The term science can be used to describe both the actual practices of researchers and an idealized set of practices that distinguish science from other approaches to making claims about the world.

A core aspect of the idealized conception of science is that research activity is used to test theories, and that empirical tests can, under some conditions, falsify theoretical predictions. Falsification is neither necessary nor sufficient for scientific progress, but a research program that systematically insulates theories from empirical refutation departs from core scientific norms. Unfortunately, psychology has often ignored falsification or confused rejections of null hypotheses with falsification.

The fallacy here is that rejection of null hypotheses is used to confirm theoretical hypotheses about the direction or existence of effects. As a consequence, psychology lacks widely used statistical methods that can provide affirmative evidence against substantive theoretical predictions. Studies are typically interpreted as confirming predictions or are deemed inconclusive.

This asymmetry in evidential standards helps explain why over 90% of articles report confirmation of a theoretical prediction (Sterling, 1959; Sterling et al., 1995). Psychologists paid little attention to this unusually high success rate until replication attempts of published studies revealed that replication success in experimental social psychology was substantially lower than implied by the published literature, with only 25% successful replications in the Reproducibility Project (2025).

Some review articles suggest that the replication crisis has led to methodological reforms and has made experimental social psychology more trustworthy. This is partially correct. Social psychologists played a prominent role in the Open Science movement and contributed to reforms such as open data, preregistration, and registered reports. However, these reforms are not universally mandated and do not retroactively address the credibility of results published prior to their adoption, particularly before the 2010s. Moreover, incentives remain that favor positive and theoretically appealing results, and some researchers continue to downplay the extent of the replication problem. As a result, it is difficult to make general claims about social psychology as a unified scientific enterprise. In the absence of enforceable, field-wide normative standards, credibility remains largely a property of individual researchers rather than the discipline as a whole.

Social Priming

Priming is a general term in psychology referring to the automatic influence of stimuli on subsequent thoughts, feelings, or behaviors. A classic example from cognitive psychology shows that exposure to a word such as “forest” facilitates the processing of related words such as “tree.”

Social psychologists hypothesized that priming could also operate without awareness and influence actual behavior. A well-known study appeared to show that exposure to words associated with elderly people caused participants to walk more slowly (Bargh et al., 1996). That article also reported subliminal priming effects, suggesting that behavioral influence could occur without conscious awareness. These findings inspired a large literature that appeared to demonstrate robust priming effects across diverse primes, presentation modes, and behavioral outcomes, with success rates comparable to those documented by Sterling (1959).

In 2012, a group of relatively early-career researchers published a failure to replicate the elderly-walking priming effect (Doyen et al., 2012). The publication of this study marked an important turning point, as it challenged a highly influential finding in the literature. Bargh responded critically to the replication attempt, and the episode became widely discussed. Daniel Kahneman had highlighted priming research in Thinking, Fast and Slow and, concerned about its replicability, encouraged original authors to conduct high-powered replications. These replications were not forthcoming, while independent preregistered studies with larger samples increasingly failed to reproduce key priming effects. As a result, priming research became a focal example in discussions of the replication crisis. Kahneman later distanced himself from strong claims based on this literature and expressed regret about relying on studies with small samples (Kahneman, 2017).

Willful Ignorance and Incompetence In Response to Credibility Concerns

In 2016, Albarracín (as senior author) and colleagues published a meta-analysis concluding that social priming effects exist, although the average effect size was relatively small (d ≈ .30; Weingarten et al., 2016). An effect of this magnitude corresponds to roughly one-third of a standard deviation, which is modest in behavioral terms.

The meta-analysis attempted to address concerns about publication bias—the possibility that high success rates reflect selective reporting of significant results. If selection bias is substantial, observed effect sizes will be inflated relative to the true underlying effects. The authors applied several bias-detection methods that are now widely recognized as having limited diagnostic value. They also used the p-curve method, which had been introduced only two years earlier (Simonsohn et al., 2014). However, the p-curve results were interpreted too optimistically. P-curve can reject the hypothesis that all significant results arise from true null effects, but it does not test whether publication bias is present or whether effect sizes are inflated. Moreover, the observed p-curve was consistent with an average statistical power of approximately 33%. Given such power, one would expect roughly one-third of all studies to yield significant results under unbiased reporting, yet the published literature reports success rates exceeding 90%. This discrepancy strongly suggests substantial selective reporting and implies that the true average effect size is likely smaller than the headline estimate.

Sotola (2022) reexamined Weingarten et al.’s meta-analysis using a method called z-curve. Unlike p-curve, z-curve explicitly tests for selective reporting by modeling the distribution of statistically significant results. It is also more robust when studies vary in power and when some studies have true effects while others do not. Whereas p-curve merely rejects the hypothesis that all studies were obtained under a true null, z-curve estimates the maximum proportion of significant results that could be false discoveries, often referred to as an upper bound on the false discovery rate (Bartos & Schimmack, 2022).

Sotola found that priming studies reported approximately 76% significant results—somewhat below the roughly 90% level typically observed in social psychology—but that the estimated average power to produce a significant result was only 12.40%. Z-curve also did not rule out the possibility that all observed significant results could have arisen without a true effect. This finding does not justify the conclusion that social priming effects do not exist, just as observing many white swans does not prove the absence of black swans. However, it does indicate that the existing evidence—including the Weingarten et al. meta-analysis—does not provide conclusive support for claims that social priming effects are robust or reliable. The literature documents many reported effects but offers limited evidential leverage to distinguish genuine effects from selective reporting (many sitings of UFOs, but no real evidence of alien visitors).

Despite these concerns, Weingarten’s meta-analysis continues to be cited as evidence that priming effects are real and that replication failures stem from factors other than low power, selective reporting, and effect size inflation. For example, Iso-Ahola (2025) cites Weingarten et al. while arguing that there is no replication crisis. Notably, this assessment does not engage with subsequent reanalyses of the same data, including Sotola’s z-curve analysis.

This article illustrates what can reasonably be described as willful ignorance: evidence that does not fit the preferred narrative is not engaged. The abstract’s claim that “there is no crisis of replication” is comparable, in terms of evidential standards, to assertions such as “climate change is a hoax”—claims that most scientists regard as unscientific because they dismiss a large and well-documented body of contrary evidence. Declaring the replication problem nonexistent, rather than specifying when, where, and why it does not apply, undermines psychology’s credibility and its aspiration to be taken seriously as a cumulative science.

Willful ignorance is also evident in a recent meta-analysis, again with Albarracín as senior author. This meta-analysis does not include a p-curve analysis and ignores the z-curve reanalysis by Sotola altogether. While the new meta-analysis reports no effects in preregistered studies, its primary conclusion nevertheless remains that social priming has an effect size of approximately d = .30. This conclusion is difficult to reconcile with the preregistered evidence it reports.

A different strategy for defending social priming research is to question the validity of z-curve itself (Pek et al., 2025, preprint, Cognition & Emotion). For example, Pek et al. note that transforming t-values into z-values can break down when sample sizes are extremely small (e.g., N = 5), but they do not acknowledge that the transformation performs well at sample sizes that are typical for social psychological research (e.g., N ≈ 30). Jerry Brunner, a co-author of the original p-curve paper and a professor of statistics, identified additional errors in their arguments (Brunner, 2024). Despite detailed rebuttals, Pek et al. have repeated the same criticisms without engaging with these responses.

This pattern is best described as willful incompetence. Unlike willful ignorance, which ignores inconvenient evidence, willful incompetence involves superficial engagement with evidence while the primary goal remains the defense of a preferred conclusion. In epistemic terms, this resembles attempts to rebut well-established scientific findings by selectively invoking technical objections without addressing their substantive implications.

Z-Curve Analysis of Social Priming

To illustrate how z-curve works and what it reveals about social priming, I analyzed the new meta-analysis of social priming using z-curve. Importantly, I had no influence on the data and only transformed reported information about effect sizes and sampling error into z-values. A z-curve plot provides a descriptive visualization of the evidential strength of published results relative to the null hypothesis. At this descriptive level, few assumptions are required.

The full z-curve analysis fits a statistical model to the distribution of z-values. Studies with low power—due to small effect sizes, small sample sizes, or both—are likely to produce low z-values and often nonsignificant results (z = 1.96 ≈ p = .05). Studies with high power (e.g., 80% power corresponds to z ≈ 2.8) require either moderate-to-large effect sizes or very large sample sizes. Inspection of the plot shows that most studies cluster at low z-values, with relatively few studies producing z-values greater than 2.8. Thus, even before modeling the data, the distribution indicates that the literature is dominated by low-powered studies.

The actual z-curve analysis fits a model to the distribution of z-values. Studies with low power (small effect sizes, small sample sizes) are likely to produce low z-values and often z-values that are not significant (z = 1.96 ~ p = .05). Studies that have high power (80% power ~ z = 2.8) have moderate to large effect sizes or really large sample sizes). Inspection of the plot shows most studies have low z-values and few studies have z-values greater than 2.8. Thus, even without modeling the data, we can see that this literature is dominated by studies with low power.

