The Short Version

Bargh, Chen, and Burrows (1996) reported that priming students with words related to old age made them walk more slowly, with effect sizes above one standard deviation (d = 1.04 and .79) across two studies of just 30 participants each. The finding became a cornerstone of behavioral-priming research and a famous casualty of the replication crisis after Doyen et al. (2012) failed to reproduce it. The Doyne et al. (2012) article came at the right time to cause a paradigm shift, but it was not the first replication failure.

The first replication failure appeared only a couple of years after the 1996 article: Dijksterhuis et al. (1998) found the same comparison at roughly a quarter of a standard deviation (d = .25 and .29), nonsignificant, and reinterpreted the disappearance as a side condition for a new contrast effect. Because social psychologists tracked the sign of an effect rather than its magnitude, a series of studies that did not reproduce Bargh’s result were published as successful demonstrations of moderators instead of as replication failures.

By 2012, elderly priming had been reported in 8 articles with 12 studies and 15 tests. I show that a meta-analysis at this time would have shown a wide prediction interval with possible effect sizes ranging from -0.1 to +1.0. Thus, Doyen et al.’s replication failure was entirely consistent with the full existing evidence. It was therefore entirely reasonable for Kahneman (2012) to ask for new and stronger evidence that Bargh never delivered. Since then, independent preregistered studies large failed to replicate past effects and priming theorists have largely abandoned priming research. The death of the priming paradigm provides a valuable lessons about the need to build theories on robust empirical foundations to avoid investing resources on phenomena that do not exist.

The Long Version

John A. Bargh studied with Robert Zajonc at the University of Michigan, earning his Ph.D. in 1981. Zajonc was an early champion of unconscious processes and used masked, subliminal presentations to study influences occurring outside conscious awareness. At New York University, Bargh developed a related program on automatic social cognition. At the time, studies from several laboratories suggested that stimuli presented outside awareness could influence feelings, judgments, and immediate reactions to other stimuli. Some of this evidence has since been challenged: meta-analyses find many subliminal effects hard to replicate, and concerns have been raised about publication bias and about whether participants were ever fully unaware of the masked stimuli.

Bargh matters for the history of psychology because his 1996 article made a much stronger claim. Rather than showing that unnoticed stimuli can shift immediate perceptions or evaluations, Bargh and colleagues claimed that activating a social concept could have a lasting influence on overt behavior without people being aware of that influence. In their famous elderly-priming experiment, students completed a scrambled-sentence task in which, in one condition, several words were related to old age and, in the control condition, were not. The words were visible, but participants were presumably unaware of the manipulation’s purpose or its possible effect on their behavior. Told to go to another room for a second study, participants then had their walking speed down the hallway measured as the real dependent variable. Bargh et al. reported that a few old-age words made students walk more slowly than controls.

The difference was not small. Effect sizes for two-group differences are often expressed in standard-deviation units. Cohen (1988) classified d = .50 as a medium effect and d = .80 as large. For comparison, an IQ test has a standard deviation of about 15 points, so half a standard deviation is 7.5 IQ points. In Bargh et al.’s first study, Experiment 2a, the effect was slightly larger than a full standard deviation, d = 1.04 — an exceptionally large effect for such a subtle manipulation.

Psychologists rarely run direct replications, but Bargh et al.’s article contained one. Experiment 2b used essentially the same procedure; again, primed participants walked significantly more slowly, and the effect stayed large, d = .79. The article thus appeared to offer unusually convincing evidence: two independent studies, same procedure, both producing significant and large effects.

The 1996 article spawned a large literature using primes such as money or God to influence behavior. Then, in 2012, Doyen et al. reported that they could not replicate the elderly-priming effect and suggested the original findings might be, at least partly, methodological artifacts. Walking speed in the original studies was timed manually with a stopwatch. And although the person timing walking speed was blind to condition, Doyen et al. noted it was unclear whether the experimenter who administered the priming task was also blind. If experimenters knew which participants had been primed, their expectations could have shaped participants’ behavior.

Doyen et al. tested this in a second experiment by manipulating experimenters’ expectations directly: some were led to expect primed participants to walk more slowly, others to walk faster. Objectively measured walking speed tracked those expectations — the elderly-prime effect appeared only when experimenters expected slowing — and the manual stopwatch measurements tracked them even more strongly. Doyen et al. thus provided experimental evidence that researchers’ expectations could produce the outcome of a behavioral-priming study.

Bargh responded in March 2012 with a Psychology Today post titled “Nothing in Their Heads.” He opened by noting that the 1996 finding had been theoretically predicted and fit a growing literature on automatic influences on behavior, but much of the post attacked the quality of Doyen et al.’s work and the peer review at PLOS ONE. Knowledgeable social-psychology editors and reviewers, he argued, would have caught the methodological problems; he had not been asked to review the paper, and implied that had he done so, he would have recommended rejection.

The tone drew wide criticism — Srivastava (2012), for one, characterized the episode as Bargh going “bananas.” The attack on the journal prompted a reply from the PLOS ONE editors on Bargh’s blog post (cf. Hodgkinson, 2012; Srivastava, 2012). Bargh later expressed regret over the tone and took the post down (Bartlett, 2013).

Bargh’s Defense of His Results in 2012

Bargh’s first substantive defense concerned experimenter effects. He stated that the experimenter in the original study had been blind to hypothesis and condition, and that a different person, also blind to condition, measured walking speed. If accurate, this substantially weakens Doyen et al.’s suggestion that experimenter expectations produced the original findings. But it does nothing for the more basic result: Doyen et al. used a larger sample and objective measurement and still failed to reproduce the effect.

Bargh therefore proposed several procedural differences to explain the replication failure. First, he argued that Doyen et al. had drawn participants’ attention to walking by telling them to “go straight down the hall when leaving,” and that making an automatic behavior conscious could eliminate the priming effect. But Doyen et al.’s article contains no such instruction; it says only that participants were “clearly directed to the end of the corridor” — and Bargh et al.’s own procedure had likewise directed participants toward the elevator down the hall. It is unclear the difference existed at all.

Second, Bargh questioned the strength of the manipulation: Doyen et al. put an elderly-related word in all 30 scrambled-sentence items, and Bargh argued that too many related words could make participants consciously aware of the theme and cancel an unconscious effect. Doyen et al. did find some evidence that participants could identify the elderly theme when directly probed — but nearly all denied noticing any connection between the sentence task and their walking.

Third, Bargh appealed to culture: priming works only if the association already exists in participants’ minds, so Belgian students might not link old age with slowness as American students do. Possible in principle — but Doyen et al. had adapted their materials to the Belgian sample by surveying 80 people about concepts associated with old age and selecting the frequent responses. Bargh et al.’s original article, by contrast, never measured whether their own participants associated the elderly stereotype with slower walking.

