Last updated: · 17 min read
In brief
Ego depletion, the idea that willpower runs down like a fuel tank, was apparently confirmed for nearly two decades. Then 23 labs ran the same pre-registered test, and the effect fell to essentially nothing. Fraud was not the cause. Journals prefer significant results, failures go in the file drawer, and flexible analysis turns chance into findings. When journals accept papers before results exist, the first hypothesis comes out supported 44% of the time, against 96% in standard papers. Medicine and nutrition largely share those incentives, and that fix has reached medical journals only patchily.
Contents
In 2016, twenty-three laboratories on four continents, from Australia and Indonesia to Belgium, Sweden, Canada and the United States, reported the results of the most rigorous test ego depletion had ever received. The protocol was identical at every site and registered publicly before a single measurement was taken, which fixed in advance the analytic choices earlier ego depletion researchers had been free to make after seeing their data.
Six years earlier, the pooled results of 198 published tests had put the effect at d = 0.62, a solid, medium-to-large effect (d measures the gap between two groups in standard deviations, and zero means no gap at all). Ego depletion, the theory that self-control draws on a single finite resource that depletes with use, had been staked out by Roy Baumeister and colleagues in 1998 and apparently confirmed, across hundreds of studies, for nearly two decades. It entered undergraduate textbooks. It reached management advice, productivity coaching and self-help, where willpower became a fuel tank to be rationed before lunch.
Twenty-three labs ran the same pre-registered protocol on 2,141 people, and the estimate fell from d = 0.62 to d = 0.04, which is essentially nothing, and the result did not come from one underpowered study failing to replicate a well-powered literature.
The correction came through the same institutional machinery as the findings it undercut: scientists, standard methods, a peer-reviewed psychology journal. Baumeister and Kathleen Vohs, the theory’s leading defenders, objected that the computerized task used to tire people out might not tap self-control at all. So in 2021 a 36-lab pre-registered test led by Vohs tried again with 3,531 participants. It found no reliable effect either.
The pattern
Ego depletion was one case of a pattern the literature produces at scale.
In 2010, Dana Carney, Amy Cuddy and Andy Yap published a study, with 42 participants, claiming that two minutes in an expansive physical posture, arms wide and hands on hips, elevated testosterone, lowered cortisol and increased tolerance for financial risk. Cuddy presented the findings in a 2012 TED talk that has since reached more than 76 million viewers. The finding moved into executive coaching, corporate training programmes, and job-interview preparation advice telling candidates to pose like a superhero in the bathroom before walking into the room.
By 2015, replications were failing to find the hormonal effects. In 2016, Dana Carney, the paper’s first author, published a statement explicitly abandoning the theory. She named the problems directly: a tiny sample of 42, participants run in batches until the effect appeared, an outlier dropped from the hormone analyses, the smaller of two p-values reported, and self-report questions kept because they “worked.” Cuddy did not recant. She narrowed the claim from measurable hormonal changes to subjective feelings of confidence and continued presenting the research.
John Bargh, Mark Chen, and Lara Burrows published their elderly priming study in 1996. Participants exposed to words associated with old age, such as “Florida,” “bingo” and “wrinkled,” walked measurably more slowly down the hallway afterward. The finding became a centrepiece of social priming research and appeared in Daniel Kahneman’s book Thinking, Fast and Slow as evidence for the automatic, thoroughgoing influence of context on behavior.
In 2012, Stéphane Doyen and colleagues ran the study again. They used infrared timing equipment rather than a researcher with a stopwatch, kept the experimenters blind to each participant’s condition, and used a larger sample, and found no slowing at all. Then they ran a second experiment in which they told the experimenters what to expect. The walking-speed effect reappeared only when the experimenters expected to find it. Bargh responded by calling the Belgian researchers “incompetent or ill-informed” in a blog post he subsequently deleted.
Kahneman, who had staked a portion of his book’s credibility on social priming findings, sent an open letter that September addressed to researchers in the field. He saw, he wrote, “a train wreck looming.” He later acknowledged in public, replying to replication researchers who had taken his priming chapter apart, that his treatment of social priming in Thinking, Fast and Slow had been too credulous.