The plot also reveals clear evidence of selective reporting. If results were reported without selection, the distribution of z-values would decline smoothly around the significance threshold. Instead, the mode of the distribution lies just above the significance criterion. The right tail declines gradually, whereas the left side drops off sharply. There are too many results with p ≈ .04 and too few with p ≈ .06. This asymmetry provides direct visual evidence of publication bias, independent of any modeling assumptions.

Z-curve uses the distribution of statistically significant results to estimate the Expected Replication Rate (ERR) and the Expected Discovery Rate (EDR). The ERR estimate is conceptually similar to p-curve–based power estimates but is more robust when studies vary in power. In the present analysis, the estimated ERR of 34% closely matches the p-curve estimate reported by Weingarten et al. (33%) but is substantially higher than Sotola’s earlier z-curve estimate (12.5%). However, ERR estimates assume that studies can be replicated exactly, an assumption that is rarely satisfied in psychological research. Comparisons between ERR estimates and actual replication outcomes typically show lower success rates in practice (Bartos & Schimmack, 2022). Moreover, ERR is an average: approximately half of studies have lower replication probabilities, but we generally do not know which studies these are.

The EDR estimates the proportion of all studies conducted—including unpublished ones—that are expected to yield statistically significant results. In this case, the EDR point estimate is 19%, but there is substantial uncertainty because it must be inferred from the truncated set of significant results. Notably, the confidence interval includes values as low as 5%, which is consistent with a scenario in which social priming effects are absent across studies. Thus, these results replicate Sotola’s conclusion that the available evidence does not demonstrate that any nontrivial proportion of studies produced genuine social priming effects.

Pek et al. (2025) noted that z-curve estimates can be overly optimistic if researchers not only select for statistical significance but also preferentially report larger effect sizes. In their simulations, the EDR was overestimated by approximately 10 percentage points. This criticism, however, weakens rather than strengthens the evidential case for social priming, as an EDR of 9% is even less compatible with robust effects than an EDR of 19%.

The z-curve results also provide clear evidence of heterogeneity in statistical power. Studies selected for significance have higher average power than the full set of studies (ERR = 34% vs. EDR = 18%). Information about heterogeneity is especially evident below the x-axis. Studies with nonsignificant results (z = 0 to 1.95) have estimated average power of only 18–20%. Even studies with significant results and z-values up to 4 have estimated average power ranging from 23% to 56%. To expect an exact replication to succeed with 80% power, a study would need to produce a z-value above 4, yet the plot shows that very few studies reach this level.

Adjusting Alpha To Lower False Positive Risk

Z-curve can also be used to examine how changing the significance threshold affects false discoveries. With the conventional α = .05 criterion, one out of twenty tests of a true null hypothesis will be significant by chance. Lowering α to .01 reduces this rate to one in one hundred. However, stricter thresholds also reduce power and discovery rates. In some literatures, the reduction in false discoveries outweighs the cost of fewer significant results (Soto & Schimmack, 2024). This is not the case for social priming.

Setting α = .01 (z = 2.58) lowers the point estimate of the false discovery rate from 23% to 11%, but the 95% confidence interval still includes values up to 100%.

Setting α = .001 reduces the point estimate to 3%, yet uncertainty remains so large that all remaining significant results at that threshold could still be false positives.

P-Hacking Real Effects

It is possible to obtain more favorable conclusions about social priming by adopting additional assumptions. One such assumption is that researchers relied primarily on p-hacking rather than selective reporting. Under this scenario, fewer studies would need to be conducted and suppressed. When z-curve is fit under a pure p-hacking assumption, the estimates appear substantially more optimistic.

Under this model, evidence of p-hacking produces an excess of results just below p = .05, which are excluded from estimation. The resulting estimates suggest average power between 40% (EDR = .43) and 52% (ERR = .52), with relatively little heterogeneity. Nonsignificant results with z ≈ 1 are estimated to have average power of 46%, and significant results with z ≈ 4 have average power of 52%. If this model were correct, false positives would be rare and replication should be straightforward, especially with larger samples. The main difficulty with this interpretation is that preregistered replication studies consistently report average effect sizes near zero, directly contradicting these optimistic estimates (Dai et al., 2023).

Conclusion

So, is experimental social psychology a science? The most charitable answer is that it currently resembles a science with limited cumulative results in this domain. Meteorology is not a science because it acknowledges that weather varies; it is a science because it can predict weather with some reliability. Until social priming researchers can specify conditions under which priming effects reliably emerge in preregistered, confirmatory studies, the field lacks the predictive success expected of a mature empirical science.

Meanwhile willful ignorance and incompetence hamper progress towards this goal and undermine credible claims of psychology to be a science. Many psychology departments are being remained to have science in their name, but only acting in accordance with normative rules of science will make psychology a credible science.

Credible sciences also have a history of failures. Making mistakes is part of exploration. Covering them up is not. Meta-analyses of p-hacked studies without bias correction are misleading. Even worse are public significance statements directed at the general public rather than peers. The most honest public significance statement about social priming is “We fucked up. Sorry, we will do better in the future.”

Behavioral or social priming is the poster child of the replication crisis. Bargh declined Kahneman’s offer to rehabilitate it by showing that he could replicate his result. The same is true for other social psychologists who became famous for changing people’s behaviors without their knowledge / awareness.

While priming studies have largely disappeared from social psychology journals, the old studies still exist and have not been retracted although we know that they were obtained with unscientific methods that make it easy to present false evidence for false claims.

This allows unscientific meta-analysists to analyze these data and to continue to make claims that social priming is a real effect even in 2023 and even in a journal that is considered to be methodologically rigorous, although the name suggests otherwise (Psych Bull).

Dai, W., Yang, T., White, B. X., Palmer, R., Sanders, E. K., McDonald, J. A., Leung, M., & Albarracín, D. (2023). Priming behavior: A meta-analysis of the effects of behavioral and nonbehavioral primes on overt behavioral outcomes. Psychological Bulletin, 149(1-2), 67–98. https://doi-org.myaccess.library.utoronto.ca/10.1037/bul0000374

In the old days, the social power of censorship (peer-review) in scientific journals made it difficult to fight back against paradigm prisoners, who try to keep their little word of academia alive. Fortunately, consumers of scientific research now have options to ensure that they are not feeding their minds junk science.

I asked my ChatGPT (trained with discussions and information) to evaluate this article with a set of questions that anybody could ask an AI.

Critically evaluate this article.
Is the literature review accurate or misrepresent the broader literature
0 = totally false to 10 = totally accurate and consistent with current literature

Is this meta-analysis up to date or uses outdated methods
0 = totally outdated to 10 = totally up to date

Are the results interpreted correctly.
0 = totally misrepresents the results to 10 = totallly accurate

Integration with existing literature.
0 = not integrated at all, 10 = accurately interpreted in the context of broader literature

The scores are less important (as they would require comparison scores) than the reasons for the scores. Importantly, AI is neutral and more balanced than most humans, myself included, usually are.

Strengths

• The paper integrates its moderator findings into established theoretical disputes (perception–behavior link vs goal mediation), and it connects specific moderation patterns (e.g., goal value manipulations) to prior work and theoretical interpretations.
• It frames its contribution clearly as both (a) an expanded synthesis and (b) a mechanism-relevant test across moderators.

Limits

• Integration is strongest for the authors’ preferred theoretical framing; it is thinner on integrating the skeptical/critical meta-science side beyond noting that bias methods have “become ever more sophisticated” and providing the Lakens critique as a prompt. In other words, it engages critique more as a motivation for adding diagnostics than as a serious alternative interpretation of what the literature’s apparent “robustness” means. Priming_behavior_

I did ask a couple of follow up questions, mainly about the well-known problem that average effect sizes are meaningless when studies are heterogenous; priming sometimes works and sometimes it does not. To make priming research actually useful, we need to specify WHEN priming works. Priming MAY work or priming SOMETIMES works, is not a scientific finding.

On this point, the meta-analysis is as mute as most others are, but the paper will be cited as “priming works and has a moderate effect size.” Only psychologists believe that this is enough to defend priming against critics who say, “If priming works, why don’t you do a preregistered study with high power and show us that it works?”

ChatGPT Summary: This Meta-Analysis Tell Us When Priming Works?

The authors present an ambitious meta-analysis of priming effects on behavior and argue that replication failures can be reconciled with a “moderate” average effect size by appealing to heterogeneity and moderators. In principle, this is a legitimate defense: heterogeneous effects can exist even when many individual studies fail to replicate. In practice, however, the paper does not deliver what this defense requires.