Finally, Bargh appealed to the accumulated literature: stereotype and behavioral priming had been replicated many times, so it was unreasonable to doubt the phenomenon over a single failure. This is persuasive only if the published record is an unbiased sample of all experiments run. That was precisely what the emerging replication crisis called into question. Journals favored novel, significant results and rarely published failed replications, so the sheer number of published successes could not reveal how often behavioral-priming experiments actually worked.

Doyen (2012) Was Not the First Failure

Commentators on the deleted blog post noted that Doyen et al. (2012) was not the first study to fail to reproduce elderly priming. As Nordbeck (2012) put it, Commentators on the deleted blog post noted that Doyen et al. (2012) was not the first study to fail to reproduce elderly priming. As Nordbeck (2012) put it,

It is a bit of a shame that many of the arguments Bargh uses in his criticism of the Doyen study are arbitrary, unsupported and, on occasion, false in light of other research (even some from the area of priming) (Nordbeck, 2012).

The earlier failures had been published, but not as failures. They appeared as successful demonstrations of moderators: conditions under which the effect was supposed to grow, shrink, or reverse (Cesario et al., 2006; Dijksterhuis et al., 1998; Hull et al., 2002). Bargh later cited these very studies without noting that none of them had reproduced his basic result — a difference between an elderly prime and a control group.

That this could happen reflects a habit of the field. Social psychologists tracked patterns of statistical significance more than the magnitude of effects. Evidence for a moderator requires a significant interaction, and once an interaction turns up, attention shifts from the main effect to the conditional effects that explain it. The claim is no longer “priming works” but “priming works differently under condition X” — and a study can support that claim while quietly failing to reproduce the main effect it was built on.

Dijksterhuis et al. (1998) is the clearest case, appearing just two years after the original. Studies 2a and 2b each contained the two conditions needed to test elderly priming — an elderly prime and a neutral prime, followed by the same judgment task. In both, primed participants walked slightly more slowly, but the effects were small and nonsignificant, d = .25 and .29, against Bargh’s d = 1.04 and .79. Same direction, a quarter of the magnitude.

But testing Bargh was not the point of their paper; behavioral contrast was. Some primed participants also judged a specific elderly exemplar — the Dutch Queen Mother, Princess Juliana — and then walked faster than both the neutral and the ordinary elderly-prime groups. That contrast effect was significant in both studies and became the headline. The authors did notice that their ordinary elderly prime had failed to reproduce Bargh’s assimilation effect, called it “somewhat surprising,” and proposed that the intervening judgment task had wiped it out — reading the small same-direction means as “residual assimilation.” The failure was not overlooked; it was reinterpreted into a footnote. By this reading, the first evidence that elderly priming is not as large or robust as advertised appeared fourteen years before Doyen.

Their explanation is itself revealing. If inserting an innocuous judgment task can cut an effect by roughly 75%, then the effect is extraordinarily sensitive to procedural detail. Researchers wanted theoretically predicted moderators that would specify when and why priming occurs. What the evidence kept pointing to instead were unknown moderators: incidental features of a procedure that swing the effect from large to nothing. A phenomenon that surfaces only under a narrow and poorly understood set of conditions is not the robust effect Bargh’s original experiments described.

Dijksterhuis was only the first. Hull et al. (2002) ran the paradigm in two studies and found priming only among participants high in self-consciousness; the overall effects were moderate but nonsignificant, ds = .57 and .54, in small samples. Cesario et al. (2006) added a youth prime that sped participants up, but the elderly-versus-control difference was small and nonsignificant, d = .23. Jeffries and Fazio (2008) found an interaction with a stopping rule on an anagram task and no main effect at all, d = −.05. N. Wyer (2011) produced the first robust replication — d = .70 on walking speed and d = 1.03 on working memory. And in 2012, the same year as Doyen, one article reported strong effects in one study (ds = 1.26, 1.05) but weak ones in another (ds = .29, .31).

Seen in this company, Doyen’s failure is unremarkable. Some studies produce large estimates and others produce weak estimates and all estimates in small samples have large sampling error and make estimation of the true effect size impossible. The common solution to imprecise estimates in small studies is to combine the studies in a meta-analysis.

A Meta-Analysis of Elderly Priming

Existing meta-analyses of priming pool many kinds of primes and outcomes, and the resulting heterogeneity tells us little about any one paradigm. So I conducted a meta-analysis restricted to elderly priming: 15 tests from 12 studies in 8 articles. Because publication bias is evident in the broader literature, I used a selection model that estimates the bias and returns a corrected effect size (Vevea & Hedges, 1995), with clustered bootstrapping to handle multiple tests nested within articles and to build the confidence and prediction intervals.

The bias-corrected effect was d = .42, 95% CI [−.01, .71]. The point estimate is close to the much larger meta-analysis of Dai et al. (2023), but the interval is wide and includes zero. The studies are small and individually imprecise, and the heterogeneity is itself barely pinned down: tau = .26, 95% CI [.00, .37]. Nothing here compels the conclusion that Bargh’s and Doyen’s results reflect different true effects.

The estimated mean and variation of the population effect sizes produce a 95% prediction interval that ranges form d = -0.10 to d = 1.03.

Thus, a replication study so large that sampling error is negligible could land anywhere from essentially nothing to a very large effect, because the existing evidence simply does not fix the size of the effect.

The meta-analysis also cannot explain how Bargh got two significant results from samples of N = 30. If the true effect were d = .42, a study that small has only about a 20% chance of reaching significance, so two independent significant results would occur about 4% of the time. Either Bargh was lucky, or something in his particular setup inflated the effect — for instance, a confound in the word list, if “Florida” slows NYU students’ walking by evoking a laid-back-Southern stereotype rather than an elderly one.

In short, a meta-analysis of the studies available in 2012 would have shown Bargh that Doyen’s result was entirely consistent with the broader evidence, however much it clashed with his own. There was no need to reach for incompetence. His deeper error was assuming that his two original studies, together with conceptual replications using other primes, had already established a general effect of elderly priming on behavior.

The Fall-Out

Concerns about the credibility of social psychology were already building. Daniel Kahneman believed in priming and had featured it prominently in Thinking, Fast and Slow, yet he was growing worried about the field’s reputation and raised it with Bargh directly (Bartlett, 2012). In a widely circulated email to Bargh and other leading priming researchers, he proposed a simple remedy: if Doyen et al.’s failure was a fluke or a botch, the experts could settle the matter by running rigorous replications and showing the effects held. With an expected effect of d = .40, pooling resources for N = 400 would give roughly 98% power to detect it.

