Category Archives: Priming

A New Look at the Implicit Revolution

Psychology is not a unified paradigmatic science. That is, it lacks an overarching theory like evolution theory in biology. In a science without an empirically grounded paradigm, progress is made very much like evolution made progress in a process of trial and error. Some ideas may thrive for a moment, but if they are not fruitful, they are discarded. The emergence of a new idea is often characterized as a revolution, and psychology has seen its fair share of revolutions. Behaviorism replaced introspectionism and the cognitive revolution replaced behaviorism. For better or worse, cognitivism is dominating psychology at the moment. The cognitive revolution also had a strong influence on social psychology with the rise of social cognition research.

In the early days, social psychologists focussed on higher cognitive processes like attributions. However, in the 1980s, the implicit revolution shifted focus towards lower cognitive processes that may occur without awareness. This was not the first time, unconscious processes became popular. A special issue in the American Psychologists in 1992 called it the New Look 3 (Greenwald, 1992).

The first look was Freud’s exploration of conscious and unconscious processes. A major hurdle for this first look was conceptual confusion and a lack of empirical support. Puritan academic may also have shied away from the sexual content in Freudian theories (e.g., sexual desire directed at the mother).

However, the second look did try to study many of Freud’s ideas with empirical methods. For example, Silverman and Weinberger (1985) presented the phrase “Mommy and I are one” on a computer screen so quickly that participants were unable to say what they saw. This method is called subliminal priming. The idea was that the unconscious has a longing to be loved by mommy and that presenting this phrase would gratify the unconscious. Numerous studies used the “Mommy and I are one” priming method to see effects on behavior.

Greenwald (1992) reviewed this evidence.

Can subliminal presentations result in cognitive analyses of multiword strings? There have been reports of such effects, especially in association with tests of psychoanalytic hypotheses. The best known of these findings (described as subliminal psychodynamic activation [SPA], using “Mommy and I are One” as the text of a subliminal stimulus; Silverman & Weinberger, 1985) has been identified, on the basis of meta-analysis, as a reproducible phenomenon (Hardaway, 1990; Weinberger & Hardaway, 1990).

Despite this strong evidence, many researchers remain skeptical about the SPA result (see, e.g., the survey reported in Appendix B). Such skepticism is almost certainly due to the lack of widespread enthusiasm for the SPA result’s proposed psychodynamic interpretation (Silverman & Weinberger, 1985).

Because of the positive affective values of words in the critical stimulus (especially Mommy and I) , it is possible that observed effects might be explained by cognitive analysis limited to the level of single words. Some support for that interpretation is afforded by Hardaway’s demonstration (1990, p. 183, Table 3) that other affectively positive strings that include Mommy or One also produce significant effects. However, these other effects are weaker than the effect of the specific string, “Mommy and I are One.”

In summary of evidence from studies of subliminal activation, it is now well established that analysis occurs for stimuli presented at exposure conditions in a region between objective and subjective thresholds; this analysis can extract at least some semantic content of single words.

The New Look 3, however, was less interested in Freudian theory. Most of the influential subliminal priming studies used ordinary stimuli to study common topics in social psychology, including prejudice.

For example, Greenwald (1992) cites Devine’s (1989) highly influential subliminal priming studies with racial stimuli as evidence that “experiments using stimulus conditions that are clearly above objective thresholds (but presumably below subjective thresholds) have obtained semantic activation findings with apparent relative ease” (p. 769).

25 years later, in their Implicit Revolution article, Greenwald and Banaji feature Devine’s influential article.

Patricia Devine’s (1989) dissertation research extended the previously mentioned subliminal priming methods of Bargh and Pietromonaco (1982) to automatic stereotypes. Devine’s article brought attention to the possibility of dissociation between automatic stereotype activation
and controlled inhibition of stereotype expression
” (p. 865).

In short, subliminal priming has played an important role in the implicit revolution. However, subliminal priming is still rare. Most studies use clearly visible stimuli. This is surprising, given the clear advantages of subliminal priming to study unconscious processes. A major concern with stimuli that are presented with awareness is that participants can control their behavior. In contrast, if they are not even aware that a racial stimulus was presented, they have no ability to supress a prejudice response.

Another revolution explains why subliminal studies remain rare despite their obvious advantages. This revolution has been called the credibility revolution, replication revolution, or open science revolution. The credibility revolution started in 2011, after a leading social cognition journal published a controversial article that showed time-reversed subliminal priming effects (Bem, 2011). This article revealed a fundamental problem in the way social psychologists conducted their research. Rather than using experiments to see whether effects exist, they used experiments to accumulate evidence in favor of effects. Studies that failed to show the expected effects were hidden. In the 2010s, it has become apparent that this flawed use of the scientific method has produced large literatures with results that cannot be replicated. A major replication project found that less than 25% of results in social psychological experiments could be replicated (OSC, 2015). Given these results, it is unclear which results provided credible evidence.

Despite these troubling findings, social psychologists continue to cite old studies like Devine’s (1989) study (it was just one study!) as if it provided conclusive evidence for subliminal priming of prejudice. If we need any evidence for Freud’s theory of repression, social psychologists would be a prime example. Through various defense mechanisms they maintain the belief that old findings that were obtained with bad scientific practices provided credible evidence that can inform our understanding of the unconscious.

Here I show that this is wishful thinking. To do so, I conducted a modern meta-analysis of subliminal priming studies. Unlike traditional meta-analysis that do not take publication bias into account, this new method provides a strong test of publication bias and corrects for its effect on the results. While there are several new methods, z-curve has been shown to be superior to other methods (Brunner & Schimmack, 2020).

The figure shows the results. The red line at z = 1.96, corresponds to the significance criterion of .05. It is easy to see that this criterion acts like a censor. Results with z-scores greater than 1.96 (i.e., p < .05) are made public and can enter researchers awareness. Results that are not significant, z < 1.06, are repressed and may linger only in the unconscious of researchers who prefer not to think about their failures.

Statistical evidence of repression is provided by a comparison of the observed discovery rate (i.e., the percentage of published results that are significant) of 90% and the expected discovery rate based on the z-curve model (i.e., the grey curve in the figure) of 13%. Evidently, published results are selected from a much larger number of analyses that failed to support subliminal priming. This clear evidence of selection for significance undermines the credibility of individual studies in the subliminal priming literature.

However, there is some evidence of heterogeneity across studies. This is seen in the increasing numbers below the x-axis. Whereas studies with z-scores below 4, have low average power, studies with z-scores above 4, have a mean power greater than 80%. This suggests that replications of these studies could produce significant results. This information could be used to salvage a few solid findings from a pile of junk findings. Closer examination of these studies is beyond the purpose of this blog post, and Devine’s study is not one of them.

The main point of this analysis is that there is strong scientific evidence to support the claim that subliminal priming researchers did not use the scientific method properly. By selecting only results that support the existence of subliminal priming, they created only illusory evidence in support of subliminal priming. Thirty years after Devine’s (1989) subliminal prejudice study was published, we have no scientific evidence in support of the claim that racial stimuli can bypass consciousness and directly influence behavior.

However, Greenwald and other social psychologists who made a career out of these findings repress the well-known fact that published results in experimental social psychology are not credible and cite them as if they are credible evidence (Greenwald & Banaj, 2017).

Social psychologists are of course very familiar with deception. First, they became famous for deceiving participants (Milgram studies). In 2011, it became apparent that they were deceiving themselves. Now, it seems they are willing to deceive others to avoid facing the inconvenient truth that decades of research have produced no scientific results.

The inability to face ego-threatening information is of course not new to psychologists. Freud studied defense mechanisms and social psychologists studied cognitive biases and motivated reasoning. Right now, this trait is on display in Donald Trump and his supporters inability to face the fact that he lost an election. It is ironic that social psychologists have the same inability when their own egos are on the line.

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.

 

‘Before you know it’ by John A. Bargh: A quantitative book review

November 28, Open Draft/Preprint (Version 1.0)
[Please provide comments and suggestions]

In this blog post I present a quantitative review of John A Bargh’s book “Before you know it: The unconscious reasons we do what we do”  A quantitative book review is different from a traditional book review.  The goal of a quantitative review is to examine the strength of the scientific evidence that is provided to support ideas in the book.  Readers of a popular science book written by an eminent scientist expect that these ideas are based on solid scientific evidence.  However, the strength of scientific evidence in psychology, especially social psychology has been questioned.  I use statistical methods to examine how strong the evidence actually is.

One problem in psychological publishing is publication bias in favor of studies that support theories, so called publication bias.  The reason for publication bias is that scientific journals can publish only a fraction of results that scientists produce.  This leads to heavy competition among scientists to produce publishable results, and journals like to publish statistically significant results; that is studies that provide evidence for an effect (e.g., “eating green jelly beans cures cancer” rather than “eating red jelly beans does not cure cancer”).  Statisticians have pointed out that publication bias undermines the meaning of statistical significance, just like counting only hits would undermine the meaning of batting averages. Everybody would have an incredible batting average of 1.00.

For a long time it was assumed that publication bias is just a minor problem. Maybe researchers conducted 10 studies and reported only 8 significant results while not reporting the remaining two studies that did not produce a significant result.  However, in the past five years it has become apparent that publication bias, at least in some areas of the social sciences, is much more severe, and that there are more unpublished studies with non-significant results than published results with significant results.

In 2012, Daniel Kahneman (2012) raised doubts about the credibilty of priming research in an open email letter addressed to John A. Bargh, the author of “Before you know it.”  Daniel Kahneman is a big name in psychology; he won a Nobel Prize for economics in 2002.  He also wrote a popular book that features John Bargh’s priming research (see review of Chapter 4).  Kahneman wrote “As all of you know, of course, questions have been raised about the robustness of priming results…. your field is now the poster child for doubts about the integrity of psychological research.”

Kahneman is not an outright critic of priming research. In fact, he was concerned about the future of priming research and made some suggestions how Bargh and colleagues could alleviate doubts about the replicability of priming results.  He wrote:

“To deal effectively with the doubts you should acknowledge their existence and confront them straight on, because a posture of defiant denial is self-defeating. Specifically, I believe that you should have an association, with a board that might include prominent social psychologists from other fields. The first mission of the board would be to organize an effort to examine the replicability of priming results.”

However, prominent priming researchers have been reluctant to replicate their old studies.  At the same time, other scientists have conducted replication studies and failed to replicate classic findings. One example is Ap Dijksterhuis’s claim that showing words related to intelligence before taking a test can increase test performance.  Shanks and colleagues tried to replicate this finding in 9 studies and came up empty in all 9 studies. More recently, a team of over 100 scientists conducted 24 replication studies of Dijsterhuis’s professor priming study.  Only 1 study successfully replicated the original finding, but with a 5% error rate, 1 out of 20 studies is expected to produce a statistically significant result by chance alone.  This result validates Shanks’ failures to replicate and strongly suggests that the original result was a statistical fluke (i.e., a false positive result).

Proponent of priming research like  Dijksterhuis “argue that social-priming results are hard to replicate because the slightest change in conditions can affect the outcome” (Abbott, 2013, Nature News).  Many psychologists consider this response inadequate.  The hallmark of a good theory is that it predicts the outcome of a good experiment.  If the outcome depends on unknown factors and replication attempts fail more often than not, a scientific theory lacks empirical support.  For example,  Kahneman wrote in an email that the apparent “refusal to engage in a legitimate scientific conversation … invites the interpretation that the believers are afraid of the outcome” (Abbott, 2013, Nature News).

It is virtually impossible to check on all original findings by conducting extensive and expensive replication studies.  Moreover, proponents of priming research can always find problems with actual replication studies to dismiss replication failures.  Fortunately, there is another way to examine the replicability of priming research. This alternative approach, z-curve, uses a statistical approach to estimate replicability based on the results reported in original studies.  Most important, this approach examines how replicable and credible original findings were based on the results reported in the original articles.  Therefore, original researches cannot use inadequate methods or slight variations in contextual factors to dismiss replication failures. Z-curve can reveal that the original evidence was not as strong as dozens of published studies may reveal because it takes into account that published studies were selected to provide evidence for priming effects.

