some third variable; a hidden moderator.

Methodologically, however, nonreplications must be understood as interaction effects in that they suggest that the effect of the crucial influence depends on the idiosyncratic conditions under which the original experiment was conducted” (p. 64). 

These statements reveal a fundamental misunderstanding of statistical inferences.  A significant result never proofs that the null-hypothesis is false.  The inference that a real effect rather than sampling error caused the observed result can be a mistake. This mistake is called a false positive or a type-I error. S&S seems to believe that type-I errors do not exist. Accordingly, Bem’s significant results show real supernatural abilities.  If this were the case, it would be meaningless to report statistical significance tests. The only possible error that could be made would be false negatives or type-II error; the theory makes the correct prediction, but a study failed to produce a significant result. And if theoretical predictions are always correct, it is also not necessary to subject theories to empirical tests, because these tests either correctly show that a prediction was confirmed or falsely fail to confirm a prediction.

S&S’s belief in published results has a religious quality.  Apparently we know nothing about the world, but once a significant result is published in a social psychology journal, ideally JPSP, it becomes a holy truth that defies any evidence that non-believers may produce under the misguided assumption that further inquiry is necessary. Elderly priming is real, amen.

More Confusing Nonsense

At some point, I was no longer surprised by S&S’s claims, but I did start to wonder about the reviewers and editors who allowed this manuscript to be published apparently with light or no editing.  Why would a self-respecting journal publish a sentence like this?

As a consequence, the mere coexistence of exact replications that are both successful and unsuccessful is likely to leave researchers helpless about what to conclude from such a pattern of outcomes.

Didn’t S&S claim that exact replication studies do not exist? Didn’t they tell readers that every inconsistent finding has to be interpreted as an interaction effect?  And where do they see inconsistent results if journals never publish non-significant results?

Aside from these inconsistencies, inconsistent results do not lead to a state of helpless paralysis. As S&S suggested themselves, they conduct a meta-analysis. Are S&S suggesting that we need to spare researchers from inconsistent results to protect them from a state of helpless confusion? Is this their justification for publishing only significant results?

Even Massive Replication Failures in Registered Replication Reports are Uninformative

In response to the replication crisis, some psychologists started to invest time and resources in major replication studies called many lab studies or registered replication studies.  A single study was replicated in many labs.  The total sample size of many labs gives these studies high precision in estimating the average effect size and makes it even possible to demonstrate that an effect size is close to zero, which suggests that the null-hypothesis may be true.  These studies have failed to find evidence for classic social psychology findings, including Strack’s facial feedback studies. S&S suggest that even these results are uninformative.

Conducting exact replications in a registered and coordinated fashion by different laboratories does not remove the described shortcomings. This is also the case if exact replications are proposed as a means to estimate the “true size” of an effect. As the size of an experimental effect always depends on the specific error variance that is generated by the context, exact replications can assess only the efficiency of an intervention in a given situation but not the generalized strength of a causal influence.

Their argument does not make any sense to me.  First, it is not clear what S&S mean by “the size of an experimental effect always depends on the specific error variance.”  Neither unstandardized nor standardized effect sizes depend on the error variance. This is simple to see because error variance depends on the sample size and effect sizes do not depend on sample size.  So, it makes no sense to claim that effect sizes depend on error variance.

Second, it is not clear what S&S mean by specific error variance that is generated by the context.  I simply cannot address this argument because the notion of context generated specific error variance is not a statistical construct and S&S do not explain what they are talking about.

Finally, it is not clear why meta-analysis of replication studies cannot be used to estimate the generalized strength of a causal influence, which I believe to mean “an effect size”?  Earlier S&S alluded to meta-analysis as a way to resolve inconsistencies in the literature, but now they seem to suggest that meta-analysis cannot be used.

If S&S really want to imply that meta-analyses are useless, it is unclear how they would make sense of inconsistent findings.  The only viable solution seems to be to avoid inconsistencies by suppressing non-significant results in order to give the impression that every theory in social psychology is correct because theoretical predictions are always confirmed.  Although this sounds absurd, it is the inevitable logical consequence of S&S’s claim that non-significant results are uninformative, even if over 20 labs independently and in combination failed to provide evidence for a theoretical predicted effect.

The Great History of Social Psychological Theories

S&S next present Über-social psychologist, Leon Festinger, as an example why theories are good and failed studies are bad.  The argument is that good theories make correct predictions, even if bad studies fail to show the effect.

“Although their theoretical analysis was valid, it took a decade before researchers were able to reliably replicate the findings reported by Festinger and Carlsmith (1959).”

As a former student, I was surprised by this statement because I had learned that Festinger’s theory was challenged by Bem’s theory and that social psychologists had been unable to resolve which of the two theories was correct.  Couldn’t some of these replication failures be explained by the fact that Festinger’s theory sometimes made the wrong prediction?

It is also not surprising that researchers had a hard time replicating Festinger and Carlsmith original findings.  The reason is that the original study had low statistical power and replication failures are expected even if the theory is correct. Finally, I have been around social psychologists long enough to have heard some rumors about Festinger and Carlsmith’s original studies.  Accordingly, some of Festinger’s graduate students also tried and failed to get the effect. Carlsmith was the ‘lucky’ one who got the effect, in one study p < .05, and he became the co-author of one of the most cited articles in the history of social psychology. Naturally, Festinger did not publish the failed studies of his other graduate students because surely they must have done something wrong. As I said, that is a rumor.  Even if the rumor is not true, and Carlsmith got lucky on the first try, luck played a factor and nobody should expect that a study replicates simply because a single published study reported a p-value less than .05.

Failed Replications Did Not Influence Social Psychological Theories

Argument quality reaches a new low with the next argument against replication studies.

 “If we look at the history of social psychology, theories have rarely been abandoned because of failed replications.”

This is true, but it reveals the lack of progress in theory development in social psychology rather than the futility of replication studies.  From an evolutionary perspective, theory development requires selection pressure, but publication bias protects bad theories from failure.

The short history of open science shows how weak social psychological theories are and that even the most basic predictions cannot be confirmed in open replication studies that do not selectively report significant results.  So, even if it is true that failed replications have played a minor role in the past of social psychology, they are going to play a much bigger role in the future of social psychology.

The Red Herring: Fraud

S&S imply that Roediger suggested to use replication studies as a fraud detection tool.

if others had tried to replicate his [Stapel’s] work soon after its publication, his misdeeds might have been uncovered much more quickly

S&S dismiss this idea in part on the basis of Stroebe’s research on fraud detection.

To their own surprise, Stroebe and colleagues found that replications hardly played any role in the discovery of these fraud cases.

Now this is actually not surprising because failed replications were hardly ever published.  And if there is no variance in a predictor variable (significance), we cannot see a correlation between the predictor variable and an outcome (fraud).  Although failed replication studies may help to detect fraud in the future, this is neither their primary purpose, nor necessary to make replication studies valuable. Replication studies also do not bring world peace or bring an end to global warming.

For some inexplicable reason S&S continue to focus on fraud. For example, they also argue that meta-analyses are poor fraud detectors, which is as true as it is irrelevant.

They conclude their discussion with an observation by Stapel, who famously faked 50+ articles in social psychology journals.

As Stapel wrote in his autobiography, he was always pleased when his invented findings were replicated: “What seemed logical and was fantasized became true” (Stapel, 2012). Thus, neither can failures to replicate a research finding be used as indicators of fraud, nor can successful replications be invoked as indication that the original study was honestly conducted.

I am not sure why S&S spend so much time talking about fraud, but it is the only questionable research practice that they openly address.  In contrast, they do not discuss other questionable research practices, including suppressing failed studies, that are much more prevalent and much more important for the understanding of the replication crisis in social psychology than fraud.  The term “publication bias” is not mentioned once in the article. Sometimes what is hidden is more significant than what is being published.

Conclusion

The conclusion section correctly predicts that the results of the reproducibility project will make social psychology look bad and that social psychology will look worse than other areas of psychology.

But whereas it will certainly be useful to be informed about studies that are difficult to replicate, we are less confident about whether the investment of time and effort of the volunteers of the Open Science Collaboration is well spent on replicating studies published in three psychology journals. The result will be a reproducibility coefficient that will not be greatly informative, because of justified doubts about whether the “exact” replications succeeded in replicating the theoretical conditions realized in the original research.

As social psychologists, we are particularly concerned that one of the outcomes of this effort will be that results from our field will be perceived to be less “reproducible” than research in other areas of psychology. This is to be expected because for the reasons discussed earlier, attempts at “direct” replications of social psychological studies are less likely than exact replications of experiments in psychophysics to replicate the theoretical conditions that were established in the original study.

Although psychologists should not be complacent, there seem to be no reasons to panic the field into another crisis. Crises in psychology are not caused by methodological flaws but by the way people talk about them (Kruglanski & Stroebe, 2012).

S&S attribute the foreseen (how did they know?) bad outcome in the reproducibility project to the difficulty of replicating social psychological studies, but they fail to explain why social psychology journals publish as many successes as other disciplines.

The results of the reproducibility project provide an answer to this question.  Social psychologists use designs with less statistical power that have a lower chance of producing a significant result. Selection for significance ensures that the success rate is equally high in all areas of psychology, but lower power makes these successes less replicable.

To avoid further embarrassments in an increasingly open science, social psychologists must improve the statistical power of their studies. Which social psychological theories will survive actual empirical tests in the new world of open science is unclear.  In this regard, I think it makes more sense to compare social psychology to a ship wreck than a train wreck.  Somewhere down on the floor of the ocean is some gold. But it will take some deep diving and many failed attempts to find it.  Good luck!