Although substantial heterogeneity is documented, the moderator analyses do not clearly identify which studies work and which do not. Most examined moderators are weak, inconsistent, or explain only a small fraction of the variance. As a result, the analysis does not partition the literature into a subset of theoretically coherent, reliably effective studies versus a subset that fails. Without such discrimination, heterogeneity becomes descriptive rather than explanatory.

This creates a central tension in the paper’s conclusions. The authors argue for a nonzero average priming effect while simultaneously acknowledging widespread replication failures and publication bias. Yet they do not show that the moderators they test successfully predict when priming should occur. Consequently, the results do not support a practical or falsifiable claim about replicability. A new study cannot be classified, based on their findings, as likely to succeed or fail.

The strongest conclusion supported by the evidence is therefore modest: priming effects may exist under some conditions, but those conditions are not empirically established by the present meta-analysis. Claims of “moderate” effects should be interpreted as population averages over a poorly understood mixture of successful and unsuccessful studies, rather than as evidence that priming reliably works in practice.

In short, the paper shows that priming has not been decisively ruled out—but it does not show when, how, or how often it actually works.

POSTSCRIPT

PET allows for an effect size of d = 0.025. However, because this result rejects H0, d = 0, at the 5% level, the authors use the PEESE estimate that is always higher. If they had used alpha = .01 or a minim effect size of d = .1, PET would not have been rejected, and the average effect size estimate would be close to zero. Did the authors p-hack PET to be significant? It does not matter. The evidence is weak and the main problem remains. Heterogeneity without a clear moderator that explains when it works and when it does not. This is psycho-science, not real science.

PPS

Priming may work, but NOT when a study is preregistered. (hm?)

The File-Drawer Problem

A single study is rarely enough to provide sufficient evidence for a theoretically derived hypothesis. To make sense of inconsistent results across multiple studies, psychologists began to conduct meta-analysis. The key contribution of meta-analyses is that pooling evidence from multiple studies reduces sampling error and allows for more precise estimation of effect sizes.

The key problem of meta-analysis is the assumption that individual studies are an unbiased sample of all studies that were conducted. Selective publishing of statistically significant results in favor of a prediction leads to inflated effect size estimates. This problem has been dubbed the file drawer problem. Whereas significant results are submitted for publication, non-significant results are put into a file drawer.

Rosenthal (1979) pointed out that a literature consisting entirely of statistically significant findings could, in principle, reflect no true effects. However, such a scenario was often considered unlikely under the assumption of honest testing with a fixed Type I error rate, because studies without real effects produce a significant result only about 1 out of 20 times when the error rate is controlled with alpha = .05. In addition, Rosenthal proposed a statistic, fail-safe N, to evaluate this risk, and meta-analyses often found that fail-safe N was large enough to infer a real effect.

The assessment of the published literature in psychology shifted dramatically in the early 2010s. Critically, Simmons, Nelson, and Simonsohn (2011) showed with simulations that a few statistical tricks could increase the probability of significant results without real effects from 1:20 to nearly 1:2. Even consistent statistically significant results in several studies were no longer unlikely. Presenting 9 significant results would not require 180 studies, but only 18 (Bem, 2011), or even fewer with more extreme use of questionable statistical practices that later became known as p-hacking. This highly cited article created a crisis of confidence in single studies, and by extension also in meta-analytic findings.

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The False Positive Detection Problem

A few years later, Simonsohn, Nelson, and Simmons (2014) published a statistical method, p-curve, to probe the credibility of sets of statistically significant results, often drawn from meta-analyses. They referred to this method as a “key to the file drawer.” The analogy is potentially confusing. P-curve does not test whether publication bias exists, nor does it determine whether questionable statistical practices were used. It also does not estimate how many studies are in the proverbial file drawer. In fact, p-hacking implies that file drawers can be small, even if significant results are false positives. When p-hacking is present, the size of the file drawer is therefore no longer informative.

What p-curve does, and what it does better than fail-safe N, is to assess whether the observed set of statistically significant results is inconsistent with the hypothesis that all tested effects are exactly zero. Simonsohn et al. (2014) call this property evidential value. Formally, significance tests are applied to the distribution of significant p-values to evaluate the null hypothesis implied by this scenario. When this hypothesis can be rejected using conventional significance tests, the data are said to have evidential value. Later versions of p-curve also include stronger tests, but the underlying logic remains the same.

Equipped with a new diagnostic tool, psychologists had a different way to evaluate published studies. While p-curve still shares a limitation of significance testing—namely that it cannot provide affirmative evidence for the null hypothesis, such as the claim that all published significant results are false positives—it can nevertheless show that a set of studies fails to provide evidence against this extreme null hypothesis. Lack of evidence is still valuable information, especially when a set of statistically significant results appears to suggest strong support for a hypothesis, but this support is potentially driven by selective reporting or p-hacking rather than true effects.

P-Curve Coding

P-curve made it possible to evaluate the hypothesis that many, if not most (Ioannidis, 2005), published results are false positives. If this were the case, many p-curve meta-analyses of a specific hypothesis should be flat or left-skewed. In contrast, true hypotheses should produce right-skewed p-curves. Surprisingly, this simple approach to examine the false positive rate has not been systematically applied.

I conducted a review of p-curve articles to see what we have learned about false positives from a decade of p-curve analyses. The article introducing p-curve has been cited more than 1,000 times (WoS, December 30, 2025). I reviewed two samples of articles. First, I sampled the most highly cited articles. These articles are of interest because they may introduce many readers to p-curve, including readers who are not experts in meta-analysis. These articles are also more likely to report high-visibility results. The second set of articles focused on the most recent articles. The rationale is that more recent articles reflect current practice in how p-curve is used and how p-curve results are interpreted.

P-curve results were coded first in terms of evidential value (right-skewed vs. not right-skewed). The second classification concerned the proper interpretation of right-skewed p-curves. Correct interpretations were limited to claims about evidential value. However, some articles misinterpreted p-curve as a bias test and falsely inferred a low risk of bias from a p-curve with evidential value.

The coding scheme had three categories. First, articles that did not report a p-curve analysis were coded as irrelevant. Second, articles that reported a p-curve analysis and correctly limited discussion to evidential value were coded as correct. Third, some articles reported a p-curve analysis but made claims about bias, selection bias, or p-hacking that are invalid. Namely, these articles interpreted results showing evidential value to conclude that publication bias or p-hacking were not a concern. This conclusion is invalid because data can show evidential value while biases can still inflate effect size estimates simultaneously. These articles were coded as incorrect.

Articles were found using WebOfScience. Articles classified as editorial material were excluded. The list of coded articles and their coding is available on the Open Science Framework (OSF) project.

P-Curve Results

I coded 142 articles. A large number of them (k = 95; 67%) cited the p-curve article but did not report a p-curve analysis. An additional two articles stated that a p-curve analysis had been conducted but did not provide a clear description of the results. All 45 articles that reported a p-curve analysis found evidential value. Some of these articles showed flat p-curves for specific subsets of studies, but this pattern was attributed to theoretically meaningful moderators (e.g., Tucker-Drob & Bates, 2015). Importantly, none of the reviewed p-curve analyses suggested that all reported results were false positives.

To further probe this issue, I conducted an automated search of all 990 abstracts retrieved from Web of Science for references to p-curve results indicating no evidential value or flat p-curves. This search did not identify a single abstract reporting such a result.

In terms of interpretations, the results are also notable. More articles misrepresented p-curve as a bias test (k = 28) than correctly presented p-curve as a test of evidential value. Because p-curves were almost always right-skewed, these misinterpretations frequently led authors to infer a low risk of bias, which is not a valid inference from a right-skewed p-curve.

Once, p-curve was even used to discount evidence of bias obtained with other methods. For example, “Funnel plot analysis showed evidence of publication bias, but p-curve analysis suggested that our results could not be caused by selective reporting” (Goubran et al., 2025).

Discussion

Two influential theoretical articles raised concerns that many published rejections of null hypotheses could be false positive results (Ioannidis, 2005; Simmons et al., 2011). P-curve provides an opportunity to evaluate this prediction empirically, but the evidence obtained in p-curve meta-analyses has not been systematically examined. I found that p-curve results always showed evidential value. This finding is in stark contrast to scenarios that suggest the majority of statistically significant results are false (Ioannidis, 2005).

At the same time, p-curve is often misunderstood and misinterpreted as a bias test. This interpretation may lead to a false sense of the credibility of published results. Just as replication failures do not justify the inference that the original result was a false positive (Maxwell et al., 2006), evidential value does not imply that results can be replicated.

There are several possible explanations for the failure to find evidence of false positive results in meta-analyses. One explanation is that false positives are more likely to arise in individual studies than in meta-analyses, which require multiple studies testing the same hypothesis. Sustaining a literature of false positives would therefore require repeated and consistent use of extremely questionable research practices. Few researchers may be motivated to use extreme p-hacking repeatedly to force significant results in the absence of a real effect. Bem (2011) may represent an unusual case in that he appeared to be highly motivated to convince skeptical scientists of the existence of extrasensory perception and to present evidence that met prevailing methodological standards in experimental social psychology. More commonly, researchers may advance claims based on selective or suggestive evidence without attempting to build a cumulative evidential record.

