Evidence Library: complete collection

A quiz can do more than show what you know. Answering questions from memory can help you keep the material. That idea, retrieval practice, has substantial support as a way to improve later learning. How much it helps depends on what you would otherwise be doing, what you are learning and how learning is measured. A large classroom review found an average advantage for testing: the gain was smaller when the alternative was restudying than when learners did no additional relevant activity. Yang and colleagues, 2021.

The practical change is simple: before you look at material again, try to recall it. That does not mean every quiz improves understanding, or that memorizing an answer prepares you to solve an unfamiliar problem.

What counts as retrieval practice?

Imagine reading a short explanation of how a heat pump works. You could read it again. You could copy the explanation into your notes. Or you could close the page and try to explain the process, then reopen it to check what you missed.

Only the third activity involves retrieval: producing information without the source in front of you. Retrieval can take the form of a short answer, a practice problem, a spoken explanation or a diagram drawn from memory. The testing effect is the finding that retrieval can improve later performance compared with an alternative such as more study.

The comparison matters. Adding a ten-minute quiz to a lesson is a different test from spending ten minutes on a quiz instead of another useful activity. Neither comparison is wrong. The first asks whether extra practice helps. The second asks whether a quiz is a better use of the same ten minutes.

A well-known experiment tested more than fact recall

In a 2011 study, Jeffrey Karpicke and Janell Blunt compared four ways of studying science texts. Their first experiment assigned 80 undergraduates to study once, study repeatedly, make a concept map with the text available, or practice retrieving the material. The retrieval group alternated recall with chances to study again, and it spent the same amount of time as the concept-mapping group.

The final test came a week later. It asked about facts stated in the text and also asked questions that required inferences. Retrieval practice produced better performance than the other three conditions. A second experiment extended the comparison to different texts and final-test formats. Karpicke and Blunt, 2011.

So the benefit can reach beyond reproducing isolated words. That does not make concept maps useless. The students in these experiments drew their maps with the text in front of them; drawing a map from memory would itself be retrieval. And answering an inference question about a passage you studied is not the same as a broad gain in reasoning ability.

How far does the benefit travel? A 2018 meta-analysis by Steven Pan and Timothy Rickard pooled 192 transfer effects from 122 experiments. A transfer test asks for something different from the practice questions. Compared with studying the material again without a test, practice tests improved performance on transfer tests (d = 0.40). Transfer was strongest across test formats and to application and inference questions. It was weakest when the final test rearranged the practiced items or covered material that learners had studied but never practiced retrieving. Three conditions mattered most: whether the practice answers matched the answers needed later, whether the retrieval practice was elaborated, and how well learners did on the practice test. After adjustment for publication bias, the analysis often predicted no transfer when none of those conditions was present. Pan and Rickard, 2018.

The classroom evidence is broader, but uneven

The classroom review mentioned at the start, a 2021 meta-analysis by Yang and colleagues, pooled 222 independent studies involving 48,478 students. On average, classroom testing improved achievement. The advantage was smaller against restudying than against no relevant additional activity. Against other elaborative activities, the estimated advantage was small and its confidence interval included no difference. Feedback, test design and the match between practice and assessment also mattered. Yang and colleagues, 2021.

In a 2025 meta-analysis, Ariel Gonçalves, Bruno Muniz and Antônio Jaeger took up that comparison with other active methods. Across 44 studies, retrieval had a small overall advantage over elaborative study activities (g = 0.14). The advantage depended on feedback. It was larger when learners received feedback (g = 0.50), and elaborative study came out ahead when they did not. It also appeared mainly against concept mapping and group discussion, the kind of comparison Karpicke and Blunt used. Against other elaborative tasks, the effects were indistinguishable. Gonçalves, Muniz and Jaeger, 2025.

A separate review of applied school and classroom experiments also found benefits across varied settings. But only 6% of its experiments were run outside so-called WEIRD societies: Western, educated, industrialized, rich and democratic. That does not make the findings unusable. It limits how confidently they describe every educational setting. Agarwal, Nunes and Blunt, 2021.

So the evidence goes beyond one memorable laboratory result. But you still have to judge it task by task. A spelling quiz, an explanation of a biological process and a software troubleshooting exercise ask different things of the learner.

A boundary worth taking seriously: mathematics

A 2025 review looked specifically at mathematics learning. Across seven studies comparing retrieval practice with restudy, the average estimate favored retrieval, but its uncertainty interval included no benefit. The authors judged the evidence inconclusive. The same review found clearer average support for spacing mathematics practice. Murray, Horner and Göbel, 2025.

That does not prove retrieval fails in mathematics. It does mean you should not carry the overall classroom result, unchanged, into every subject.

Researchers have argued about this boundary before. In 2015, Tamara van Gog and John Sweller proposed that the testing effect shrinks, and may even disappear, as material gets more complex: that is, as a task requires learners to handle more interacting elements at once, as in a multi-step problem. van Gog and Sweller, 2015. Jeffrey Karpicke and William Aue replied that complexity had not been defined in a measurable way or manipulated in the key experiments. In their view, the null results came from the retrieval tasks used (recalling isolated words, or immediate, massed practice), not from complex material. Karpicke and Aue, 2015. The mathematics review does not settle that dispute, but it shows why the question still matters in practice.

Whatever the explanation, a learner who cannot yet carry out a procedure may need explanation and guided examples before practicing alone becomes useful. The practical question is what the learner can do afterward, not whether the activity carries an evidence-based label.

How to apply the finding without overselling it

For an ordinary study session, a reasonable way to start is to read or work through the material, put it aside, try to reproduce the important ideas, and then check what you got. The check matters. A blank answer or a confident mistake shows you what to revisit. And in the 2025 comparison, retrieval's advantage over other active study methods appeared mainly when learners received feedback. This routine applies the evidence; it is not a claim that one fixed sequence is best for every learner.

Choose prompts that resemble the way the knowledge will be used. If the goal is to explain a process, ask for an explanation. If the goal is to identify a fault, present a fault to diagnose. Remembering a definition can contribute to those tasks, but a correct definition alone does not demonstrate either skill.

Workplace training works the same way. Asking employees to name three escalation rules tests different knowledge from giving them a scenario and asking which rule applies. A useful evaluation checks the intended performance after a delay. Course completion and how confident people feel right afterward cannot substitute for that outcome.

You can also combine retrieval with spaced practice, returning to material in later sessions. These are separate choices: retrieval concerns what the learner does; spacing concerns when practice happens. Keeping them separate helps you see what a training program actually changed.

Retrieval practice has earned a place among useful learning methods. Its strongest practical message is specific: build in chances to produce what you have learned, then check what improves. The support for that approach is substantial. A universal quiz format, a guaranteed gain or automatic transfer to job performance is a different question.

Standing with your hands on your hips might make you feel different. That does not mean it changes your hormones, improves your judgment, or helps you get a job.

The evidence on power posing is clearest when you take those claims one at a time. The original claims about testosterone, cortisol and risk-taking have not held up in replications. One 2026 study from a single lab, not preregistered, found that sitting upright rather than hunched changed risk-taking over the course of a game; it needs independent replication. Short-term changes in how people describe their feelings have more support. But the few studies that also included an ordinary, neutral posture suggest a twist: slumping lowers feelings and behavior compared with that neutral posture, while a power pose adds little. The evidence that a brief pose produces useful changes in everyday performance is much less convincing.