The collaboration never happened. Independent researchers ran preregistered replications instead, often with disappointing results — in Dai et al.’s (2023) meta-analysis, the preregistered studies, most of them replications, produced essentially no effect at all (d = .02).

In 2017, Kahneman returned to the problem, citing Overall (1969) on why underpowered research is not merely wasteful but pernicious: it inflates the share of false positives among published findings. Bargh’s experiments, with 15 participants per condition, had little power to detect any plausible effect and cannot account for the near-90% success rates in the published priming literature. Hundreds of studies manufactured the appearance of a robust phenomenon that low power, publication bias, heterogeneity, and near-zero preregistered effects do not support.

So the classic behavioral-priming paradigms simply faded from the research frontier. In that sense the field is practically dead — a stark case of strong belief outrunning weak evidence. Researchers can always find a reason to dismiss a failure and build ever more elaborate theory around inconsistent results, all without first establishing that the phenomenon the theory explains is real. As the meta-analysis above shows, even the 2012 evidence carried enough uncertainty to justify Kahneman’s call.

Which raises the obvious question: why wouldn’t a true believer, with the resources of a Yale professor, simply run the study and prove the point? Bartlett (2013) put it to Bargh directly:

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 was unenthusiastic. He wouldn’t ask graduate students worried about their job prospects to spend time on stigmatized research, and he was aware that some critics thought he had a “special touch” with priming — a word that sounds like praise but isn’t. “I don’t think anyone would believe me,” he said.

The same article also reports an interview with Axel Cleeremans, one of Doyen’s collaborators. Cleeremans reports that his collaborators and he found found the tone of Bargh’s letter insulting, but that they also took his criticism seriously enough to conduct another replication study that addressed his stated concerns. The study also failed to replicate the original results. Another unpublished replication failure was posted online by Pashler et al. (2011; Srivastava, 2012)

While the evidence that elderly priming works was mixed and inconclusive, Bargh expressed strong confidence in his findings and his theory of unconscious activation of behavior. In his blog post, he believed that the long-term future of priming research was secure because the phenomenon rested on a large and converging empirical foundation:

Like many scientists, I take the long view and continue to have faith in science as a cumulative process, with particular studies that vary in their methods and approaches converging on deeper underlying principles and mechanisms. No single experiment, standing by itself, should be the basis for concluding anything, maybe most especially in psychological research. And when a single study does not replicate another one whose findings are solidly embedded in theories of more than one scientific field and which is consistent with dozens if not hundreds of other conceptual replications, then responsible scientists—and responsible science journalists—do not rush to judgment and make claims that the entire phenomenon in question is illusory. Thomas Kuhn famously argued in The Structure of Scientific Revolutions that it is the accumulation of contrary evidence over time, not single studies, which is needed to overturn established concepts and principles in any branch of science.

A decade on, his faith in cumulative science has been vindicated — just not as he expected. Failure after failure, and no convincing new evidence from the original researchers, has left claims about unconscious behavioral priming no better established than Freud’s speculations about the unconscious. Priming researchers published and circulated their successes and buried their failures, manufacturing the look of robustness; and as shown here, even the successes never told a clean story or gave clear evidence that elderly priming had ever produced a reliable effect.

Bargh was right about one thing: no single failure should have settled it. What mattered was the accumulation of evidence. That accumulation just happened to vindicate Doyen’s skepticism rather than his own confidence. Maybe, somewhere in his unconscious, Bargh knows this too — which might be why he never tried to replicate his 1996 findings.

The Lesson

The Lesson

Bargh is not the first scientist to spend much of a career on an idea that never lived up to its promise. That is an occupational hazard of working at the edge of a field: the questions are hard, the methods imperfect, and a genuine breakthrough is difficult to tell from a false lead until many technical problems are solved. Strong belief supplies the motivation to push through those obstacles — but it also makes the warning signs of failed studies easier to miss. Economists call inflated asset prices “irrational exuberance”: a stock can stay overvalued for as long as enough investors share the illusion, then crash to its true worth. Psychological theories kept aloft by shared belief rather than evidence behave the same way, as the citation history of Bargh’s 1996 article shows.

That casual attitude toward evidence is on display in Matthew Lieberman’s 2012 blog post on Doyen’s failure — a post that mentions, in passing, an unpublished non-replication from Lieberman’s own lab:

There have been multiple unpublished non-replications of the elderly-walking (including one in my lab that I may discuss in a future blog), but it is hard to know what to make of them given that they haven’t been peer-reviewed.

The catch-22 is clean. We trust only peer-reviewed findings, but psychology journals publish overwhelmingly significant results (Sterling, 1959; Sterling et al., 1995). So the failures stay invisible — unless they are dressed up as significant interactions, or land in a venue like PLOS ONE that isn’t gatekept by the same community. More telling still is what Lieberman took the stakes to be:

At a certain level it does not matter whether the exact primes Bargh used produce a change in walking speed over the exact distance he measured. Some have said ‘We need to replicate this exactly. Conceptual replications aren’t good enough’. But I’m not sure why we care about this specific manipulation unless we are about to start using it as an intervention to treat patients. What we care about is whether priming-induced automatic behavior in general is a real phenomenon. Does priming a concept verbally cause us to act as if we embody the concept within ourselves? The answer to this question is a resounding yes.

The “resounding yes” rests entirely on a published record that reports successes and buries failures — and, worse, treats interaction effects that masked the very replication failures at issue as further confirmation. Shown only the hits, it is easy to conclude the phenomenon must be real. Kahneman (2017) later admitted he had trusted that record too much when he built on it in his book. The lasting contribution of the controversy is that younger psychologists now treat direct replication as something more than an optional courtesy.

Younger scientists can lower the risk by studying the previous generation’s mistakes. We are fond of saying that each generation stands on the shoulders of giants. We say less often that many equally gifted scientists climbed just as high and backed ideas that proved wrong. The ones whose theories survived were not necessarily wiser or more careful at the outset; to a real extent, nature happened to cooperate. Darwin’s mechanism of natural selection withstood ever more stringent tests; Lamarck’s mechanism of inheritance did not. Neither man could have known which way it would go when he set out.

Because you cannot know in advance whether nature will cooperate, the main lesson of what Kahneman (2012) called the “train wreck” of priming research is methodological before it is anything else: do not expect clean answers from small samples, and do not trust significant results from journals that never publish the null ones. And beyond method, a matter of temperament — stay skeptical, and resist the pull to become a believer. As Feynman put it:

The first principle is that you must not fool yourself, and you are the easiest person to fool.