Appendix

S&S’s article was published in a “prestigious” psychology journal and has already garnered 114 citations. It ranks #21 in my importance rankings of articles in meta-psychology.  So, I was curious why the article gets cited.  The appendix lists 51 citing articles with the relevant citation and the reason for citing S&S’s article.   The table shows the reasons for citations in decreasing order of frequency.

S&S are most frequently cited for the claim that exact replications are impossible, followed by the reason for this claim that effects in psychological research are sensitive to the unique context in which a study is conducted.  The next two reasons for citing the article are that only conceptual replications (CR) test theories, whereas the results of exact replications (ER) are uninformative.  The problem is that every study is a conceptual replication because exact replications are impossible. So, even if exact replications were uninformative this claim has no practical relevance because there are no exact replications.  Some articles cite S&S with no specific claim attached to the citation.  Only two articles cite them for the claim that there is no replication crisis and only 1 citation cites S&S for the claim that there is no evidence about the prevalence of QRPs.   In short, the article is mostly cited for the uncontroversial and inconsequential claim that exact replications are impossible and that effect sizes in psychological studies can vary as a function of unique features of a particular sample or study.  This observation is inconsequential because it is unclear how unknown unique characteristics of studies influence results.  The main implication of this observation is that study results will be more variable than we would expect from a set of exact replication studies. For this reason, meta-analysts often use random-effects model because fixed-effects meta-analysis assumes that all studies are exact replications.

ER impossible 11
Contextual Sensitivity 8
CR test theory 8
ER uninformative 7
Mention 6
ER/CR Distinction 2
No replication crisis 2
Disagreement 1
CR Definition 1
ER informative 1
ER useful for applied research 1
ER cannot detect fraud 1
No evidence about prevalence of QRP 1
Contextual sensitivity greater in social psychology 1

the most influential citing articles and the relevant citation.  I haven’t had time to do a content analysis, but the article is mostly cited to say (a) exact replications are impossible, and (b) conceptual replications are valuable, and (c) social psychological findings are harder to replicate.  Few articles cite to article to claim that the replication crisis is overblown or that failed replications are uninformative.  Thus, even though the article is cited a lot, it is not cited for the main points S&S tried to make.  The high number of citation therefore does not mean that S&S’s claims have been widely accepted.

(Disagreement)
The value of replication studies.

Simmons, DJ.
“In this commentary, I challenge these claims.”

(ER/CR Distinction)
Bilingualism and cognition.

Valian, V.
“A host of methodological issues should be resolved. One is whether the field should undertake exact replications, conceptual replications, or both, in order to determine the conditions under which effects are reliably obtained (Paap, 2014; Simons, 2014; Stroebe & Strack, 2014).”

(Contextual Sensitivity)
Is Psychology Suffering From a Replication Crisis? What Does “Failure to Replicate” Really Mean?“
Maxwell et al. (2015)
A particular replication may fail to confirm the results of an original study for a variety of reasons, some of which may include intentional differences in procedures, measures, or samples as in a conceptual replication (Cesario, 2014; Simons, 2014; Stroebe & Strack, 2014).”

(ER impossible)
The Chicago face database: A free stimulus set of faces and norming data 

Debbie S. Ma, Joshua Correll, & Bernd Wittenbrink.
The CFD will also make it easier to conduct exact replications, because researchers can use the same stimuli employed by other researchers (but see Stroebe & Strack, 2014).”

(Contextual Sensitivity)
“Contextual sensitivity in scientific reproducibility”
vanBavel et al. (2015)
“Many scientists have also argued that the failure to reproduce results might reflect contextual differences—often termed “hidden moderators”—between the original research and the replication attempt”

(Contextual Sensitivity)
Editorial Psychological Science

Linday,
As Nosek and his coauthors made clear, even ideal replications of ideal studies are expected to fail some of the time (Francis, 2012), and failure to replicate a previously observed effect can arise from differences between the original and replication studies and hence do not necessarily indicate flaws in the original study (Maxwell, Lau, & Howard, 2015; Stroebe & Strack, 2014). Still, it seems likely that psychology journals have too often reported spurious effects arising from Type I errors (e.g., Francis, 2014).

(ER impossible)
Best Research Practices in Psychology: Illustrating Epistemological and Pragmatic Considerations With the Case of Relationship Science

Finkel et al. (2015).
“Nevertheless, many scholars believe that direct replications are impossible in the human sciences—S&S (2014) call them “an illusion”— because certain factors, such as a moment in historical time or the precise conditions under which a sample was obtained and tested, that may have contributed to a result can never be reproduced identically.”

Conceptualizing and evaluating the replication of research results
Fabrigar and Wegener (2016)
(CR test theory)
“Traditionally, the primary presumed strength of conceptual replications has been their ability to address issues of construct validity (e.g., Brewer & Crano, 2014; Schmidt, 2009; Stroebe & Strack, 2014). “

(ER impossible)
“First, it should be recognized that an exact replication in the strictest sense of the term can never be achieved as it will always be impossible to fully recreate the contextual factors and participant characteristics present in the original experiment (see Schmidt (2009); S&S (2014).”

(Contextual Sensitivity)
“S&S (2014) have argued that there is good reason to expect that many traditional and contemporary experimental manipulations in social psychology would have different psychological properties and effects if used in contexts or populations different from the original experiments for which they were developed. For example, classic dissonance manipulations and fear manipulations or more contemporary priming procedures might work very differently if used in new contexts and/or populations. One could generate many additional examples beyond those mentioned by S&S.”

(ER impossible)
“Another important point illustrated by the above example is that the distinction between exact and conceptual replications is much more nebulous than many discussions of replication would suggest. Indeed, some critics of the exact/conceptual replication distinction have gone so far as to argue that the concept of exact replication is an “illusion” (Stroebe & Strack, 2014). Though we see some utility in the exact/conceptual distinction (especially regarding the goal of the researcher in the work), we agree with the sentiments expressed by S&S. Classifying studies on the basis of the exact/conceptual distinction is more difficult than is often appreciated, and the presumed strengths and weaknesses of the approaches are less straightforward than is often asserted or assumed.”

(Contextual Sensitivity)
“Furthermore, assuming that these failed replication experiments have used the same operationalizations of the independent and dependent variables, the most common inference drawn from such failures is that confidence in the existence of the originally demonstrated effect should be substantially undermined (e.g., see Francis (2012); Schimmack (2012)). Alternatively, a more optimistic interpretation of such failed replication experiments could be that the failed versus successful experiments differ as a function of one or more unknown moderators that regulate the emergence of the effect (e.g., Cesario, 2014; Stroebe & Strack, 2014).”

Replicating Studies in Which Samples of Participants Respond to Samples of Stimuli.
(CR Definition)
Westfall et al. (2015).
Nevertheless, the original finding is considered to be conceptually replicated if it can be convincingly argued that the same theoretical constructs thought to account for the results of the original study also account for the results of the replication study (Stroebe & Strack, 2014). Conceptual replications are thus “replications” in the sense that they establish the reproducibility of theoretical interpretations.”

(Mention)
“Although establishing the generalizability of research findings is undoubtedly important work, it is not the focus of this article (for opposing viewpoints on the value of conceptual replications, see Pashler & Harris, 2012; Stroebe & Strack, 2014).“

Introduction to the Special Section on Advancing Our Methods and Practices
(Mention)
Ledgerwood, A.
We can and surely should debate which problems are most pressing and which solutions most suitable (e.g., Cesario, 2014; Fiedler, Kutzner, & Krueger, 2012; Murayama, Pekrun, & Fiedler, 2013; Stroebe & Strack, 2014). But at this point, most can agree that there are some real problems with the status quo.

***Theory Building, Replication, and Behavioral Priming: Where Do We Need to Go From Here?
Locke, EA
(ER impossible)
As can be inferred from Table 1, I believe that the now popular push toward “exact” replication (e.g., see Simons, 2014) is not the best way to go. Everyone agrees that literal replication is impossible (e.g., Stroebe & Strack, 2014), but let us assume it is as close as one can get. What has been achieved?

The War on Prevention: Bellicose Cancer: Metaphors Hurt (Some) Prevention Intentions”
(CR test theory)
David J. Hauser1 and Norbert Schwarz
“As noted in recent discussions (Stroebe & Strack, 2014), consistent effects of multiple operationalizations of a conceptual variable across diverse content domains are a crucial criterion for the robustness of a theoretical approach.”

ON THE OTHER SIDE OF THE MIRROR: PRIMING IN COGNITIVE AND SOCIAL PSYCHOLOGY 
Doyen et al. “
(CR test theory)
In contrast, social psychologists assume that the primes activate culturally and situationally contextualized representations (e.g., stereotypes, social norms), meaning that they can vary over time and culture and across individuals. Hence, social psychologists have advocated the use of “conceptual replications” that reproduce an experiment by relying on different operationalizations of the concepts under investigation (Stroebe & Strack, 2014). For example, in a society in which old age is associated not with slowness but with, say, talkativeness, the outcome variable could be the number of words uttered by the subject at the end of the experiment rather than walking speed.”

***Welcome back Theory
Ap Dijksterhuis
(ER uninformative)
“it is unavoidable, and indeed, this commentary is also about replication—it is done against the background of something we had almost forgotten: theory! S&S (2014, this issue) argue that focusing on the replication of a phenomenon without any reference to underlying theoretical mechanisms is uninformative”

On the scientific superiority of conceptual replications for scientific progress
Christian S. Crandall, Jeffrey W. Sherman
(ER impossible)
But in matters of social psychology, one can never step in the same river twice—our phenomena rely on culture, language, socially primed knowledge and ideas, political events, the meaning of questions and phrases, and an ever-shifting experience of participant populations (Ramscar, 2015). At a certain level, then, all replications are “conceptual” (Stroebe & Strack, 2014), and the distinction between direct and conceptual replication is continuous rather than categorical (McGrath, 1981). Indeed, many direct replications turn out, in fact, to be conceptual replications. At the same time, it is clear that direct replications are based on an attempt to be as exact as possible, whereas conceptual replications are not.