Another explanation is that the statistical null-hypothesis is unlikely to be true (Cohen, 1994). What are the chances that an experimental manipulation has no effect whatsoever on behavior? Subliminal stimuli are often cited as candidates, but even in this literature concerns have been raised that effects may be driven by partial stimulus detection. In correlational research, it is even less likely that two variables have a true correlation of exactly zero. As a result, p-hacking may often inflate effect sizes rather than generate false positive results in the strict sense of rejecting a false null hypothesis.

The problem is when rejection of the nil-hypothesis is confused with credible evidence for a meaningful effect. For example, a p-curve analysis of ego depletion shows evidential value (Carter et al., 2019), but even the original authors were unable to replicate the effect (Vohs et al., 2019). This example illustrates that evidential value is a necessary but not sufficient condition for a credible science. Even if effect sizes are not exactly zero, they can be dramatically inflated. As p-curve is limited to the assessment of evidential value, other methods are required to (a) assess whether published results are biased by selection or p-hacking, (b) estimate population effect sizes while correcting for bias, and (c) estimate the false positive risk in heterogeneous meta-analyses, where a subset of statistically significant results may be false positives.

However, it is also possible that p-curve results are biased and provide spurious evidence of evidential value, that is, evidential value itself may constitute a meta-level false positive. In this case, p-curve would falsely reject the null hypothesis that all statistically significant results are false positives. One possible source of bias is that studies with stronger (but false) evidence may be more likely to be included in meta-analyses than studies with weaker (false) evidence. For example, some researchers may p-hack to more stringent thresholds (e.g., α = .01) or apply Bonferroni corrections, while standard meta-analytic coding practices may mask these selection processes. However, p-hacking of this kind would be expected to produce left-skewed or flat p-curves, such that explaining the near-absence of flat p-curves would require the additional assumption that extreme p-hacking is rare. At present, this possibility cannot be ruled out, but it appears unlikely to account for the overwhelming predominance of right-skewed p-curves.

A more plausible explanation is selective reporting of p-curve results. Because reporting p-curve analyses is optional, meta-analysts may be more likely to include p-curve results when they show evidential value and omit them when p-curves are flat or left-skewed. Evaluating this form of meta-analytic selection bias requires auditing meta-analyses that did not report p-curve results and applying the method retrospectively.

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Conclusion

The most important finding is that concerns about many false positive results in psychology journals are not based on empirical evidence. False positives in single studies are not important because no single study can serve as an empirical foundation for a theory. There is no evidence that entire literatures are just a collection of false positive results. This does not mean that published results are credible. Publication bias, inflation of effect sizes, low replicability, method factors in correlational studies, and lack of construct validation remains serious obstacles that have sometimes been overshadowed by concerns about false positive results. These issues deserve more attention in the future.

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Concerns about credibility are widespread, but they often do not clearly distinguish between different sciences. One problem is that it is difficult to compare sciences quantitatively. One way to do so is to examine the strength of empirical evidence. We cannot compare effect sizes across sciences, but we can compare how precise effect size estimates are and how often rejections of null hypotheses may be false.

The first “science-wide” study was based on empirical results in medicine (Jager & Leek, 2013). Their methods and results were challenged, and it took some time before alternative methods became available. A better method is z-curve (Bartos & Schimmack, 2022; Brunner & Schimmack, 2020). Z-curve has been mostly used in psychology. A comparison with medicine showed that clinical trials have less power, but report results more honestly than psycholgy, where focal tests confirm predicts with success rates over 90% (Schimmack, 2020; Schimmack & Bartos, 2023).

A recent article extracted confidence intervals from four epidemiology journals.

Ackley, S. F., Andrews, R. M., Seaman, C., Flanders, M., Chen, R., Wang, J., Lopes, G., Sims, K. D., Buto, P., Ferguson, E., Allen, I. E., & Glymour, M. M. (2025). Trends in the distribution of P values in epidemiology journals: A statistical, P-curve, and simulation study. American Journal of Epidemiology, 194(12), 3630–3639. https://doi.org/10.1093/aje/kwaf184

The authors were not aware of z-curve, but I was able to analyze their shared data. I examined trends over time and found no evidence that z-curve parameters correlated with publication year. Thus, the results are representative of the literature. An initial analysis with standard z-curve showed no evidence of selection bias. Therefore, I fitted the full data, including non-significant results.

The key findings are: (a) The observed and expected discovery rates are 91%. This means that 91% of the results are significant, but the reason is not selection bias – as it is often in psycholoy – but high power to reject false null hypotheses; (b) a very low false positive risk even with alpha = .05, and a high probability that an exact replication study with a new sample from the same population would produce a significant result again. However, there is some evidence of p-hacking. That is there are more just significant results (2 to 2.4) than the model predicts, Excessive Just Significance Test, p = .0008. Visual inspection of the plot shows, however, that the effect size is small, observed 0.25%, expected 0.24%, and that statistical significance reflects mainly the large sample size.

In short, this is a healthy literature that instills confidence in epidemiological research. The reason is that epidemiological studies typically have large sample sizes and aim for precise effect size estimation. With this goal in mind, studies have high power to reject the null hypothesis of no effect, if only because doing so is not very informative. In contrast, psychologists often use small samples that are sometimes not even large enough to test a null hypothesis properly. Comparing epidemiology with psychology is therefore a bit like comparing apples and oranges, but this false comparison is often made when science as a whole is evaluated. In reality, different sciences face different problems. Low power and replicability are a problem for sciences that invest few resources in many studies, such as psychology. We cannot generalize from replication failures in these sciences to other sciences.

For psychology, effect sizes estimation mostly remains a scientific utopia, but the z-curve of epidemiology shows what that utopia looks like.

First, a sigh of relief. We made it through 2025, despite the rise of evil in the world. Let’s all hope or pray that 2026 will be better. In our little and mostly harmless world of psychology, however, things were rather calm. Here are some stats from my blog post to review 2025.

Clicks and Engagement

Many of these stats are bots and 1second visits, but some are real humans who are interested in scientific psychology and how to make it better. As long as I see these levels of engagement, I feel encouraged to keep the blog going. Likes and comments are rare, but very much appreciated. As the saying goes, one comment is worth more than 1,000 visits.

Content

The posts about “Fast and Slow” are still the most viewed pages. Reconstruction of a train wreck is home to Kahneman’s humble response to the z-curve analysis of the priming chapter, but the “Meta-Scientific Perspective” post is a review of all chapters.

The surprising addition is my farewell to personality psychology. It was an emotional rant expressing my frustration with bad measurement practices and unwillingness to improve them in the field.

Personality Psychology: Bye Bye, Au revoir, Auf Wiedersehen – Replicability-Index

I was ready to give up on it entirely, but ironically, I am still teaching an undergraduate course on personality, which I define as the study of personality differences. Fortunately, there is enough research and open data that I can analyze myself that I can teach the course form a coherent scientific perspective. The textbook is now available on the blog.

Personality Science: The Science of Human Diversity – Replicability-Index

Another surprise is that the new post on terror management made the Top 10 list. I thank the author for including z-curve in their meta-analysis. The article shows that an entire literature with more than 800 studies can be made up of studies with low replicability and a high false positive risk. It also shows how z-curve is superior to p-curve that can only reject the null hypothesis that all (100%) of the studies are false positives, but not that 95% are.

R.I.P Terror Management: A Z-Curve Analysis – Replicability-Index

Below the Top 10 are still some noteworthy posts from 2025.

Why Uri Simonsohn is a Jerk – Replicability-Index (967 views)
I found an old email that referred to Uri as a jerk. The complaint was that the datacolada team are all about open science and criticism of others, but do not even allow people who are criticized to post an open response on their blog. No comments, please! I say that is not open science. That is just like legacy journals that do not publish comments they do not like (yes, I mean you Psychological Methods).

Review of “On the Poor Statistical Properties of the P-Curve Meta-Analytic Procedure” – Replicability-Index (657 views)

A related post features a critique of p-curve that later triggered a “no comments allowed” response by Uri on the datacolada blog. After 10 years of p-curve, it is fair to say that it has only produced one notable finding. Most of the time, p-curve shows evidential value; that is, we can reject the null hypothesis that all results are false positives. So, concerns about massive p-hacking in the false positive article are not empirically supported. The area of false positive paranoia is coming to an end. More on this, in a forthcoming post.

The Ideology versus the Science of Evolved Sex Differences – Replicability-Index (649 views)

My personality textbook includes a scientific review of the research on sex-differences. It debunks many stereotypes that are often dressed up as pseudo-scientific evolutionary wet dreams of sexist pseudo-scientists like Roy F. Baumeister, who still is treated by some psychologist as an eminent scholar. To be a science, psychology has to hold psychologists accountable to scientific standards. Otherwise, it is just a cult.