The systematic picture came from the Open Science Collaboration, which spent several years replicating 100 published psychology experiments. Its results appeared in 2015: 97% of the originals had statistically significant findings, against 36% of the replications, and replication effect sizes averaged roughly half the originals.
Then there is Daryl Bem. In 2011, Bem published a paper in a mainstream social psychology journal reporting nine experiments, eight of them significant, as evidence of extrasensory perception. Participants appeared to know what images a computer would display before the computer had selected them. The paper used the same kind of statistical methods found in any other paper in the journal that year. Replications failed. When methodologists examined the original, they found nothing that broke the field’s prevailing rules, only the ordinary flexibility those rules allowed.
If standard methods can produce eight apparently significant studies out of nine for an effect that is physically impossible, the fault lies in the methods, and Bem’s paper, though it did not start the replication crisis, made that impossible to ignore.
Where fraud fits
In 2011, Diederik Stapel, a Dutch social psychologist at Tilburg University, was dismissed for fabricating data wholesale; the investigation that followed found fraud across years of research, in 55 of his publications. He invented datasets entirely.
Stapel does not explain the replication crisis. The ego depletion labs, the power pose researchers and the social priming researchers whose findings collapsed were not fabricating data. They were running studies and writing papers using methods the field accepted and rewarded. The replication crisis did not require fraud to operate. It required only that researchers respond to the incentives in front of them. Stapel is the outlier.
How the system produces this
Set Stapel aside, and every finding described above passed peer review, using methods that were standard for the field and data nobody had fabricated.
The central flaw in that process had been described decades earlier. Robert Rosenthal named the file drawer problem in 1979, though Theodore Sterling had documented the phenomenon empirically two decades before that, finding that 97% of the articles in four major psychology journals that used significance tests reported rejecting the null hypothesis.
Journals publish significant findings at a much higher rate than null results. Failed experiments, whether they found no effect, an effect in the wrong direction or no publishable story, accumulate unpublished. The literature is therefore the subset of all experiments run that survived a filter strongly biased toward the positive.
What this produces at scale: a researcher runs twenty experiments testing a hypothesis that is false. Nineteen return null results. One returns a false positive by chance, the expected outcome when a 5% significance threshold is applied to a true null. The nineteen go nowhere and the one gets published. The field acquires a positive study and no corrective information. Multiply this across a field, across decades, and the literature fills with chance findings dressed as accumulated evidence.
P-hacking operates inside a single study rather than across many, which makes it harder to detect and more pervasive. A researcher finishes data collection and gets p = 0.06, just short of significance. They remove two participants who showed unusual response patterns before the formal analysis. Now p = 0.047. Or they add a covariate that was available but not originally planned. Or they run the analysis at multiple sample sizes and stop where the data look cleanest. The published paper will record none of this, only the final analysis, presented as if it were the only one run. A handful of these “researcher degrees of freedom” (decisions about which outcome measures to report, which covariates to add, when to stop collecting data, and which experimental conditions to drop) can inflate the false positive rate from the nominal 5% to over 60%. The researcher who does this is responding rationally to a reward structure that treats p < 0.05 as the entire difference between success and failure.
HARKing, short for Hypothesizing After Results are Known, is the third mechanism. Norbert Kerr coined the term in 1998. The mechanism: a researcher runs an experiment expecting to find effect X, finds effect Y instead, constructs a hypothesis that would have predicted Y, and writes the paper as if that hypothesis was there from the beginning. The published article reads as theory confirmation. The incentive is structural: confirmatory findings are more publishable than exploratory ones. A result reported as predicted is received differently from the same result reported as stumbled upon. Every exploratory finding has a reason to present itself as confirmatory, and no one reading the final paper can tell the difference.
These three mechanisms running simultaneously produce a predictable mathematical result. John Ioannidis worked out the arithmetic in 2005. In fields where the ratio of true to false hypotheses being tested is low (a description that fits much of social psychology, where speculative theories are tested in cheap lab experiments with small convenience samples), where samples are underpowered, analytical flexibility is high, and publication incentives strongly favor positive results, the published literature can end up with more false positives than true ones.