That distinction matters if you are deciding whether to strike a pose before a difficult conversation or presentation. A personal ritual is one thing. A demonstrated way to perform better is another.

What the original study claimed

In 2010, Dana Carney, Amy Cuddy, and Andy Yap reported that holding expansive poses, rather than contracted ones, changed participants' hormones, feelings of power, and willingness to take a financial risk. The appeal was obvious: two one-minute poses appeared to produce several desirable changes at once. The paper made a physiological claim as well as a psychological one. Original study.

The study compared groups assigned to different postures. It did not show that everyone who stood a certain way became more powerful. Nor did it measure the outcomes people often care about when they hear the advice: handling an interview, giving a clear presentation, or resolving a conflict.

Think about someone preparing for a salary discussion. Feeling more confident could help, make no difference, or even hurt, depending on what that confidence leads them to say. To show a practical benefit, a study would need to measure something closer to the actual goal. A change in a questionnaire score cannot answer that question on its own.

The larger replication separated the outcomes

In a 2015 conceptual replication, Eva Ranehill and colleagues tested 200 people, compared with 42 in the original study. Participants in expansive poses reported feeling more powerful, but the researchers did not find the predicted changes in testosterone, cortisol, or financial risk-taking. Replication paper.

The procedures were similar, not identical. Among other changes, participants held the poses for longer and received their instructions by computer, and the experimenter did not know which condition they were in. Differences like these matter when you ask why results disagree. They also raise a practical problem: if an intervention depends on a narrow set of unstated conditions, it is too early to advise people to use it anywhere.

The replication did not erase every result. It drew a useful line: changing posture could change how powerful people said they felt without producing the hormone and risk-taking effects originally attached to it.

Why “power posing works” is too broad

A 2022 review by Robert Körner and colleagues pooled studies of different body positions, including expansive poses and upright postures. It found effects on self-reports and behavioral measures, but not on physiological measures. Its sensitivity analyses suggested that the behavioral results were influenced by publication bias, unusually influential results, or both.

Effects were also noticeably larger in two kinds of study: those without a cover story, and those in which each participant tried more than one posture. Both designs make the hypothesis easier to guess. So the authors suggested that demand characteristics (participants responding to what they think the researcher expects) might partly explain the results. The review supports some posture effects, but it limits how confidently you can read the behavioral findings.

Keep self-reports, behavior and physiology separate. A single yes-or-no answer about all three hides the question you actually need answered. And a finding pooled across different body positions and tasks cannot show that one particular expansive pose will improve an interview or presentation.

There is another complication. Many posture experiments compare an expansive position with a contracted one. Suppose the expansive group feels better. Did expansion help, did contraction make people uncomfortable, or both? That comparison alone cannot tell you. Only a neutral comparison can separate those possibilities.

This is easy to miss because the advice is about adding something to ordinary life: “Stand this way and improve your confidence.” A study that compares two deliberately different positions may be answering a different question.

Two meta-analyses report results for the studies that did include a neutral comparison, and they point the same way (they draw partly on the same studies). Emma Elkjær and colleagues found that contractive postures produced worse outcomes than neutral ones (g = 0.45 across eight studies), while expansive postures barely differed from neutral (g = 0.06 across six studies). Elkjær and colleagues, 2022. Körner's review found the same pattern for self-reports and behavior: power poses and upright postures did not differ from control conditions (g = 0.02), while slumped postures fell below them (g = −0.22). Körner and colleagues, 2022.

In plain terms, the familiar contrast between a power pose and a slump mostly measures the cost of slumping. That is the reverse of what the popular advice assumes, which is that the pose adds something. Both estimates rest on small numbers of studies, and Elkjær and colleagues call for more research with neutral control groups.

Narrower laboratory work is still useful. In a 2025 laboratory study, Wainio-Theberge, Spiousas and Armony tracked changes in mood alongside measured body position and muscle activity. They reported relationships involving neck angle and how hard the posture was to hold. That is evidence about immediate experience and possible mechanisms. It does not show that the original hormone claims were right, or that the posture improves performance outside the laboratory.

What newer studies add

Read only its positive summary, and a 2024 study of hormones and risk-taking might look like a revival of the original finding. The results need a closer look. Among 92 participants, the researchers found no main effect of pose on testosterone, cortisol, reported power or risk-taking. They did find a statistical interaction involving cortisol change, posture and risk-taking.

An interaction is a narrower, conditional claim. It is not the same as saying that an expansive pose lowers cortisol or makes people more willing to take risks. Reporting it as confirmation of those claims would make the study sound more decisive than it was.

In 2026, two authors of the 2025 laboratory study approached risk-taking differently. Instead of instructing a pose, Soren Wainio-Theberge and Jorge Armony changed the furniture: a raised tablet led 96 participants to sit upright, while a low table made 99 others hunch over. Participants then played the Balloon Analogue Risk Task. Each pump of a virtual balloon adds in-game money to that round's pot, but if the balloon pops before the player cashes out, the round pays nothing. Over the course of the game, upright participants increased their pumping more than hunched participants did (p = .03 in the main model; a simpler slope analysis gave p = .02), although the overall difference between the groups fell short of significance (p = .06). Wainio-Theberge and Armony, 2026.

So the risk-taking question is not closed. But this is one study from one laboratory, with a mostly young, female sample, and the authors note that it was not preregistered. They found no overall effect of posture on mood. They also compared their groups with people from another study who used an ordinary desk. That comparison suggested that the upright group, not the hunched one, was the unusual group: the reverse of the meta-analytic pattern. But the desk group was not randomly assigned. A finding like this needs an independent replication before it can support advice.

Researchers have also tested posture instructions in everyday life. In a 2025 study, participants followed different instructions about how to hold their bodies (body-display instructions) before actions they planned to take. The study found no detectable advantage, either in taking those actions or in the feelings it measured. Only 127 of the 270 people initially recruited completed at least three weeks. That loss of participants limits how broadly the result applies. Still, the study gives little support for treating power posing as a dependable everyday performance tool.

Should you strike a pose before a presentation?

There is no need to turn an ordinary preference about posture into a scientific commitment. If a comfortable stance helps you settle before speaking, use it. What the research does not support is a promise of hormonal transformation, or the assumption that feeling powerful will make your next decision better. And if the neutral-comparison findings hold, the more useful advice is less about striking a pose than about not spending the minutes beforehand hunched over.

For a presentation, ask what success requires: knowing the material, explaining it clearly and handling questions. A posture exercise neither measures nor supplies those abilities. If you try a routine beforehand, judge it by those goals, not by how impressive its scientific explanation sounds.

Power posing is a good lesson in reading evidence, because parts of the original story can fail while narrower findings remain. The facial feedback evidence is another example: an unreliable demonstration can sit alongside better-supported findings from other procedures. Ask what changed, compared with what, and for how long. Then ask whether that change is the one you need.

Sorting people into visual, auditory or verbal learning styles is not a well-supported way to decide how to teach them. That does not mean no study has ever found a benefit. A 2024 meta-analysis found a small average advantage for instruction matched to a learner's style. But only about a quarter of its outcome measures showed the pattern the theory requires, and study quality was low. Clinton-Lisell and Litzinger, 2024. A 2025 review that pooled four earlier matching meta-analyses (143 studies) put the average matching effect at d = .04, close to zero; it did not include the 2024 meta-analysis. Hattie and O'Leary, 2025.