Psychologists really confuse academic freedom with “you can say the stupidest things”, like one article that compared use of AI to dishonest research practices.

Is Using AI in Science Really “Research Misconduct”? A Response to Guest & van Rooij – Replicability-Index (649 views)

Many of these articles could be published as blog posts, saving us (tax payers) money.

Traffic

Most of the traffic still comes from search engines and over 90% of this traffic comes from Google. Next is Facebook, where I maintain the Psychological Methods Discussion Group.
The group was very active during the Replication Crisis times, but little discussion occurs these days. I would love to move it somewhere else, but I have not found an easy and cheap alternative. Interestingly, Open Science advocates also do not seem to see value in hosting an open forum for discussion. I tried to post on APS, but you have to pay to correct their misinformation. So, there you have it. Psychology lacks an open discussion forum (OSF); talk about scientific utopia. I left fascist X a long time ago, but still get traffic from there. I am now posting on Bluesky with little direct engagement, but apparently some people notice the posts and visit.

Most interesting are the visits from ChatGPT. I am fully aware of the ecological problems, but AI will fix many of the problems that psychology faces, and equally environmentally problematic conferences serve more the purpose of taxpayer-paid vacations than advancing science. Nothing wrong with perks for underpaid academics, but let’s not pretend it advances science when talks are just sales pitches for the latest pseudo-innovation. Anyhow, blogging is now more important than publishing in costly peer-reviewed journals because AI does not care about peer-review and is blocked from work behind paywalls.

Some academics rail against AI, but appearently they never used one. ChatGPT constantly finds errors in my drafts and helps me to correct them before I post them. It also finds plenty of mistakes in published articles and we often have a chuckle that this stuff passed human peer review. On that note, human peer-review sucks and can be easily replaced with AI reviews. At least you don’t have to wait months to get some incoherent nonsensical reviews that only show lack of expertise by the reviewers.

The traffic from ChatGPT also underestimates the importance of AI. Few people actually click on links to check information, but ChatGPT’s answer is still influenced by my content. Ultimately, the real criterion for impact will be how much our work influences AI answers.

Location

The United States continues to dominate psychology. Europe has more people, but only a few European countries invest (waste?) money on psychology. A clear North-West vs the rest difference is visible. Former communist East is just poor, but the problem in the South is religion.

One of the highlights of 2025 was my visit of the Winter school in Padua, one of the oldest universities. I learned that it was relatively free and Galileo made important discoveries there, but he ran into “a little problem” when he moved to Florence and clashed with the Catholic church. The lesson is that the broader culture influences science and currently the USA is showing that its values are inconsistent with science. Religious fundamentalism in the Confederate states is incompatible with science, especially a social one. China is on the rise, and it seems more likely that they will be the next home of psychology, unless Europe gets its act together. China is a totalitarian regime, but a communist dictatorship seems better than religious ones for science and for the future of the planet.

Forecast 2026

The main prediction is that traffic from ChatGPT and China will increase. Possibly, traffic from other AIs like Gemini will also emerge. Other developments are harder to predict and that is the fun of blogging. I don’t have to invest months of my limited remaining life span to fight stupid reviewers to be allowed to pay $3,000 or more of Canadian tax-payers money to share my work with the world. I can do so for free and just see whether somebody found the work interesting. Fortunately, I am paid well enough so that I do not have to worry about the incentive structure in academia that everybody knows leads to fast, cheap, and bad science, but nobody is able to change. For those of you who are still a cog in this mindless machine, I can say there is hope. The tyranny of publication cartels is weakening and maybe sometimes it is better to just post a preprint than to try the 10th journal for the stamp of approval in a peer-reviewed (predatory) journal. Academia is a long game. The rewards come at the end when you can do what you want without concerns about approval. Humanist psychologists call this self-actualization. I call it the freedom of not giving a fuck anymore.

See you in 2026,
Ulrich Schimmack

Happy New Year

What Is Science?

What is science? According to ChatGPT, the most basic concept of science lacks a clear definition. There is not one science, but many sciences that share overlapping features, creating a family resemblance rather than a set of necessary and sufficient conditions. As Laudan (1983) argued, “the search for a demarcation criterion between science and non-science is a pseudo-problem.”

Attempts to define science in terms of verification, falsifiability, empirical content, prediction, method, progress, or realism have all faced objections. Nevertheless, these concepts remain relevant for distinguishing science from other belief systems.

Even in the absence of strict definitions, concepts can be characterized by prototypes. Psychology distinguishes between descriptive prototypes, which capture typical features (e.g., feathers and flight for birds), and ideal prototypes, which represent standards rather than averages. Nobody is perfectly healthy or happy, but comparison to an ideal allows meaningful evaluation. I argue that science functions in the same way: not as a fixed set of practices, but as an ideal prototype against which actual scientific activity can be evaluated.

An old-fashioned ideal prototype of science describes it as a collective effort to test beliefs and to revise or replace them when new information reveals inconsistencies (Hume, Popper, Peirce, Dewey). A defining feature of this ideal is openness—openness to new evidence and openness to changing beliefs.

The value science places on discovery reflects this openness. Novelty matters because scientific inquiry is oriented toward progressive improvement in understanding. The history of science shows that expanding, revising, and sometimes challenging existing belief systems is a central driver of progress, even when that progress is slow and non-linear.

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Paradigms and Confined Openness

The definition of science as an ideal prototype differs from descriptions of actual scientific practice because reality rarely matches ideals. Scientists are human agents embedded in social and institutional contexts, and their behavior is shaped by incentives that can conflict with norms of openness and belief revision. Kuhn’s analysis of paradigms and paradigm shifts illustrates these tensions between epistemic ideals and community dynamics.

A scientific paradigm functions much like a culture: it has foundational beliefs, socialization practices, initiation rituals, and a collective goal of preservation and expansion. Within paradigms, researchers may revise beliefs and pursue novelty, but foundational assumptions are typically treated as off-limits. For example, a foundational assumption in mainstream social psychology is that experiments are the primary source of valuable knowledge, privileging laboratory studies over field research.

This produces what I call confined openness: openness to criticism, replication, and revision within a paradigm, combined with resistance to challenges that target its foundations. A visitor to a scientific conference would see many hallmarks of science on display, yet might not notice that certain questions are never asked.

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The Replication Crisis in Social Psychology

In the early 2010s, it became evident that common research practices in experimental social psychology deviated from the ideal of open inquiry in which evidence can genuinely threaten beliefs. A key flashpoint was Bem (2011), which reported evidence for a phenomenon incompatible with established physical and psychological assumptions. The lesson was not that Bem committed fraud, but that ordinary analytic flexibility combined with selective publication can make implausible claims appear empirically supported (Schimmack, 2012).

The core problem was that researchers could accumulate confirmatory evidence without reporting nonconfirmatory outcomes. When null or contradictory results are systematically underreported, the published literature ceases to constrain belief revision. Psychology has long exhibited unusually high rates of statistically significant findings; Sterling (1959) reported that roughly 97% of tests rejected the null, and later work confirmed this excess of positive results (Motyl et al., 2017).

In addition, many journals are organized around specific paradigms and explicitly aim to promote them. Such journals are structurally unlikely to publish work that challenges the paradigm’s core assumptions.

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Open Science and Its Limits

In response, researchers advocated reforms under the banner of open science, typically operationalized as procedural transparency and reproducibility: sharing data, materials, and code; preregistration; replication; and safeguards against selective reporting. These reforms improve error detection and accountability within paradigms by making claims easier to audit and by reducing reporting flexibility.

The replication crisis also socialized a new generation of researchers to view credibility as a methodological and institutional problem rather than a matter of personal integrity. However, the open science movement’s focus on single studies and single findings risks deflecting attention from deeper structural sources of closedness. These include incentive systems that reward publishable success, norms that delimit legitimate questions, and paradigm-level assumptions treated as nonnegotiable.

The most fundamental constraint is the trap of paradigmatic research described by Kuhn. Paradigms restrict openness by confining criticism to questions that can be addressed within an accepted framework. In mature sciences, stable theoretical foundations allow paradigmatic research to produce cumulative progress. Psychology, by contrast, lacks a unifying paradigm and is fragmented into numerous micro-paradigms sustained as much by social and institutional commitments as by decisive empirical support. Debates such as the personality–situation controversy illustrate how paradigm boundaries can become sites of identity and norm enforcement rather than objects of open-ended inquiry.

Current incentive structures exacerbate this problem. Science operates as a reputational marketplace in which publications, grants, and visibility are assumed to signal quality. Yet producers and evaluators largely overlap. Reviewers, editors, and panelists are drawn from within paradigms, creating selection pressures favoring work that extends existing frameworks. These dynamics propagate into citation counts, funding decisions, and career advancement, reinforcing paradigmatic stability.