My colleagues and I used z-curve to estimate the average replicability of priming studies that were cited in Kahneman’s chapter on priming research.  We found that the average probability of a successful replication was only 14%. Given the small number of studies (k = 31), this estimate is not very precise. It could be higher, but it could also be even lower. This estimate would imply that for each published significant result, there are  9 unpublished non-significant results that were omitted due to publication bias. Given these results, the published significant results provide only weak empirical support for theoretical claims about priming effects.  In a response to our blog post, Kahneman agreed (“What the blog gets absolutely right is that I placed too much faith in underpowered studies”).

Our analysis of Kahneman’s chapter on priming provided a blue print for this  quantitative book review of Bargh’s book “Before you know it.”  I first checked the notes for sources and then linked the sources to the corresponding references in the reference section.  If the reference was an original research article, I downloaded the original research article and looked for the most critical statistical test of a study. If an article contained multiple studies, I chose one test from each study.  I found 168 usable original articles that reported a total of 400 studies.  I then converted all test statistics into absolute z-scores and analyzed them with z-curve to estimate replicability (see Excel file for coding of studies).

Figure 1 shows the distribution of absolute z-scores.  90% of test statistics were statistically significant (z > 1.96) and 99% were at least marginally significant (z > 1.65), meaning they passed a less stringent statistical criterion to claim a success.  This is not surprising because supporting evidence requires statistical significance. The more important question is how many studies would produce a statistically significant result again if all 400 studies were replicated exactly.  The estimated success rate in Figure 1 is less than half (41%). Although there is some uncertainty around this estimate, the 95% confidence interval just reaches 50%, suggesting that the true value is below 50%.  There is no clear criterion for inadequate replicability, but Tversky and Kahneman (1971) suggested a minimum of 50%.  Professors are also used to give students who scored below 50% on a test an F.  So, I decided to use the grading scheme at my university as a grading scheme for replicability scores.  So, the overall score for the replicability of studies cited by Bargh to support the ideas in his book is F.

 

Before.You.Know.It.Final

This being said, 41% replicability is a lot more than we would expect by chance alone, namely 5%.  Clearly some of the results mentioned in the book are replicable. The question is which findings are replicable and which ones are difficult to replicate or even false positive results.  The problem with 41% replicable results is that we do not know which results we can trust. Imagine you are interviewing 100 eyewitnesses and only 42 of them are reliable. Would you be able to identify a suspect?

It is also possible to analyze subsets of studies. Figure 2 shows the results of all experimental studies that randomly assigned participants to two or more conditions.  If a manipulation has an effect, it produces mean differences between the groups. Social psychologists like these studies because they allow for strong causal inferences and make it possible to disguise the purpose of a study.  Unfortunately, this design requires large samples to produce replicable results and social psychologists often used rather small samples in the past (the rule of thumb was 20 per group).  As Figure 2 shows, the replicability of these studies is lower than the replicability of all studies.  The average replicability is only 24%.  This means for every significant result there are at least three non-significant results that have not been reported due to the pervasive influence of publication bias.

Before.You.Know.It.BS.EXP.png

If 24% doesn’t sound bad enough, it is important to realize that this estimate assumes that the original studies can be replicated exactly.  However, social psychologists have pointed out that even minor differences between studies can lead to replication failures.  Thus, the success rate of actual replication studies is likely to be even less than 24%.

In conclusion, the statistical analysis of the evidence cited in Bargh’s book confirms concerns about the replicability of social psychological studies, especially experimental studies that compared mean differences between two groups in small samples. Readers of the book should be aware that the results reported in the book might not replicate in a new study under slightly different conditions and that numerous claims in the book are not supported by strong empirical evidence.

Replicability of Chapters

I also estimated the replicability separately for each of the 10 chapters to examine whether some chapters are based on stronger evidence than others. Table 1 shows the results. Seven chapters scored an F, two chapters scored a D, and one chapter earned a C-.   Although there is some variability across chapters, none of the chapters earned a high score, but some chapters may contain some studies with strong evidence.

Table 1. Chapter Report Card

Chapter 1 28 F
Chapter 2 40 F
Chapter 3 13 F
Chapter 4 47 F
Chapter 5 50 D-
Chapter 6 57 D+
Chapter 7 24 F
Chapter 8 19 F
Chapter 9 31 F
Chapter 10 62 C-

Credible Findings in the Book

Unfortunately, it is difficult to determine the replicability of individual studies with high precision.  Nevertheless, studies with high z-scores are more replicable.  Particle physicists use a criterion value of z > 5 to minimize the risk that the results of a single study are not a false positive.  I found that psychological studies with a z-score greater than 4 had an 80% chance of being replicated in actual replication studies.  Using this rule as a rough estimate of replicability, I was also able to identify credible claims in the book.  Highlighting these claims does not mean that the other claims are wrong. It simply means that they are not supported by strong evidence.

Chapter 1:    

According to Chapter 1, there seems “to be a connection between the strength of the unconscious physical safety motivation and a person’s political attitudes.”   The notes list a number of articles to support this claim.  The only conclusive evidence in these studies is that self-reported political attitudes (a measure of right-wing authoritarianism) is correlated with self-reported beliefs that the world is dangerous (Duckitt et al., JPSP, 2002, 2 studies, z = 5.42, 6.93).  The correlation between self-report measures is hardly evidence for unconscious physical safety motives.

Another claim is that “our biological mandate to reproduce can have surprising manifestations in today’s world.”   This claim is linked to a study that examined the influence of physical attractiveness on call backs for a job interview.  In a large field experiment, researchers mailed (N = 11,008 resumes) to real job ads and found that both men and women were more likely to be called for an interview if the application included a picture of a highly attractive applicant versus a not so attractive applicant (Busetta et al., 2013, z = 19.53).  Although this is an interesting and important finding, it is not clear that the human resource offices preference for attractive applicants was driven by their “biological mandate to reproduce.”

Chapter 2: 

Chapter 2 introduces the idea that there is a fundamental connection between physical sensations and social relationships.  “… why today we still speak so easily of a warm friend, or a cold father. We always will. Because the connection between physical and social warmth, and between physical and social coldness, is hardwired into the human brain.”   Only one z-score surpassed the 4-sigma threshold.  This z-score comes from a brain imaging study that found increased sensorimotor activation in response to hand-washing products (soap) after participants had lied in a written email, but not after they had lied verbally;  Schaefer et al., 2015, z = 4.65).  There are two problems with this supporting evidence.  First, z-scores in fMRI studies require a higher threshold than z-scores in other studies because brain imaging studies allow for multiple comparisons that increase the risk of a false positive result (Vul et al., 2009).  More important, even if this finding could be replicated, it does not provide support for the claim that these neurological connections are hard-wired into humans’ brains.

The second noteworthy claim in Chapter 2 is that infants “have a preference for their native language over other languages, even though they don’t yet understand a word.” This claim is not very controversial given ample evidence that humans’ prefer familiar over unfamilar stimuli (Zajonc, 1968, also cited in the book).  However, it is not so easy to study infants’ preferences (after all, they are not able to tell us).  Developmental researchers use a visual attention task to infer preferences. If an infant looks longer at one of two stimuli, it indicates a preference for this stimulus. Kinzler et al. (PNAS, 2007) reported six studies. For five studies, z-scores ranged from 1.85 to 2.92, which is insufficient evidence to draw strong conclusions.  However, Study 6 provided convincing evidence (z = 4.61) that 5-year old children in Boston preferred a native speaker to a child with a French accent. The effect was so strong that 8 children were sufficient to demonstrate it.  However, a study with 5-year olds hardly provides evidence for infants’ preferences. In addition, the design of this study holds all other features constant. Thus, it is not clear how strong this effect is in the real world when many other factors can influence the choice of a friend.

Chapter 3

Chapter 3 introduces the concept of priming. “Primes are like reminders, whether we are aware of the reminding or not”   It uses two examples to illustrate priming with and without awareness. One example implies that people can be aware of the primes that influenced their behavior.  If you are in the airport, smell Cinnabon, and find yourself suddenly in front of the Cinnabon counter you are likely to know that the smell made you think about Cinnabon and decide to eat one. The second example introduces the idea that primes can influence behavior without awareness. If you were caught off in traffic, you may respond more hostile to a transgression of a co-worker without being aware that the earlier experience in traffic influenced your reaction.  The supporting references contain two noteworthy (z > 4) findings that show how priming can be used effectively as reminders (Rogers & Milkman, 2016, Psychological Science, Studies 2a (N = 920, z = 5.45) and Study 5 (N = 305, z = 5.50). In Study 2a, online participants were presented with the following instruction:

In this survey, you will have an opportunity to
support a charitable organization called Gardens
for Health that provides lasting agricultural
solutions to address the problem of chronic
childhood malnutrition. On the 12th page of this
survey, please choose answer “A” for the last
question on that page, no matter your opinion. The
previous page is Page 1. You are now on Page 2.
The next page is Page 3. The picture below will
be on top of the NEXT button on the 12th page.
This is intended to remind you to select
answer “A” for the last question on that page. If you
follow these directions, we will donate $0.30 to
Gardens for Health.

Elefant.png

On pages 2-11 participants either saw distinct animals or other elephants.

elefant2.png

 

Participants in the distinct animal condition were more likely to press the response that led to a donation than participants who saw a variety of elephants (z = 5.45).

Study 5 examined whether respondents would be willing to pay for a reminder.  They were offered 60 cents extra payment for responding with “E” to the last question.  They could either pay 3 cents to get an elephant reminder or not.  53% of participants were willing to pay for the reminder, which the authors compared to 0, z = 2 × 10^9.  This finding implies that participants are not only aware of the prime when they respond in the primed way, but are also aware of this link ahead of time and are willing to pay for it.

In short, Chapter 3 introduces the idea of unconscious or automatic priming, but the only solid evidence in the reference section supports the notion that we can also be consciously aware of priming effects and use them to our advantage.

Chapter 4

Chapter 4 introduces the concept of arousal transfer; the idea that arousal from a previous event can linger and influence how we react to another event.  The book reports in detail a famous experiment by Dutton and Aaron (1974).

“In another famous demonstration of the same effect, men who had just crossed a rickety pedestrian bridge over a deep gorge were found to be more attracted to a woman they met while crossing that bridge. How do we know this? Because they were more likely to call that woman later on (she was one of the experimenters for the study and had given these men her number after they filled out a survey for her) than were those who met the same woman while crossing a much safer bridge. The men in this study reported that their decision to call the woman had nothing to do with their experience of crossing the scary bridge. But the experiment clearly showed they were wrong about that, because those in the scary-bridge group were more likely to call the woman than were those who had just crossed the safe bridge.”

First, it is important to correct the impression that men were asked about their reasons to call back.  The original article does not report any questions about motives.  This is the complete section in the results that mentions the call back.

“Female interviewer. In the experimental group, 18 of the 23 subjects who agreed to
the interview accepted the interviewer’s phone number. In the control group, 16 out of 22 accepted (see Table 1). A second measure of sexual attraction was the number of subjects who called the interviewer. In the experimental group 9 out of 18 called, in the control group 2 out of 16 called (x2 = 5.7, p < .02). Taken in conjunction with the sexual
imagery data, this finding suggests that subjects in the experimental group were more
attracted to the interviewer.”

A second concern is that the sample size was small and the evidence for the effect was not very strong.  In the experimental group 9 out of 18 called, in the control
group 2 out of 16 called (x2 = 5.7, p < .02) [z = 2.4].

Finally, the authors mention a possible confound in this field study.  It is possible that men who dared to cross the suspension bridge differ from men who crossed the safe bridge, and it has been shown that risk taking men are more likely to engage in casual sex.  Study 3 addressed this problem with a less colorful, but more rigorous experimental design.

Male students were led to believe that they were participants in a study on electric shock and learning.  An attractive female confederate (a student working with the experimenter but pretending to be a participants) was also present.  The study had four conditions. Male participants were told that they would receive weak or strong shock and they were told that the female confederate would receive weak or strong shock.  They then were asked to fill out a questionnaire before the study would start; in fact, the study ended after participants completed the questionnaire and they were told about the real purpose of the study.