The practical point is the gap between having a preference and showing that teaching to it improves learning. Someone may enjoy diagrams, dislike lectures or choose to listen to a book. None of that tells you which method will help that person understand and remember a particular subject.

The claim that needs testing

The learning-styles matching claim is sometimes called the meshing hypothesis. In its familiar form, it says that visual learners benefit especially from visual instruction, verbal learners from verbal instruction, and auditory learners from auditory instruction.

Testing that claim takes more than a questionnaire and a test score. Researchers have to identify the proposed styles, assign learners within each style to different teaching methods, and test everyone on the same suitable outcome. The critical result is a crossover: the best teaching method switches with the learner's supposed style. Harold Pashler and colleagues made this the central requirement in a major review. Pashler and colleagues, 2008.

Take a hypothetical lesson on the water cycle, taught to self-described visual and verbal learners with either a diagram or a spoken explanation. If the diagram works better for both groups, that supports the diagram for this lesson. It does not support dividing the class by learning style. If the people who prefer diagrams score higher whichever way they are taught, that does not show a matching benefit either; the groups may differ in other ways. Only a crossover would: the visual learners doing better with the diagram while the verbal learners do better with the spoken explanation.

That is also why a lesson that feels good is not enough to settle the question. A learner may prefer a method that makes the material feel familiar. What counts is what the learner understands and can use afterward.

Why the classic critique still matters

Pashler and colleagues concluded that the available research did not provide adequate evidence for building learning-style assessments into teaching. Their argument was about the matching prescription, not about whether learners differ. Preferences and abilities were separate issues. Pashler and colleagues, 2008.

That distinction guards against overcorrecting. Evidence against style matching does not mean everyone has the same knowledge, reads equally well or can access the same materials. Captions, readable text and accessible documents do not need a learning-style theory to justify them. And explaining an unfamiliar concept another way after someone struggles is not the same as assigning that person a permanent learner category.

So the question is narrow: does a specific classification improve the choice of teaching method? Many good reasons to adapt teaching do not need that classification at all.

What newer evidence adds

The 2024 review by Virginia Clinton-Lisell and Christine Litzinger found a small average benefit for matched over unmatched instruction across 21 studies (g = 0.31, 95% confidence interval 0.05 to 0.57). Leaving this result out would make the evidence look more uniform than it is.

But the crossover pattern the theory requires appeared in only 26% of outcome measures, and most studies that showed it did not meet the review's quality standards. The included studies used single learning sessions, so longer-term effects remain uncertain. Given the costs of implementation and the low study quality, the authors judged the benefits too small and too infrequent to warrant widespread adoption. Clinton-Lisell and Litzinger, 2024.

In a separate experiment, Melzner and Kappes presented course material about motivational theories to 222 prospective teachers, as figures or as text. They did not find that matching the format to visual or verbal preferences improved learning. Nor did matching improve the learners' measured judgments about learning. This tests those preferences, materials and outcomes, not every possible form of personalization. Melzner and Kappes, published online 2024.

A 2026 study by Papadatou-Pastou and colleagues ran the crossover test with 194 primary school students aged 10 to 12. Each child learned about weather forecasts, climate change and clouds through visual, auditory and audiovisual presentations, and was classified by both self-report and a learning-style inventory. The outcome was immediate recognition of the material just taught, measured by multiple-choice questions after each format. Matched instruction gave no significant benefit, and there was no crossover. Audiovisual presentation beat both single formats for every style group. And the children's self-reported styles were not significantly associated with the inventory's classifications. Papadatou-Pastou, Touloumakos and Theotokatou, 2026. That is the pattern from the water-cycle example: a format that helps everyone supports the format, not the sorting.

The 2025 review cited at the top, by John Hattie and Timothy O'Leary, untangles another source of confusion. Drawing on 17 meta-analyses, they separated the four that tested matching (143 studies, average d = .04) from the 13 correlational ones linking learning preferences or strategies with achievement (average r = .24). They argue that the correlational studies often confuse learning styles with learning strategies. The two kinds of study answer different questions. A correlation between a reported preference and higher scores does not show that assigning instruction by that preference caused better learning. Hattie and O'Leary, 2025.

What to do with this evidence

If you teach, train or design courses, the evidence does not make a strong case for buying a questionnaire and building parallel learning-style tracks. Better starting questions are about the task and the learner's actual difficulties.

Does the material require seeing a spatial relationship? Does the learner understand the vocabulary? Can they explain the idea without copying it? Can they use it in an example that differs from the one demonstrated? The answers tell you something about learning that a preference label cannot.

Take a training course on reading charts. It could show the chart, explain the relationship that matters and ask learners to interpret a new case. If someone struggles, the fix might be explaining an unfamiliar axis or correcting a wrong inference. None of those decisions requires treating the person as permanently visual or verbal. This is an illustration, not a lesson design that has been tested as a package.

Learner choice still has value. People can choose a format for convenience, enjoyment or access without claiming that it is their scientifically best route to remembering. The mistake comes when a preference becomes a limit: “I am an auditory learner, so diagrams are not for me.” The matching evidence does not support that conclusion.

Retrieval practice and spacing raise other questions about how to design instruction, with their own boundaries and uncertainties. Whatever the method, the job is the same: check whether the teaching improves the intended learning, and change it when it does not. Learning-style labels have not proved to be a dependable shortcut for those decisions.

The marshmallow test cannot tell you a child's future. Waiting for a larger reward has been associated with some later outcomes, but those associations are less simple and less consistent than the popular story suggests. They depend on the children studied, the outcome measured, and what else the analysis takes into account.

Later research has weakened the idea that a few minutes of preschool waiting reveal a powerful, independent cause of lifelong success. At age 26, Sperber and colleagues found little reliable prediction from preschool waiting once their analysis included earlier characteristics. In mid-life, Benjamin and colleagues found that a measure of preschool waiting did not predict 11 adult outcomes, including income and net worth. None of this shows the opposite: that waiting tells you nothing at all.

For parents, teachers, and anyone applying behavioral science, the useful distinction is between predicting an outcome, explaining it, and changing it. The popular marshmallow story often slides between all three without noticing.

One task, several different questions

In the familiar task, a child can take a smaller reward now or wait for a larger one. Researchers record what the child does and, in follow-up studies, check whether it is associated with later characteristics or achievements.

Follow-ups published in 1988 and 1990 by Walter Mischel, Yuichi Shoda and Philip Peake helped establish the connection between preschool waiting and adolescent outcomes. These were longitudinal associations: behavior measured in preschool was related to measures collected years later.

That design leaves several possible explanations. Waiting could reflect something about the child that also affects later performance. It could reflect the child's circumstances. It could involve several influences at once. Seeing that children who wait tend to do better later does not tell you which explanation is correct.

Nor does it show that getting a child to wait longer will produce those later advantages. To answer that question, researchers would need evidence about an intervention and its later consequences. A predictive association is not an instruction manual.

The 2018 replication changed the scale of the claim

Tyler Watts, Greg Duncan, and Haonan Quan revisited the question in a different cohort in 2018. Their main analysis focused on children whose mothers had not completed college. Waiting was associated with later academic achievement, but the relationship was smaller than in the original studies, and it became substantially smaller after accounting for family background, early cognitive ability, and the home environment. Study.

This is not a case of a statistical control making inconvenient evidence disappear. Adjustment changes the question. Instead of asking whether children who wait tend to do better later, it asks whether waiting adds information once those other measured differences are held constant.