***Are most published social psychological findings false?
Stroebe, W.
(ER uninformative)
This near doubling of replication success after combining original and replication effects is puzzling. Because these replications were already highly powered, the increase is unlikely to be due to the greater power of a meta-analytic synthesis. The two most likely explanations are quality problems with the replications or publication bias in the original studies or. An evaluation of the quality of the replications is beyond the scope of this review and should be left to the original authors of the replicated studies. However, the fact that all replications were exact rather than conceptual replications of the original studies is likely to account to some extent for the lower replication rate of social psychological studies (Stroebe & Strack, 2014). There is no evidence either to support or to reject the second explanation.”

(ER impossible)
“All four projects relied on exact replications, often using the material used in the original studies. However, as I argued earlier (Stroebe & Strack, 2014), even if an experimental manipulation exactly replicates the one used in the original study, it may not reflect the same theoretical variable.”

(CR test theory)
“Gergen’s argument has important implications for decisions about the appropriateness of conceptual compared to exact replication. The more a phenomenon is susceptible to historical change, the more conceptual replication rather than exact replication becomes appropriate (Stroebe & Strack, 2014).”

(CR test theory)
“Moonesinghe et al. (2007) argued that any true replication should be an exact replication, “a precise processwhere the exact same finding is reexamined in the same way”. However, conceptual replications are often more informative than exact replications, at least in studies that are testing theoretical predictions (Stroebe & Strack, 2014). Because conceptual replications operationalize independent and/or dependent variables in a different way, successful conceptual replications increase our trust in the predictive validity of our theory.”

There’s More Than One Way to Conduct a Replication Study: Beyond Statistical Significance”
Anderson & Maxwell
(Mention)
“It is important to note some caveats regarding direct (exact) versus conceptual replications. While direct replications were once avoided for lack of originality, authors have recently urged the field to take note of the benefits and importance of direct replication. According to Simons (2014), this type of replication is “the only way to verify the reliability of an effect” (p. 76). With respect to this recent emphasis, the current article will assume direct replication. However, despite the push toward direct replication, some have still touted the benefits of conceptual replication (Stroebe & Strack, 2014). Importantly, many of the points and analyses suggested in this paper may translate well to conceptual replication.”

Reconceptualizing replication as a sequence of different studies: A replication typology
Joachim Hüffmeier, Jens Mazei, Thomas Schultze
(ER impossible)
The first type of replication study in our typology encompasses exact replication studies conducted by the author(s) of an original finding. Whereas we must acknowledge that replications can never be “exact” in a literal sense in psychology (Cesario, 2014; Stroebe & Strack, 2014), exact replications are studies that aspire to be comparable to the original study in all aspects (Schmidt, 2009). Exact replications—at least those that are not based on questionable research practices such as the arbitrary exclusion of critical outliers, sampling or reporting biases (John, Loewenstein, & Prelec, 2012; Simmons, Nelson, & Simonsohn, 2011)—serve the function of protecting against false positive effects (Type I errors) right from the start.

(ER informative)
Thus, this replication constitutes a valuable contribution to the research process. In fact, already some time ago, Lykken (1968; see also Mummendey, 2012) recommended that all experiments should be replicated  before publication. From our perspective, this recommendation applies in particular to new findings (i.e., previously uninvestigated theoretical relations), and there seems to be some consensus that new findings should be replicated at least once, especially when they were unexpected, surprising, or only loosely connected to existing theoretical models (Stroebe & Strack, 2014; see also Giner-Sorolla, 2012; Murayama et al., 2014).”

(Mention)
Although there is currently some debate about the epistemological value of close replication studies (e.g., Cesario, 2014; LeBel & Peters, 2011; Pashler & Harris, 2012; Simons, 2014; Stroebe & Strack, 2014), the possibility that each original finding can—in principal—be replicated by the scientific community represents a cornerstone of science (Kuhn, 1962; Popper, 1992).”

(CR test theory)
So far, we have presented “only” the conventional rationale used to stress the importance of close replications. Notably, however, we will now add another—and as we believe, logically necessary—point originally introduced by S&S (2014). This point protects close replications from being criticized (cf. Cesario, 2014; Stroebe & Strack, 2014; see also LeBel & Peters, 2011). Close replications can be informative only as long as they ensure that the theoretical processes investigated or at least invoked by the original study are shown to also operate in the replication study.

(CR test theory)
The question of how to conduct a close replication that is maximally informative entails a number of methodological choices. It is important to both adhere to the original study proceedings (Brandt et al., 2014; Schmidt, 2009) and focus on and meticulously measure the underlying theoretical mechanisms that were shown or at least proposed in the original studies (Stroebe & Strack, 2014). In fact, replication attempts are most informative when they clearly demonstrate either that the theoretical processes have unfolded as expected or at which point in the process the expected results could no longer be observed (e.g., a process ranging from a treatment check to a manipulation check and [consecutive] mediator variables to the dependent variable). Taking these measures is crucial to rule out that a null finding is simply due to unsuccessful manipulations or changes in a manipulation’s meaning and impact over time (cf. Stroebe & Strack, 2014). “

(CR test theory)
Conceptual replications in laboratory settings are the fourth type of replication study in our typology. In these replications, comparability to the original study is aspired to only in the aspects that are deemed theoretically relevant (Schmidt, 2009; Stroebe & Strack, 2014). In fact, most if not all aspects may differ as long as the theoretical processes that have been studied or at least invoked in the original study are also covered in a conceptual replication study in the laboratory.”

(ER useful for applied research)
For instance, conceptual replications may be less important for applied disciplines that focus on clinical phenomena and interventions. Here, it is important to ensure that there is an impact of a specific intervention and that the related procedure does not hurt the members of the target population (e.g., Larzelere et al., 2015; Stroebe & Strack, 2014).”

From intrapsychic to ecological theories in social psychology: Outlines of a functional theory approach
Klaus Fiedler
(ER uninformative)
Replicating an ill-understood finding is like repeating a complex sentence in an unknown language. Such a “replication” in the absence of deep understanding may appear funny, ridiculous, and embarrassing to a native speaker, who has full control over the foreign language. By analogy, blindly replicating or running new experiments on an ill-understood finding will rarely create real progress (cf. Stroebe & Strack, 2014). “

Into the wild: Field research can increase both replicability and real-world impact
Jon K. Maner
(CR test theory)
Although studies relying on homogeneous samples of laboratory or online participants might be highly replicable when conducted again in a similar homogeneous sample of laboratory or online participants, this is not the key criterion (or at least not the only criterion) on which we should judge replicability (Westfall, Judd & Kenny, 2015; see also Brandt et al., 2014; Stroebe & Strack, 2014). Just as important is whether studies replicate in samples that include participants who reflect the larger and more diverse population.”

Romance, Risk, and Replication: Can Consumer Choices and Risk-Taking Be Primed by Mating Motives?
Shanks et al.
(ER impossible)
There is no such thing as an “exact” replication (Stroebe & Strack, 2014) and hence it must be acknowledged that the published studies (notwithstanding the evidence for p-hacking and/or publication bias) may have obtained genuine effects and that undetected moderator variables explain why the present studies failed to obtain priming.   Some of the experiments reported here differed in important ways from those on which they were modeled (although others were closer replications and even these failed to obtain evidence of reliable romantic priming).

(CR test theory)
As S&S (2014) point out, what is crucial is not so much exact surface replication but rather identical operationalization of the theoretically relevant variables. In the present case, the crucial factors are the activation of romantic motives and the appropriate assessment of consumption, risk-taking, and other measures.”

A Duty to Describe: Better the Devil You Know Than the Devil You Don’t
Brown, Sacha D et al.
(Mention)
Ioannidis (2005) has been at the forefront of researchers identifying factors interfering with self-correction. He has claimed that journal editors selectively publish positive findings and discriminate against study replications, permitting errors in data and theory to enjoy a long half-life (see also Ferguson & Brannick, 2012; Ioannidis, 2008, 2012; Shadish, Doherty, & Montgomery, 1989; Stroebe & Strack, 2014). We contend there are other equally important, yet relatively unexplored, problems.

A Room with a Viewpoint Revisited: Descriptive Norms and Hotel Guests’ Towel Reuse Behavior
(Contextual Sensitivity)
Bohner, Gerd; Schlueter, Lena E.
On the other hand, our pilot participants’ estimates of towel reuse rates were generally well below 75%, so we may assume that the guests participating in our experiments did not perceive the normative messages as presenting a surprisingly low figure. In a more general sense, the issue of greatly diverging baselines points to conceptual issues in trying to devise a ‘‘direct’’ replication: Identical operationalizations simply may take on different meanings for people in different cultures.

***The empirical benefits of conceptual rigor: Systematic articulation of conceptual hypotheses can reduce the risk of non-replicable results (and facilitate novel discoveries too)
Mark Schaller
(Contextual Sensitivity)
Unless these subsequent studies employ methods that exactly replicate the idiosyncratic context in which the effect was originally detected, these studies are unlikely to replicate the effect. Indeed, because many psychologically important contextual variables may lie outside the awareness of researchers, even ostensibly “exact” replications may fail to create the conditions necessary for a fragile effect to emerge (Stroebe & Strack, 2014)

A Concise Set of Core Recommendations to Improve the Dependability of Psychological Research
David A. Lishner
(CR test theory)
The claim that direct replication produces more dependable findings across replicated studies than does conceptual replication seems contrary to conventional wisdom that conceptual replication is preferable to direct replication (Dijksterhuis, 2014; Neulip & Crandall, 1990, 1993a, 1993b; Stroebe & Strack, 2014).
(CR test theory)
However, most arguments advocating conceptual replication over direct replication are attempting to promote the advancement or refinement of theoretical understanding (see Dijksterhuis, 2014; Murayama et al., 2014; Stroebe & Strack, 2014). The argument is that successful conceptual replication demonstrates a hypothesis (and by extension the theory from which it derives) is able to make successful predictions even when one alters the sampled population, setting, operations, or data analytic approach. Such an outcome not only suggests the presence of an organizing principle, but also the quality of the constructs linked by the organizing principle (their theoretical meanings). Of course this argument assumes that the consistency across the replicated findings is not an artifact of data acquisition or data analytic approaches that differ among studies. The advantage of direct replication is that regardless of how flexible or creative one is in data acquisition or analysis, the approach is highly similar across replication studies. This duplication ensures that any false finding based on using a flexible approach is unlikely to be repeated multiple times.