The questionnaire contained two questions about the attractive female confederate. “How much would you like to kiss her?” and “How much would you like to ask her out on a date?”  Participants who were anticipating strong shock had much higher average ratings than those who anticipated weak shock, z = 4.46.

Although this is a strong finding, we also have a large literature on emotions and arousal that suggests frightening your date may not be the best way to get to second base (Reisenzein, 1983; Schimmack, 2005).  It is also not clear whether arousal transfer is a conscious or unconscious process. One study cited in the book found that exercise did not influenced sexual arousal right away, presumably because participants attributed their increased heart rate to the exercise. This suggests that arousal transfer is not entirely an unconscious process.

Chapter 4 also brings up global warming.  An unusually warm winter day in Canada often make people talk about global warming.  A series of studies examined the link between weather and beliefs about global warming more scientifically.  “What is fascinating (and sadly ironic) is how opinions regarding this issue fluctuate as a function of the very climate we’re arguing about. In general, what Weber and colleagues found was that when the current weather is hot, public opinion holds that global warming is occurring, and when the current weather is cold, public opinion is less concerned about global warming as a general threat. It is as if we use “local warming” as a proxy for “global warming.” Again, this shows how prone we are to believe that what we are experiencing right now in the present is how things always are, and always will be in the future. Our focus on the present dominates our judgments and reasoning, and we are unaware of the effects of our long-term and short-term past on what we are currently feeling and thinking.”

One of the four studies produced strong evidence (z = 7.05).  This study showed a correlation between respondents’ ratings of the current day’s temperature and their estimate of the percentage of above average warm days in the past year.  This result does not directly support the claim that we are more concerned about global warming on warm days for two reasons. First, response styles can produce spurious correlations between responses to similar questions on a questionnaire.  Second, it is not clear that participants attributed above average temperatures to global warming.

A third credible finding (z = 4.62) is from another classic study (Ross & Sicoly, 1974, JPSP, Study 2a).  “You will have more memories of yourself doing something than of your spouse or housemate doing them because you are guaranteed to be there when you do the chores. This seems pretty obvious, but we all know how common those kinds of squabbles are, nonetheless. (“I am too the one who unloads the dishwasher! I remember doing it last week!”)”   In this study, 44 students participated in pairs. They were given separate pieces of information and exchange information to come up with a joint answer to a set of questions.  Two days later, half of the participants were told that they performed poorly, whereas the other half was told that they performed well. In the success condition, participants were more likely to make self-attributions (i.e., take credit) than expected by chance.

Chapter 5

In Chapter 5, John Bargh tell us about work by his supervisor Robert Zajonc (1968).  “Bob was doing important work on the mere exposure effect, which is, basically, our tendency to like new things more, the more often we encounter them. In his studies, he repeatedly showed that we like them more just because they are shown to us more often, even if we don’t consciously remember seeing them”  The 1968 classic article contains two studies with strong evidence (Study 2, z = 6.84, Study 3 z = 5.81).  Even though the sample sizes were small, this was not a problem because the studies presented many stimuli at different frequencies to all participants. This makes it easy to spot reliable patterns in the data.

zajonc

 

 

 

 

 

 

 

Chapter 5 also introduces the concept of affective priming.  Affective priming refers to the tendency to respond emotionally to a stimulus even if a task demands to ignore it.  We simply cannot help to feel good or bad and turn our emotions off.  The experimental way to demonstrate this is to present an emotional stimulus quickly followed by a second emotional stimulus. Participants have to respond to the second stimulus and ignore the first stimulus.  It is easier to perform the task when the two stimuli have the same valence, suggesting that the valence of the first stimulus was processed even though participants had to ignore it.  Bargh et al. (1996, JESP) reported that this even happens  when the task is simply to pronounce the second word (Study 1 z = 5.42, Study 2 z = 4.13, Study 3, z = 3.97).

The book does not inform readers that we have to distinguish two types of affective priming effects.  Affective priming is a robust finding when participants’ task is to report on the valence (is it good or bad) of the second stimulus following the prime.  However, this finding has been interpreted by some researches as an interference effect, similar to the Stroop effect.  This explanation would not predict effects on a simple pronounciation task.  However, there are fewer studies with the pronounciation task and some of these have failed to replicate Bargh et al.’s original findings, despite the strong evidence observed in their studies. First, Klauer and Musch (2001) failed to replicate Bargh et al.’s findings that affective priming influences pronunciation of target words in three studies with good statistical power. Second, DeHouwer et al. (2001) were able to replicate it with degraded primes, but also failed to replicate the effect with visible primes that were used by Bargh et al.  In conclusion, affective priming is a robust effect when participants have to report on the valence of the second stimulus, but this finding does not necessarily imply that primes unconsciously activate related content in memory.

Chapter 5 also reports about some surprising associations between individuals’ names, or better their initials, and the places they live, professions, and partners. These correlations are relatively small, but they are based on large datasets and very unlikely to be just statistical flukes (z-scores ranging from 4.65 to 49.44).  The causal process underlying these correlations is less clear.  One possible explanation is that we have unconscious preferences that influence our choices. However, experimental studies that tried to study this effect in the laboratory are less convincing.  Moreover, Hodson and Olson failed to find a similar effect across a variety of domains such as liking of animals (Alicia is not more likely to like ants than Samantha), foods, or leisure activities. They found a significant correlation for brand names (p = .007), but this finding requires replication.   More recently, Kooti, Magno, and Weber (2014) examined name effects on social media. They found significant effects for some brand comparisons (Sega vs. Nintendo), but not for others (Pepsi vs. Coke).  However, they found that twitter users were more likely to follow other twitter uses with the same first name. Taken together, these results suggest that individuals’ names predict some choices, but it is not clear when or why this is the case.

The chapter ends with a not very convincing article (z = 2.39, z = 2.22) that it is actually very easy to resist or override unwanted priming effects. According to this article, simply being told that somebody is a team member can make automatic prejudice go away.  If it were so easy to control unwanted feelings, it is not clear why racism is still a problem 50 years after the civil rights movement started.

In conclusion Chapter 5 contains a mix of well-established findings with strong support (mere-exposure effects, affective priming) and several less supported ideas. One problem is that priming is sometimes presented as an unconscious process that is difficult to control and at other times these effects seem to be easily controllable. The chapter does not illuminate under which conditions we should suspect priming to influence our behavior in ways we don’t notice or cannot control and when we notice them and have the ability to control them.

Chapter 6

Chapter 6 deals with the thorny problem in psychological science that most theories make correct predictions sometimes. Even a broken clock tells the time right twice a day. The problem is to know in which context a theory makes correct predictions and when it does not.

“Entire books—bestsellers—have appeared in recent years that seem to give completely conflicting advice on this question: can we trust our intuitions (Blink, by Malcolm Gladwell), or not (Thinking, Fast and Slow, by Daniel Kahneman)? The answer lies in between. There are times when you can and should, and times when you can’t and shouldn’t [trust your gut].

Bargh then proceeds to make 8 evidence-based recommendation when it is advantages to rely on intuition without effortful deliberation (gut feelings).

Rule #1: supplement your gut impulse with at least a little conscious reflection, if you have the time to do so.

Rule # 2: when you don’t have the time to think about it, don’t take big chances for small gains going on your gut alone.

Rule #3: when you are faced with a complex decision involving many factors, and especially when you don’t have objective measurements (reliable data) of those important factors, take your gut feelings seriously.

Rule #4: be careful what you wish for, because your current goals and needs will color what you want and like in the present.

Rule #5: when our initial gut reaction to a person of a different race or ethnic group is negative, we should stifle it.

Rule #6: we should not trust our appraisals of others based on their faces alone, or on photographs, before we’ve had any interaction with them.

Rule #7: (it may be the most important one of all): You can trust your gut about other people—but only after you have seen them in action.

Rule #8: it is perfectly fine for attraction be one part of the romantic equation, but not so fine to let it be the only, or even the main, thing.

Unfortunately, the credible evidence in this chapter (z > 4) is only vaguely related to these rules and insufficient to claim that these rules are based on solid scientific evidence.

Morewedge and Norton (2009) provide strong evidence that people in different cultures (US z = 4.52, South Korea z = 7.18, India z = 6.78) believe that dreams provide meaningful information about themselves.   Study 3 used a hypothetical scenario to examine whether people would change their behavior in response to a dream.  Participants were more likely to say that they would change a flight after dreaming about a plane crash in the night before the flight than if they thought about a plane crash the evening before and dreams influenced behavior about as much as hearing about an actual plane crash (z = 10.13).   In a related article, Morewedge and colleagues (2014) asked participants to rate types of thoughts (e.g., dreams, problem solving, etc.) in terms of spontaneity or deliberation. A second rating asked about the extent to which the type of thought would generate self-insight or is merely a reflection of the current situation.  They found that spontaneous thoughts were considered to generate more self-insight (Study 1 z = 5.32, Study 2 z = 5.80).   In Study 5, they also found that more spontaneous recollection of a recent positive or negative experience with their romantic partner predicted hypothetical behavioral intention ratings (““To what extent might recalling the experience affect your likelihood of ending the relationship, if it came to mind when you tried to remember it”) (z = 4.06). These studies suggest that people find spontaneous, non-deliberate thoughts meaningful and that they are willing to use them in decision making.  The studies do not tell us under which circumstances listening to dreams and other spontaneous thoughts (gut feelings) is beneficial.

Inbar, Cone, and Gilovich (2010) created a set of 25 choice problems (e.g., choosing an entree, choosing a college).  They found that “the more a choice was seen as objectively evaluable, the more a rational approach was seen as the appropriate choice strategy” (Study 1a, z = 5.95).  In a related study, they found “the more participants
thought the decision encouraged sequential rather than holistic processing, the more they thought it should be based on rational analysis” (Study 1b, z = 5.02).   These studies provide some insight into people’s beliefs about optimal decision rules, but they do not tell us whether people’s beliefs are right or wrong, which would require to examine people’s actual satisfaction with their choices.

Frederick (2005) examined personality differences in the processing of simple problems (e.g., A bat and a ball cost $1.10. The bat costs $1.00 more than the ball. How much does the ball cost?).  The quick answer is 10 cent, but the correct answer is 5 cent.  In this case, the gut response is false.  A sample of over 3,000 participants answered several similar questions. Participants who performed above average were more willing to delay gratification (get $3,800 in a month rather than $3,400 now) than participants with below average performance (z > 5).  If we consider the bigger reward a better choice, these results imply that it is not good to rely on gut responses when it is possible to use deliberation to get the right answer.

Two studies by Wilson and Schooler (1991) are used to support the claim that we can overthink choices.

“In their first study, they had participants judge the quality of different brands of jam, then compared their ratings with those of experts. They found that the participants who were asked to spend time consciously analyzing the jam had preferences that differed further from those of the experts, compared to those who responded with just the “gut” of their taste buds.”  The evidence in this study with a small sample is not very strong and requires replication  (N = 49, z = 2.36).

“In Wilson and Schooler’s second study, they interviewed hundreds of college students about the quality of a class. Once again, those who were asked to think for a moment about their decisions were further from the experts’ judgments than were those who just went with their initial feelings.”

Wilson.Schooler

The description in the book does not match the actual study.  There were three conditions.  In the control condition, participants were asked to read the information about the courses carefully.  In the reasons condition, participants were asked to write down their reasons. and in the rate all condition participants were asked to rate all pieces of information, no matter how important, in terms of its effect on their choices. The study showed that considering all pieces of information increased the likelihood of choosing a poorly rated course (a bad choice), but had a much smaller effect on ratings of highly rated courses (z = 4.14 for the interaction effect).  All conditions asked for some reflection and it remains unclear how students would respond if they went with their initial feelings, as described in the book.  Nevertheless, the study suggests that good choices require focusing on important factors and paying attention to trivial factors can lead to suboptimal choices.  For example, real estate agents in hot markets use interior design to drive up prices even though the design is not part of the sale.