Priming behavior: A meta-analysis of the effects of behavioral and nonbehavioral primes on overt behavioral outcomes.

Brief Introduction

The replication crisis has not been kind to priming research. Social priming has become the poster child for the kind of replication failures that are expected when researchers conduct underpowered studies, use flexible analyses, and selectively publish results that crossed, or nearly crossed, the conventional threshold for statistical significance, p < .05. The problem is not mysterious. If many small studies are run and only the successful ones enter the published literature, the published record will exaggerate effects, hide failures, and create the illusion of a robust phenomenon.

Yet defenders of social priming continue to insist that priming is real and robust. Their main defense is no longer a stream of new, well-powered, preregistered experiments showing that classic priming paradigms work. Instead, the defense has shifted to meta-analysis. The argument is that even if individual studies are weak, the combined literature still shows an effect. Dai et al. (2023) make this argument explicitly. They conclude that the field has moved beyond the question of whether priming exists and should now focus on mechanisms.

That conclusion is not supported by the evidence. A meta-analysis of p-hacked studies is not a cure for p-hacking. If the primary studies were produced by low power, selective reporting, flexible analysis, and publication bias, then the meta-analysis inherits those problems. A significant average effect does not show that priming is robust. It does not identify a reliable paradigm. It does not show that effects occur outside awareness. It does not explain why preregistered and direct replication attempts have often failed. And it does not justify moving from existence questions to mechanism questions.

An empirical science needs paradigms that can reliably produce the phenomenon under specified conditions. If behavioral priming is real and robust, proponents should be able to demonstrate it prospectively in well-powered studies. Cohen made this point long ago: science requires studies with a decent chance of detecting the effects they are designed to test. If the true effect is around d = .30 or d = .40, then the classic small priming studies were severely underpowered. Underpowered studies can generate significant results, but those results will be selected, inflated, and difficult to replicate.

This raises the obvious question: if priming works, why are its strongest defenders not still doing programmatic priming research? A robust phenomenon should generate active research programs: stable paradigms, preregistered replications, planned moderator tests, and cumulative theory development. Instead, much of the contemporary defense of priming relies on retrospective meta-analyses of old, heterogeneous, mostly nonpreregistered studies. Actions speak louder than words. If priming is robust, show that it works in the lab.

I have tried to publish a critique of Dai et al.’s meta-analysis in traditional psychology journals. Psychological Bulletin, which published the original meta-analysis, was not interested in publishing a correction of its conclusions. PSPR was also not interested in a paper that challenges the integrity of the evidentiary practices behind one of social psychology’s most famous literatures. Fortunately, journal gatekeeping does not prevent readers from evaluating the arguments for themselves.

The following list summarizes the main problems in Dai et al.’s meta-analysis and explains why their conclusion that behavioral priming is a robust phenomenon is not supported by their own evidence.

Scientific Problems in Dai et al. (2023) Meta-Analysis

1. A significant average effect is not evidence of a robust phenomenon.

Dai et al.’s main empirical result is a positive mean effect, d = 0.37, across 351 studies, 224 reports, and 862 effect sizes. They interpret this as evidence of a moderate and robust priming effect. But a positive grand mean only shows that the average coded effect is greater than zero. It does not show that any specific priming paradigm works reliably, that the effect is predictable, or that the literature has identified the conditions under which the effect occurs. This is the central inferential error. A heterogeneous collection of effects can have a positive mean even if many individual paradigms are unreliable, null, or false positive.

2. The literature is highly heterogeneous.

Dai et al. report substantial heterogeneity in the overall analysis and therefore use random-effects models. Their results show “substantial variability across studies and contexts,” but they still conclude that the effect is robust across procedures. That is too strong. High heterogeneity means the average effect is not a good description of individual studies or future studies. Robustness would require a narrow range of expected effects, or at least identifiable and replicated boundary conditions. Heterogeneity alone is not evidence for a robust phenomenon.

3. They do not report prediction intervals.

A random-effects meta-analysis with large heterogeneity needs prediction intervals. A confidence interval around the mean asks whether the average effect is different from zero. A prediction interval asks what effect size should be expected in a new study. That is the relevant quantity for “robustness.” If the prediction interval includes zero or negative effects, the literature does not support the claim that priming reliably produces positive behavioral effects. Your reanalysis indicates that Dai et al.’s estimates imply very wide prediction intervals, including negative effects, which directly contradicts the robustness claim.

4. Publication bias is present by their own analyses.

Dai et al. do not find a clean literature. They report evidence of small-study bias and funnel asymmetry. Their PET–PEESE analyses indicated that small studies reported larger effects, and the PEESE-adjusted estimate was reduced to d = 0.291, although still statistically significant. A reduced but still significant average does not eliminate the publication-bias problem. It merely says that one model still leaves a nonzero mean. It does not show that the published literature is robust, nor that individual paradigms are replicable.

5. Some bias-correction methods give much smaller estimates.

Dai et al. use multiple publication-bias adjustments, including PET–PEESE, Vevea and Woods selection models, and Mathur and VanderWeele sensitivity analyses. They acknowledge that selection models should be used to explore a range of estimates rather than to obtain one preferred estimate. The conclusion nevertheless emphasizes robustness. That is selective interpretation. A fair conclusion would stress the uncertainty and model dependence of the bias-corrected estimates, not reassure the field.

6. Their selection models do not handle dependence among effect sizes.

Dai et al. explicitly note that Vevea and Woods selection methods do not account for statistical dependence among effect sizes. This matters because their dataset contains multiple effect sizes from the same studies, samples, and reports. If selection-bias corrections are applied in a way that ignores dependence, the adjusted estimates and uncertainty intervals can be misleading. This weakens the evidentiary basis for strong claims about robustness.

7. The preregistered studies are essentially null.

This is one of the most damaging findings. Dai et al. report that only a small number of reports were preregistered, but those preregistered studies did not show the same effect pattern as the nonpreregistered literature. In your summary, the key contrast is preregistered studies around d = .02 versus nonpreregistered studies around d = .37. That contrast is fatal to a simple robustness claim. If priming were robust, preregistered studies should not collapse toward zero.

8. They dismiss preregistered failures asymmetrically.

Dai et al. explain the preregistered/null pattern by pointing to the small number of preregistered studies, replication difficulties, or possible differences between original studies and replications. That may be partly true, but it creates an asymmetric evidentiary standard. Positive nonpreregistered findings are treated as evidence for priming; preregistered failures are treated as inconclusive. This is precisely the kind of post hoc protection that prevents a theory from being falsified.