(CR test theory)
Does this mean conceptual replication should be abandoned in favor of direct replication? No, absolutely not. Conceptual replication is essential for the theoretical advancement of psychological science (Dijksterhuis, 2014; Murayama et al., 2014; Stroebe & Strack, 2014), but only if dependability in findings via direct replication is first established (Cesario, 2014; Simons, 2014). Interestingly, in instances where one is able to conduct multiple studies for inclusion in a research report, one approach that can produce confidence in both dependability of findings and theoretical generalizability is to employ nested replications.

(ER cannot detect fraud)
A second advantage of direct replications is that they can protect against fraudulent findings (Schmidt, 2009), particularly when different research groups conduct direct replication studies of each other’s research. S&S (2014) make a compelling argument that direct replication is unlikely to prove useful in detection of fraudulent research. However, even if a fraudulent study remains unknown or undetected, its impact on the literature would be lessened when aggregated with nonfraudulent direct replication studies conducted by honest researchers.

***Does cleanliness influence moral judgments? Response effort moderates the effect of cleanliness priming on moral judgments.
Huang
(ER uninformative)
Indeed, behavioral priming effects in general have been the subject of increased scrutiny (see Cesario, 2014), and researchers have suggested different causes for failed replication, such as measurement and sampling errors (Stanley and Spence,2014), variation in subject populations (Cesario, 2014), discrepancy in operationalizations (S&S, 2014), and unidentified moderators (Dijksterhuis,2014).

UNDERSTANDING PRIMING EFFECTS IN SOCIAL PSYCHOLOGY: AN OVERVIEW AND INTEGRATION
Daniel C. Molden
(ER uninformative)
Therefore, some greater emphasis on direct replication in addition to conceptual replication is likely necessary to maximize what can be learned from further research on priming (but see Stroebe and Strack, 2014, for costs of overemphasizing direct replication as well).

On the automatic link between affect and tendencies to approach and avoid: Chen and Bargh (1999) revisited
Mark Rotteveel et al.
(no replication crisis)
Although opinions differ with regard to the extent of this “replication crisis” (e.g., Pashler and Harris, 2012; S&S, 2014), the scientific community seems to be shifting its focus more toward direct replication.

(ER uninformative)
Direct replications not only affect one’s confidence about the veracity of the phenomenon under study, but they also increase our knowledge about effect size (see also Simons, 2014; but see also S&S, 2014).

Single-Paper Meta-Analysis: Benefits for Study Summary, Theory Testing, and Replicability
McShane and Bockenholt
(ER impossible)
The purpose of meta-analysis is to synthesize a set of studies of a common phenomenon. This task is complicated in behavioral research by the fact that behavioral research studies can never be direct or exact replications of one another (Brandt et al. 2014; Fabrigar and Wegener 2016; Rosenthal 1991; S&S 2014; Tsang and Kwan 1999).

(ER impossible)
Further, because behavioral research studies can never be direct or exact replications of one another (Brandt et al. 2014; Fabrigar and Wegener 2016; Rosenthal 1991; S&S 2014; Tsang and Kwan 1999), our SPM methodology estimates and accounts for heterogeneity, which has been shown to be important in a wide variety of behavioral research settings (Hedges and Pigott 2001; Klein et al. 2014; Pigott 2012).

A Closer Look at Social Psychologists’ Silver Bullet: Inevitable and Evitable Side   Effects of the Experimental Approach
Herbert Bless and Axel M. Burger
(ER/CR Distinction)
Given the above perspective, it becomes obvious that in the long run, conceptual replications can provide very fruitful answers because they address the question of whether the initially observed effects are potentially caused by some perhaps unknown aspects of the experimental procedure (for a discussion of conceptual versus direct replications, see e.g., Stroebe & Strack, 2014; see also Brandt et al., 2014; Cesario, 2014; Lykken, 1968; Schwarz & Strack, 2014).  Whereas conceptual replications are adequate solutions for broadening the sample of situations (for examples, see Stroebe & Strack, 2014), the present perspective, in addition, emphasizes that it is important that the different conceptual replications do not share too much overlap in general aspects of the experiment (see also Schwartz, 2015, advocating for  conceptual replications)

Men in red: A reexamination of the red-attractiveness effect
Vera M. Hesslinger, Lisa Goldbach, & Claus-Christian Carbon
(ER impossible)
As Brandt et al. (2014) pointed out, a replication in psychological research will never be absolutely exact or direct (see also, Stroebe & Strack, 2014), which is, of course, also the case in the present research.

***On the challenges of drawing conclusions from p-values just below 0.05
Daniel Lakens
(no evidence about QRP)
In recent years, researchers have become more aware of how flexibility during the data-analysis can increase false positive results (e.g., Simmons, Nelson & Simonsohn, 2011). If the true Type 1 error rate is substantially inflated, for example because researchers analyze their data until a p-value smaller than 0.05 is observed, the robustness of scientific knowledge can substantially decrease. However, as Stroebe & Strack (2014, p. 60) have pointed out: ‘Thus far, however, no solid data exist on the prevalence of such research practices.’

***Does Merely Going Through the Same Moves Make for a ‘‘Direct’’ Replication? Concepts, Contexts, and Operationalizations
Norbert Schwarz and Fritz Strack
(Contextual Sensitivity)
In general, meaningful replications need to realize the psychological conditions of the original study. The easier option of merely running through technically identical procedures implies the assumption that psychological processes are context insensitive and independent of social, cultural, and historical differences (Cesario, 2014; Stroebe & Strack, 2014). Few social (let alone cross-cultural) psychologists would be willing to endorse this assumption with a straight face. If so, mere procedural equivalence is an insufficient criterion for assessing the quality of a replication.

The Replication Paradox: Combining Studies can Decrease Accuracy of Effect Size Estimates
(ER uninformative)
Michèle B. Nuijten, Marcel A. L. M. van Assen, Coosje L. S. Veldkamp, and Jelte M. Wicherts
Replications with nonsignificant results are easily dismissed with the argument that the replication might contain a confound that caused the null finding (Stroebe & Strack, 2014).

Retro-priming, priming, and double testing: psi and replication in a test-retest design
Rabeyron, T
(Mention)
Bem’s paper spawned numerous attempts to replicate it (see e.g., Galak et al., 2012; Bem et al., submitted) and reflections on the difficulty of direct replications in psychology (Ritchie et al., 2012). This aspect has been associated more generally with debates concerning the “decline effect” in science (Schooler, 2011) and a potential “replication crisis” (S&S, 2014) especially in the fields of psychology and medical sciences (De Winter and Happee, 2013).

Do p Values Lose Their Meaning in Exploratory Analyses? It Depends How You Define the Familywise Error Rate
Mark Rubin
(ER impossible)
Consequently, the Type I error rate remains constant if researchers simply repeat the same test over and over again using different samples that have been randomly drawn from the exact same population. However, this first situation is somewhat hypothetical and may even be regarded as impossible in the social sciences because populations of people change over time and location (e.g., Gergen, 1973; Iso-Ahola, 2017; Schneider, 2015; Serlin, 1987; Stroebe & Strack, 2014). Yesterday’s population of psychology undergraduate students from the University of Newcastle, Australia, will be a different population to today’s population of psychology undergraduate students from the University of Newcastle, Australia.

***Learning and the replicability of priming effects
Michael Ramscar
(ER uninformative)
In the limit, this means that in the absence of a means for objectively determining what the information that produces a priming effect is, and for determining that the same information is available to the population in a replication, all learned priming effects are scientifically unfalsifiable. (Which also means that in the absence of an account of what the relevant information is in a set of primes, and how it produces a specific effect, reports of a specific priming result — or failures to replicate it — are scientifically uninformative; see also [Stroebe & Strack, 2014.)

***Evaluating Psychological Research Requires More Than Attention to the N: A Comment on Simonsohn’s (2015) “Small Telescopes”
Norbert Schwarz and Gerald L. Clore
(CR test theory)
Simonsohn’s decision to equate a conceptual variable (mood) with its manipulation (weather) is compatible with the logic of clinical trials, but not with the logic of theory testing. In clinical trials, which have inspired much of the replicability debate and its statistical focus, the operationalization (e.g., 10 mg of a drug) is itself the variable of interest; in theory testing, any given operationalization is merely one, usually imperfect, way to realize the conceptual variable. For this reason, theory tests are more compelling when the results of different operationalizations converge (Stroebe & Strack, 2014), thus ensuring, in the case in point, that it is not “the weather” but indeed participants’ (sometimes weather-induced) mood that drives the observed effect.

Internal conceptual replications do not increase independent replication success
Kunert, R
(Contextual Sensitivity)
According to the unknown moderator account of independent replication failure, successful internal replications should correlate with independent replication success. This account suggests that replication failure is due to the fact that psychological phenomena are highly context-dependent, and replicating seemingly irrelevant contexts (i.e. unknown moderators) is rare (e.g., Barrett, 2015; DGPS, 2015; Fleming Crim, 2015; see also Stroebe & Strack, 2014; for a critique, see Simons, 2014). For example, some psychological phenomenon may unknowingly be dependent on time of day.