Open science rightly targets misaligned incentives for transparency and reproducibility (Nosek et al., 2015), but it remains focused on improving paradigmatic research rather than evaluating paradigms themselves. As a result, research programs can become highly replicable without producing theoretical progress. For example, it is highly replicable that self-report measures and Implicit Association Test scores correlate weakly. Yet this regularity alone does not resolve whether the discrepancy reflects measurement error or a substantive distinction between conscious and unconscious processes (Schimmack, 2021).

After more than a decade of reform, these deeper concerns remain largely unaddressed. Researchers can adopt open practices while leaving foundational assumptions intact. While implausible claims are now harder to publish, the incentive structure still rewards work that stabilizes paradigms rather than subjects them to serious challenge.

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Meta-Analysis, Meta-Science, and Meta-Paradigmatic Critique

The term meta has a long history in psychology. Meta-analysis emerged in the 1970s to integrate evidence across studies, and today meta-analyses are highly cited because they summarize large literatures. However, meta-analyses typically aggregate results produced within paradigms rather than evaluating the paradigms themselves. Theoretical questions and under-studied alternatives fall outside their scope, and conclusions are shaped by publication bias and researcher allegiance.

Addressing these limitations requires moving beyond meta-analysis to meta-science. Meta-science evaluates research programs rather than producing new findings. Meta-scientists function as knowledgeable consumers who assess whether bodies of research adhere to best practices and whether paradigms remain epistemically productive.

Yet most meta-science operates at a high level of abstraction, focusing on general properties of science rather than sustained critique of specific paradigms. What is needed instead is meta-paradigmatic evaluation: paradigm-specific critique conducted by domain experts who are institutionally independent of the paradigms they evaluate.

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Toward Open Meta-Paradigmatic Science

Systematic paradigm evaluation is likely to encounter resistance, just as open science did. Meta-paradigmatic critique may be framed as a threat to academic freedom. But academic freedom has never been absolute. Researchers accept ethics review and other forms of oversight when fundamental norms are at stake. Critical evaluation does not restrict inquiry; it is a constitutive feature of science.

Unlike open science reforms, meta-paradigmatic evaluation requires institutional change. It must be recognized as a legitimate scholarly activity with its own funding, review panels, positions, and journals. While meta-science is itself imperfect and subject to capture, it offers a cost-effective means of preventing the long-term stagnation of research programs.

Existing outlets provide only partial solutions. Journals with low rejection rates reduce gatekeeping but carry high costs and low prestige. Specialized journals such as Meta-Psychology welcome critical evaluation but remain marginal. Journals devoted to meta-science typically operate at an abstract level and do not engage deeply with specific paradigms.

What is missing are field-specific, meta-paradigmatic journals insulated from paradigm capture. Meta-paradigmatic critique requires deep disciplinary expertise combined with institutional independence—an uncommon combination given current training and reward structures.

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Conclusion: Science as Utopia

The ideal prototype of science is a utopia: a state that cannot be fully realized but that serves as a regulative aspiration. Open and honest reporting of results should not be an utopia; it is a minimal requirement of scientific practice, and reward structures must support it.

A more demanding utopia requires something further: openness to sustained critical examination of fundamental beliefs. Such beliefs can carry emotional and identity-laden significance for scientists, comparable to religious beliefs for believers. Because humans naturally resist scrutiny of core commitments, openness at this level cannot be left to individual virtue. It must be institutionalized.

Open and independent challenges to scientific paradigms—especially at the level of foundational assumptions—should therefore be understood not as threats to science, but as necessary conditions for its long-term epistemic vitality.

After more than a decade of reform, these deeper concerns remain largely unaddressed. Researchers can adopt open practices while leaving foundational assumptions intact. While implausible claims are now harder to publish, the incentive structure still rewards work that stabilizes paradigms rather than subjects them to serious challenge.

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Core References

Laudan, L. (1983). The demise of the demarcation problem. In R. S. Cohen & L. Laudan (Eds.), Physics, philosophy and psychoanalysis: Essays in honor of Adolf Grünbaum (pp. 111–127). D. Reidel. (SciSpace)

Kuhn, T. S. (1970). The structure of scientific revolutions (2nd ed.). University of Chicago Press. (UW-Madison Libraries)

Nosek, B. A., Spies, J. R., & Motyl, M. (2012). Scientific utopia: II. Restructuring incentives and practices to promote truth over publishability. Perspectives on Psychological Science, 7(6), 615–631. https://doi.org/10.1177/1745691612459058 (SAGE Journals)

Nosek, B. A., Alter, G., Banks, G. C., Borsboom, D., Bowman, S. D., Breckler, S. J., et al. (2015). Promoting an open research culture. Science, 348(6242), 1422–1425. https://doi.org/10.1126/science.aab2374 (Aspen Institute)

Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17(4), 551–566. https://doi.org/10.1037/a0029487 (UBC Emotion & Self Lab)

Schimmack, U. (2020). A meta-psychological perspective on the decade of replication failures in social psychology. Canadian Psychology/Psychologie canadienne, 61(4), 364–376. https://doi.org/10.1037/cap0000246 (CoLab)

Schimmack, U. (2021). Invalid claims about the validity of implicit association tests by prisoners of the implicit social-cognition paradigm. Perspectives on Psychological Science, 16(2), 435–442. https://doi.org/10.1177/1745691621991860 (SAGE Journals)

Bem, D. J. (2011). Feeling the future: Experimental evidence for anomalous retroactive influences on cognition and affect. Journal of Personality and Social Psychology, 100(3), 407–425. https://doi.org/10.1037/a0021524 (American Psychological Association)

Sterling, T. D. (1959). Publication decisions and their possible effects on inferences drawn from tests of significance—or vice versa. Journal of the American Statistical Association, 54, 30–34. (The James Lind Library)

Motyl, M., Demos, A. P., Carsel, T. S., Hanson, B. E., Melton, Z. J., Mueller, A. B., Prims, J. P., Sun, J., Washburn, A. N., Wong, K. M., Yantis, C. A., & Skitka, L. J. (2017). The state of social and personality science: Rotten to the core, not so bad, getting better, or getting worse? Journal of Personality and Social Psychology. https://doi.org/10.1037/pspa0000084 (sciencedaily.com)

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At its best, science is amazing. It produces discoveries that change our understanding of the world—and the world itself. Human lives have been transformed by scientific knowledge and technology, often for the better. It has certainly made my life better than that of my ancestors.

Yet science continues to be under attack. Historically, religious dogma sometimes clashed with scientific progress. It took the Catholic Church more than three centuries before Pope John Paul II formally acknowledged that Galileo was right to claim that the Earth moves around the Sun.

A more recent and devastating example is Nazi Germany, where science was subordinated to ideological pseudo-science in order to justify mass murder. The regime also drove out many Jewish scientists, some of whom later contributed to the Allied war effort. Later still, scientific progress in the Eastern Bloc was hampered by putting party loyalty over scientific excellence rather than evidence. These episodes illustrate a recurring lesson: science requires ethical guardrails, but it does not survive political domination.

Today, science is advancing rapidly in parts of the world, including China, for example through major investments in green energy. At the same time, the United States has increasingly undermined scientific consensus on issues such as vaccines and climate change and has placed growing pressure on scientific institutions. A number of observers warn that these developments threaten academic freedom and risk slowing scientific progress. One prominent justification for attacks on universities is the claim—advanced by some conservative academics, including Jonathan Haidt and Jordan Peterson—that universities are ideological “cesspools” in which naïve students are indoctrinated by hard-left professors.

This image of universities is both inaccurate and unscientific. For example, modern genetics has shown that humans are one species with a single, shared gene pool, not distinct biological races that can be ranked by skin color. This is not “woke ideology”; it is a straightforward empirical fact that only conflicts with racist belief systems.

Critics often argue that universities are repeating historical mistakes by ignoring science in order to impose liberal or radical-left values on campus. But what, concretely, are these alleged policies? Following the murder of George Floyd, many North American universities examined whether systemic racism contributes to a hostile climate for Black students or whether hiring practices unfairly favor applicants from privileged backgrounds. For example, universities may prefer a White applicant from Harvard whose parents also attended Harvard over a Black applicant from Michigan State University—despite comparable or superior qualifications.

Whether such policies reduce inequality or create new inequalities is an important and difficult empirical question. However, the underlying goal of diversity, equity, and inclusion programs—to promote fairness and equal protection—is grounded in the 14th Amendment of the U.S. Constitution. Efforts to bring social outcomes more in line with these principles are not radical; they are consistent with constitutional ideals and basic human rights. Opposition often aligns with existing power and status hierarchies rather than with empirical evidence.