9. Most included studies were not preregistered.

Dai et al.’s descriptive table reports that among 224 included reports, only three reported preregistration. That means the positive average is overwhelmingly based on the older, flexible, nonpreregistered literature. This is exactly the kind of literature in which selective reporting, optional stopping, outcome switching, participant exclusions, and analytic flexibility can inflate effects.

10. Participant exclusions and covariate use are common.

Dai et al. report that many reports included covariates or excluded participants. Their study-quality section treats preregistration, covariates, and exclusions as indicators relevant to possible p-hacking. These features do not prove bias in any particular study, but they are red flags in a literature where the main evidentiary claim depends on many small, flexible, nonpreregistered experiments.

11. Their “quality assessment” is weak.

Dai et al. count random assignment, participant blindness, and signs of p-hacking. But random assignment was an inclusion criterion, so it cannot distinguish stronger from weaker studies. For blindness, only 37% of studies used funneled debriefing; for the rest, they state that it was hard to determine whether participants were blind, but that awareness was probably unlikely because priming effects are subtle. That is not a strong quality assessment. It assumes what needs to be shown.

12. Awareness is inadequately handled.

The controversial claim is not that cues can influence behavior when participants notice them. The controversial claim is influence without awareness of the prime’s relevance or influence. Yet Dai et al.’s own descriptive table shows that only 37.82% of effect sizes came from studies with funneled debriefing, and 84.22% used supraliminal primes. This means their broad meta-analysis does not primarily test the strongest implicit-priming claim.

13. Supraliminal cue effects are conflated with implicit priming.

Most studies in Dai et al. involve visible primes. Visible primes may influence behavior through ordinary cueing, demand, construal, motivation, or conscious goal activation. That is not the same as showing that behavior is guided outside awareness. Their conclusion about priming as a long-debated phenomenon slides between the broad, relatively uncontroversial claim that incidental cues can influence behavior and the stronger, controversial claim that behavior is automatically influenced outside awareness.

14. The dataset combines many theoretically distinct phenomena.

Dai et al. include primes involving achievement, common behaviors, money/marketing/finance, morality/God/prosociality, motivation, sex/gender/romantic behavior, and stereotypes. They also include verbal and visual primes, subliminal and supraliminal primes, performance outcomes, donations, choices, consumption, reaction times, and other behavioral measures. A positive average across this broad mixture does not validate a single phenomenon called behavioral priming. It may simply show that many different manipulations sometimes influence many different behaviors.

15. “Behavioral” versus “nonbehavioral” priming is too broad to identify mechanism.

Their core theoretical contrast is behavioral versus nonbehavioral primes. But they find no meaningful difference between the two: nonbehavioral primes d = 0.394 and behavioral primes d = 0.344, with B = 0.05, p = .14. They interpret this as suggesting overlapping processes. But a null difference between broad categories does not identify a mechanism. It may simply show that the categories are too crude, heterogeneous, or underpowered for mechanistic inference.

16. Moderator analyses are weak because the relevant moderator conditions are rare.

Dai et al. acknowledge that most included studies did not manipulate the key theoretical moderators: 89% did not manipulate goal value, 91% did not manipulate goal expectancy, and 82% did not include a filler task between priming and behavior. This makes strong moderator conclusions inappropriate. A literature cannot establish mechanisms if the relevant moderators are mostly absent.

17. Uneven moderator distributions reduce power.

Dai et al. explicitly state that the distribution of key moderators was highly uneven and that RVE has low power for moderators with uneven distributions. This is an important limitation. Moderator claims require interaction evidence, and interactions require much larger samples than main effects. A sparse and uneven moderator structure cannot support the claim that the field has moved from existence to mechanisms.

18. Simple effects are not evidence of moderation.

Even if some simple effects appear strong in certain moderator cells, the relevant evidence is the interaction. A significant effect in one condition and a nonsignificant effect in another is not evidence that the conditions differ. If the interaction evidence is weak, underpowered, or selected, moderator claims are unstable. This is especially important because the literature is already biased toward significant results.

19. Heterogeneity is treated as theoretical richness rather than an evidentiary problem.

Dai et al. repeatedly frame variability as consistent with different mechanisms or contextual dependence. But unexplained heterogeneity is not evidence for moderators. It is evidence that the effect is not yet predictable. The field cannot move to mechanism questions until it has reliable paradigms that produce the effect under specified conditions.

20. Their conclusion overstates what meta-analysis can show.

Dai et al.’s conclusion says their synthesis provides “solid evidence” that priming is real, not merely a bubble of publication bias, and that it should “reassure the field.” That is stronger than the data warrant. Meta-analysis of a selected, heterogeneous, mostly nonpreregistered literature can suggest that some effects may be real. It cannot establish that behavioral priming is robust as a general phenomenon.

21. The power implications are not drawn.

If the true effect is d = .29 to .37, typical small priming studies are underpowered. Many classic experiments with n = 20–40 per cell would have low power to detect effects of this size. Dai et al. do not make this implication central. If most original studies were underpowered, then significant findings are expected to be selected and inflated, and moderator analyses are even less credible.

22. The positive average is compatible with many false positives.

A significant average effect does not tell us how many individual significant findings are false positives. In a heterogeneous literature with low power and selection for significance, many significant findings can be false positives even if the mean effect is positive. This is why z-curve and related evidential-value analyses are needed. Dai et al.’s focus on mean effect size does not answer the false-discovery question.

23. Their methods estimate effects, not replicability.

Dai et al. assess mean effects and publication-bias-adjusted mean effects. But robustness is fundamentally about whether findings replicate. A field can have a nonzero average effect and still have poor replication prospects if studies are underpowered, selected, and heterogeneous. Their analysis does not directly estimate expected replication rates or discovery rates.

24. Failed replications are not integrated as severe tests.

Dai et al. cite failed replications as part of the motivation for the meta-analysis, but the conclusion effectively downgrades their importance once the average effect remains positive. That is not a balanced evidentiary treatment. Large, preregistered, or direct replication failures should receive greater weight as severe tests of the robustness claim, not be absorbed into a heterogeneous average and then explained away.

25. “Robust to publication bias” is too weak a criterion.

Their claim that the effect remains statistically significant after some bias adjustments does not establish robustness. A robust phenomenon should show reliable effects in well-powered, preregistered studies and should produce predictable effects in new studies. Surviving some bias corrections is a much lower standard.

26. The meta-analysis does not identify a robust paradigm.

The key scientific question is not whether the average across 862 effects is positive. The key question is: which priming paradigm reliably produces the effect? Dai et al. do not identify such a paradigm. Without a robust paradigm, the field cannot credibly study mechanisms, moderators, or applications.