We are born sensitive to violations of fair treatment and with the ability to detect those who are causing harm to others, and assign blame and responsibility to them. Recent research has shown that even children three to five years old are quite sensitive to fairness in social exchanges. They preferred to throw an extra prize (an eraser) away than to give more to one child than another—even when that extra prize could have gone to themselves. This is not an accurate description of the studies.  Study 1 (z > 5) found that 6 to 8 year old children preferred to give 2 erasers to one kid and 2 erasers to another kid and to throw the fifth eraser away to maintain equality (20 out of 20, p < .0001).  However, “the 3-to 5-year-olds showed no preference to throw a resource away (14 out of 24, p = .54)” (p. 386).  Subsequent studies used only 6-8 year old children. Study 4 examined how children would respond if erasers are divided between themselves and another kid. 17 out of 20 (p = .003, z = 2.97 preferred to throw the eraser away rather than getting one more for themselves.  However, in a related article, Shaw and Olson, 2012b) found that children preferred favoritism (getting more erasers) when receiving more erasers was introduced as winning a contest (Study 2, z = 4.65). These studies are quiet interesting, but they do not support the claim that equality norms are inborn, nor do they help us to figure out when we should or should not listen to our gut or whether it is better for us to be equitable or selfish.

The last, but in my opinion most interesting and relevant, piece of evidence in Chapter 6 is a large (N = 16,624) survey study of relationship satisfaction (Cacioppo et al., 2013, PNAS, z = 6.58).   Respondents reported their relationship satisfaction and how they had met.   Respondents who had met their partner online were slightly more satisfied than respondents who had met their partner offline.  There were also differences between different types of meeting online.  Respondents who met their partner in a bar had one of the lowest average level of satisfaction.  The study did not reveal why online dating is slightly more successful, but both forms of dating probably involve a combination of deliberation and “gut” reactions.

In conclusion, Chapter 6 provides some interesting insights into the way people make choices. However, the evidence does not provide a scientific foundation for recommendations when it is better to follow your instinct and when it is better to rely on logical reasoning and deliberation.  Either the evidence of the reviewed studies is too weak or the studies do not use actual choice outcomes as outcome variable. The comparison of online and offline dating is a notable exception.

Chapter 7

Chapter 7 uses an impressive field experiment to support the idea that “our mental representations of concepts such as politeness and rudeness, as well as innumerable other behaviors such as aggression and substance abuse, become activated by our direct perception of these forms of social behavior and emotion, and in this way are contagious.”   Keizer et al. (2008) conducted the study in an alley in Groningen, a city in the Netherlands.  In one condition, bikes were parked in front of a wall with graffiti, despite an anti-graffiti sign.  In the other condition, the wall was clean.  Researchers attached fliers to the bikes and recorded how many users would simply throw the fliers on the ground.  They recorded the behaviors of 77 bike riders in each condition. In the graffiti condition, 69% of riders littered. In the clean condition, only 33% of riders littered (z = 4.51).

Kreizer.Study1.png

In Study 2, the researchers put up a fence in front of the entrance to a car park that required car owners to walk an extra 200m to get to their car, but they left a gap that allowed car owners to avoid the detour.  There was also a sign that forbade looking bikes to the fence.  In one condition, bikes were not locked to the fence. In the experimental condition, the norm was violated and four bikes were locked to the fence.  41 car owners’ behaviors were observed in each condition.  In the experimental condition, 82% of participants stepped through the gap. In the control condition, only 27% of car owners stepped through the gap (z = 5.27).

Keizer.Study2.png

It is unlikely that bike riders or car owners in these studies consciously processed the graffiti or the locked bikes.  Thus, these studies support the hypothesis that our environment can influence behavior in subtle ways without our awareness.  Moreover, these studies show these effects with real-world behavior.

Another noteworthy study in Chapter 7 examined happiness in social networks (Fowler & Christakis, 2008).   The authors used data from the Framingham Heart Study, which is a unique study where most inhabitants of a small town, Framingham, participated in the study.   Researchers collected many measures, including a measure of happiness. They also mapped social relationships among them.  Fowler and Christakis used sophisticated statistical methods to examine whether people who were connected in the social network (e.g., spouses, friends, neighbors) had similar levels of happiness. They did (z = 9.09).  I may be more likely to believe these findings because I have found this in my own research on married couples (Schimmack & Lucas, 2010).  Spouses are not only more similar to each other at one moment in time, they also change in the same direction over time.  However, the causal mechanism underlying this effect is more elusive.  Maybe happiness is contagious and can spread through social networks like a disease. However, it is also possible that related members in social networks are exposed to similar environments.  For example, spouses share a common household income and money buys some happiness.  It is even less clear whether these effects occur outside of people’s awareness or not.

Chapter 8 ends with the positive message that a single person can change the word because his or her actions influence many people. “The effect of just one act, multiplies and spreads to influence many other people. A single drop becomes a wave”  This rosy conclusion overlooks that the impact of one person decreases exponentially when it spreads over social networks. If you are kind to a neighbor, the neighbor may be slightly more likely to be kind to the pizza delivery man, but your effect on the pizza delivery man is already barely noticeable.  This may be a good thing when it comes to the spreading of negative behaviors.  Even if the friend of a friend is engaging in immoral behaviors, it doesn’t mean that you are more likely to commit a crime. To really change society it is important to change social norms and increase individuals’ reliance on these norms even when situational influences tell them otherwise.   The more people have a strong norm not to litter, the less it matters whether there are graffiti on the wall or not.

Chapter 8

Chapter 8 examines dishonesty and suggests that dishonesty is a general human tendency. “When the goal of achievement and high performance is active, people are more likely to bend the rules in ways they’d normally consider  dishonest and immoral, if doing so helps them attain their performance goal”

Of course, not all people cheat in all situations even if they think they can get away with it.  So, the interesting scientific question is who will be dishonest in which context?

Mazar et al. (2008) examined situational effects on dishonesty.  In Study 2 (z = 4.33) students were given an opportunity to cheat in order to receive a higher reward. The study had three conditions, a control condition that did not allow students to cheat, a cheating condition, and a cheating condition with an honor pledge.  In the honor pledge condition, the test started with the sentence “I understand that this short survey falls under MIT’s [Yale’s] honor system”.   This manipulation eliminated cheating.  However, even in the cheating condition “participants cheated only 13.5% of the possible average magnitude.  Thus, MIT/Yale students are rather honest or the incentive was too small to tempt them (an extra $2).  Study 3 found that students were more likely to cheat if they were rewarded with tokens rather than money, even though they later could exchange tokens for money.  The authors suggests that cheating merely for tokens rather than real money made it seem less like “real” cheating (z = 6.72).

Serious immoral acts cannot be studied experimentally in a psychology laboratory.  Therefore, research on this topic has to rely on self-report and correlations. Pryor (1987) developed a questionnaire to study “Sexual Harassment Proclivities in Men.”  The questionnaire asks men to imagine being in a position of power and to indicate whether they would take advantage of their power to incur sexual favors if they know they can get away with it.  To validate the scale, Pryor showed that it correlated with a scale that measures how much men buy into rape myths (r = .40, z = 4.47).   Self-reports on these measures have to be taken with a grain of salt, but the results suggest that some men are willing to admit that they would abuse power to gain sexual favors, at least in anonymous questionnaires.

Another noteworthy study found that even prisoners are not always dishonest. Cohn et al. (2015) used a gambling task to study dishonesty in 182 prisoners in a maximum security prison.  Participants were given the opportunity to flip 10 coins and to keep all coins that showed head.  Importantly, the coin toss was not observed.  As it is possible, although unlikely, that all 10 coins show head by chance, inmates could keep all coins and hide behind chance.  The randomness of the outcome makes it impossible to accuse a particular prisoner of dishonesty.  Nevertheless, the task makes it possible to measure dishonesty of the group (collective dishonesty) because the percentage of coin tosses that were reported should be close to chance (50%). If it is significantly higher than chance, it shows that some prisoners were dishonest. On average, prisoners reported 60% head, which reveals some dishonesty, but even convicted criminals were more likely to respond honestly than not (the percentage increased from 60% to 66% when they were primed with their criminal identity, z = 2.39).

I see some parallels between the gambling task and the world of scientific publishing, at least in psychology.  The outcome of a study is partially determined by random factors. Even if a scientist does everything right, a study may produce a non-significant result due to random sampling error. The probability of observing a non-significant result is called a type-II error. The probability of observing a significant result is called statistical power.  Just like in a coin toss experiment, the observed percentage of significant results should match the expected percentage based on average power.  Numerous studies have shown that researchers report more significant results than the power of their studies justifies. As in the coin toss experiment, it is not possible to point the finger at a single outcome because chance might have been in a researcher’s favor, but in the long run the odds “cannot be always in your favor” (Hunger Games).  Psychologists disagree whether the excess of significant results in psychology journals should be attributed to dishonesty.  I think it is and it fits Bargh’s observation that humans, and most scientists are humans, have a tendency to bend the rules when doing so helps them to reach their goal, especially when the goal is highly relevant (e.g., get a job, get a grant, get tenure). Sadly, the extent of over-reporting significant results is considerably larger than the 10 to 15% overreporting of heads in the prisoner study.

Chapter 9

Chapter 9 introduces readers to Metcalfe’s work on insight problems (e.g., how to put 27 animals into 4 pens so that there is an odd number of animals in all four pens).  Participants had to predict quickly whether they would be able to solve the problem. They then got 5 minutes to actually solve the problem. Participants were not able to predict accurately which insight problems they would solve.  Metcalfe concluded that the solution for insight problems comes during a moment of sudden illumination that is not predictable.  Bargh adds “This is because the solver was working on the problem unconsciously, and when she reached a solution, it was delivered to her fully formed and ready for use.”  In contrast, people are able to predict memory performance on a recognition test, even when they were not able to recall the answer immediately.  This phenomenon is known as the tip-of-the-tongue effect (z = 5.02).  This phenomenon shows that we have access to our memory even before we can recall the final answer.  This phenomenon is similar to the feeling of familiarity that is created by mere exposure (Zajonc, 1968). We often know a face is familiar without being able to recall specific memories where we encountered it.

The only other noteworthy study in Chapter 9 was a study of sleep quality (Fichten et al., 2001).  “The researchers found that by far, the most common type of thought that kept them awake, nearly 50 percent of them, was about the future, the short-term events coming up in the next day or week. Their thoughts were about what they needed to get done the following day, or in the next few days.”   It is true that 48% thought about future short-term events, but only 1% described these thoughts as worries, and 57% of these thoughts were positive.  It is not clear, however, whether this category distinguished good and poor sleepers.  What distinguished good sleepers from poor sleepers, especially those with high distress, was the frequency of negative thoughts (z = 5.59).

Chapter 10

Chapter 10 examines whether it is possible to control automatic impulses. Ample research by personality psychologists suggests that controlling impulses is easier for some people than others.  The ability to exert self-control is often measured with self-report measures that predict objective life outcomes.

However, the book adds a twist to self-control. “The most effective self-control is not through willpower and exerting effort to stifle impulses and unwanted behaviors. It comes from effectively harnessing the unconscious powers of the mind to much more easily do the self-control for you.”

There is a large body of strong evidence that some individuals, those with high impulse control and conscientiousness, perform better academically or at work (Tangney et al., 2004; Study 1 z = 5.90, Galla & Duckworth, Studies 1, 4, & 6, Ns = 488, 7.62, 5.18).  Correlations between personality measures and outcomes do not reveal the causal mechanism that leads to these positive outcomes.  Bargh suggests that individuals who score high on self-control measures are “the ones who do the good things less consciously, more automatically, and more habitually. And you can certainly do the same.”   This maybe true, but empirical work to demonstrate this is hard to find.  At the end of the chapter, Bargh cites a recent study by Milyavskaya and Michael Inzlicht that suggested avoiding temptations is more important than being able to exert self-control in the face of temptation, willful or unconsciously.