(Contextual Sensitivity greater in social psychology)
When the chances of unknown moderator influences are greater and replicability is achieved (internal, conceptual replications), then the same should be true when chances are smaller (independent, direct replications). Second, the unknown moderator account is usually invoked for social psychological effects (e.g. Cesario, 2014; Stroebe & Strack, 2014). However, the lack of influence of internal replications on independent replication success is not limited to social psychology. Even for cognitive psychology a similar pattern appears to hold.

On Klatzky and Creswell (2014): Saving Social Priming Effects But Losing Science as We Know It?
Barry Schwartz
(ER uninformative)
The recent controversy over what counts as “replication” illustrates the power of this presumption. Does “conceptual replication” count? In one respect, conceptual replication is a real advance, as conceptual replication extends the generality of the phenomena that were initially discovered. But what if it fails? Is it because the phenomena are unreliable, because the conceptual equivalency that justified the new study was logically flawed, or because the conceptual replication has permitted the intrusion of extraneous variables that obscure the original phenomenon? This ambiguity has led some to argue that there is no substitute for strict replication (see Pashler & Harris, 2012; Simons, 2014, and Stroebe & Strack, 2014, for recent manifestations of this controversy). A significant reason for this view, however, is less a critique of the logic of conceptual replication than it is a comment on the sociology (or politics, or economics) of science. As Pashler and Harris (2012) point out, publication bias virtually guarantees that successful conceptual replications will be published whereas failed conceptual replications will live out their lives in a file drawer.  I think Pashler and Harris’ surmise is probably correct, but it is not an argument for strict replication so much as it is an argument for publication of failed conceptual replication.

Commentary and Rejoinder on Lynott et al. (2014)
Lawrence E. Williams
(CR test theory)
On the basis of their investigations, Lynott and colleagues (2014) conclude ‘‘there is no evidence that brief exposure to warm therapeutic packs induces greater prosocial responding than exposure to cold therapeutic packs’’ (p. 219). This conclusion, however, does not take into account other related data speaking to the connection between physical warmth and prosociality. There is a fuller body of evidence to be considered, in which both direct and conceptual replications are instructive. The former are useful if researchers particularly care about the validity of a specific phenomenon; the latter are useful if researchers particularly care about theory testing (Stroebe & Strack, 2014).

The State of Social and Personality Science: Rotten to the Core, Not So Bad, Getting Better, or Getting Worse?
(no replication crisis)
Motyl et al. (2017) “The claim of a replicability crisis is greatly exaggerated.” Wolfgang Stroebe and Fritz Strack, 2014

Promise, peril, and perspective: Addressing concerns about reproducibility in social–personality psychology
Harry T. Reis, Karisa Y. Lee
(ER impossible)
Much of the current debate, however, is focused narrowly on direct or exact replications—whether the findings of a given study, carried out in a particular way with certain specific operations, would be repeated. Although exact replications are surely desirable, the papers by Fabrigar and by Crandall and Sherman remind us that in an absolute sense they are fundamentally impossible in social–personality psychology (see also S&S, 2014).

Show me the money
(Contextual Sensitivity)
Of course, it is possible that additional factors, which varied or could have varied among our studies and previously published studies (e.g., participants’ attitudes toward money) or among the online studies and laboratory study in this article (e.g., participants’ level of distraction), might account for these apparent inconsistencies. We did not aim to conduct a direct replication of any specific past study, and therefore we encourage special care when using our findings to evaluate existing ones (Doyen, Klein, Simons, & Cleeremans, 2014; Stroebe & Strack, 2014).

***From Data to Truth in Psychological Science. A Personal Perspective.
Strack
(ER uninformative)
In their introduction to the 2016 volume of the Annual Review of Psychology, Susan Fiske, Dan Schacter, and Shelley Taylor point out that a replication failure is not a scientific problem but an opportunity to find limiting conditions and contextual effects. To allow non-replications to regain this constructive role, they must come with conclusions that enter and stimulate a critical debate. It is even better if replication studies are endowed with a hypothesis that relates to the state of the scientific discourse. To show that an effect occurs only under one but not under another condition is more informative than simply demonstrating noneffects (S&S, 2014). But this may require expertise and effort.

 

How Replicable are Focal Hypothesis Tests in the Journal Psychological Science?

Over the past five years, psychological science has been in a crisis of confidence.  For decades, psychologists have assumed that published significant results provide strong evidence for theoretically derived predictions, especially when authors presented multiple studies with internal replications within a single article (Schimmack, 2012). However, even multiple significant results provide little empirical evidence, when journals only publish significant results (Sterling, 1959; Sterling et al., 1995).  When published results are selected for significance, statistical significance loses its ability to distinguish replicable effects from results that are difficult to replicate or results that are type-I errors (i.e., the theoretical prediction was false).

The crisis of confidence led to several initiatives to conduct independent replications. The most informative replication initiative was conducted by the Open Science Collaborative (Science, 2015).  It replicated close to 100 significant results published in three high-ranked psychology journals.  Only 36% of the replication studies replicated a statistically significant result.  The replication success rate varied by journal.  The journal “Psychological Science” achieved a success rate of 42%.

The low success rate raises concerns about the empirical foundations of psychology as a science.  Without further information, a success rate of 42% implies that it is unclear which published results provide credible evidence for a theory and which findings may not replicate.  It is impossible to conduct actual replication studies for all published studies.  Thus, it is highly desirable to identify replicable findings in the existing literature.

One solution is to estimate replicability for sets of studies based on the published test statistics (e.g., F-statistic, t-values, etc.).  Schimmack and Brunner (2016) developed a statistical method, Powergraphs, that estimates the average replicability of a set of significant results.  This method has been used to estimate replicability of psychology journals using automatic extraction of test statistics (2016 Replicability Rankings, Schimmack, 2017).  The results for Psychological Science produced estimates in the range from 55% to 63% for the years 2010-2016 with an average of 59%.   This is notably higher than the success rate for the actual replication studies, which only produced 42% successful replications.

There are two explanations for this discrepancy.  First, actual replication studies are not exact replication studies and differences between the original and the replication studies may explain some replication failures.  Second, the automatic extraction method may overestimate replicability because it may include non-focal statistical tests. For example, significance tests of manipulation checks can be highly replicable, but do not speak to the replicability of theoretically important predictions.

To address the concern about automatic extraction of test statistics, I estimated replicability of focal hypothesis tests in Psychological Science with hand-coded, focal hypothesis tests.  I used three independent data sets.

Study 1

For Study 1, I hand-coded focal hypothesis tests of all studies in the 2008 Psychological Science articles that were used for the OSC reproducibility project (Science, 2015).

OSC.PS

The powergraphs show the well-known effect of publication bias in that most published focal hypothesis tests report a significant result (p < .05, two-tailed, z > 1.96) or at least a marginally significant result (p < .10, two-tailed or p < .05, one-tailed, z > 1.65). Powergraphs estimate the average power of studies with significant results on the basis of the density distribution of significant z-scores.  Average power is an estimate of replicabilty for a set of exact replication studies.  The left graph uses all significant results. The right graph uses only z-scores greater than 2.4 because questionable research practices may produce many just-significant results and lead to biased estimates of replicability. However, both estimation methods produce similar estimates of replicability (57% & 61%).  Given the small number of statistics the 95%CI is relatively wide (left graph: 44% to 73%).  These results are compatible with the low actual success rate for actual replication studies (42%) and the estimate based on automated extraction (59%).

Study 2

The second dataset was provided by Motyl et al. (JPSP, in press), who coded a large number of articles from social psychology journals and psychological science. Importantly, they coded a representative sample of Psychological Science studies from the years 2003, 2004, 2013, and 2014. That is, they did not only code social psychology articles published in Psychological Science.  The dataset included 281 test statistics from Psychological Science.

PS.Motyl

The powergraph looks similar to the powergraph in Study 1.  More important, the replicability estimates are also similar (57% & 52%).  The 95%CI for Study 1 (44% to 73%) and Study 2 (left graph: 49% to 65%) overlap considerably.  Thus, two independent coding schemes and different sets of studies (2008 vs. 2003-2004/2013/2014) produce very similar results.

Study 3

Study 3 was carried out in collaboration with Sivaani Sivaselvachandran, who hand-coded articles from Psychological Science published in 2016.  The replicability rankings showed a slight positive trend based on automatically extracted test statistics.  The goal of this study was to examine whether hand-coding would also show an increase in replicability.  An increase was expected based on an editorial by D. Stephen Linday, incoming editor in 2015, who aimed to increase replicability of results published in Psychological Science by introducing badges for open data and preregistered hypotheses. However, the results failed to show a notable increase in average replicability.

PS.2016

The replicability estimate was similar to those in the first two studies (59% & 59%).  The 95%CI ranged from 49% to 70%. These wide confidence intervals make it difficult to notice small improvements, but the histogram shows that just significant results (z = 2 to 2.2) are still the most prevalent results reported in Psychological Science and that non-significant results that are to be expected are not reported.

Combined Analysis 

Given the similar results in all three studies, it made sense to pool the data to obtain the most precise estimate of replicability of results published in Psychological Science. With 479 significant test statistics, replicability was estimated at 58% with a 95%CI ranging from 51% to 64%.  This result is in line with the estimated based on automated extraction of test statistics (59%).  The reason for the close match between hand-coded and automated results could be that Psych Science publishes short articles and authors may report mostly focal results because space does not allow for extensive reporting of other statistics.  The hand-coded data confirm that replicabilty in Psychological Science is likely to be above 50%.