27. One-off applied studies do not establish cumulative science.

The literature contains many isolated demonstrations involving different primes, outcomes, populations, and contexts. That pattern can produce a significant meta-analytic average while still lacking cumulative progress. A robust phenomenon should generate programmatic research around stable paradigms. Dai et al.’s synthesis does not show that this has happened.

28. The analysis treats conceptual replication as strength, but it also weakens interpretability.

A broad conceptual-replication database increases sample size, but it also combines many different true effects. That helps reject the null hypothesis that the average is zero, but it makes it harder to know what was actually established. If the procedures differ too much, the grand mean becomes theoretically thin.

29. The conclusion moves from “some effects may be real” to “the field should be reassured.”

The defensible conclusion is modest: some incidental priming effects may be real, and the average coded effect remains positive under some bias corrections. The stronger conclusion—that behavioral priming is robust and that the field can move beyond existence questions—is not supported.

30. The strongest claim about implicit influence is not established.

Priming with awareness is not controversial. The important claim is that incidental cues influence later behavior outside awareness of their influence. Dai et al.’s database is mostly supraliminal, often lacks funneled debriefing, and combines many visible cue manipulations. Therefore, even if their average effect were accepted, it would not establish the stronger claim that behavior is robustly influenced outside awareness.

Conclusion

Dai et al.’s conclusion that behavioral priming is robust is stronger than their evidence permits. Their own results show substantial heterogeneity, evidence of small-study and publication bias, sparse preregistration, null effects in preregistered studies, highly uneven moderator distributions, and limited assessment of awareness. A positive average effect across a heterogeneous and mostly nonpreregistered literature may show that some incidental cue effects are real, but it does not identify a reliable priming paradigm, establish robust boundary conditions, or justify moving from existence questions to mechanism questions. Robustness requires prospective replication under specified conditions, not merely a statistically significant grand mean.

This blog post follows up on an introduction to meta-analyses with heterogeneous data.

Modeling Heterogeneity in Meta-Analyses – Replicability-Index

We can distinguish two types of meta-analysis. Meta-analyses of direct replication studies combine studies with the same or very similar population effect sizes. So-called fixed-effect meta-analyses produce more precise estimates of the shared population effect size, because the sampling error of the combined data is smaller than the sampling error of the individual studies.

However, psychologists often conduct conceptual replication studies that vary conditions, stimuli, and dependent variables. Meta-analyses of these studies are more challenging because the studies have varying population effect sizes (van Erp et al., 2017). As a result, the average effect size is relatively uninformative and provides no information about the effect sizes of specific studies. The standard solution has been to model this heterogeneity by assuming a normal distribution for the population effect sizes, in addition to the normal distribution of sampling error. The previous post showed that (a) this assumption can lead to biased estimates when the true distribution of population effect sizes is not normal, and (b) developments in statistics make the assumption unnecessary. Meta-analysts can therefore drop the problematic normality assumption by adopting more flexible mixture models that make no assumption about the shape of the population effect-size distribution.

What is a Positive Effect?

The main contribution of this post is to reveal a theoretical contradiction between the assumption of normally distributed population effect sizes and the way studies are coded in meta-analyses. To see the problem, it helps to ask a simple question: what is a positive effect?

The difficulty of defining a positive outcome is well recognized in medicine. A positive diagnosis usually means bad news — except when people hoping for a child learn that they are pregnant. Cochrane meta-analyses address this by coding results not only by the direction of change in an outcome (increase or decrease) but also by whether that change is beneficial or harmful: for mortality, an increase is harmful; for longevity, an increase is beneficial. For the meta-analyst, what matters is keeping the sign of an effect constant across studies, while the interpretation depends on the substantive meaning of the average. “Women live longer than men” is a positive difference if women are coded 1 and men 0, and a negative difference if the coding is reversed.

The default coding in a meta-analysis that tests a prediction is to assign signs according to the predicted direction: results supporting the hypothesis receive a positive value, and results contradicting it receive a negative sign.

This coding, combined with the assumption of a normal distribution of population effect sizes, leads to a paradoxical implication. The paradox is clearest in the extreme case where the average effect size is zero. Under the normality assumption, a mean of zero implies that half of the true effects are consistent with the prediction and half are opposite to it — that the theory predicts the direction of the effect no better than a coin flip. This implication is usually implausible, which is better read as evidence against the distributional assumption than as a verdict on the theory. Even when the average effect is small but non-zero, normally distributed heterogeneity implies that a substantial proportion of true effects run opposite to the prediction.

This state of affairs is often overlooked when meta-analytic results are interpreted. For example, Chen et al. (2025) reported large heterogeneity, with a 95% prediction interval from −1.05 to 1.77, implying that many studies have large true effects opposite to the predicted direction. Yet none of the published studies reported such results. The prediction interval implies a population of wrong-direction true effects that does not appear in the published record, and this implication went unexamined: are these effects real but suppressed by publication bias, or are they phantoms produced by an incorrect distributional assumption?

In short, coding a meta-analysis by agreement with a theoretical prediction, combined with the assumption of a normal distribution of effect sizes, predicts that many studies have true effects in the wrong direction. Because the actual data often show no such results, the prediction raises a question: do these wrong-direction effects exist and were suppressed by publication bias, or are they phantom effects manufactured by a false distributional assumption?

Modeling Only Positive Effect Sizes

When the data contain few negative effect-size estimates, the normality assumption can do more than inflate estimates of heterogeneity; it can also bias the effect-size estimate itself. The reason is that sampling error produces many negative estimates for small effects, even when the population effect is positive. If the data do not show these expected negative results, a model that assumes complete data infers that the positive results must have been produced by a larger population effect. This inflates the effect-size estimate, especially when the average effect is small.

To avoid this inflation, the truncation of the data at zero must be modeled. For example, if the true population effects follow a normal distribution centered at zero, a model that knows the data are truncated at zero expects a half-normal distribution and correctly infers that the mean of the full distribution is zero. A model that does not know the data are truncated fits a full normal distribution to the observed half-normal data and estimates a mean greater than zero.

To illustrate this, I ran a simulation with 64 conditions, varying the mean of the population effect sizes (4 levels), their standard deviation (4 levels), and the proportion of true null hypotheses (4 levels) — the same design used previously to show the problem of assuming normality when the true distribution is non-normal. The previous simulation showed that models with flexible distribution assumptions perform better than models that assume a normal distribution when the actual distribution is not normal.