Conclusion

The book “Before you know it: The unconscious reasons we do what we do” is based on the authors’ personal experiences, studies he has conducted, and studies he has read. The author is a scientist and I have no doubt that he shares with his readers insights that he believes to be true.  However, this does not automatically make them true.  John Bargh is well aware that many psychologists are skeptical about some of the findings that are used in the book.  Famously, some of Bargh’s own studies have been difficult to replicate.  One response to concerns about replicability could have been new demonstrations that important unconscious priming effects can be replicated. In an interview Tom Bartlett (January, 2013) suggested this to John Bargh.

“So why not do an actual examination? Set up the same experiments again, with additional safeguards. It wouldn’t be terribly costly. No need for a grant to get undergraduates to unscramble sentences and stroll down a hallway. Bargh says he wouldn’t want to force his graduate students, already worried about their job prospects, to spend time on research that carries a stigma. Also, he is aware that some critics believe he’s been pulling tricks, that he has a “special touch” when it comes to priming, a comment that sounds like a compliment but isn’t. “I don’t think anyone would believe me,” he says.”

Beliefs are subjective.  Readers of the book have their own beliefs and may find part of the book interesting and may be willing to change some of their beliefs about human behavior.  Not that there is anything wrong with this, but readers should also be aware that it is reasonable to treat the ideas presented in this book with a healthy does of skepticism.  In 2011, Daniel Kahneman wrote ““disbelief is not an option. The results are not made up, nor are they statistical flukes. You have no choice but to accept that the major conclusions of these studies are true.”  Five years later, it is pretty clear that Kahneman is more skeptical about the state of priming research and results of experiments with small samples in general.  Unfortunately, it is not clear which studies we can believe until replication studies distinguish real effects from statistical flukes. So, until we have better evidence, we are still free to belief what we want about the power of unconscious forces on our behavior.

 

Reconstruction of a Train Wreck: How Priming Research Went off the Rails

This blog post focusses on Chapter 4 about Implicit Priming in Kahneman’s book “Thinking” Fast and Slow.”  A review of the book and other chapters can be found here: https://replicationindex.com/2020/12/30/a-meta-scientific-perspective-on-thinking-fast-and-slow/

Authors:  Ulrich Schimmack, Moritz Heene, and Kamini Kesavan

Abstract:
We computed the R-Index for studies cited in Chapter 4 of Kahneman’s book “Thinking Fast and Slow.” This chapter focuses on priming studies, starting with John Bargh’s study that led to Kahneman’s open email.  The results are eye-opening and jaw-dropping.  The chapter cites 12 articles and 11 of the 12 articles have an R-Index below 50.  The combined analysis of 31 studies reported in the 12 articles shows 100% significant results with average (median) observed power of 57% and an inflation rate of 43%.  The R-Index is 14. This result confirms Kahneman’s prediction that priming research is a train wreck and readers of his book “Thinking Fast and Slow” should not consider the presented studies as scientific evidence that subtle cues in their environment can have strong effects on their behavior outside their awareness.

Introduction

In 2011, Nobel Laureate Daniel Kahneman published a popular book, “Thinking Fast and Slow”, about important finding in social psychology.

In the same year, questions about the trustworthiness of social psychology were raised.  A Dutch social psychologist had fabricated data. Eventually over 50 of his articles would be retracted.  Another social psychologist published results that appeared to demonstrate the ability to foresee random future events (Bem, 2011). Few researchers believed these results and statistical analysis suggested that the results were not trustworthy (Francis, 2012; Schimmack, 2012).  Psychologists started to openly question the credibility of published results.

In the beginning of 2012, Doyen and colleagues published a failure to replicate a prominent study by John Bargh that was featured in Daniel Kahneman’s book.  A few month later, Daniel Kahneman distanced himself from Bargh’s research in an open email addressed to John Bargh (Young, 2012):

“As all of you know, of course, questions have been raised about the robustness of priming results…. your field is now the poster child for doubts about the integrity of psychological research… people have now attached a question mark to the field, and it is your responsibility to remove it… all I have personally at stake is that I recently wrote a book that emphasizes priming research as a new approach to the study of associative memory…Count me as a general believer… My reason for writing this letter is that I see a train wreck looming.”

Five years later, Kahneman’s concerns have been largely confirmed. Major studies in social priming research have failed to replicate and the replicability of results in social psychology is estimated to be only 25% (OSC, 2015).

Looking back, it is difficult to understand the uncritical acceptance of social priming as a fact.  In “Thinking Fast and Slow” Kahneman wrote “disbelief is not an option. The results are not made up, nor are they statistical flukes. You have no choice but to accept that the major conclusions of these studies are true.”

Yet, Kahneman could have seen the train wreck coming. In 1971, he co-authored an article about scientists’ “exaggerated confidence in the validity of conclusions based on small samples” (Tversky & Kahneman, 1971, p. 105).  Yet, many of the studies described in Kahneman’s book had small samples.  For example, Bargh’s priming study used only 30 undergraduate students to demonstrate the effect.

Replicability Index

Small samples can be sufficient to detect large effects. However, small effects require large samples.  The probability of replicating a published finding is a function of sample size and effect size.  The Replicability Index (R-Index) makes it possible to use information from published results to predict how replicable published results are.

Every reported test-statistic can be converted into an estimate of power, called observed power. For a single study, this estimate is useless because it is not very precise. However, for sets of studies, the estimate becomes more precise.  If we have 10 studies and the average power is 55%, we would expect approximately 5 to 6 studies with significant results and 4 to 5 studies with non-significant results.

If we observe 100% significant results with an average power of 55%, it is likely that studies with non-significant results are missing (Schimmack, 2012).  There are too many significant results.  This is especially true because average power is also inflated when researchers report only significant results. Consequently, the true power is even lower than average observed power.  If we observe 100% significant results with 55% average powered power, power is likely to be less than 50%.

This is unacceptable. Tversky and Kahneman (1971) wrote “we refuse to believe that a serious investigator will knowingly accept a .50 risk of failing to confirm a valid research hypothesis.”

To correct for the inflation in power, the R-Index uses the inflation rate. For example, if all studies are significant and average power is 75%, the inflation rate is 25% points.  The R-Index subtracts the inflation rate from average power.  So, with 100% significant results and average observed power of 75%, the R-Index is 50% (75% – 25% = 50%).  The R-Index is not a direct estimate of true power. It is actually a conservative estimate of true power if the R-Index is below 50%.  Thus, an R-Index below 50% suggests that a significant result was obtained only by capitalizing on chance, although it is difficult to quantify by how much.

How Replicable are the Social Priming Studies in “Thinking Fast and Slow”?

Chapter 4: The Associative Machine

4.1.  Cognitive priming effect

In the 1980s, psychologists discovered that exposure to a word causes immediate and measurable changes in the ease with which many related words can be evoked.

[no reference provided]

4.2.  Priming of behavior without awareness

Another major advance in our understanding of memory was the discovery that priming is not restricted to concepts and words. You cannot know this from conscious experience, of course, but you must accept the alien idea that your actions and your emotions can be primed by events of which you are not even aware.

“In an experiment that became an instant classic, the psychologist John Bargh and his collaborators asked students at New York University—most aged eighteen to twenty-two—to assemble four-word sentences from a set of five words (for example, “finds he it yellow instantly”). For one group of students, half the scrambled sentences contained words associated with the elderly, such as Florida, forgetful, bald, gray, or wrinkle. When they had completed that task, the young participants were sent out to do another experiment in an office down the hall. That short walk was what the experiment was about. The researchers unobtrusively measured the time it took people to get from one end of the corridor to the other.”

“As Bargh had predicted, the young people who had fashioned a sentence from words with an elderly theme walked down the hallway significantly more slowly than the others. walking slowly, which is associated with old age.”

“All this happens without any awareness. When they were questioned afterward, none of the students reported noticing that the words had had a common theme, and they all insisted that nothing they did after the first experiment could have been influenced by the words they had encountered. The idea of old age had not come to their conscious awareness, but their actions had changed nevertheless.“

[John A. Bargh, Mark Chen, and Lara Burrows, “Automaticity of Social Behavior: Direct Effects of Trait Construct and Stereotype Activation on Action,” Journal of Personality and Social Psychology 71 (1996): 230–44.]

t(28)=2.86 0.008 2.66 0.76
t(28)=2.16 0.039 2.06 0.54

MOP = .65, Inflation = .35, R-Index = .30

4.3.  Reversed priming: Behavior primes cognitions

“The ideomotor link also works in reverse. A study conducted in a German university was the mirror image of the early experiment that Bargh and his colleagues had carried out in New York.”

“Students were asked to walk around a room for 5 minutes at a rate of 30 steps per minute, which was about one-third their normal pace. After this brief experience, the participants were much quicker to recognize words related to old age, such as forgetful, old, and lonely.”

“Reciprocal priming effects tend to produce a coherent reaction: if you were primed to think of old age, you would tend to act old, and acting old would reinforce the thought of old age.”

t(18)=2.10 0.050 1.96 0.50
t(35)=2.10 0.043 2.02 0.53
t(31)=2.50 0.018 2.37 0.66

MOP = .53, Inflation = .47, R-Index = .06

4.4.  Facial-feedback hypothesis (smiling makes you happy)

“Reciprocal links are common in the associative network. For example, being amused tends to make you smile, and smiling tends to make you feel amused….”

“College students were asked to rate the humor of cartoons from Gary Larson’s The Far Side while holding a pencil in their mouth. Those who were “smiling” (without any awareness of doing so) found the cartoons funnier than did those who were “frowning.”

[“Inhibiting and Facilitating Conditions of the Human Smile: A Nonobtrusive Test of the Facial Feedback Hypothesis,” Journal of Personality and Social Psychology 54 (1988): 768–77.]

The authors used the more liberal and unconventional criterion of p < .05 (one-tailed), z = 1.65, as a criterion for significance. Accordingly, we adjusted the R-Index analysis and used 1.65 as the criterion value.

t(89)=1.85 0.034 1.83 0.57
t(75)=1.78 0.034 1.83 0.57

MOP = .57, Inflation = .43, R-Index = .14

These results could not be replicated in a large replication effort with 17 independent labs. Not a single lab produced a significant result and even a combined analysis failed to show any evidence for the effect.

4.5. Automatic Facial Responses

In another experiment, people whose face was shaped into a frown (by squeezing their eyebrows together) reported an enhanced emotional response to upsetting pictures—starving children, people arguing, maimed accident victims.

[Ulf Dimberg, Monika Thunberg, and Sara Grunedal, “Facial Reactions to

Emotional Stimuli: Automatically Controlled Emotional Responses,” Cognition and Emotion, 16 (2002): 449–71.]

The description in the book does not match any of the three studies reported in this article. The first two studies examined facial muscle movements in response to pictures of facial expressions (smiling or frowning faces).  The third study used emotional pictures of snakes and flowers. We might consider the snake pictures as being equivalent to pictures of starving children or maimed accident victims.  Participants were also asked to frown or to smile while looking at the pictures. However, the dependent variable was not how they felt in response to pictures of snakes, but rather how their facial muscles changed.  Aside from a strong effect of instructions, the study also found that the emotional picture had an automatic effect on facial muscles.  Participants frowned more when instructed to frown and looking at a snake picture than when instructed to frown and looking at a picture of a flower. “This response, however, was larger to snakes than to flowers as indicated by both the Stimulus factor, F(1, 47) = 6.66, p < .02, and the Stimulus 6 Interval factor, F(1, 47) = 4.30, p < .05.”  (p. 463). The evidence for smiling was stronger. “The zygomatic major muscle response was larger to flowers than to snakes, which was indicated by both the Stimulus factor, F(1, 47) = 18.03, p < .001, and the Stimulus 6 Interval factor, F(1, 47) = 16.78, p < .001.”  No measures of subjective experiences were included in this study.  Therefore, the results of this study provide no evidence for Kahneman’s claim in the book and the results of this study are not included in our analysis.

4.6.  Effects of Head-Movements on Persuasion

“Simple, common gestures can also unconsciously influence our thoughts and feelings.”