The specific arithmetic: if 10% of tested hypotheses are true, with 80% statistical power and a p = 0.05 threshold, running 100 tests yields 8 true positives and 4.5 false positives on average. The false discovery rate, the fraction of positive results that are wrong, is about 36%. Lower the base rate of true hypotheses, as you would in a field that tests highly speculative claims in small, flexible studies, and the false discovery rate climbs past 50%. At that point the literature can be more wrong than right.
What p < 0.05 means, and what it doesn’t
A p-value below 0.05 means: if the null hypothesis were true, results this extreme would appear by chance less than 5% of the time. It does not mean there is a 95% probability the finding is real. It does not confirm the hypothesis. Ronald Fisher, who popularized the p-value, intended it as a weak signal worth following up with further experimentation, not a binary publication criterion.
The null hypothesis significance testing framework that became psychology’s dominant standard is a hybrid of two incompatible statistical philosophies: Fisher’s significance testing and the Neyman-Pearson hypothesis-testing framework. Neither originator endorsed the combined approach; both criticized the other’s system in print. The p < 0.05 threshold, a convention from Fisher’s agricultural statistics applied with the fixed accept-or-reject logic of industrial quality control, became a universal publication gate through institutional inertia rather than statistical logic. Its misuse collapses a continuous measure of evidence into a binary pass/fail decision, and in doing so creates exactly the incentive to cross the threshold by whatever means are available.
Why rational people did this
Most of the researchers whose work collapsed were neither corrupt nor incompetent. The useful question is why ordinary career incentives made this behavior predictable in any scientist working in the field.
Academic careers depend on publications, and specifically on publications in high-status journals, which prefer statistically significant results. A researcher who runs three experiments and gets one significant result publishes the one. The other two go into the file drawer.
Every researcher faces the same calculation, because careers are judged on output rather than process: the significant result counts and the null does not.
Grant funding compounds the problem. Research funding is substantially easier to secure with a track record of published findings. Null results don’t build that track record. A researcher who consistently finds that their hypotheses don’t hold faces harder grant cycles, a thinner publication list, and diminishing institutional support, all flowing from a CV that looks, by the metrics that matter, like failure. For many researchers, the incentive to find positive results is a condition of continued employment.
Peer review does not correct for this. Reviewers are experts in the field being reviewed, and they are also invested in that field’s prior findings. A paper challenging an established result, such as one questioning social priming, faces reviewers who have built theoretical frameworks, written grants, and published papers that depend on those findings holding. When expertise comes bundled with a stake in a particular set of results, the bar for a paper that challenges an established finding can sit higher than the bar for one that confirms it, even when the methods are equally sound.
None of this excuses lazy research design or motivated reasoning, both of which were present. In Stapel’s case, none of it excuses fabrication. The point is that the same distorted literature would have emerged without any of those individual failings.
Because the failure lies in misaligned incentives, the reforms worth following are those that change what journals publish and what careers reward.
What science is doing
The replication crisis went public around 2011. By then the methodological critique had been building in specialist literature for years; what changed was the visibility — the Bem debacle, the Stapel fraud and the failed priming replications of 2011–2012, followed by the 2015 OSC paper and the TED-talk findings that hadn’t replicated, made it impossible for the field to pretend the problem was marginal. What followed was a reform effort, uneven in uptake and incomplete in scope, in which some of the reforms demonstrably changed outcomes.
Pre-registration is the most widely adopted reform. Researchers register their hypothesis, sample size, and analytic plan in a public repository before data collection begins. This makes HARKing detectable: if the analysis that was run differs from the analysis on record, anyone can check the paper against the plan, and good practice requires authors to disclose and explain the change. It formally separates exploratory from confirmatory research — both are legitimate, but in the old system they looked identical in published form, and exploratory findings were routinely treated as confirmatory evidence. The Open Science Framework and AsPredicted are the primary platforms, and many journals now flag pre-registered studies with an Open Science badge.
But pre-registration does not eliminate publication bias. It changes what researchers do before they write, not what editors decide to accept.
One team tested this directly, comparing 193 pre-registered psychology studies with 193 matched studies that were not pre-registered. Positive-result rates did not drop substantially. Effect sizes were numerically smaller in pre-registered studies, but the difference was not statistically significant. Pre-registered studies had larger samples and more frequent power analyses, so pre-registration was improving study design. It did not show that pre-registration stopped p-hacking or HARKing, and the publication incentive stayed where it was.