Imagine two children who differ in language skills, family circumstances and how long they waited. If they also differ in later school performance, it is hard to pin that difference on waiting alone. Adding the earlier measures to the analysis tests whether waiting carries any extra predictive information.

Adjustment is useful, but what it means still depends on the model. A variable might help cause both waiting and later achievement. Or it might be part of the very developmental process researchers want to understand. Neither adding every available control nor refusing to use controls solves that problem automatically.

The 2018 study itself started a published argument. In 2020, Armin Falk, Fabian Kosse and Pia Pinger argued that the two studies measured waiting differently: waiting times in the newer study were more heavily censored, meaning the task's time limit cut off more of the range, which biases the simple correlations toward zero. They also argued that some controls were not fixed before the task, which makes a drop in the association hard to interpret. When their reanalysis used only background variables determined in advance, it produced estimates closer to the original studies. Falk, Kosse and Pinger, 2020.

Watts and Duncan replied that their achievement correlations were smaller but still a partial replication, and they defended their models as a way to probe what the correlation means. Watts and Duncan, 2020. The exchange shows the previous point at work: how large the association looks depends on how waiting was measured and which variables count as fair controls.

The same data produced a different interpretation

In 2020, Laura Michaelson and Yuko Munakata published a preregistered reanalysis of the same cohort the 2018 paper used. Making different choices about measures and analyses, they found associations between preschool waiting and three of five adolescent outcomes. The associations with problem behavior held across several model forms. Reanalysis.

Their interpretation gave social support a larger role. Waiting might carry information about the child's early social environment rather than serve as a clean measure of self-control. The analysis supported that possibility; it did not experimentally prove that social support was the cause.

This is why a simple “replicated” or “failed” label misleads. The two teams were not just giving different statistical answers to an identical question. They made different decisions about how to measure outcomes, divide the sample, and account for earlier characteristics.

It is also one cohort analyzed more than once. Counting each paper as an independent group of children would make the evidence look more extensive than it is.

What happened when the children reached adulthood?

A 2024 follow-up by Sperber and colleagues looked at 702 participants from that same cohort at age 26. Once the analysis included earlier characteristics, preschool waiting showed little reliable prediction of adult functioning.

One exception stands out. When waiting was scored as passing or failing the full seven-minute task, an association with adult body mass index remained after adjustment. That pass/fail analysis was exploratory and had not been preregistered, so the association needs confirmation. It means you cannot say every adjusted association was zero. It does not make the body mass index result an established exception either.

The study also had a measurement limit. The task stopped at seven minutes, so it could not tell apart children able to wait longer than that. The adult sample was not representative of all children, and age 26 is one stage of adulthood. These details limit how far the finding reaches. They do not restore the much stronger popular promise.

The original cohort, children from Stanford's Bing Nursery School, has also reached middle age. In 2012 and 2013, Daniel Benjamin and colleagues, including Mischel himself, surveyed 113 of them; they averaged 46 years old. The team preregistered its analysis, and the main result was the one it had predicted: a measure built from preschool waiting did not predict 11 mid-life outcomes, including net worth, income, debt and educational attainment (average correlation 0.02). A combined index that added survey measures of self-regulation from ages 17, 27 and 37 predicted 10 of the 11 outcomes in the expected direction, 6 of them significantly (average correlation 0.19). Including preschool waiting in the index did not improve its predictions. Benjamin and colleagues, 2020.

That sample was small, and the authors describe it as well educated and wealthy on average. But it is a different cohort from the 2024 study, and it points the same way on preschool waiting. It also shows what did predict mid-life outcomes in that sample: self-regulation measured later in life. So two adult follow-ups, in two different cohorts, give little reason to use this brief task as a broad forecast of an individual child's adult life.

What parents and practitioners can take from it

Do not turn the marshmallow test into a character test. A child who takes the reward is making a choice in one particular situation. That choice does not reveal a permanent lack of discipline, and a child who waits has not secured a successful future.

Self-control is also much broader than this task. A finding about waiting for a snack does not settle every question about persistence, planning, distraction, or managing impulses. No single measure can carry a whole psychological construct. Research on personality and life outcomes asks related predictive questions with broader trait measures, and keeps the same distinction between an association and one person's future.

If you want to help a child learn, look at the problem more directly. Is the child having trouble understanding the material, starting the activity, or staying with a difficult task? Those are different problems. A preschool waiting score does not tell you which one you are facing or what will help.

A measure can predict something without causing it, and even a useful prediction may offer very little guidance about what to do next. Read with those limits, the marshmallow test is informative. Read as a tiny examination of someone's destiny, it is not.

Some of the most useful behavioral research is about how people differ: what they tend to enjoy, how they usually act, and which situations bring out their strengths. Claims about those differences deserve the same scrutiny as claims about a clever intervention. Do the reported links between personality and life outcomes show up again when researchers collect new data?

In a large project that retested selected links between the Big Five personality traits and life outcomes, most did. The results give good reason to take personality seriously. They also give reason to be careful about how strong the relationships are and what they can predict. They do not show that a trait determines anyone's future. Soto, 2019.

What the project tested

Christopher Soto's Life Outcomes Of Personality Replication project, or LOOPR, selected 78 trait–outcome associations from an earlier review that could feasibly be tested again. The project gathered new survey data from four US online samples. It measured personality with the Big Five Inventory–2 and assessed outcomes through self-report, sometimes adapting or shortening the original measures.

Eighty-seven percent of the selected associations were statistically significant in the expected direction. The replication effects were typically 77 percent as large as the original effects. That 77 percent is the median ratio of new to original effect sizes; it does not mean a personality test predicts 77 percent of a person's life. The hypotheses and analysis plan were registered during data collection, before analysis. Project methods and results.

These were selected associations, not a random sample of every claim made about personality. And some original studies used different designs, including longitudinal data that followed people over time. Reproducing an association in a one-time (cross-sectional) questionnaire is useful evidence, but it does not reproduce every feature of those studies.

What a successful replication tells you

Suppose people with higher and lower scores on a trait differ, on average, in some outcome. Finding a similar relationship in a new sample makes the original observation more credible. It reduces the worry that the first result depended entirely on one unusual group or one lucky analysis.

That still leaves several questions. How strong is the relationship? How much overlap is there between people with different scores? Does the measurement capture what matters for the decision you want to make? Would the relationship remain useful in another population or setting?

A statistically detectable association can be too weak to support a confident judgment about one person. Imagine a trait score that helps distinguish average preferences in a large group. It would not follow that everyone with a high score wants the same job, prefers the same exercise, or will respond to the same advice. A group-level tendency is information, not an assignment.

That is also why the shrinking effect sizes matter. A relationship can survive replication and still be less useful than its original estimate suggested. “It replicated” should open the next question (how well, and under what conditions?), not end the discussion.

The question about other populations has started to get answers, and so far they call for caution. The Africa Long Life Study used data on 2,770 young adults in Kenya, Namibia and South Africa, with outcomes measured over two to three years. It used a different trait framework, the “Big Two” of agency and communion, rather than the Big Five. Higher scores on both predicted better self-rated health and less anxiety and depression later, and communion predicted being employed. But the associations were smaller than those previously observed in Western countries (correlations between .02 and .11 in absolute size), and they depended on analytic choices such as which country and which time lag were analyzed. Haehner and colleagues, 2026.

Association is not a recipe for change

An association between a trait and an outcome does not show that deliberately changing the trait will change the outcome. Nor does it show whether an apparent personality difference is partly connected to other traits or circumstances.