“In one demonstration, people were asked to listen to messages through new headphones. They were told that the purpose of the experiment was to test the quality of the audio equipment and were instructed to move their heads repeatedly to check for any distortions of sound. Half the participants were told to nod their head up and down while others were told to shake it side to side. The messages they heard were radio editorials.”

“Those who nodded (a yes gesture) tended to accept the message they heard, but those who shook their head tended to reject it. Again, there was no awareness, just a habitual connection between an attitude of rejection or acceptance and its common physical expression.”

F(2,66)=44.70 0.000 7.22 1.00

MOP = 1.00, Inflation = .00,  R-Index = 1.00

[Gary L. Wells and Richard E. Petty, “The Effects of Overt Head Movements on Persuasion: Compatibility and Incompatibility of Responses,” Basic and Applied Social Psychology, 1, (1980): 219–30.]

4.7   Location as Prime

“Our vote should not be affected by the location of the polling station, for example, but it is.”

“A study of voting patterns in precincts of Arizona in 2000 showed that the support for propositions to increase the funding of schools was significantly greater when the polling station was in a school than when it was in a nearby location.”

“A separate experiment showed that exposing people to images of classrooms and school lockers also increased the tendency of participants to support a school initiative. The effect of the images was larger than the difference between parents and other voters!”

[Jonah Berger, Marc Meredith, and S. Christian Wheeler, “Contextual Priming: Where People Vote Affects How They Vote,” PNAS 105 (2008): 8846–49.]

z = 2.10 0.036 2.10 0.56
p = .05 0.050 1.96 0.50

MOP = .53, Inflation = .47, R-Index = .06

4.8  Money Priming

“Reminders of money produce some troubling effects.”

“Participants in one experiment were shown a list of five words from which they were required to construct a four-word phrase that had a money theme (“high a salary desk paying” became “a high-paying salary”).”

“Other primes were much more subtle, including the presence of an irrelevant money-related object in the background, such as a stack of Monopoly money on a table, or a computer with a screen saver of dollar bills floating in water.”

“Money-primed people become more independent than they would be without the associative trigger. They persevered almost twice as long in trying to solve a very difficult problem before they asked the experimenter for help, a crisp demonstration of increased self-reliance.”

“Money-primed people are also more selfish: they were much less willing to spend time helping another student who pretended to be confused about an experimental task. When an experimenter clumsily dropped a bunch of pencils on the floor, the participants with money (unconsciously) on their mind picked up fewer pencils.”

“In another experiment in the series, participants were told that they would shortly have a get-acquainted conversation with another person and were asked to set up two chairs while the experimenter left to retrieve that person. Participants primed by money chose to stay much farther apart than their nonprimed peers (118 vs. 80 centimeters).”

“Money-primed undergraduates also showed a greater preference for being alone.”

[Kathleen D. Vohs, “The Psychological Consequences of Money,” Science 314 (2006): 1154–56.]

F(2,49)=3.73 0.031 2.16 0.58
t(35)=2.03 0.050 1.96 0.50
t(37)=2.06 0.046 1.99 0.51
t(42)=2.13 0.039 2.06 0.54
F(2,32)=4.34 0.021 2.30 0.63
t(38)=2.13 0.040 2.06 0.54
t(33)=2.37 0.024 2.26 0.62
F(2,58)=4.04 0.023 2.28 0.62
chi^2(2)=10.10 0.006 2.73 0.78

MOP = .58, Inflation = .42, R-Index = .16

4.9  Death Priming

“The evidence of priming studies suggests that reminding people of their mortality increases the appeal of authoritarian ideas, which may become reassuring in the context of the terror of death.”

The cited article does not directly examine this question.  The abstract states that “three experiments were conducted to test the hypothesis, derived from terror management theory, that reminding people of their mortality increases attraction to those who consensually validate their beliefs and decreases attraction to those who threaten their beliefs” (p. 308).  Study 2 found no general effect of death priming. Rather, the effect was qualified by authoritarianism. Mortality salience enhanced the rejection of dissimilar others in Study 2 only among high authoritarian subjects.” (p. 314), based on a three-way interaction with F(1,145) = 4.08, p = .045.  We used the three-way interaction for the computation of the R-Index.  Study 1 reported opposite effects for ratings of Christian targets, t(44) = 2.18, p = .034 and Jewish targets, t(44)= 2.08, p = .043. As these tests are dependent, only one test could be used, and we chose the slightly stronger result.  Similarly, Study 3 reported significantly more liking of a positive interviewee and less liking of a negative interviewee, t(51) = 2.02, p = .049 and t(49) = 2.42, p = .019, respectively. We chose the stronger effect.

[Jeff Greenberg et al., “Evidence for Terror Management Theory II: The Effect of Mortality Salience on Reactions to Those Who Threaten or Bolster the Cultural Worldview,” Journal of Personality and Social Psychology]

t(44)=2.18 0.035 2.11 0.56
F(1,145)=4.08 0.045 2.00 0.52
t(49)=2.42 0.019 2.34 0.65

MOP = .56, Inflation = .44, R-Index = .12

4.10  The “Lacy Macbeth Effect”

“For example, consider the ambiguous word fragments W_ _ H and S_ _ P. People who were recently asked to think of an action of which they are ashamed are more likely to complete those fragments as WASH and SOAP and less likely to see WISH and SOUP.”

“Furthermore, merely thinking about stabbing a coworker in the back leaves people more inclined to buy soap, disinfectant, or detergent than batteries, juice, or candy bars. Feeling that one’s soul is stained appears to trigger a desire to cleanse one’s body, an impulse that has been dubbed the “Lady Macbeth effect.”

[Lady Macbeth effect”: Chen-Bo Zhong and Katie Liljenquist, “Washing Away Your Sins:

Threatened Morality and Physical Cleansing,” Science 313 (2006): 1451–52.]

F(1,58)=4.26 0.044 2.02 0.52
F(1,25)=6.99 0.014 2.46 0.69

MOP = .61, Inflation = .39, R-Index = .22

The article reports two more studies that are not explicitly mentioned, but are used as empirical support for the Lady Macbeth effect. As the results of these studies were similar to those in the mentioned studies, including these tests in our analysis does not alter the conclusions.

chi^2(1)=4.57 0.033 2.14 0.57
chi^2(1)=5.02 0.025 2.24 0.61

MOP = .59, Inflation = .41, R-Index = .18

4.11  Modality Specificity of the “Lacy Macbeth Effect”

“Participants in an experiment were induced to “lie” to an imaginary person, either on the phone or in e-mail. In a subsequent test of the desirability of various products, people who had lied on the phone preferred mouthwash over soap, and those who had lied in e-mail preferred soap to mouthwash.”

[Spike Lee and Norbert Schwarz, “Dirty Hands and Dirty Mouths: Embodiment of the Moral-Purity Metaphor Is Specific to the Motor Modality Involved in Moral Transgression,” Psychological Science 21 (2010): 1423–25.]

The results are presented as significant with a one-sided t-test. “As shown in Figure 1a, participants evaluated mouthwash more positively after lying in a voice mail (M = 0.21, SD = 0.72) than after lying in an e-mail (M = –0.26, SD = 0.94), F(1, 81) = 2.93, p = .03 (one-tailed), d = 0.55 (simple main effect), but evaluated hand sanitizer more positively after lying in an e-mail (M = 0.31, SD = 0.76) than after lying in a voice mail (M = –0.12, SD = 0.86), F(1, 81) = 3.25, p = .04 (one-tailed), d = 0.53 (simple main effect).”  We adjusted the significance criterion for the R-Index accordingly.

F(1,81)=2.93 0.045 1.69 0.52
F(1,81)=3.25 0.038 1.78 0.55

MOP = .54, Inflation = .46, R-Index = .08

4.12   Eyes on You

“On the first week of the experiment (which you can see at the bottom of the figure), two wide-open eyes stare at the coffee or tea drinkers, whose average contribution was 70 pence per liter of milk. On week 2, the poster shows flowers and average contributions drop to about 15 pence. The trend continues. On average, the users of the kitchen contributed almost three times as much in ’eye weeks’ as they did in ’flower weeks.’ ”

[Melissa Bateson, Daniel Nettle, and Gilbert Roberts, “Cues of Being Watched Enhance Cooperation in a Real-World Setting,” Biology Letters 2 (2006): 412–14.]

F(1,7)=11.55 0.011 2.53 0.72

MOP = .72, Inflation = .28, R-Index = .44

Combined Analysis

We then combined the results from the 31 studies mentioned above.  While the R-Index for small sets of studies may underestimate replicability, the R-Index for a large set of studies is more accurate.  Median Obesrved Power for all 31 studies is only 57%. It is incredible that 31 studies with 57% power could produce 100% significant results (Schimmack, 2012). Thus, there is strong evidence that the studies provide an overly optimistic image of the robustness of social priming effects.  Moreover, median observed power overestimates true power if studies were selected to be significant. After correcting for inflation, the R-Index is well below 50%.  This suggests that the studies have low replicability. Moreover, it is possible that some of the reported results are actually false positive results.  Just like the large-scale replication of the facial feedback studies failed to provide any support for the original findings, other studies may fail to show any effects in large replication projects. As a result, readers of “Thinking Fast and Slow” should be skeptical about the reported results and they should disregard Kahneman’s statement that “you have no choice but to accept that the major conclusions of these studies are true.”  Our analysis actually leads to the opposite conclusion. “You should not accept any of the conclusions of these studies as true.”

k = 31,  MOP = .57, Inflation = .43, R-Index = .14,  Grade: F for Fail

Powergraph of Chapter 4kfs

Schimmack and Brunner (2015) developed an alternative method for the estimation of replicability.  This method takes into account that power can vary across studies. It also provides 95% confidence intervals for the replicability estimate.  The results of this method are presented in the Figure above. The replicability estimate is similar to the R-Index, with 14% replicability.  However, due to the small set of studies, the 95% confidence interval is wide and includes values above 50%. This does not mean that we can trust the published results, but it does suggest that some of the published results might be replicable in larger replication studies with more power to detect small effects.  At the same time, the graph shows clear evidence for a selection effect.  That is, published studies in these articles do not provide a representative picture of all the studies that were conducted.  The powergraph shows that there should have been a lot more non-significant results than were reported in the published articles.  The selective reporting of studies that worked is at the core of the replicability crisis in social psychology (Sterling, 1959, Sterling et al., 1995; Schimmack, 2012).  To clean up their act and to regain trust in published results, social psychologists have to conduct studies with larger samples that have more than 50% power (Tversky & Kahneman, 1971) and they have to stop reporting only significant results.  We can only hope that social psychologists will learn from the train wreck of social priming research and improve their research practices.

Replicability Report No.2: Do Mating Primes have a replicable effects on behavior?

In 2000, APA declared the following decade the decade of behavior.  The current decade may be considered the decade of replicability or rather the lack thereof.  The replicability crisis started with the publication of Bem’s (2011) infamous “Feeling the future” article.  In response, psychologists have started the painful process of self-examination.

Preregistered replication reports and systematic studies of reproducibility have demonstrated that many published findings are difficult to replicate and when they can be replicated, actual effect sizes are about 50% smaller than reported effect sizes in original articles (OSC, Science, 2016).

To examine which studies in psychology produced replicable results, I created ReplicabilityReports.  Replicability reports use statistical tools that can detect publication bias and questionable research practices to examine the replicability of research findings in a particular research area.  The first replicability report examined the large literature of ego-depletion studies and found that only about a dozen studies may have produced replicable results.

This replicability report focuses on a smaller literature that used mating primes (images of potential romantic partners / imagining a romantic scenario) to test evolutionary theories of human behavior.  Most studies use the typical priming design, where participants are randomly assigned to one or more mating prime conditions or a control condition. After the priming manipulation the effect of activating mating-related motives and thoughts on a variety of measures is examined.  Typically, an interaction with gender is predicted with the hypothesis that mating primes have stronger effects on male participants. Priming manipulations vary from subliminal presentations to instructions to think about romantic scenarios for several minutes; sometimes with the help of visual stimuli.  Dependent variables range from attitudes towards risk-taking to purchasing decisions.