Changing that incentive requires a different mechanism. Registered Reports supply one, and their effect has been measured. Under this model, a journal evaluates and accepts or rejects a paper based on the research question and method, before data is collected, and commits to publish the result regardless of outcome.
That closes the main route for publication bias, rejection on the strength of the result, because the editorial decision is made before the result exists. The neuroscientist Chris Chambers launched the format in 2013 at a journal he helped edit, and it has since spread to hundreds of journals.
A later comparison set Registered Reports against a random sample of standard psychology publications. In 96% of the standard articles, the first hypothesis tested came out supported; in Registered Reports, 44%. That gap is the footprint of publication bias and flexible analysis — the explanations the authors themselves judge most plausible. The comparison is observational, and Registered Reports may attract different hypotheses, but it shows what positive-result rates look like when journals give up the ability to reject null results after the fact, an ability pre-registration leaves intact.
The Many Labs projects provide the closest thing psychology has to ground-truth systematic replication data. Many Labs 2, published in 2018, replicated 28 effects in 36 countries, with more than 15,000 participants. By standard significance criteria, just over half replicated, and three-quarters of replication effect sizes were smaller than the originals. Variation across countries, universities and samples was modest, and showed up mainly among the larger effects; effects near zero overall stayed near zero almost everywhere, instead of working in some places and not others. Many Labs 2 does what single-lab replications cannot: it separates effects that hold across settings from findings that do not reproduce outside their original conditions.
Several journals now also require raw data and analysis code to be shared publicly, which makes the analysis checkable in a way peer review cannot achieve. A reviewer sees the write-up; a researcher with the raw data can see whether the write-up accurately represents it. Brian Nosek’s Center for Open Science has driven adoption of transparency standards through an Open Science Badges program, now offered by more than 100 journals, that marks pre-registration, data sharing, and materials sharing in published papers.
Bayesian analysis and minimum sample-size requirements can both improve individual studies without touching the structural problem. Bayesian analysis asks how new data should update prior belief rather than producing a binary significance decision; it is growing in psychology and cognitive science, but it is still open to flexible analysis, and it has not restructured publication incentives or produced a measurable population-level reduction in false positives, because it does not change what gets published. Minimum sample size and power analysis requirements are similarly valuable at the level of study design, and similarly limited: adoption is uneven, not a general standard. Neither reaches as far as Registered Reports, which intervene at the editorial decision rather than at study design.
The lag and the open question
None of these reforms repairs the literature published before them, or touches the fields where they have barely arrived.
The Open Science Collaboration found that roughly 64% of a 100-study sample failed to replicate cleanly. Psychology publishes thousands of studies annually. Most of the pre-crisis literature has not been retested, and most of it probably never will be. Rigorous multi-lab replication is slow, expensive, and requires coordinating dozens of teams around a single protocol. The multi-lab ego depletion study needed twenty-three labs and 2,141 participants. The original Baumeister experiments needed one lab. Generating a finding is cheap; correcting it with the rigor the original lacked is not. Textbooks that cited ego depletion as established science were not recalled in 2016. The correction exists in the scientific record. Its reach outside that record is limited in ways that no reform of peer review can fix.
The career incentives, more broadly, are largely unchanged. Registered Reports are now offered by more than 300 journals, and pre-registration is encouraged across psychology, but for most psychology research neither is compulsory. Registration is mandatory for clinical trials, psychological ones included: leading medical journals will not publish a trial that began enrolling on or after 1 July 2005 unless it was registered before the first patient enrolled. Tenure committees still lean heavily on publication counts and citation metrics, even as reform coalitions such as CoARA push institutions to abandon inappropriate uses of metrics like the journal impact factor and the h-index. A junior researcher who runs well-powered, pre-registered studies and publishes fewer papers produces a thinner CV than one who runs many small, flexible studies and publishes more positive results. The pressure toward positive findings has been partially counteracted in subfields that have adopted the reforms, but it remains.