A later LOOPR analysis asked whether the associations held across demographic groups, and what happened when other personality traits were taken into account. Many relationships held across groups. But adjusting for overlapping traits weakened many of the associations. This was a further analysis of the same project data, not a second independent replication. Soto, 2021.

A larger analysis that followed people forward in time reached a similar two-part conclusion. Emorie Beck and Joshua Jackson pooled raw data from 171,395 people in 10 longitudinal panel studies and tested whether Big Five traits predicted 14 later life outcomes. Most associations held up, and few depended on who was studied. But 21 of the 70 trait–outcome associations were not robust across most analyses. For 38 of the 70, the result depended on which background variables were included, and in some models, adding or removing one of those variables flipped the direction of the association. Beck and Jackson, 2022.

Here is an everyday example. Imagine that people who describe themselves as organized also report finishing projects on time. That hypothetical pattern would be worth knowing. But it would not, by itself, tell a manager whether to teach organization, reduce an excessive workload, clarify priorities, or change how deadlines are set. Those are intervention questions. They require evidence about interventions.

The same boundary applies to assessment products. Evidence for links between Big Five traits and outcomes does not automatically validate every questionnaire, score interpretation, or recommendation sold under the label “personality.” A product that promises to identify your ideal career or prescribe your routine makes additional claims, and those claims need their own evidence. The guide to evaluating personality tests shows how to check a specific instrument, score and intended use.

How to use this evidence

Personality is one useful way to understand how people differ. Use it alongside what you know about skills, interests, opportunities and actual experience. If an activity keeps clashing with what you enjoy or can sustain, that is worth looking into. It is not proof that you must force yourself harder, or that a test score has settled the matter.

LOOPR is also a good model of what replication can do. It neither wiped the picture away nor left it untouched. Many associations returned, effect sizes often shrank, and measurement limits stayed in view. That tells you more than sorting a whole discipline into “works” or “doesn't work.”

If the trait framework is unfamiliar, start with the Big Five personality traits or the broader personality definition. For a different kind of evidence question, compare retrieval practice, where the central issue is what happens when a learning activity is changed.

Key sources

• Soto (2019): How replicable are links between personality traits and consequential life outcomes?
• Soto (2021): Do links between personality and life outcomes generalize?
• Beck and Jackson (2022): A mega-analysis of personality prediction
• Haehner and colleagues (2026): Personality predictors of health, well-being, relationships, and employment in Namibia, Kenya, and South Africa

Facial feedback is the idea that moving your face can influence how you feel. Research supports some small, immediate effects, but the famous pen-in-mouth experiment has not proved reliable. Those conclusions can both be true.

The reason is that the experiment and the theory are not the same thing, even though people often treat them as interchangeable. The theory is often called the facial feedback hypothesis. A failed attempt to reproduce one way of making people “smile” does not test every possible connection between facial movement and emotion. Nor does an effect found with another method rescue the original experiment.

The practical claim needs two further distinctions. First, a brief change in a happiness rating is not evidence that smiling will fix an unhappy situation or produce lasting wellbeing. Second, one smile is not the same as smiling on demand. In a 2026 experiment, a single posed smile lifted mood in a negative context. But the lift weakened when people repeated the smile, and all but vanished when they also faced a penalty for not complying.

Why researchers put a pen in people's mouths

In a 1988 experiment, Fritz Strack, Leonard Martin, and Sabine Stepper asked participants to hold a pen in their mouths in ways intended to help or hinder the muscles involved in smiling. Holding it between the teeth produced a different facial position from holding it with the lips. Participants then rated cartoons, and those holding the pen in their teeth rated the cartoons as funnier. Original paper.

The odd procedure had a purpose. Simply telling someone to smile can give away the hypothesis: they may guess that the researcher expects a happier response. The pen task tried to change facial activity without explicitly asking anyone to adopt an emotion.

But the outcome was a judgment of how funny the cartoons were. That is narrower than a general improvement in happiness. The experiment did not show that smiling improves someone's relationships, work, or life satisfaction. Each of those claims would need evidence of its own.

Seventeen replications found almost no difference

In 2016, a Registered Replication Report brought 17 laboratories together to repeat the experiment with a shared protocol. In this format, the journal reviews and accepts the plan before any of the new data are collected. The analysis included 1,894 participants. In the original study, the difference in cartoon ratings was .82 points on a ten-point scale. Across the replications, the estimated difference was .03 points, with a 95% confidence interval from −.11 to .16. Replication report.

That interval matters. This was not a smaller experiment that happened to miss statistical significance. The combined evidence placed the likely size of the difference much closer to zero than the original estimate.

The replication also differed in some details. It used updated cartoons, video instructions, and video cameras to check that people held the pen correctly. Pointing to a difference does not show that it caused the disagreement, so Tom Noah, Yaacov Schul and Ruth Mayo tested one of them. In a preregistered 2018 experiment with 166 analyzed participants, they ran the pen task with and without a camera. Without a camera, people holding the pen in their teeth rated the cartoons as funnier than people holding it with their lips (average ratings of 5.75 versus 4.92). With a camera, the difference almost disappeared (5.21 versus 5.15). Noah, Schul and Mayo, 2018.

That pattern fits the camera explanation, but the decisive test fell short. The preregistered test of whether the camera changed the effect was only marginal (p = .051, one-tailed), and the authors described it as greatly underpowered. The camera is a plausible explanation that deserves a larger test, not a settled one.

The replication report's own conclusion was narrower than “facial feedback is false.” It found that this procedure did not reproduce the original result, and it left open whether other procedures might provide better evidence.

The broader literature did not disappear

Facial feedback research includes more than pens and cartoons. A 2019 meta-analysis by Nicholas Coles and colleagues brought together studies that used different ways of changing facial activity and measuring emotion. It concluded that effects on emotional experience were small and variable.

“Small and variable” is not a satisfying slogan, but the variation raises useful research questions. Does the method produce something resembling a natural smile? Does the person know what the researcher expects? Is there something amusing to respond to, or is the setting emotionally neutral? Each of these can change what an experiment is actually testing.

The second question has been tested directly. In six experiments with 995 participants across 29 countries, Coles and colleagues told some participants that posed expressions would affect their mood, told others that they would not, and told others nothing. What people were told changed the size of the effect, but it did not explain the effect away. Participants still reported more happiness after posing a smile even when the researchers had said that facial poses do not influence emotions. Coles and colleagues, 2023.

A later exploratory reanalysis, published online in 2023 and in a 2024 journal issue, proposed that social context helps explain the differences. It regrouped earlier studies by features such as whether another person was present. That can suggest a hypothesis. But the studies were not randomly assigned to those contexts, so the regrouping cannot settle the explanation by itself.

What the Many Smiles project found

The Many Smiles Collaboration, published in 2022, tested several procedures across 19 countries. Participants copied smiling faces, deliberately moved facial muscles into a smile, or completed a pen-in-mouth task. The project collected data from 3,878 people; its primary analysis used 1,504 after preregistered exclusions, including exclusions related to awareness of the hypothesis.

The study found evidence that copying a smile (facial mimicry) and deliberately moving the face into one (voluntary facial action) could increase reported happiness. The pen task gave less clear evidence. So the project supports a narrower version of facial feedback, but it gives no new reason to trust the familiar pen demonstration.