PS.combined

It is important to realize that the 58% estimate is an average.  Powergraphs also show average replicability for segments of z-scores. Here we see that replicabilty for just-significant results (z < 2.5 ~ p > .01) is only 35%. Even for z-score between 2.5 and 3.0 (~ p > .001) is only 47%.  Once z-scores are greater than 3, average replicabilty is above 50% and with z-scores greater than 4, replicability is greater than 80%.  For any single study, p-values can vary greatly due to sampling error, but in general a published result with a p-value < .001 is much more likely to replicate than a p-value > .01 (see also OSC, Science, 2015).

Conclusion

This blog-post used hand-coding of test-statistics published in Psychological Science, the flagship journal of the Association for Psychological Science, to estimate replicabilty of published results.  Three dataset produced convergent evidence that the average replicabilty of exact replication studies is 58% +/- 7%.  This result is consistent with estimates based on automatic extraction of test statistics.  It is considerably higher than the success rate of actual replication studies in the OSC reproducibility project (42%). One possible reason for this discrepancy is that actual replication studies are never exact replication studies, which makes it more difficult to obtain statistical significance if the original studies are selected for significance. For example, the original study may have had an outlier in the experimental group that helped to produce a significant result. Not removing this outlier is not considered a questionable research practice, but an exact replication study will not reproduce the same outlier and may fail to reproduce a just-significant result.  More broadly, any deviation from the assumptions underlying the computation of test statistics will increase the bias that is introduced by selecting significant results.  Thus, the 58% estimate is an optimistic estimate of the maximum replicability under ideal conditions.

At the same time, it is important to point out that 58% replicability for Psychological Science does not mean psychological science is rotten to the core (Motyl et al., in press) or that most reported results are false (Ioannidis, 2005).  Even results that did not replicate in actual replication studies are not necessarily false positive results.  It is possible that more powerful studies would produce a significant result, but with a smaller effect size estimate.

Hopefully, these analyses will spur further efforts to increase replicability of published results in Psychological Science and in other journals.  We are already near the middle of 2017 and can look forward to the 2017 results.

 

 

 

Bayesian Meta-Analysis: The Wrong Way and The Right Way

Carlsson, R., Schimmack, U., Williams, D.R., & Bürkner, P. C. (in press). Bayesian Evidence Synthesis is no substitute for meta-analysis: a re-analysis of Scheibehenne, Jamil and Wagenmakers (2016). Psychological Science.

In short, we show that the reported Bayes-Factor of 36 in the original article is inflated by pooling across a heterogeneous set of studies, using a one-sided prior, and assuming a fixed effect size.  We present an alternative Bayesian multi-level approach that avoids the pitfalls of Bayesian Evidence Synthesis, and show that the original set of studies produced at best weak evidence for an effect of social norms on reusing of towels.

Replicability Ranking of Psychology Departments

Evaluations of individual researchers, departments, and universities are common and arguably necessary as science is becoming bigger. Existing rankings are based to a large extent on peer-evaluations. A university is ranked highly if peers at other universities perceive it to produce a steady stream of high-quality research. At present the most widely used objective measures rely on the quantity of research output and on the number of citations. These quantitative indicators of research quality work are also heavily influenced by peers because peer-review controls what gets published, especially in journals with high rejection rates, and peers decide what research they cite in their own work. The social mechanisms that regulate peer-approval are unavoidable in a collective enterprise like science that does not have a simple objective measure of quality (e.g., customer satisfaction ratings, or accident rates of cars). Unfortunately, it is well known that social judgments are subject to many biases due to conformity pressure, self-serving biases, confirmation bias, motivated biases, etc. Therefore, it is desirable to complement peer-evaluations with objective indicators of research quality.

Some aspects of research quality are easier to measure than others. Replicability rankings focus on one aspect of research quality that can be measured objectively, namely the replicability of a published significant result. In many scientific disciplines such as psychology, a successful study reports a statistically significant result. A statistically significant result is used to minimize the risk of publishing evidence for an effect that does not exist (or even goes in the opposite direction). For example, a psychological study that shows effectiveness of a treatment for depression would have to show that the effect in the study reveals a real effect that can be observed in other studies and in real patients if the treatment is used for the treatment of depression.

In a science that produces thousands of results a year, it is inevitable that some of the published results are fluke findings (even Toyota’s break down sometimes). To minimize the risk of false results entering the literature, psychology like many other sciences, adopted a 5% error rate. By using a 5% as the criterion, psychologists ensured that no more than 5% of results are fluke findings. With thousands of results published in each year, this still means that more than 50 false results enter the literature each year. However, this is acceptable because a single study does not have immediate consequences. Only if these results are replicated in other studies, findings become the foundation of theories and may influence practical decisions in therapy or in other applications of psychological findings (at work, in schools, or in policy). Thus, to outside observers it may appear safe to trust published results in psychology and to report about these findings in newspaper articles, popular books, or textbooks.

Unfortunately, it would be a mistake to interpret a significant result in a psychology journal as evidence that the result is probably true.  The reason is that the published success rate in journals has nothing to do with the actual success rate in psychological laboratories. All insiders know that it is common practice to report only results that support a researcher’s theory. While outsiders may think of scientists as neutral observers (judges), insiders play the game of lobbyist, advertisers, and self-promoters. The game is to advance one’s theory, publish more than others, get more citations than others, and win more grant money than others. Honest reporting of failed studies does not advance this agenda. As a result, the fact that psychological studies report nearly exclusively success stories (Sterling, 1995; Sterling et al., 1995) tells outside observers nothing about the replicability of a published finding and the true rate of fluke findings could be 100%.

This problem has been known for over 50 years (Cohen, 1962; Sterling, 1959). So it would be wrong to call the selective reporting of successful studies an acute crisis. However, what changed is that some psychologists have started to criticize the widely accepted practice of selective reporting of successful studies (Asendorpf et al., 2012; Francis, 2012; Simonsohn et al., 2011; Schimmack, 2012; Wagenmakers et al., 2011). Over the past five years, psychologists, particularly social psychologists, have been engaged in heated arguments over the so-called “replication crisis.”

One group argues that selective publishing of successful studies occurred, but without real consequences on the trustworthiness of published results. The other group argues that published results cannot be trusted unless they have been successfully replicated. The problem is that neither group has objective information about the replicability of published results.  That is, there is no reliable estimate of the percentage of studies that would produce a significant result again, if a representative sample of significant results published in psychology journals were replicated.

Evidently, it is not possible to conduct exact replication studies of all studies that have been published in the past 50 years. Fortunately, it is not necessary to conduct exact replication studies to obtain an objective estimate of replicability. The reason is that replicability of exact replication studies is a function of the statistical power of studies (Sterling et al., 1995). Without selective reporting of results, a 95% success rate is an estimate of the statistical power of the studies that achieved this success rate. Vice versa, a set of studies with average power of 50% is expected to produce a success rate of 50% (Sterling, et al., 1995).

Although selection bias renders success rates uninformative, the actual statistical results provide valuable information that can be used to estimate the unbiased statistical power of published results. Although selection bias inflates effect sizes and power, Brunner and Schimmack (forcecoming) developed and validated a method that can correct for selection bias. This method makes it possible to estimate the replicability of published significant results on the basis of the original reported results. This statistical method was used to estimate the replicabilty of research published by psychology departments in the years from 2010 to 2015 (see Methodology for details).

The averages for the 2010-2012 period (M = 59) and the 2013-2015 period (M = 61) show only a small difference, indicating that psychologists have not changed their research practices in accordance with recommendations to improve replicability in 2011  (Simonsohn et al., 2011). For most of the departments the confidence intervals for the two periods overlap (see attached powergraphs). Thus, the more reliable average across all years is used for the rankings, but the information for the two time periods is presented as well.

There are no obvious predictors of variability across departments. Private universities are at the top (#1, #2, #8), the middle (#24, #26), and at the bottom (#44, #47). European universities can also be found at the top (#4, #5), middle (#25) and bottom (#46, #51). So are Canadian universities (#9, #15, #16, #18, #19, #50).

There is no consensus on an optimal number of replicability.  Cohen recommended that researchers should plan studies with 80% power to detect real effects. If 50% of studies tested real effects with 80% power and the other 50% tested a null-hypothesis (no effect = 2.5% probability to replicate a false result again), the estimated power for significant results would be 78%. The effect on average power is so small because most of the false predictions produce a non-significant result. As a result, only a few studies with low replication probability dilute the average power estimate. Thus, a value greater than 70 can be considered broadly in accordance with Cohen’s recommendations.

It is important to point out that the estimates are very optimistic estimates of the success rate in actual replications of theoretically important effects. For a representative set of 100 studies (OSC, Science, 2015), Brunner and Schimmack’s statistical approach predicted a success rate of 54%, but the success rate in actual replication studies was only 37%. One reason for this discrepancy could be that the statistical approach assumes that the replication studies are exact, but actual replications always differ in some ways from the original studies, and this uncontrollable variability in experimental conditions posses another challenge for replicability of psychological results.  Before further validation research has been completed, the estimates can only be used as a rough estimate of replicability. However, the absolute accuracy of estimates is not relevant for the relative comparison of psychology departments.

And now, without further ado, the first objective rankings of 51 psychology departments based on the replicability of published significant results. More departments will be added to these rankings as the results become available.