Modeling Heterogeneity in Meta-Analyses – Replicability-Index

This time, the simulation selected only positive effect-size estimates. The prediction was that ashr and RMA would be biased, because they assume no selection on the sign of an effect, whereas z-curve and weightr are selection models that can be specified to model selection on sign. Weightr, however, may still be biased when the distributional assumption is violated, because its selection-weight parameters can absorb the non-normality, fitting a non-normal distribution by distorting the estimated selection process. Z-curve was expected to perform well because it makes no assumption about the shape of the effect-size distribution and can model truncated data.

The results confirmed these predictions, which follow directly from the models’ assumptions. Z-curve had the smallest error (RMSE = .046), followed by RMA and ashr (RMSE = .094), with weightr the worst (RMSE = .168).

The poor performance of the weight-function selection model is noteworthy, because it is commonly assumed to produce more credible results when data are selected. This confidence is justified only when the distributional assumption holds. When it does not, the selection model can produce worse estimates than a model that does not correct for selection at all, such as RMA. A false distributional assumption can even yield negative estimates of the average population effect when all studies have positive population effects.

Finally, it is worth noting that ashr was not designed for meta-analysis, but to analyze data from studies with many predictor variables, where the sign of an effect is often arbitrary and roughly equal numbers of positive and negative results are expected. When all of these results are available, as in genomics, the model works well — indeed, without selection it is equivalent to z-curve. The bias identified here arises only when a model built for complete data is applied to selected meta-analytic results (e.g., van Zwet et al., 2024).

In conclusion, for meta-analysis it is problematic to assume that negative effect sizes estimates are common and produced by studies with negative population effect sizes. It is therefore necessary to allow for selection based on the sign of an effect size independent of selection for statistical significance. The most suitable models for meta-analyses therefore need to assume selection for sign without assuming a particular distribution of population effect sizes. The only model that checks both boxes is z-curve.

Illustration with Actual Data

Chen et al.’s (2025) meta-analysis of terror management studies serves as a useful example, because it analyzed the data with both a random-effects model and a weight-function selection model, and because the set of studies is large (k = [FILL IN]). As noted earlier, the models that assumed normality estimated very high heterogeneity, with a prediction interval extending well into negative values — implying that a substantial proportion of studies have true effects opposite to the theoretical prediction.

The histogram shows the distribution of the observed effect-size estimates. There are many small positive estimates, but negative estimates are rare. This is not what a normal distribution would produce: a normal distribution centered on the positive mean, with the estimated heterogeneity, would place substantial mass below zero and thus predict many negative estimates. The near-absence of negative estimates therefore points to one of two conclusions — either negative results were suppressed by publication bias, or the true distribution of effects is not normal.

Chen et al. (2025) did not model selection for sign, despite the visible asymmetry around zero. I refitted the model with a selection step at p = .5 (one-tailed), distinguishing positive (p < .5) from negative (p > .5) results. This model estimated a negative average effect, d = −.336, with large heterogeneity (tau = .956). A negative mean for a literature whose observed effects are overwhelmingly positive is implausible on its face. It arises because the model can only reconcile the near-absence of negative results with a normal distribution by assuming that a large number of negative and null results were suppressed — so many that the true distribution is centered below zero, and the observed positive results are merely its selected upper tail. This is possible only if one accepts both that negative results were heavily suppressed and that the true effect distribution is normal.

The random-effects model faces a different problem. It assumes no selection and fits a normal distribution to a set of effect sizes that are visibly skewed. Fitting a symmetric normal to this right-skewed distribution inflates the mean, which RMA estimates at .81.

The ash model makes no assumption about the shape of the effect-size distribution and produces a similar mean, .80, but a smaller median, .62, reflecting the right skew visible in the observed data.

Both RMA and ash, however, take the observed data at face value, even though the data contain few negative results. Z-curve can model truncated data without assuming a normal distribution. The next figure shows the z-curve plot with local power and local effect-size estimates. This model does not assume publication bias.

Z-curve models truncation of the data at zero and makes no distributional assumption about the population effect sizes. The z-curve plot shows the histogram with the fitted model, along with local average effect sizes below the x-axis and local power estimates beneath them. Even the non-significant results are estimated to have moderate effect sizes (~.5), and the overall mean is .77.

As with ash, the median is smaller than the mean — .63 versus .77 — reflecting the same right skew. That two flexible methods independently recover both a mean near .8 and a median near .62 indicates the skew is a real feature of the effect distribution, not an artifact of either method. A random-effects model cannot represent this asymmetry, because assuming normality forces its mean and median to coincide.

Across models, then, the mean estimates agree reasonably well — z-curve (.77), ash (.80), and the random-effects model (.81) all indicate a moderate-to-large average effect — with the weight-function selection model the lone exception, producing an implausible negative estimate. For this literature, truncation and the normality assumption have a relatively small effect on the point estimate, consistent with the simulations, which showed close agreement among models when the average effect is large. This is the favorable case, however: when the average effect is small, the normality assumption’s implied negative effects and the truncation at zero have a much larger impact.

So far, all models assumed no selection for statistical significance. This is unlikely, because published articles predominantly report significant results that support theoretical predictions (Sterling et al., 1995), and Chen et al. (2025) found evidence of publication bias in this literature. Z-curve can model publication bias by fitting only the significant results and estimating the distribution of the non-significant results that were not reported.

Taking publication bias into account has two effects. First, the effect-size estimates decrease. Second, the average is now computed over a larger reference set that includes the estimated non-significant studies, which have smaller effects. The mean effect size is reduced to .52 and the median to .34. Even after this correction the distribution remains right-skewed — the mean exceeds the median — and the median of .34 is the more representative value for a typical study.

In conclusion, meta-analytic models that make different assumptions produce different results. Making sense of these differences requires testing the assumptions and preferring models that avoid assumptions that cannot be tested. In this example, the data show clear evidence of selection on the sign of the effect, further evidence of selection against non-significant positive results, and evidence that the population distribution is not normal (median < mean). A model that accommodates these features of the data — z-curve — produced lower estimates than the random-effects model, while the weight-function selection model produced an implausible negative estimate.

It is not possible to generalize from this single example to all meta-analyses, but the results raise the possibility that many published effect-size estimates are biased by false distribution assumptions, especially when publication bias is also present. To assess the extent of these biases, such literatures should be reexamined with methods that can model selection and avoid the untestable assumption of normally distributed population effects — as z-curve does.

Meta-psychology was born from a simple observation: the way psychologists used significance testing created a distorted literature. Researchers treated p < .05 as a license to publish and p > .05 as a reason to abandon a finding. Journals rewarded significant results, reviewers demanded them, and authors learned to find them. The result was predictable: literatures stuffed with too many significant results, exaggerated effect sizes, and too few honest failures (Sterling, 1959; Sterling et al., 1995).