The two sample sizes matter too. “Nearly 4,000 participants” describes the data collected, not the number included in every analysis. Preregistering exclusions makes the analysis plan clearer, but you should still know which participants the main result describes.

And the measured change was still an immediate report of feeling. The study did not test how long a benefit lasts, or what happens when people smile again and again.

What happens when smiling is repeated or required?

Much popular advice is not about one smile in a laboratory. It is about smiling through a shift, a sales call or a bad week. Research on emotional labor, the work of displaying the feelings a job requires, has often linked that kind of smiling to worse work-related mood, lower wellbeing and more burnout. In 2026, Coles, Annabel Dang and Joao Takayanagi tested three features that separate workplace smiling from the laboratory: smiling in a negative emotional context, smiling repeatedly, and smiling to avoid a financial penalty. Coles, Dang and Takayanagi, 2026.

The study was a Registered Report: the journal reviewed and accepted the design before the results were known, which limits the room for choosing an analysis after seeing the data. It extended the Many Smiles procedure and collected data from 1,201 people.

No single prediction fit all the results. In negative contexts, one posed smile still raised reported happiness compared with expressing feelings naturally. That benefit weakened when people posed the smile repeatedly, and it was virtually nil when they also faced the threat of a penalty for not complying. In positive contexts, repeated or enforced smiling lowered reported happiness. The authors conclude that a posed smile can lift mood in some situations and dampen it in others.

A feeling is an outcome, but it is not every outcome

Do not dismiss a change in reported emotion just because it is subjective. Feelings are part of what emotion researchers want to understand. The mistake comes when that outcome is quietly swapped for something else.

Imagine an employer asking staff who are upset about an unpredictable schedule to smile more. The 2026 experiment did not study a real job, but it tested the ingredients of this request: an unpleasant situation, repetition and pressure to comply. A single smile before a difficult phone call is closer to the condition that raised happiness. A smile demanded all shift is closer to the conditions under which the lift weakened or vanished. And even a real lift in mood would say nothing about whether the schedule becomes manageable. The study and the workplace problem operate at different levels.

For the same reason, these experiments do not test smiling as a treatment for depression. They study a more limited question about facial movement and short-term emotional experience.

When you hear “smiling makes you happy,” ask which smile, compared with what, and measured how. A change on a rating scale during an experiment can be real without carrying the much larger promise attached to it. The power posing research makes the same point about body posture: keep feelings separate from hormones and performance.

Picture a form that ends with a statement such as “I confirm that the information above is true,” followed by a signature line. You fill in the form, then sign. What if you signed at the top instead, before writing anything? The idea is that you would think about honesty before deciding what to report, rather than after. A 2012 paper reported evidence that this simple change reduced dishonest reporting.

The finding did not hold up in a substantial later replication effort. Separately, PNAS retracted the original paper in 2021 over concerns about the validity of its data. Those are two different developments. The replication tested the proposed effect; the retraction changed whether the original paper could be relied on as evidence. Kristal and colleagues, 2020; official retraction notice.

The original claim

Lisa Shu and colleagues reported that asking people to sign an honesty declaration at the beginning of a form reduced dishonest reporting compared with signing at the end. Their paper described laboratory studies and an insurance field experiment. The proposed explanation was that signing first brought ethical standards to mind before the opportunity to misreport. Original paper, now retracted.

The appeal was its apparent simplicity. An organization would not need to make the task easier, increase monitoring or change the financial incentive. It could just move a signature box.

But a simple change still has to be shown to work. A cheap intervention that does not improve the outcome can still use up attention and crowd out a better solution. The real question is whether moving the signature actually reduces dishonest reporting in the setting where it will be used.

What the later tests found

In 2020, Ariella Kristal and colleagues, including several authors of the original paper, reported five conceptual replications and one preregistered direct replication of the original paper's first laboratory experiment. A conceptual replication tests a related claim with a changed procedure. A direct replication tries to reproduce the original procedure more closely. Across the tests, the researchers did not reproduce a benefit from signing first rather than last. The direct replication involved 1,235 participants and assessed the original study's reporting outcomes. Replication paper.

The difference between the two kinds of replication matters. A string of failed variations would be weaker evidence against a specific original result than one closely matched test of that result. This project did not stop at variations. It deliberately went back to the original laboratory question, which makes its result especially relevant to the claim that moving the signature, by itself, makes people more honest.

It does not show that every honesty reminder fails. A different intervention, tested against a different comparison, can give a different answer. That is why the intervention and the comparison need to stay visible.

The replication paper was corrected too

In June 2026, PNAS published a correction to the 2020 replication paper. It repaired reported confidence intervals and effect-size signs in the direct replication, clarified sample and condition counts, and corrected descriptions of some procedures. The corrected results still report no detected sign-first benefit on the three preregistered outcomes. Official correction.

The correction does not reverse the broad conclusion, but it belongs in the account. Papers that challenge a famous finding need the same scrutiny as papers that support it. If you use the replication's numbers, take them from the corrected record, not an older downloaded copy. And keep the two notices apart: the 2026 correction concerns the replication paper; the 2021 retraction concerns the original paper.

Signing first is not the same as adding a pledge

Consider three hypothetical forms:

• Form A has no honesty declaration.
• Form B asks for a declaration at the bottom.
• Form C asks for the same declaration at the top.

Comparing B with C tests placement. Comparing A with C changes both whether there is a declaration and where it appears. If C outperformed A, that alone would not show an advantage of signing first over signing last.

This small distinction has large consequences. Two studies can both be described as “honesty nudges” while testing different interventions. A favorable result for one does not rescue an unsuccessful result for the other. The replication paper itself discusses this problem when comparing field applications. Kristal and colleagues.

A 2024 megastudy shows the distinction in practice. Janis Zickfeld and colleagues tested 21 honesty oaths and a no-oath condition with 21,506 participants in the UK and US. Participants played an incentivized online tax game in which they could underreport their income, and they took the oath before reporting. Ten of the 21 oaths significantly improved tax compliance compared with no oath, by 4.5 to 8.5 percentage points, and the most effective nearly halved tax evasion. The authors concluded that an oath's effect depended on its content. Zickfeld and colleagues, 2024.

That is a comparison of A with C: an oath before reporting versus no oath. It supports the idea that some commitments to honesty, made before the opportunity to cheat, can reduce dishonest reporting in this kind of game. It does not test moving the same declaration from the bottom of a form to the top, and a tax game played online is not a real tax return or insurance claim. If you want an honesty statement on a form, test the specific wording against no statement, in the setting where you will use it.

What the retraction adds

The PNAS notice, published on September 13, 2021, retracts the original article and says that evidence raised questions about the validity of the data. That is a reason not to use the paper as reliable support for the intervention. PNAS retraction.

Keep the failed replication and the retraction apart. A result may fail to replicate for reasons that have nothing to do with misconduct. And questions about data integrity matter even if a separate study supports a similar effect. Evidence for a claim has to be judged across valid studies; publication status belongs to the particular paper.

Nor should anyone use the notice to infer which individual was responsible for any invalid data. That is a different factual claim, and it requires its own evidence. The practical conclusion here does not depend on settling who was to blame.

What to do with the claim now

Do not cite the 2012 paper as established evidence that moving a signature to the top makes people more honest. If someone proposes the intervention, describe the later replication results and the retraction alongside the original claim.

If you are designing a form, start by defining the behavior you want to change and how you will measure it. A clearer form, a verification process and an honesty declaration are different proposals. None of them gains evidence just by being filed under behavioral science.