Rank University 2010-2015 2010-2012 2013-2015
1 U Penn 72 69 75
2 Cornell U 70 67 72
3 Purdue U 69 69 69
4 Tilburg U 69 71 66
5 Humboldt U Berlin 67 68 66
6 Carnegie Mellon 67 67 67
7 Princeton U 66 65 67
8 York U 66 63 68
9 Brown U 66 71 60
10 U Geneva 66 71 60
11 Northwestern U 65 66 63
12 U Cambridge 65 66 63
13 U Washington 65 70 59
14 Carleton U 65 68 61
15 Queen’s U 63 57 69
16 U Texas – Austin 63 63 63
17 U Toronto 63 65 61
18 McGill U 63 72 54
19 U Virginia 63 61 64
20 U Queensland 63 66 59
21 Vanderbilt U 63 61 64
22 Michigan State U 62 57 67
23 Harvard U 62 64 60
24 U Amsterdam 62 63 60
25 Stanford U 62 65 58
26 UC Davis 62 57 66
27 UCLA 61 61 61
28 U Michigan 61 63 59
29 Ghent U 61 58 63
30 U Waterloo 61 65 56
31 U Kentucky 59 58 60
32 Penn State U 59 63 55
33 Radboud U 59 60 57
34 U Western Ontario 58 66 50
35 U North Carolina Chapel Hill 58 58 58
36 Boston University 58 66 50
37 U Mass Amherst 58 52 64
38 U British Columbia 57 57 57
39 The University of Hong Kong 57 57 57
40 Arizona State U 57 57 57
41 U Missouri 57 55 59
42 Florida State U 56 63 49
43 New York U 55 55 54
44 Dartmouth College 55 68 41
45 U Heidelberg 54 48 60
46 Yale U 54 54 54
47 Ohio State U 53 58 47
48 Wake Forest U 51 53 49
49 Dalhousie U 50 45 55
50 U Oslo 49 54 44
51 U Kansas 45 45 44

 

“Do Studies of Statistical Power Have an Effect on the Power of Studies?” by Peter Sedlmeier and Gerg Giegerenzer

The article with the witty title “Do Studies of Statistical Power Have an Effect on the Power of Studies?” builds on Cohen’s (1962) seminal power analysis of psychological research.

The main point of the article can be summarized in one word: No. Statistical power has not increased after Cohen published his finding that statistical power is low.

One important contribution of the article was a meta-analysis of power analyses that applied Cohen’s method to a variety of different journals. The table below shows that power estimates vary by journal assuming that the effect size was medium according to Cohen’s criteria of small, medium, and large effect sizes. The studies are sorted by power estimates from the highest to the lowest value, which provides a power ranking of journals based on Cohen’s method. I also included the results of Sedlmeier and Giegerenzer’s power analysis of the 1984 volume of the Journal of Abnormal Psychology (the Journal of Social and Abnormal Psychology was split into Journal of Abnormal Psychology and Journal of Personality and Social Psychology). I used the mean power (50%) rather than median power (44%) because the mean power is consistent with the predicted success rate in the limit. In contrast, the median will underestimate the success rate in a set of studies with heterogeneous effect sizes.

JOURNAL TITLE YEAR Power%
Journal of Marketing Research 1981 89
American Sociological Review 1974 84
Journalism Quarterly, The Journal of Broadcasting 1976 76
American Journal of Educational Psychology 1972 72
Journal of Research in Teaching 1972 71
Journal of Applied Psychology 1976 67
Journal of Communication 1973 56
The Research Quarterly 1972 52
Journal of Abnormal Psychology 1984 50
Journal of Abnormal and Social Psychology 1962 48
American Speech and Hearing Research & Journal of Communication Disorders 1975 44
Counseler Education and Supervision 1973 37

 

The table shows that there is tremendous variability in power estimates for different journals ranging from as high as 89% (9 out of 10 studies will produce a significant result when an effect is present) to the lowest estimate of  37% power (only 1 out of 3 studies will produce a significant result when an effect is present).

The table also shows that the Journal of Abnormal and Social Psychology and its successor the Journal of Abnormal Psychology yielded nearly identical power estimates. This finding is the key finding that provides empirical support for the claim that power in the Journal of Abnormal Psychology has not increased over time.

The average power estimate for all journals in the table is 62% (median 61%).  The list of journals is not a representative set of journals and few journals are core psychology journals. Thus, the average power may be different if a representative set of journals had been used.

The average for the three core psychology journals (JASP & JAbnPsy,  JAP, AJEduPsy) is 67% (median = 63%) is slightly higher. The latter estimate is likely to be closer to the typical power in psychology in general rather than the prominently featured estimates based on the Journal of Abnormal Psychology. Power could be lower in this journal because it is more difficult to recruit patients with a specific disorder than participants from undergraduate classes. However, only more rigorous studies of power for a broader range of journals and more years can provide more conclusive answers about the typical power of a single statistical test in a psychology journal.

The article also contains some important theoretical discussions about the importance of power in psychological research. One important issue concerns the treatment of multiple comparisons. For example, a multi-factorial design produces an exponential number of statistical comparisons. With two conditions, there is only one comparison. With three conditions, there are three comparisons (C1 vs. C2, C1 vs. C3, and C2 vs. C3). With 5 conditions, there are 10 comparisons. Standard statistical methods often correct for these multiple comparisons. One consequence of this correction for multiple comparisons is that the power of each statistical test decreases. An effect that would be significant in a simple comparison of two conditions would not be significant if this test is part of a series of tests.

Sedlmeier and Giegerenzer used the standard criterion of p < .05 (two-tailed) for their main power analysis and for the comparison with Cohen’s results. However, many articles presented results using a more stringent criterion of significance. If the criterion used by authors would have been used for the power analysis, power decreased further. About 50% of all articles used an adjusted criterion value and if the adjusted criterion value was used power was only 37%.

Sedlmeier and Giegerenzer also found another remarkable difference between articles in 1960 and in 1984. Most articles in 1960 reported the results of a single study. In 1984 many articles reported results from two or more studies. Sedlmeier and Giegerenzer do not discuss the statistical implications of this change in publication practices. Schimmack (2012) introduced the concept of total power to highlight the problem of publishing articles that contain multiple studies with modest power. If studies are used to provide empirical support for an effect, studies have to show a significant effect. For example, Study 1 shows an effect with female participants. Study 2 examines whether the effect can also be demonstrated with male participants. If Study 2 produces a non-significant result, it is not clear how this finding should be interpreted. It may show that the effect does not exist for men. It may show that the first result was just a fluke finding due to sampling error. Or it may show that the effect exists equally for men and women but studies had only 50% power to produce a significant result. In this case, it is expected that one study will produce a significant result and one will produce a non-significant result, but in the long-run significant results are equally likely with male or female participants. Given the difficulty of interpreting a non-significant result, it would be important to conduct a more powerful study that examines gender differences in a more powerful study with more female and male participants. However, this is not what researchers do. Rather, multiple study articles contain only the studies that produced significant results. The rate of successful studies in psychology journals is over 90% (Sterling et al., 1995). However, this outcome is extremely likely in multiple studies where studies have only 50% power to get a significant result in a single attempt. For each additional attempt, the probability to obtain only significant results decreases exponentially (1 Study, 50%, 2 Studies 25%, 3 Studies 12.5%, 4 Studies 6.75%).

The fact that researchers only publish studies that worked is well-known in the research community. Many researchers believe that this is an acceptable scientific practice. However, consumers of scientific research may have a different opinion about this practice. Publishing only studies that produced the desired outcome is akin to a fund manager that only publishes the return rate of funds that gained money and excludes funds with losses. Would you trust this manager to take care of your retirement? It is also akin to a gambler that only remembers winnings. Would you marry a gambler who believes that gambling is ok because you can earn money that way?

I personally do not trust obviously biased information. So, when researchers present 5 studies with significant results, I wonder whether they really had the statistical power to produce these results or whether they simply did not publish results that failed to confirm their claims. To answer this question it is essential to estimate the actual power of individual studies to produce significant results; that is, it is necessary to estimate the typical power in this field, of this researcher, or in the journal that published the results.

In conclusion, Sedlmeier and Gigerenzer made an important contribution to the literature by providing the first power-ranking of scientific journals and the first temporal analyses of time trends in power. Although they probably hoped that their scientific study of power would lead to an increase in statistical power, the general consensus is that their article failed to change scientific practices in psychology. In fact, some journals required more and more studies as evidence for an effect (some articles contain 9 studies) without any indication that researchers increased power to ensure that their studies could actually provide significant results for their hypotheses. Moreover, the topic of statistical power remained neglected in the training of future psychologists.

I recommend Sedlmeier and Gigerenzer’s article as essential reading for anybody interested in improving the credibility of psychology as a rigorous empirical science.

As always, comments (positive or negative) are always welcome.

Distinguishing Questionable Research Practices from Publication Bias

It is well-known that scientific journals favor statistically significant results (Sterling, 1959). This phenomenon is known as publication bias. Publication bias can be easily detected by comparing the observed statistical power of studies with the success rate in journals. Success rates of 90% or more would only be expected if most theoretical predictions are true and empirical studies have over 90% statistical power to produce significant results. Estimates of statistical power range from 20% to 50% (Button et al., 2015, Cohen, 1962). It follows that for every published significant result an unknown number of non-significant results has occurred that remained unpublished. These results linger in researchers proverbial file-drawer or more literally in unpublished data sets on researchers’ computers.

The selection of significant results also creates an incentive for researchers to produce significant results. In rare cases, researchers simply fabricate data to produce significant results. However, scientific fraud is rare. A more serious threat to the integrity of science is the use of questionable research practices. Questionable research practices are all research activities that create a systematic bias in empirical results. Although systematic bias can produce too many or too few significant results, the incentive to publish significant results suggests that questionable research practices are typically used to produce significant results.

In sum, publication bias and questionable research practices contribute to an inflated success rate in scientific journals. So far, it has been difficult to examine the prevalence of questionable research practices in science. One reason is that publication bias and questionable research practices are conceptually overlapping. For example, a research article may report the results of a 2 x 2 x 2 ANOVA or a regression analysis with 5 predictor variables. The article may only report the significant results and omit detailed reporting of the non-significant results. For example, researchers may state that none of the gender effects were significant and not report the results for main effects or interaction with gender. I classify these cases as publication bias because each result tests a different hypothesis., even if the statistical tests are not independent.