This critique is now familiar. Null-hypothesis significance testing, reduced to a dichotomous decision rule, encourages bad scientific behavior. It turns evidence into a yes-or-no ritual, treats p = .049 as a discovery and p = .051 as a non-event, and rewards selective reporting. Meta-psychologists have made this point repeatedly, and largely correctly.

But there is an irony. Having criticized psychologists for using a dichotomous significance test to decide which original findings count, meta-psychologists often reach for the same logic to decide whether a literature is biased.

The original sin was this: p < .05 means the effect is real.

The meta-analytic version becomes this: p < .05 means publication bias is present.

The form of the reasoning has not changed. Only the target has moved up one level.

Why this fails is clearest if we ask what a significance test can ever legitimately buy us. The most charitable defense of significance testing is that a significant result may carry information about the sign of an effect: it can tell us which direction is more plausible, even when it says little about magnitude (Jones & Tukey, 2000). That defense collapses for publication bias, because the sign is known before we collect a single study. Selective reporting favors significant results; it does not run the other way. A test whose only defensible output is a direction we already know contributes little.

What it contributes instead is a verdict that is uninformative in both directions. A significant bias test conflates magnitude with detectability: in a large literature, a trivial and harmless amount of selection can reject the null. A nonsignificant bias test conflates small bias with low power: in a small literature, severe selection can easily fail to reach significance. Either way, the binary outcome tells us little about the quantity we care about. “There is publication bias, p < .05″ is, to borrow Cohen’s (1994) famous example, about as useful as “the earth is round, p < .05.” And “There was no evidence of publication bias, p > .05” is akin to “The earth is flat, p > .05.”

The deeper irony is that meta-psychologists have relocated the mistake they diagnosed. Original researchers treated significance as a discovery machine. Bias researchers sometimes treat significance as a bias-detection machine (Siegel et al., 2021). The error is identical: a difficult inferential problem is compressed into a binary decision.

Some have pushed the argument further, claiming that tests for publication bias are useless (e.g., Simonsohn, 2014). But the folly of nil-hypothesis testing, which incidentally undermines p-curve as much as many other significance-based methods, is not a reason to ignore publication bias. We do not abandon original research because the significance ritual is empty (Cohen, 1994). We replace the ritual with something more informative.

The reform for original research was to report effect-size estimates with confidence intervals that express uncertainty. The reform for bias detection should be the same. The goal is not to decide whether bias exists, but to estimate how much is present, how uncertain that estimate is, and whether the amount of bias consistent with the data changes the substantive conclusion.

Some publication-bias methods already estimate quantities of this kind, or carry the information needed to. Yet in practice that information is discarded, and the result is reduced to whether a test was significant or a method “detected bias” (Siegel et al., 2021). And no common metric for the amount of bias has been widely adopted.

The most natural metric is the excess of significant results. If a literature reports significant findings 80% of the time but the true probability of producing significant results is between 20% and 40%, we have clear evidence of substantial bias.

This is why the amount matters more than its presence. Bias can be easy to detect yet too small to change any conclusion, or large enough to overturn a conclusion yet impossible to detect in a small set of studies, where these tests have the least power (Renkewitz & Keiner, 2019). A binary test cannot tell these cases apart; an estimate with an interval can.

In short, meta-analysis needs the same methodological reform that original research needed. It is time to abandon the nil-hypothesis ritual and replace it with estimation: estimate the amount of publication bias, quantify the uncertainty with confidence intervals, and evaluate whether conclusions remain credible after adjusting for the plausible levels of selection.

Fortunately, unlike unpublished primary studies hidden in file drawers, the data behind published meta-analyses are often available or recoverable. That makes it possible to reexamine decades of meta-analytic conclusions and ask the question that matters: not whether publication bias can be detected, but whether the amount of bias compatible with the data changes what we should believe.

The past decade has not been kind to experimental social psychology. Study after study failed to replicate and entire literatures have turned out to be built on nothing (a.k.a. statistical noise mining).

“Another day, another idol falls. This one has been teetering for years, so the collapse didn’t come as a shock. But that doesn’t make it any less painful.” (Michael Inzlicht).

It all started with a leading journal publishing an article with the crazy claim that people can foresee the future and practicing after a test can improve exam scores (Bem, 2011). This claim was quickly revealed to be false (and possibly a hoax, Gelman) after a big replication study failed to show the same results (Galak, J., LeBoeuf, R. A., Nelson, L. D., & Simmons, J. P., 2012).

In a media interview Bem explained that his experiments were never meant to be taken seriously. (Daniel Engber, 2017, Slate).

“If you looked at all my past experiments, they were always rhetorical devices. I gathered data to show how my point would be made. I used data as a point of persuasion, and I never really worried about, ‘Will this replicate or will this not?’

While the past decade has not been good for experimental social psychologists, it has produced a new group of psychologists to examine the causes of the replication crisis in experimental social psychology. As they look at the practices of research psychologists, they are meta-psychologists, psychologists who study other psychologists.

One of them is Blake McShane, who did his dissertation on statistical models to analyze time-series data (McShane, 2010). Given his background in statistics, managerial science, applied economics, and marketing, it is fair to say that he entered this field without first-hand experience of research practices that produced the replication crisis. He also does not cite seminal papers that foreshadowed the crisis by Cohen (1962, 1990, 1994). Instead, his main approach to examining meta-psychological questions appears to rely on his expertise in conducting simulation studies (McShane & Böckenholt, 2014, McShane, Böckenholt, & Hansen, 2016, 2020).

The problem with these simulation studies is that they repeat the same problems that plagued experimental social psychology at the meta-level. Just like Bem’s studies are not empirical tests, but rhetorical devices, McShane’s simulations are rhetorical devices to illustrate a point that does not require simulation evidence, namely.

[models] perform reasonably well in the setting for which they were designed, …[but] they are sensitive to deviations from their model assumptions.

In the 2016 article, the simulations violated assumptions of models that assume homogeneity and they failed. However, the simulations met the assumptions of another model and (no surprise) it worked well. However, McShane did not cite an earlier study that showed the model also has problems when its assumptions are not met (Hedges & Vevea, 1996).

Later simulation studies further confirmed that McShane’s preferred model does not work so well under realistic conditions (Carter et al., 2019), a finding not cited by McShane et al. in 2020. Pressed on this point that his simulations favored his preferred model, he might reply

“If you looked at all my past simulations, they were always rhetorical devices. I created conditions to show how things work when assumptions are met. I used simulations as a point of persuasion, and I never really worried about, ‘Does this apply to real data’ ”

In conclusion, a simulation that shows a model works when its assumptions are true and does not work when its assumptions are false is merely a demonstration, not an evaluation of a model under realistic conditions.