The nudges-at-scale evidence review explains why the broader intervention literature also needs careful interpretation. The procrastination and deadlines case shows another situation in which a replication and a retraction answer related but distinct questions.

Key sources

• Shu and colleagues (2012): Signing at the beginning makes ethics salient… (retracted)
• Kristal and colleagues (2020): Signing at the beginning versus at the end does not decrease dishonesty
• PNAS (2021): Official retraction notice
• PNAS (2026): Correction to the replication paper
• Zickfeld and colleagues (2024): Effectiveness of ex ante honesty oaths in reducing dishonesty depends on content

Can you protect yourself from procrastination by setting deadlines in advance? A well-known 2002 paper by Dan Ariely and Klaus Wertenbroch offered an appealing answer: people chose to impose deadlines on themselves, those deadlines could improve their performance, and deadlines imposed by someone else worked even better in the paper's comparison.

Psychological Science retracted the paper on September 2, 2026. A close replication of its proofreading study, published that July, had also failed to reproduce the reported performance advantage. The paper is no longer reliable evidence for that claim. This history does not settle whether deadlines help in other situations. Original paper, now retracted; replication; retraction.

Three questions that can get confused

The paper's title, Procrastination, Deadlines, and Performance: Self-Control by Precommitment, bundles three questions that need separate answers.

First, will people choose to constrain themselves? Second, does the constraint improve the outcome? Third, if people choose a constraint, do they choose a useful version of it?

Everyday advice merges these questions all the time. Someone installs an app that blocks distracting websites and assumes the app works. A student asks a friend to enforce a deadline and assumes the deadline improved the work. But choosing a commitment device shows only that the person is willing to use it. It does not show that the commitment caused a benefit.

That distinction still holds now that one famous paper no longer counts as dependable evidence. For any commitment, ask what changed in the outcome, compared with what would have happened without it.

What the replication tested

Kyle Hyndman and Alberto Bisin attempted a close replication of Study 2, the proofreading experiment. Participants worked on texts with inserted errors under one of three deadline arrangements: a single final deadline, evenly spaced intermediate deadlines imposed by the researchers, or intermediate deadlines they could set themselves.

The replication did not find the original advantage for imposed deadlines on outcomes that included errors found and timeliness. Many participants did not finish the task, which limits what the result can show. The authors could not obtain the original instructions, so they reconstructed the task and described the procedural choices they made. That makes it a close replication, not an identical one. Hyndman and Bisin, 2026.

Even so, it is a more informative test than comparing an essay assignment with an unrelated workplace project and deciding that deadlines “work” in one but not the other. The replication went back to a similar task with a similar set of deadline conditions. Its result weakens confidence in the original comparison and leaves other deadline questions open.

The replication also kept the first two questions apart. In the authors' 2025 manuscript, about nine in ten participants who could set binding intermediate deadlines for themselves chose to do so. People still wanted the constraint. The constraint still did not produce the performance advantage. Hyndman and Bisin, 2025 manuscript.

Two earlier experiments, which the replication authors cite, point the same way. Nicholas Burger, Gary Charness and John Lynham found that evenly spaced interim deadlines led to lower completion of a lengthy task in their setting. Alberto Bisin and Kyle Hyndman, the same pair behind the replication, found strong student demand for self-imposed deadlines, but those deadlines did not increase completion rates, and students did not set them well. Burger, Charness and Lynham, 2011; Bisin and Hyndman, 2020. These are different tasks and samples, and neither tests every kind of deadline. They do suggest that the 2002 pattern, in which chosen deadlines helped and imposed ones helped more, was not a dependable general rule.

Why the paper was retracted

The journal's notice, first published on September 2, 2026, says the editor could no longer attest to the reliability of the article's findings. It gives three reasons: questions raised by the replication, uncertainty about the authenticity and completeness of a dataset believed to relate to the original study, and an investigation by Data Colada. Both original authors agree with the retraction. Journal notice.

Data Colada is a blog run by three researchers: Uri Simonsohn, Joe Simmons and Leif Nelson. In two posts dated August 31 and September 2, 2026, they concluded from their own analysis of the data files that the data in Study 1 and Study 2 had been tampered with. Study 1 compared executive-education students who wrote three papers under different deadline rules; Study 2 was the proofreading experiment. Neither the notice nor the posts are a formal misconduct ruling about any person. Data Colada 138; Data Colada 139.

The notice concerns the reliability of this one publication. It does not identify which individual was responsible for any data problems, and it does not show that deadline interventions never help.

Retraction changes how you can use the original article. You can still discuss it as part of the history of an idea, but do not present its findings as secure support for advice. Calling it “a famous study” does not solve the problem.

What this means for ordinary deadlines

Imagine a team whose work passes through three stages, each depending on the one before. Intermediate dates may have an obvious job here: the next person needs a finished piece before starting. That is a coordination question. It is different from asking whether deadlines you set for yourself improve your own performance by helping your self-control.

Or consider a personal deadline set before you understand the work. The date might give you structure. It might also be unrealistic and commit you to a plan you cannot finish. Both situations are hypothetical. They show why the task and purpose matter; they are not findings from the retracted paper.

So start by asking what a proposed deadline is for. Is it coordinating people, allocating scarce time, making an obligation explicit, or trying to overcome avoidance? What would count as success: starting, finishing, producing better work, or all three? And what is the alternative?

The evidence here cannot answer all of those questions. It does take a once-prominent paper off the list of dependable answers.

If you have cited this study

When a book, course or presentation relies on this study, find the specific passage and the claim it supports. Replace the citation with an accurate account of the replication and retraction. Then ask whether independent evidence supports the recommendation. Do not assume the rest of the book is false, and do not keep an unsupported claim just because it sits inside a useful book.

For another case with separate replication and publication-status events, see signing first and honesty. For the different question of connecting a future situation with a planned response, see implementation intentions.

Key sources

• Ariely and Wertenbroch (2002): Procrastination, deadlines, and performance (retracted)
• Hyndman and Bisin (2026): Replication of the proofreading study
• Psychological Science (2026): Official retraction notice
• Data Colada 138 (2026): Artificial Deadlines, Part 1
• Data Colada 139 (2026): Artificial Deadlines, Part 2
• Burger, Charness and Lynham (2011): Field and online experiments on self-control
• Bisin and Hyndman (2020): Present-bias, procrastination and deadlines in a field experiment

Ego depletion is the claim that exerting self-control on one task temporarily makes you worse at another. Its best-known explanation treats self-control as a limited resource that gets used up.

The simple version is not established. Several large, preregistered studies found effects close to zero, including multilaboratory projects led by Martin Hagger in 2016 and Kathleen Vohs in 2021. Other collaborations found positive effects, including a 2025 study by Junhua Dang and colleagues that used a much longer initial task. Together they leave open when one demanding task affects another. They do not show that everyone draws from a single store of willpower.

The gap between feeling drained and running out of willpower matters in everyday life. Feeling exhausted after a difficult afternoon is worth taking seriously. But the feeling does not tell you which scientific explanation is correct, or prove that an earlier decision emptied a measurable reserve of self-control.

How the resource idea was tested

The influential 1998 paper by Roy Baumeister and colleagues used several pairs of tasks. In one experiment, people resisted tempting chocolates and ate radishes instead; afterward, they gave up sooner on unsolvable puzzles. Other experiments paired different acts of choice or regulation with later performance. The authors interpreted the pattern as evidence for a shared, limited resource. Original paper.