Questionable research practices are practices that change the probability of obtaining a specific significant result. An example would be a study with multiple outcome measures that would support the same theoretical hypothesis. For example, a clinical trial of an anti-depressant might include several depression measures. In this case, a researcher can increase the chances of a significant result by conducting tests for each measure. Other questionable research practices would be optional stopping once a significant result is obtained, selective deletion of cases based on the results after deletion. A common consequence of these questionable practices is that they will produce results that meet the significance criterion, but deviate from the distribution that is expected simply on the basis of random sampling error.

A number of articles have tried to examine the prevalence of questionable research practices by comparing the frequency of p-values above and below the typical criterion of statistical significance, namely a p-value less than .05. The logic is that random error would produce a nearly equal amount of p-values just above .05 (e.g., p = .06) and below .05 (e.g., p = .04). According to this logic, questionable research practices are present, if there are more p-values just below the criterion than p-values just above the criterion (Masicampo & Lalande, 2012).

Daniel Lakens has pointed out some problems with this approach. The most crucial problem is that publication bias alone is sufficient to predict a lower frequency of p-values below the significance criterion. After all, these p-values imply a non-significant result and non-significant results are subject to publication bias. The only reason why p-values of .06 are reported with higher frequency than p-values of .11 is that p-values between .05 and .10 are sometimes reported as marginally significant evidence for a hypothesis. Another problem is that many p-values of .04 are not reported as p = .04, but are reported as p < .05. Thus, the distribution of p-values close to the criterion value provides unreliable information about the prevalence of questionable research practices.

In this blog post, I introduce an alternative approach to the detection of questionable research practices that produce just significant results. Questionable research practices and publication bias have different effects on the distribution of p-values (or corresponding measures of strength of evidence). Whereas publication bias will produce a distribution that is consistent with the average power of studies, questionable research practice will produce an abnormal distribution with a peak just below the significance criterion. In other words, questionable research practices produce a distribution with too few non-significant results and too few highly significant results.

I illustrate this test of questionable research practices with post-hoc-power analysis of three journals. One journal shows neither signs of publication bias, nor significant signs of questionable research practices. The second journal shows clear evidence of publication bias, but no evidence of questionable research practices. The third journal illustrates the influence of publication bias and questionable research practices.

Example 1: A Relatively Unbiased Z-Curve

The first example is based on results published during the years 2010-2014 in the Journal of Experimental Psychology: Learning, Memory, and Cognition. A text-mining program searched all articles for publications of F-tests, t-tests, correlation coefficients, regression coefficients, odds-ratios, confidence intervals, and z-tests. Due to the inconsistent and imprecise reporting of p-values (p = .02 or p < .05), p-values were not used. All statistical tests were converted into absolute z-scores.

The program found 14,800 tests. 8,423 tests were in the critical interval between z = 2 and z = 6 that is used for estimation of 4 non-centrality parameters and 4 weights that are used to model the distribution of z-values between 2 and 6 and to estimate the distribution in the range from 0 to 2. Z-values greater than 6 are not used because they correspond to Power close to 1. 11% of all tests fall into this region of z-scores that are not shown.

PHP-Curve JEP-LMCThe histogram and the blue density distribution show the observed data. The green curve shows the predicted distribution based on the post-hoc power analysis. Post-hoc power analysis suggests that the average power of significant results is 67%. Power for all statistical tests is estimated to be 58% (including 11% of z-scores greater than 6, power is .58*.89 + .11 = 63%). More important is the predicted distribution of z-scores. The predicted distribution on the left side of the criterion value matches the observed distribution rather well. This shows that there are not a lot of missing non-significant results. In other words, there does not appear to be a file-drawer of studies with non-significant results. There is also only a very small blip in the observed data just at the level of statistical significance. The close match between the observed and predicted distributions suggests that results in this journal are relatively free of systematic bias due to publication bias or questionable research practices.

Example 2: A Z-Curve with Publication Bias

The second example is based on results published in the Attitudes & Social Cognition Section of the Journal of Personality and Social Psychology. The text-mining program retrieved 5,919 tests from articles published between 2010 and 2014. 3,584 tests provided z-scores in the range from 2 to 6 that is being used for model fitting.

PHP-Curve JPSP-ASC

The average power of significant results in JPSP-ASC is 55%. This is significantly less than the average power in JEP-LMC, which was used for the first example. The estimated power for all statistical tests, including those in the estimated file drawer, is 35%. More important is the estimated distribution of z-values. On the right side of the significance criterion the estimated curve shows relatively close fit to the observed distribution. This finding shows that random sampling error alone is sufficient to explain the observed distribution. However, on the left side of the distribution, the observed z-scores drop off steeply. This drop is consistent with the effect of publication bias that researchers do not report all non-significant results. There is only a slight hint that questionable research practices are also present because observed z-scores just above the criterion value are a bit more frequent than the model predicts. However, this discrepancy is not conclusive because the model could increase the file drawer, which would produce a steeper slope. The most important characteristic of this z-curve is the steep cliff on the left side of the criterion value and the gentle slope on the right side of the criterion value.

Example 3: A Z-Curve with Questionable Research Practices.

Example 3 uses results published in the journal Aggressive Behavior during the years 2010 to 2014. The text mining program found 1,429 results and 863 z-scores in the range from 2 to 6 that were used for the post-hoc-power analysis.

PHP-Curve for AggressiveBeh 2010-14

 

The average power for significant results in the range from 2 to 6 is 73%, which is similar to the power estimate in the first example. The power estimate that includes non-significant results is 68%. The power estimate is similar because there is no evidence of a file drawer with many underpowered studies. In fact, there are more observed non-significant results than predicted non-significant results, especially for z-scores close to zero. This outcome shows some problems of estimating the frequency of non-significant results based on the distribution of significant results. More important, the graph shows a cluster of z-scores just above and below the significance criterion. The step cliff to the left of the criterion might suggest publication bias, but the whole distribution does not show evidence of publication bias. Moreover, the steep cliff on the right side of the cluster cannot be explained with publication bias. Only questionable research practices can produce this cliff because publication bias relies on random sampling error which leads to a gentle slope of z-scores as shown in the second example.

Prevalence of Questionable Research Practices

The examples suggest that the distribution of z-scores can be used to distinguish publication bias and questionable research practices. Based on this approach, the prevalence of questionable research practices would be rare. The journal Aggressive Behavior is exceptional. Most journals show a pattern similar to Example 2, with varying sizes of the file drawer. However, this does not mean that questionable research practices are rare because it is most likely that the pattern observed in Example 2 is a combination of questionable research practices and publication bias. As shown in Example 2, the typical power of statistical tests that produce a significant result is about 60%. However, researchers do not know which experiments will produce significant results. Slight modifications in experimental procedures, so-called hidden moderators, can easily change an experiment with 60% power into an experiment with 30% power. Thus, the probability of obtaining a significant result in a replication study is less than the nominal power of 60% that is implied by post-hoc-power analysis. With only 30% to 60% power, researchers will frequently encounter results that fail to produce an expected significant result. In this case, researchers have two choices to avoid reporting a non-significant result. They can put the study in the file-drawer or they can try to salvage the study with the help of questionable research practices. It is likely that researchers will do both and that the course of action depends on the results. If the data show a trend in the right direction, questionable research practices seem an attractive alternative. If the data show a trend in the opposite direction, it is more likely that the study will be terminated and the results remain unreported.

Simons et al. (2011) conducted some simulation studies and found that even extreme use of multiple questionable research practices (p-hacking) will produce a significant result in at most 60% of cases, when the null-hypothesis is true. If such extreme use of questionable research practices were widespread, z-curve would produce corrected power estimates well-below 50%. There is no evidence that extreme use of questionable research practices is prevalent. In contrast, there is strong evidence that researchers conduct many more studies than they actually report and that many of these studies have a low probability of success.

Implications of File-Drawers for Science

First, it is clear that researchers could be more effective if they would use existing resources more effectively. An fMRI study with 20 participants costs about $10,000. Conducting a study that costs $10,000 that has only a 50% probability of producing a significant result is wasteful and should not be funded by taxpayers. Just publishing the non-significant result does not fix this problem because a non-significant result in a study with 50% power is inconclusive. Even if the predicted effect exists, one would expect a non-significant result in ever second study.   Instead of wasting $10,000 on studies with 50% power, researchers should invest $20,000 in studies with higher power (unfortunately, power does not increase proportional to resources). With the same research budget, more money would contribute to results that are being published. Thus, without spending more money, science could progress faster.

Second, higher powered studies make non-significant results more relevant. If a study had 80% power, there is only a 20% chance to get a non-significant result if an effect is present. If a study had 95% power, the chance of a non-significant result would be just as low as the chance of a false positive result. In this case, it is noteworthy that a theoretical prediction was not confirmed. In a set of high-powered studies, a post-hoc power analysis would show a bimodal distribution with clusters of z-scores around 0 for true null-hypothesis and a cluster of z-scores of 3 or higher for clear effects. Type-I and Type-II errors would be rare.

Third, Example 3 shows that the use of questionable research practices becomes detectable in the absence of a file drawer and that it would be harder to publish results that were obtained with questionable research practices.

Finally, the ability to estimate the size of file-drawers may encourage researchers to plan studies more carefully and to invest more resources into studies to keep their file drawers small because a large file-drawer may harm reputation or decrease funding.

In conclusion, post-hoc power analysis of large sets of data can be used to estimate the size of the file drawer based on the distribution of z-scores on the right side of a significance criterion. As file-drawers harm science, this tool can be used as an incentive to conduct studies that produce credible results and thus reducing the need for dishonest research practices. In this regard, the use of post-hoc power analysis complements other efforts towards open science such as preregistration and data sharing.