Shanks et al. (2015) conducted a meta-analysis of a subset of mating priming studies that focus on consumption and risk-taking.  A funnel plot showed clear evidence of bias in the published literature.  The authors also conducted several replication studies. The replication studies failed to produce any significant results. Although this outcome might be due to low power to detect small effects, a meta-analysis of all replication studies also produced no evidence for reliable priming effects (average d = 00, 95%CI = -.12 | .11).

This replicability report aims to replicate and extend Shanks et al.’s findings in three ways.  First, I expanded the data base by including all articles that mentioned the word mating primes in a full text search of social psychology journals.  This expanded the set of articles from 15 to 36 articles and the set of studies from 42 to 92. Second, I used a novel and superior bias test.  Shanks et al. used Funnel plots and Egger’s regression of effect sizes on sampling error to examine bias. The problem with this approach is that heterogeneity in effect sizes can produce a negative correlation between effect sizes and sample sizes.  Power-based bias tests do not suffer from this problem (Schimmack, 2014).  A set of studies with average power of 60% cannot produce more than 60% significant results (Sterling et al., 1995).  Thus, the discrepancy between observed power and reported success rate provides clear evidence of selection bias. Powergraphs also make it possible to estimate the actual power of studies after correcting for publication bias and questionable research practices.  Finally, replicability reports use bias tests that can be applied to small sets of studies.  This makes it possible to find studies with replicable results even if most studies have low replicability.

DESCRIPTIVE STATISTICS

The dataset consists of 36 articles and 92 studies. The median sample size of a study was N = 103 and the total number of participants was N = 11,570. The success rate including marginally significant results, z > 1.65, was 100%.  The success rate excluding marginally significant results, z > 1.96, was 90%.  Median observed power for all 92 studies was 66%.  This discrepancy shows that the published results are biased towards significance.  When bias is present, median observed power overestimates actual power.  To correct for this bias, the R-Index subtracts the inflation rate from median observed power.  The R-Index is 66 – 34 = 32.  An R-Index below 50% implies that most studies will not replicate a significant result in an exact replication study with the same sample size and power as the original studies.  The R-Index for the 15 studies included in Shanks et al. was 34% and the R-Index for the additional studies was 36%.  This shows that convergent results were obtained for two independent samples based on different sampling procedures and that Shanks et al.’s limited sample was representative of the wider literature.

POWERGRAPH

For each study, a focal hypothesis test was identified and the result of the statistical test was converted into an absolute z-score.  These absolute z-scores can vary as a function of random sampling error or differences in power and should follow a mixture of normal distributions.  Powergraphs find the best mixture model that minimizes the discrepancy between observed and predicted z-scores.

Powergraph for Romance Priming (Focal Tests)

 

The histogram of z-scores shows clear evidence of selection bias. The steep cliff on the left side of the criterion for significance (z = 1.96) shows a lack of non-significant results.  The few non-significant results are all in the range of marginal significance and were reported as evidence for an effect.

The histogram also shows evidence of the use of questionable research practices. Selection bias would only produce a cliff to the left of the significance criterion, but a mixture-normal distribution on the right side of the significance criterion. However, the graph also shows a second cliff around z = 2.8.  This cliff can be explained by questionable research practices that inflate effect sizes to produce significant results.  These questionable research practices are much more likely to produce z-scores in the range between 2 and 3 than z-scores greater than 3.

The large amount of z-scores in the range between 1.96 and 2.8 makes it impossible to distinguish between real effects with modest power and questionable effects with much lower power that will not replicate.  To obtain a robust estimate of power, power is estimated only for z-scores greater than 2.8 (k = 17).  The power estimate is 73% based. This power estimate suggests that some studies may have reported real effects that can be replicated.

The grey curve shows the predicted distribution for a set of studies with 73% power.  As can be seen, there are too many observed z-scores in the range between 1.96 and 2.8 and too few z-scores in the range between 0 and 1.96 compared to the predicted distribution based on z-scores greater than 2.8.

The powergraph analysis confirms and extends Shanks et al.’s (2016) findings. First, the analysis provides strong evidence that selection bias and questionable research practices contribute to the high success rate in the mating-prime literature.  Second, the analysis suggests that a small portion of studies may actually have reported true effects that can be replicated.

REPLICABILITY OF INDIVIDUAL ARTICLES

The replicability of results published in individual articles was examined with the Test of Insufficient Variance (TIVA) and the Replicability-Index.  TIVA tests bias by comparing the variance of observed z-scores against the variance that is expected based on sampling error.  As sampling error for z-scores is 1, observed z-scores should have at least a variance of 1. If there is heterogeneity, variance can be even greater, but it cannot be smaller than 1.  TIVA uses the chi-square test for variances to compute the probability that a variance less than 1 was simply due to chance.  A p-value less than .10 is used to flag an article as questionable.

The Replicability-Index (R-Index) used observed power to test bias. Z-scores are converted into a measure of observed power and median observed power is used as an estimate of power.  The success rate (percentage of significant results) should match observed power.  The difference between success rate and median power shows an inflated success rate.  The R-Index subtracts inflation from median observed power.  A value of 50% is used as the minimum criterion for replicability.

Articles that pass both tests are examined in more detail to identify studies with high replicability.  Only three articles passed this test.

1   Greitemeyer, Kastenmüller, and Fischer (2013) [R-Index = .80]

The article with the highest R-Index reported 4 studies.  The high R-Index for this article is due to Studies 2 to 4.  Studies 3 and 4 used a 2 x 3 between subject design with gender and three priming conditions. Both studies produced strong evidence for an interaction effect, Study 3: F(2,111) = 12.31, z = 4.33, Study 4: F(2,94) = 7.46, z = 3.30.  The pattern of the interaction is very similar in the two studies.  For women, the means are very similar and not significantly different for each other.  For men, the two mating prime conditions are very similar and significantly different from the control condition.  The standardized effect sizes for the difference between the combined mating prime conditions and the control conditions are large, Study 3: t(110) = 6.09, p < .001, z = 5.64, d = 1.63; Study 4: t(94) = 5.12, d = 1.30.

Taken at face value, these results are highly replicable, but there are some concerns about the reported results. The means in conditions that are not predicted to differ from each other are very similar.  I tested the probability of this event to occur using TIVA and compared the means of the two mating prime conditions for men and women in the two studies.  The four z-scores were z = 0.53, 0.08, 0.09, and -0.40.  The variance should be 1, but the observed variance is only Var(z) = 0.14.  The probability of this reduction in variance to occur by chance is p = .056.  Thus, even though the overall R-Index for this article is high and the reported effect sizes are very high, it is likely that an actual replication study will produce weaker effects and may not replicate the original findings.

Study 2 also produced strong evidence for a priming x gender interaction, F(1,81) = 11.23, z = 3.23.  In contrast to studies 3 and 4, this interaction was a cross-over interaction with opposite effects of primes for males and females.  However, there is some concern about the reliability of this interaction because the post-hoc tests for males and females were both just significant, males: t(40) = 2.61, d = .82, females, t(41) = 2.10, d = .63.  As these post-hoc tests are essentially two independent studies, it is possible to use TIVA to test whether these results are too similar, Var(z) = 0.11, p = .25.  The R-Index for this set of studies is low, R-Index = .24 (MOP = .62).  Thus, a replication study may replicate an interaction effect, but the chance of replicating significant results for males or females separately are lower.

Importantly, Shanks et al. (2016) conducted two close replication of Greitemeyer’s studies with risky driving, gambling, and sexual risk taking as dependent variables.  Study 5 compared the effects of short-term mate primes on risky driving.  Although the sample size was small, the large effect size in the original study implies that this study had high power to replicate the effect, but it did not, t(77) = = -0.85, p = .40, z = -.85.  The negative sign indicates that the pattern of means was reversed, but not significantly so.  Study 6 failed to replicate the interaction effect for sexual risk taking reported by Greitemeyer et al., F(1, 93) = 1.15, p = .29.  The means for male participants were in the opposite direction showing a decrease in risk taking after mating priming.  The study also failed to replicate the significant decrease in risk taking for female participants.  Study 6 also produced non-significant results for gambling and substance risk taking.   These failed replication studies raise further concerns about the replicability of the original results with extremely large effect sizes.

Jon K. Maner, Matthew T. Gailliot, D. Aaron Rouby, and Saul L. Miller (JPSP, 2007) [R-Index = .62]

This article passed TIVA only due to the low power of TIVA for a set of three studies, TIVA: Var(z) = 0.15, p = .14.  In Study 1, male and female participants were randomly assigned to a sexual-arousal priming condition or a happiness control condition. Participants also completed a measure of socio-sexual orientation (i.e., interest in casual and risky sex) and were classified into groups of unrestricted and restricted participants. The dependent variable was performance on a dot-probe task.  In a dot-probe task, participants have to respond to a dot that appears in the location of two stimuli that compete for visual attention.  In theory, participants are faster to respond to the dot if appears in the location of a stimulus that attracts more attention.  Stimuli were pictures of very attractive or less attractive members of the same or opposite sex.  The time between the presentation of the pictures and the dot was also manipulated.  The authors reported that they predicted a three-way way interaction between priming condition, target picture, and stimulus-onset time.  The authors did not predict an interaction with gender.  The ANOVA showed a significant three-way interaction, F(1,111) = 10.40, p = .002, z = 3.15.  A follow-up two-way ANOVA showed an interaction between priming condition and target for unrestricted participants, F(1,111) = 7.69, p = .006, z = 2.72.

Study 2 replicated Study 1 with a sentence unscrambling task which is used as a subtler priming manipulation.  The study closely replicated the results of Study 1. The three way interaction was significant, F(1,153) = 9.11, and the follow up two-way interaction for unrestricted participants was also significant, F(1,153) = 8.22, z = 2.75.

Study 3 changed the primes to jealousy or anxiety/frustration.  Jealousy is a mating related negative emotion and was predicted to influence participants like mating primes.  In this study, participants were classified into groups with high or low sexual vigilance based on a jealousy scale.  The predicted three-way interaction was significant, F(1,153) = 5.74, p = .018, z = 2.37.  The follow-up two-way interaction only for participants high in sexual vigilance was also significant, F(1,153) = 8.13, p = .005, z = 2.81.

A positive feature of this set of studies is that the manipulation of targets within subjects reduces within-cell variability and increases power to produce significant results.  However, a problem is that the authors also report studies for specific targets and do not mention that they used reaction times to other targets as covariate. These analyses have low power due to the high variability in reaction times across participants.  However, surprisingly each study still produced the predicted significant result.

Study 1: “Planned analyses clarified the specific pattern of hypothesized effects. Multiple regression evaluated the hypothesis that priming would interact with participants’ sociosexual orientation to increase attentional adhesion to attractive opposite-sex targets. Attention to those targets was regressed on experimental condition, SOI, participant sex, and their centered interactions (nonsignificant interactions were dropped). Results confirmed the hypothesized interaction between priming condition and SOI, beta = .19, p < .05 (see Figure 1).”
I used r = .19 and N = 113 and obtained t(111) = 2.04, p = .043, z = 2.02.

Study 2: “Planned analyses clarified the specific pattern of hypothesized effects. Regression evaluated the hypothesis that the mate-search prime would interact with sociosexual orientation to increase attentional adhesion to attractive opposite-sex targets. Attention to these targets was regressed on experimental condition, SOI score, participant sex, and their centered interactions (nonsignificant interactions were dropped). As in Study 1, results revealed the predicted interaction between priming condition and sociosexual orientation, beta = .15, p = .04, one-tailed (see Figure 2)”
I used r = .15 and N = 155 and obtained t(153) = 1.88, p = .06 (two-tailed!), z = 1.86.

Study 3: “We also observed a significant main effect of intrasexual vigilance, beta = .25, p < .001, partial r = .26, and, more important, the hypothesized two-way interaction between priming condition and level of intrasexual vigilance, beta = .15, p < .05, partial r = .16 (see Figure 3).”
I used r = .16 and N = 155 and obtained t(153) = 2.00, p = .047, z = 1.99.