It is understandable that politically conservative professors may feel out of place in departments where most colleagues are liberal. But the same is true for female police officers or Black lawyers in elite law firms. Ironically, DEI initiatives could also benefit politically conservative academics by ensuring that universities foster inclusive environments and avoid discrimination based on political orientation. In practice, this is rarely a major problem. Most professors interact with colleagues infrequently outside formal meetings, and promotions depend far more on student evaluations, publications, and grant funding than on political views.

Concerns about ideological repression are often fueled by highly visible but rare cases. Data from the Foundation for Individual Rights and Expression (FIRE, 2023) show that sanction campaigns against scholars originate from both the political left (about 52%) and the political right (about 41%), and that most cases do not result in formal discipline. When sanctions do occur, universities typically cite violations of institutional policies or professional standards. Since early 2025, however, campus politics have become more volatile. In the aftermath of the killing of conservative activist Charlie Kirk, several universities removed or suspended faculty and staff over controversial social media posts (Inside Higher Education, September, 19, 2025) Similar controversies have been reported in Canada as well (RIndex, 2025).

Debates about universities and politics also ignore a crucial body of scientific evidence concerning political orientation itself. Research in behavioral genetics and personality psychology shows that political orientation is surprisingly trait-like—closer to being an extravert or introvert than to preferring Pepsi over Coke (Hatemi, 2010). Like personality traits, political orientation has a heritable component and shows substantial stability across adulthood. This stability helps explain why political campaigns spend billions of dollars targeting a small number of swing voters while most citizens vote consistently over time.

Another widespread misconception is that parents exert a strong and lasting influence on their adult children’s political views. Parents do influence political attitudes during childhood and adolescence, but this influence declines sharply in early adulthood (Hatemi, 2009). By adulthood, similarity between parents and their children is explained largely by genetic similarity rather than by parental socialization (Hatemi, 2010). This helps explain why political disagreements within families are common—and why Thanksgiving dinner conversations so often avoid politics.

The most important conclusion from this research is that adolescents are not blank hard drives waiting to be programmed by parents or professors. Adolescence and early adulthood are periods of exploration in which individuals actively gravitate toward ideas that fit their underlying dispositions. Students may encounter certain arguments or perspectives for the first time at universities, but they choose how to interpret and integrate them. Exposure is not indoctrination.

Longitudinal studies of university students support this conclusion. There is little evidence that conservative students enter university and reliably graduate as “flaming liberals” (Mariani & Hewitt, 2006). Where changes in political attitudes do occur, they are typically modest and better explained by self-selection, maturation, and peer sorting than by classroom instruction.

So why does the belief in widespread university indoctrination persist? One explanation lies in a common cognitive error: people often infer causation from temporal coincidence. When parents observe that their child goes to university and later adopts different political views, it is tempting to assume that university caused the change. Yet similar changes would often have occurred anyway, regardless of whether the student attended a secular university, a religious institution, or none at all.

In conclusion, universities create and transmit scientific knowledge. Societies that invest in science and higher education tend to produce citizens who are healthier and live longer lives. Scientific inquiry can challenge traditional beliefs that are not grounded in evidence, and this tension is unavoidable in knowledge-based societies. The solution is not to vilify universities, but to recognize that diversity of viewpoints is inevitable—and valuable. Creating learning environments that benefit all students while tolerating disagreement is central to the mission of universities. Anyone who genuinely cares about students’ learning and wellbeing should support efforts to promote diversity, equity, and inclusion. This includes tolerating different political viewpoints—but tolerance cannot extend to intolerance, racism, sexism, or ideologies that deny equal rights or basic human dignity.

Science is often described as objective. Given the same evidence, anyone should reach the same conclusion. In reality, things are more complicated. Even in the most rigorous sciences, researchers’ perspectives influence how they interpret evidence. This influence is even stronger in the social sciences. Psychologists, for example, cannot fully set aside their personal views when designing studies, interpreting findings, or writing textbooks. That is why it may help for you to know a little about the author of this book. 

This textbook explores fundamental questions about human nature:

• How much are people alike, and how much do they differ?
• To what extent is behavior influenced by situations (social norms, conformity) versus personality (values, dispositions)?
• How much of personality is shaped by nature (genes) and how much by nurture (culture, socialization, parenting)?

Psychologists disagree about the answers to these questions. Biologically oriented psychologists emphasize evolution and genetics. Developmental psychologists highlight parenting. Social psychologists stress the power of situations. These perspectives are sometimes called paradigms. A paradigm is like a research culture with its own fundamental beliefs and research practices. Each perspective adds valuable insights, but paradigms also create blind-spots and biases. 

Behaviorism is a good example. Behaviorism denied the existence of personality traits. Everybody was just the product of a different reinforcement schedule. It also ruled out the study of emotions and forbade self-reports. For this reason, research on personality and emotions with self-report measures only emerged in the 1980s, when the behavioristic paradigm lost its influence. I would not be a psychologist, if behaviorism had lasted another couple of decades. Instead, I attended a conference in 1990, where Skinner gave his last speech to a large audience and only a handful of psychology clapped when he criticized cognitivism. The behavioristic paradigm was dead. At another a conference, an older psychologist described himself as a prisoner of the behavioristic paradigm. That phrase stuck with me. I did not want to look back at my career and realize that I had been a prisoner.  This does not mean I am without biases, but it does mean that I am not trying you to sell the personality paradigm that has many limitations that card-carrying personality psychologists like to ignore. 

The Origin of My Perspective

My journey began in 1966, in a small town in northern (West) Germany. Too young for the student revolutions of the late 1960s, I nevertheless grew up in their aftermath, surrounded by cultural shifts that reshaped much of the Western world. I was raised in a comfortable middle-class family, with a natural affinity for math and a growing interest in social issues. Once I discovered that psychology was a science—not just speculation about dreams—I knew it was the right field for me.

In 1988, I moved to West Berlin to study psychology, just one year before the fall of the Berlin Wall—an event that profoundly shaped my worldview and my appreciation of free societies. My early academic interests were in emotion research. I studied with Professor Rainer Reisenzein, who introduced me to theories of emotion, and with Professor Hubert Feger, who focused on measurement and group processes. At that stage, personality psychology did not appeal to me. The field was dominated by grand theories, such as Freud’s, that seemed disconnected from evidence. Other approaches emphasized genetics and biology in ways that, to me, echoed the dark history of Nazi eugenics. As a young student, I rejected this line of thought. 

In 1996, I began my dissertation research on how people recall their emotions: How do you know how happy you were last month, and how accurate is that judgment? That same year, I received a scholarship to study with Ed Diener at the University of Illinois, one of the leading figures in happiness research. Working with him and his students was an extraordinary experience. After defending my dissertation in 1997, I was fortunate to secure a two-year fellowship from the German Science Foundation (DFG), which allowed me to continue working with Ed Diener in Illinois. My focus shifted from emotions to personality and well-being: Why do some people consistently experience more positive and fewer negative emotions than others? Why are some people happier? Over time, my perspective expanded. Feeling good is important, but it is not the whole story. A full picture of well-being requires asking people how satisfied they are with their lives overall. Life satisfaction became the central theme of my research, and Chapter 14 of this book summarizes some key findings in this area. 

Since 2000, I have been a faculty member at the University of Toronto, Mississauga, a unique campus that reflects the cultural diversity of Toronto. Most of my research focused on happiness (subjective well-being), but since 2011, I have been working on examining the research practices of psychologists. This work was motivated by increasing awareness that many results in psychology journals that end up in textbooks are not replicable. This scientific study of scientists’ behavior is called meta-science or meta-psychology. With Rickard Carlsson in Sweden, I co-founded a journal with the title “Meta-Psychology.” My awareness of the replication crisis helped me to select only credible results for this textbook. Another benefit for students is that this makes the book a lot shorter because some research areas have few replicable findings. For example, we still know very little about the neurological differences between people that shape their personalities. 

Writing this textbook as an active researcher comes with both strengths and weaknesses. On the one hand, I can bring you closer to the science itself—critiquing studies, highlighting controversies, and even sharing my own analyses. On the other hand, professional textbook writers are often more skilled at producing polished narratives. The problem with polished narratives, however, is that they often gloss over controversies and discourage critical thinking. They present findings as if they were unshakable facts. In reality, personality psychology is an emerging science, barely 50 years old, and many findings rest on shaky foundations. The aim of this book goes deeper. It introduces students to scientific thinking, critical evaluation of empirical findings, and quantitative reasoning about personality. That is why the word science appears in the title. I will make a clear distinction between empirical facts (e.g., monozygotic twins are more similar than dizygotic twins for most traits) and inferences or implications (e.g., genetic differences cause personality differences). Facts should not be denied. Inferences can and should be questioned.

As I said before, I did not want to believe in genetic differences, but the evidence became impossible to ignore. Rather than resisting it, I learned to see it differently. Genetic differences do not mean that some people are born with better genes. They mean people are different—and good societies allow everyone to be who they are. Genetic variation is a strength. This principle is true in human evolution and in human societies. Understanding differences, and understanding people who differ from us, is essential for modern life.