Medicine and nutrition are where this gap matters most, because there the same structural failures produce consequences that academic psychology’s failures don’t. Clinical medicine did adopt one reform early: compulsory trial registration, demanded by leading journals since 2005. Among large US heart trials, 57% of those published before 2000 reported a benefit, against 8% of those published after it, once declaring outcomes in advance on ClinicalTrials.gov had become routine, a drop the study’s authors link to that advance registration. But registration covers trials, not the far larger body of observational and laboratory research, and it is in that research, and in nutrition, that the reforms documented here have arrived least. Medicine has its own version of the pattern: Ioannidis found that about a third of highly cited clinical studies claiming a treatment worked were later contradicted or shown to have substantially smaller effects. In nutrition, the situation is arguably worse: the studies are typically small and observational, industry funding is endemic, randomizing people’s diets for years is so slow and costly that long-term trials are vastly outnumbered by observational studies, and decades of dietary recommendations have oscillated as underpowered findings cycled in and out of favor.
Take dietary fat. For decades, advice blamed fat for heart disease on the strength of observational studies and a sugar-industry-funded review that singled out fat and cholesterol and played down sugar. When the Women’s Health Initiative finally tested the broad low-fat advice in a randomized trial of nearly 49,000 women, cutting total fat produced no significant drop in heart disease or stroke. The narrower claim held up better: long-term trials that cut saturated fat did reduce cardiovascular events. Industry money played a part, but the larger story is about method: advice built on confounded observational studies ran years ahead of the trials that could test it, as academic psychology’s findings ran ahead of their evidence into management practice and self-help culture.
What remains
Managers were advised to make their hardest calls early in the day, before decision fatigue set in, because ego depletion had been established. Self-help books told readers to protect their willpower reserves by making fewer choices earlier in the day. Productivity culture built a minor industry around the concept of cognitive fuel. These were offered as practical instructions, derived from scientific findings that evaporated under closer scrutiny. The downstream applications of the original literature continue circulating in forms that the scientific correction cannot reach.
The twenty-three labs that tested ego depletion used pre-registration, coordinated multi-site protocols, and a commitment to publish regardless of outcome. Those are the structural tools that Registered Reports institutionalize. What a comparable audit would find across medicine’s clinical literature or nutritional guidance has so far only been glimpsed: when the Reproducibility Project: Cancer Biology repeated 50 experiments from 23 high-impact cancer papers, the median replication effect for positive results was 85% smaller than the original. Those fields share psychology’s conditions and, largely, its incentives. Psychology was dragged into a public reckoning over a decade, after visible failures accumulated to a critical mass. Registered Reports have reached biology and medicine journals, but patchily; most of the journals offering them are still in psychology. The open, practical question is whether they become the norm there before a comparable reckoning forces them.
Nobody has added up the cost of the wait, in patient decisions made on uncertain evidence and in dietary guidelines that have swung before and may swing again.
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Further reading
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Science Fictions: How Fraud, Bias, Negligence, and Hype Undermine the Search for TruthExplains how publication bias, flexible analysis and career incentives produce unreliable findings, and describes reforms to research practice.
The Data Detective: Ten Easy Rules to Make Sense of StatisticsExplains publication bias, selective analysis and failed replication within a practical guide to judging statistical claims.
Doctored: Fraud, Arrogance, and Tragedy in the Quest to Cure Alzheimer’sFollows investigators exposing suspect Alzheimer’s research and shows how institutional incentives and weak oversight can obstruct correction.
Calling Bullshit: The Art of Skepticism in a Data-Driven WorldProvides tools for recognizing selection bias, misleading statistics and overstated scientific claims.Recommended videos
12:22Is Most Published Research Wrong?Clear explanation of p-hacking, low power and publication bias, with famous failed findings.
4:46Is there a reproducibility crisis in science? – Matt AnticoleFive-minute animated primer on the reproducibility crisis and the reforms being tried.
14:36The Replication Crisis: Crash Course Statistics #31Covers the statistics behind false positives and why pre-registration and replication help.Cite this article
Ingrid Dahl. “Why so many published studies are wrong — and what science is doing about it.” Eikleaf, 20 May 2026, updated 2 November 2026. https://www.eikleaf.com/why-most-scientific-studies-are-wrong-and-what-science-is-doing-about-it/
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