The problem is that the results of these three independent analyses are too similar, z = 2.02, 1.86, 1.99; Var(z) < .001, p = .007.

In conclusion, there are some concerns about the replicability of these results and even if the results replicate they do not provide support for the hypothesis that mating primes have a hard-wired effect on males. Only one of the three studies produced a significant two-way interaction between priming and target (F-value not reported), and none of the three studies produced a significant three-way interaction between priming, target, and gender.  Thus, the results are inconsistent with other studies that found either main effects of mating primes or mating prime by gender interactions.

3. Bram Van den Bergh and Siegfried Dewitte (Proc. R. Soc. B, 2006) [R-index = .58]

This article reports three studies that examined the influence of mating primes on behavior in the ultimatum game.

Study 1 had a small sample size of 40 male participants who were randomly assigned to seeing pictures of non-nude female models or landscapes.  The study produced a significant main effect, F(1,40) = 4.75, p = .035, z = 2.11, and a significant interaction with finger digit ratio, F(1,40) = 4.70, p = .036, z = 2.10.  I used the main effect for analysis because it is theoretically more important than the interaction effect, but the results are so similar that it does not matter which effect is used.

Study 2 used rating of women’s t-shirts or bras as manipulation. The study produced strong evidence that mating primes (rating bras) lead to lower minimum acceptance rates in the ultimatum game than the control condition (rating t-shirts), F(1,33) = 8.88, p = .005, z = 2.78.  Once more the study also produced a significant interaction with finger digit ratio, F(1,33) = 8.76, p = .006, z = 2.77.

Study 3 had three experimental conditions, namely non-sexual pictures of older and young women, and pictures of young non-nude female models.  The study produced a significant effect of condition, F(2,87) = 5.49, p = .006, z = 2.77.  Once more the interaction with finger-digit ratio was also significant, F(2,87) = 5.42.

This article barely passed the test of insufficient variance in the primary analysis that uses one focal test per study, Var(z) = 0.15, p = .14.  However, the main effect and the interaction effects are statistically independent and it is possible to increase the power of TIVA by using the z-scores for the three main effects and the three interactions.  This test produces significant evidence for bias, Var(z) = 0.12, p = .01.

In conclusion, it is unlikely that the results reported in this article will replicate.

CONCLUSION

The replicability crisis in psychology has created doubt about the credibility of published results.  Numerous famous priming studies have failed to replicate in large replication studies.  Shanks et al. (2016) reported problems with the specific literature of romantic and mating priming.  This replicability report provided further evidence that the mating prime literature is not credible.  Using an expanded set of 92 studies, analysis with powergraphs, the test of insufficient variance, and the replicability index showed that many significant results were obtained with the help of questionable research practices that inflate observed effect sizes and provide misleading evidence about the strength and replicability of published results.  Only three articles passed the test with TIVA and R-Index and detailed examination of these studies also showed statistical problems with the evidence in these articles.  Thus, this replicability analysis of 36 articles failed to identify a single credible article.  The lack of credible evidence is consistent with Shanks et al.’s failure to produce significant results in 15 independent replication studies.

Of course, these results do not imply that evolutionary theory is wrong or that sexual stimuli have no influence on human behavior.  For example, in my own research I have demonstrated that sexually arousing opposite-sex pictures capture men’s and women’s attention (Schimmack, 2005).  However, these responses occurred in response to specific stimuli and not as carry-over effects of a priming manipulation. Thus, the problem with mating prime studies is probably that priming effects are weak and may have no notable influence on unrelated behaviors like consumer behavior or risk taking in investments.  Given the replication problems with other priming studies, it seems necessary to revisit the theoretical assumptions underlying this paradigm.  For example, Shanks et al. (2016) pointed out that behavioral priming effects are theoretically implausible because these predictions contradict well-established theories that behavior is guided by the cognitive appraisal of the situation at hand rather than unconscious residual information from previous situations. This makes evolutionary sense because behavior has to respond to the adaptive problem at hand to ensure survival and reproduction.

I recommend that textbook writers, journalists, and aspiring social psychologists treat claims about human behavior based on mating priming studies with a healthy dose of skepticism.  The results reported in these articles may reveal more about the motives of researchers than their participants.

Who is Your Daddy? Priming women with a disengaged father increases their willingness to have sex without a condom

Edited and new postscript on Dec/4/2019

Photo credit: https://www.theblot.com/pole-dancing-daddy-fun-acrobatics-7767007
Who’s your daddy?  Priming women with a disengaged father increases their willingness to have sex without a condom.

In a five study article, Danielle J. DelPriore and Sarah E. Hill from Texas Christian University wanted to examine the influence of a disengaged father on daughter’s sexual attitudes and behaviors.

It is difficult to study the determinants of sexual behavior in humans because it is neither practical nor ethical to randomly assign daughters to engaged and distant fathers to see how this influences daughters’ sexual attitudes and behaviors.

Experimental social psychologists believe that they have found a solution to this problem.  Rather than exposing individuals to the actual experiences in the real world, it is possible to expose individuals to stimuli or stories related to these events.  These studies are called priming studies.  The assumption is that priming individuals has the same effect as experiencing these events.  For example, a daughter with a loving and caring partner will respond like a daughter with a distant father if she is randomly assigned to a condition with a parental disengagement prime.

This article reports five priming studies that examined how thinking about a distant father influences daughters’ sexual attitudes.

Study 1 (N = 75 female students)

Participants in the paternal disengagement condition read the following instructions:

Take a few seconds to think back to a time when your biological father was absent for an important life event when you really needed him . . .. Describe in detail how your father’s lack of support—or his physical or psychological absence—made you feel.

Participants in the paternal engagement condition were asked to describe a time their father was physically or psychologically present for an important event.

The dependent variable was a word-stem completion task with words that could be completed with words related to sex (s_x;  _aked;  sex vs. six; naked vs. baked).

Participants primed with a disengaged father completed more word-stems in a sexual manner (M = 4.51, SD = 2.06) than participants primed with an engaged father (M = 3.63, SD = 1.50), F(1,73) = 4.51, p = .037, d = .49.

Study 2 (N = 52 female students)

Study 2 used the same priming manipulation as Study 1, but measured sexual permissiveness with the Sociosexual Orientation Inventory (SOI; Simpson & Gangestad, 1991).  Example items are “sex without love is OK,” and “I can imagine myself being comfortable and enjoying casual sex with different partners.”

Participants who thought about a disengaged father had higher sexual permissiveness scores (M = 2.57, SD = 1.88) than those who thought about an engaged father (M = 1.86, SD = 0.94), F(1,62) = 3.91, p = .052, d = .48.

Study 3 (N = 82 female students)

Study 3 changed the control condition from an engaged father to a disengaged or disappointing friend.  It is not clear why this condition was not included as a third condition Study 2 but ran as a separate experiment. The study showed that participants who thought about a disengaged dad scored higher on the sexual permissiveness scale (M = 2.90, SD = 2.25) than participants who thought about a disappointing friend (M = 2.09, SD = 1.19), F(1,80) = 4.24, p = .043, d = .45.

Study 4 (N = 62 female students)

Study 4 used maternal disengagement as the control condition. Again, it is not clear why the researchers did not run one study with four conditions (disengaged father, engaged father, disappointing friend, disengaged mother).

Participants who thought about a disengaged dad had higher scores on the sexual permissiveness scale (M = 2.85, SD = 1.84) than participants who thought about a disengaged mother (M = 1.87, SD = 1.16), F(1, 60) = 6.03, p = .017, d = .64.

Study 5 (N = 85 female students & 92 male students)

Study 5 could have gone in many directions, but it included women and men as participants and used disappointing friends as the control condition (why not using engaged and disengaged mothers/fathers in a 2 x 2 design to see how gender influences parent-child relationships?).  Even more disappointing was that the only reported (!) dependent variable was attitudes towards condoms. Why was the sexual attitude measure dropped from Study 5?

The results showed a difference between male and female participants who thought about a disengaged dad or friend.  Participants reported more negative attitudes towards condoms after thinking about a disengaged dad (M ~ 3.4 based on Figure) than participants who thought about a disengaged friend (M = 2.9 ~ based on Figure), F(1,172) = 5.10, p = .025, d = 0.33.  The interaction with gender was not significant, p = .58, but the effect of the manipulation on attitudes towards condoms was marginally significant in an analysis limited to women, (M = 3.07, SD = 1.30; M = 2.51, SD = 1.35), F(1, 172)= 3.76, p = .054, d = 0.42.  Although the interaction was not significant, the authors conclude in the general discussion section that “the effects of primed paternal disengagement on sexual risk were also found to be stronger for women than for men (Experiment 5)” (p. 242).

CONCLUSION

Based on this set of five studies, the authors conclude that “the results of the current research provide the first experimental support for PIT [Parental Investment Theory] by demonstrating a causal relationship between paternal disengagement cues and changes in women’s sexual decision making” (p. 242).

They then propose that “insight gained from this research may help inform interventions aimed at reducing some of the personal and financial costs associated with father absence, including teen pregnancy and STI risk” (p. 242)

However, before researchers or lay people get too excited about these experimental findings, it is important to examine whether they are even credible findings.  Five successful studies may seem like strong evidence for the robustness of this effect, but unfortunately the reported studies cannot be taken at face value because scientific journals report only successful studies and it is not clear how many failed studies or analysis are not reported.

To examine the credibility and replicability of these reported findings, I ran a statistical test of the reported results.  These tests suggest that the results are not credible and unlikely to replicate in independent attempts to reproduce these studies.

NstatisticpzOP
75F(1,73)=4.510.0372.080.55
64F(1,62)=3.910.0521.940.49
82F(1,80)=4.240.0432.030.53
62F(1,60)=6.030.0172.390.67
177F(1,172)=5.100.0252.240.61

OP = observed power

The Test of Insufficient Variance (TIVA) shows that variance of z-scores is much less than random sampling error would produce, var(z) = 0.03 (expected 1.00), p < .01.   The median observed power is only 55% when the success rate is 100%, showing that the success rate is inflated. The Replicability Index is 55 – (100 – 55) = 10.  This value is below the value that is expected if only significant studies are selected from a set of studies without a real effect (22). A replicabilty index of 10 suggests that other researchers will not be able to replicate the significant results reported in this article.

Conclusion

This article does not contain credible evidence about the causes of male or female sexuality, and if you did grow up without a father or with a disengaged father it does not mean that this necessarily influenced your sexual attitudes, preferences, and behaviors.  Answers to these important questions are more likely to come from longitudinal studies of real family relationships than from priming studies that assume real world experiences can be simulated in a cheap laboratory study with priming.  However, social psychologists cherish the illusion that they are real scientists because they conduct research in ‘laboratories’ as if they are chemists or microbiologists.  Somebody needs to tell them that climate science, astronomy, and zoology are real sciences, too.  The rise and fall of priming studies will be an interesting chapter in the history of psychology. 

Postscript (Dec/4/2019)

I checked on the citations of this article and found that it had been cited only 9 times. Four citations were by the authors, including a JPSP article in 2018 that reported four more priming studies. The p-values of the focal tests were, p = .030, .049, .028, and .062. The last result was accompanied by a comment that “given the extant literature demonstrating reliable effects of paternal absence-disengagement on sexually proceptive behavior in women
(as reviewed in the Introduction), a one-tailed statistical test (p = .031) could be justified here, supporting a causal effect of paternal disengagement on flirting. My criticism of the 2013 article was posted in 2016 and there was widespread awareness about questionable research practices, and concerns about the replicability of priming studies. The fact that JPSP published a similar article in 2018 shows that some influential social psychologists are unable or unwilling to improve the quality of social psychological research.

Reference

DelPriore, D.J., & Hill, S.E. (2013). The effects of paternal disengagement on women’s sexual decision making: An experimental approach, Journal of Personality and Social Psychology, 105, 234-246. DOI: 10.1037/a0032784