The scientific study of personality can also help people avoid chasing unrealistic goals rooted in social norms of perfection. Instead, we can learn to accept ourselves and become our best unique selves. This non-judgmental approach aligns with science’s aim to be objective. Whether there are truly bad, evil, or pathological personalities is a difficult question, but psychology’s history shows how dangerous it can be to label some variations as pathological. Only 50 years ago, homosexuality was considered a disorder. Today, it is accepted as a normal variation in human sexuality.

Finally, I must mention political orientation. Like sexual orientation, it has some genetic roots. Some people are drawn to familiar, traditional values; others to different cultures and new ways of living. Universities are often criticized as leftist and “woke,” accused of indoctrinating students. In reality, students’ political beliefs are largely established before they enter the classroom, and professors have little power to change them. Moreover, many conservative critiques ignore the fact that some conservative ideas are directly opposed to science. At the University of Padua, where Galileo taught, it took the Catholic Church 500 years to accept that the Earth revolves around the sun.

The conflict between traditional values and science is especially sharp in psychology. Psychological science is still concentrated in a handful of mostly secular countries in Western Europe, North America, and East Asia. In the United States, science is currently under attack by right-wing conservatives. Learning about psychology as a science will expose students to progressive ideas that challenge traditional beliefs about human nature, sexuality, gender, and race. At the same time, most topics in psychology are not political, and personality psychology is less politically charged than social psychology. As you will see in Chapter 1, however, personality psychology does have its own dark history—one that is important to confront as we move forward.

 

Snyder, J. S., & Henry, P. J. (2023). Regional Measures of Sexual-Orientation Bias Predict Where Same-Gender Couples Live. Psychological science, 34(7), 794–808. https://doi.org/10.1177/09567976231173903

Multiverse Analysis
OSF | A Multiverse Analysis of Snyder and Henry (2023) “Regional Measures of Sexual-Orientation Bias”

Summary

Snyder and Henry (2023) argue that county-level aggregation of IAT scores yields a reliable regional measure of anti-LGB bias that predicts where same-gender couples live, and they highlight a key adjusted regression (Table 3, Column 3) in which the implicit measure appears to outperform a single-item explicit measure. While aggregation can reduce random error, it does not by itself establish that IAT scores capture a distinct implicit construct; aggregation also stabilizes systematic method variance and sampling artifacts, and regional differences in self-presentation could affect explicit reports.

A reanalysis using a multiverse framework shows that the “implicit > explicit” contrast is highly model-dependent. In simple associations, implicit and explicit measures show similar relationships with the outcome. Across 42 reasonable specifications that vary outcome handling (raw, log-transformed, count model), weighting (with/without), and covariate inclusion (none, single covariates, full published set), only the published specification yields a statistically significant advantage for the IAT, while multiple alternatives yield either no difference or a statistically significant advantage for the explicit measure. The main conclusion is that the paper’s headline inference—implicit bias is a stronger predictor than explicit bias—is not robust to reasonable analytic choices and should be interpreted more cautiously.

Full Article

 

 

This article asks whether regional measures of sexual-orientation bias predict where same-gender couples live. The central claim is that county-level implicit bias provides predictive value beyond explicit measures, and that this pattern remains when adjusting for a set of county-level covariates and region indicators.

The key evidence is a regression framework in which the outcome is a county-level measure of same-gender couple prevalence (and/or counts), with implicit and explicit bias entered jointly, and then a “full” specification that adds a covariate set (policy environment, religion, education, income, political orientation, rurality, and census region). They interpret the implicit coefficient as the stronger (or uniquely informative) predictor in the adjusted model.

They motivate covariates as adjustments for structural and cultural factors that could correlate with both attitudes and residential patterns of same-gender couples. They treat the adjusted model as closer to the causal quantity of interest: the association between bias and couple locations net of these background county characteristics.

What do IATs Measure?

Researchers disagree about what IAT scores mean. The early interpretation was that IATs capture evaluative associations that are at least partly outside conscious awareness. Low correlations between IAT scores and self-reported attitudes were often taken as support for this view. This interpretation remains common, but a growing literature challenges it.

At the individual level, IAT scores correlate only modestly with other indirect measures and with behavior, suggesting that a substantial share of variance reflects random noise and systematic method variance rather than unique, construct-valid “implicit” content. One alternative view is that IATs are indirect, error-prone measures of largely the same evaluative attitudes people can report in questionnaires, with differences between methods driven in part by measurement artifacts rather than distinct underlying constructs.

Snyder and Henry (2023) adopt a related but distinct argument at the regional level. They propose that aggregation of individual IAT scores to the county level reduces random error and yields a more reliable measure of the local “implicit climate,” which can then predict county-level outcomes. This logic is reasonable as far as reliability is concerned. However, improved reliability is not the same as improved discriminant validity.

Aggregation reduces random noise, but it also stabilizes systematic components of the measure that may vary across counties (e.g., platform- and sampling-related artifacts, regional differences in who takes the test, and other method-specific influences). The same concern applies to self-reports. Social desirability and self-presentation may differ across regions, which could attenuate the implicit–explicit correlation even if the two methods track a single underlying construct.

In the present data, the county-level correlation between the IAT measure and a single-item explicit measure is reported as r = .60. This is substantial shared variance, but it still leaves considerable unique variance in each measure. With only two methods, it is difficult to draw strong conclusions about what that unique variance represents. In particular, it is possible for two imperfect measures of the same construct to show different “unique” predictive power in regression models when systematic measurement error and correlated predictors are present. Conversely, if one measure fails to predict the outcome across reasonable model specifications, that would cast doubt on claims that it contains unique valid information about the criterion.

A further question is why one measure would be a stronger predictor than the other. One possibility is validity: the more valid measure should predict relevant outcomes more strongly. Another possibility is model dependence: when two predictors are highly correlated and both contain measurement error, small analytic choices (model form, covariate set, weighting) can shift the apparent “winner” without reflecting a stable underlying difference.

It is sometimes argued that indirect measures should outperform self-report on socially sensitive topics because self-reports are suppressed by social desirability. Yet evidence for this claim is mixed; in many anonymous contexts, people report socially sensitive attitudes with little apparent inhibition, and self-reports often predict behavior at least as well as IAT scores at the individual level. The key point for the present analysis is that differential predictive power does not, by itself, establish that IAT variance is uniquely “implicit.”

The paper’s central result for the “implicit beats explicit” claim appears in Table 3, Column 3. In that specification, the implicit measure shows a stronger negative association with the outcome than the explicit measure when both are entered together and additional county covariates are included. The authors interpret this as evidence that the aggregated IAT captures something distinct and more predictive than the explicit measure.

However, the corresponding zero-order correlations in Table 1 are comparatively balanced: the implicit and explicit measures show similar correlations with the outcome. This suggests that the divergence in Table 3 is driven by the particular multivariable specification—especially the inclusion of several covariates that are themselves strongly related to both attitudes and the outcome (e.g., political conservatism, rurality, and religiosity).

One way to address sensitivity to analytic choices is to provide a strong theoretical rationale for a specific model and, ideally, preregister it. Another is to examine robustness across a transparent set of reasonable alternatives. To that end, I conducted a multiverse analysis (MVA) that focuses on the robustness of the “implicit vs explicit” contrast.

The analysis acknowledges that the outcome is highly skewed and that the authors used a weighting scheme based on the number of IAT observations per county. Accordingly, models were estimated using (a) the raw outcome (as in the paper), (b) a log-transformed outcome, and (c) a count-model approach. Each model was estimated with and without weights. Finally, models were estimated with no covariates, with individual covariates, and with the full covariate set used in Table 3. This produced 42 specifications. For each specification, I computed and tested the difference between the implicit and explicit coefficients.

The results indicate substantial model dependence. Only one specification produced a statistically significant “implicit > explicit” contrast—namely the specification corresponding to Table 3, Column 3. In contrast, 13 specifications produced a statistically significant advantage for the explicit measure over the implicit measure, and the remaining specifications were non-significant. In other words, the published pattern is atypical in the multiverse: modest changes to modeling decisions (e.g., outcome transformation or omitting weights) eliminate the reported contrast, and in a nontrivial subset of specifications the sign of the contrast reverses.

These findings illustrate the value of robustness checks in complex observational analyses. The Open Data badge made it possible to evaluate the sensitivity of the headline claim to reasonable analytic choices. The key conclusion from the MVA is not that the focal association is absent, but that the specific inference that “implicit bias is a stronger predictor than explicit bias” is not robust to alternative, defensible specifications.

At minimum, the results warrant a narrower interpretation: the data show that both regional measures relate to the outcome, but the direction and significance of the implicit–explicit contrast depends strongly on modeling decisions. A cautious reading is therefore that the evidence does not uniquely support the claim that the IAT measures a distinct “implicit” construct that outperforms explicit self-report at the county level.