The logic was that two apparently unrelated activities could draw on the same capacity. If resisting food reduced persistence on a puzzle, perhaps the first act depleted something the second act needed.

But a performance difference does not directly reveal a resource. Motivation, frustration, expectations, boredom, and task-specific demands are possible explanations, and experiments have to tell them apart. The fuel analogy makes the theory easy to picture, but it also makes the resource sound more directly measured than it is.

Suppose someone completes a tedious task and then works less hard on the next one. That observation tells you what happened and in what order. To explain it, you need to know what the first task changed and why the person responded differently afterward.

Two major projects found very small effects

A 2016 multilaboratory project led by Martin Hagger ran the same standardized experiment in 23 laboratories, with 2,141 participants. The estimated effect was d=.04, with a 95% confidence interval from −.07 to .15. Here, d is the difference between groups in standard-deviation units. The estimate was close to zero, far below a substantial depletion effect.

The project used a later procedure, not a repeat of the original radish experiment. Its null result is strong evidence about that standardized test, not about every situation involving effort.

A 2021 project led by Kathleen Vohs involved 36 laboratories and 3,531 participants. Its confirmatory analysis also found a very small, statistically nonsignificant effect, d=.06. An exploratory analysis found a slightly larger d=.08.

“Confirmatory” means the analysis was specified in advance. “Exploratory” means the researchers investigated additional possibilities. Exploratory results can be useful, but they do not count as a success for the planned test.

These projects substantially weakened the case for a large, easily produced depletion effect, and for the broad advice built on it.

Some large studies did find an effect

The evidence did not end with the large null findings. A 12-laboratory replication by Junhua Dang and colleagues, published online in 2020 and in a 2021 issue, found a small positive effect among 1,775 participants. The estimate was d=.10, increasing to .16 after excluding participants whose responses might have been random.

This result matters because it shows that “all large replications failed” is false. The change after exclusions also shows why the details of an analysis matter, not just its verdict.

In 2025, Dang and colleagues reported another collaboration, covering 14 samples and 2,078 participants. The initial task lasted roughly 30–40 minutes and required people to resist looking toward a cue. On a later task, they made more errors when they needed to withhold a response. The estimated differences were d=.35 against a long control task and .31 against a short control task. Other performance measures did not show the same effect.

The researchers preregistered only some stages of this collaboration; they added later samples and conditions outside those plans. The authors also acknowledged that their design did not separate inhibitory-control demands from visual-processing demands. The study supports a more specific task effect, and leaves important questions about its explanation open.

An effect and its explanation are different claims

Asking whether a result is statistically significant will not settle the remaining debate. Researchers also need to know which task sequences produce reliable effects, how large those effects are, and whether one explanation accounts for all of them.

A long visual-control task followed by a response-inhibition task may reveal something important. It does not automatically support claims about resisting dessert, making financial decisions, or handling family disagreements. Those activities differ in duration, meaning, incentives, and the abilities they require.

Nor would a positive result show that glucose runs low. That is a separate biological explanation, and it needs its own evidence. None of the studies discussed here justifies treating a sugary drink as a proven refill of willpower.

At the other extreme, a failed depletion experiment does not mean fatigue is imaginary, that sleep is irrelevant, or that people can concentrate indefinitely. Rejecting one explanation does not remove the experiences it was intended to explain.

What to do with the uncertainty

For a practical problem, start with the demands you can identify. If your evening plan repeatedly fails after a difficult workday, examine the plan: what does it require, what gets in the way, and could a different time or activity meet the same goal? Calling the failure “ego depletion” adds little unless it helps you choose among those changes.

Starting with the plan also avoids an unnecessary conclusion about the person. Difficulty completing one task after another does not reveal a fixed shortage of willpower. The evidence is more specific than that, and useful action should be more specific too.

Ego depletion remains a disputed family of findings and explanations. The strong practical promise, a general resource model that predicts when self-control will run out, has earned much less confidence than its popularity suggests.

For a separate self-control question, see the evidence on procrastination and deadlines: whether choosing a constraint in advance improves later performance. A result about that intervention cannot settle the resource theory, and the resource theory cannot establish that the intervention works.

Teaching students that abilities can develop is not a dependable way to produce large academic gains. The strongest case is narrower: some interventions have produced small improvements for particular students in particular settings. In the 2019 National Study of Learning Mindsets, a brief online intervention raised the grades of lower-achieving students in U.S. public high schools by about one tenth of a grade-point-average point. Other careful studies and reviews find little or no benefit.

That is a reason to be skeptical of broad promises, not a reason to tell students they cannot learn. The belief that improvement is possible, the claim that people with that belief do better, and the claim that a lesson about the belief raises grades are three different ideas.

For a teacher or school deciding where to spend time and money, the third idea is the one that counts. Encouraging language may be appealing. But whether a specific program improves learning enough to justify its cost is a question for evidence.

What a growth mindset intervention tries to change

A growth mindset is a belief that an ability can be developed rather than remaining fixed. Interventions generally try to change how students interpret difficulty: struggling with a problem need not mean that they lack the ability to learn it.

An influential 2007 paper by Lisa Blackwell, Kali Trzesniewski, and Carol Dweck combined a longitudinal study of students' beliefs with a smaller intervention study. It helped establish the argument that beliefs about intelligence could shape motivation and academic trajectories.

Those two kinds of evidence answer different questions. If students with different beliefs have different grades, the beliefs might contribute to that difference. But earlier success, instruction, and other characteristics might also influence both. Randomly assigning a lesson and measuring later outcomes asks a more direct question: did this intervention produce an improvement?

Even then, an intervention can change what students say they believe without changing what they learn. Changing how students answer a questionnaire is not yet an educational benefit.

A major national experiment found a small, targeted benefit

The 2019 National Study of Learning Mindsets, led by David Yeager and colleagues, tested a brief online intervention in U.S. public high schools. Its preregistered analysis found improved grades among lower-achieving students. The estimated benefit was about one tenth of a grade-point-average point, a standardized effect of d=.11. That figure expresses the group difference in standard-deviation units, which allows comparisons across different achievement measures.

That is a small effect, not a transformation in achievement. It is also evidence that a blanket claim of “no benefits anywhere” goes too far.

The result applied to lower-achieving students. It is not a claim that every student gains the same amount. The researchers also examined how results varied with school context. Those differences are informative, but school context itself was not randomly assigned. They do not provide a proven recipe for making the intervention work in any school.

The study also reported a favorable result for advanced mathematics enrollment in tenth grade. In an analysis of 6,690 students from 41 schools, including both lower- and higher-achieving students, enrollment was 36 percent in the intervention group versus 33 percent in the control group. This analysis was exploratory and had not been preregistered. It concerns a different outcome and a broader student group than the primary GPA result. Treat it as promising evidence that needs confirmation. Course-enrollment analysis.

A targeted benefit is still a benefit worth examining. The decision turns on its reliability, size, cost, and relevance to the students a school intends to serve.

Why two reviews reached different conclusions

In a 2023 systematic review and meta-analysis, Brooke Macnamara and Alexander Burgoyne examined achievement effects and the quality of the evidence. The overall estimate was d=.05. Several adjustments for possible publication bias reduced it further and made it statistically indistinguishable from zero. A set of six studies meeting their highest-quality criteria produced d=.02, with a confidence interval from −.06 to .10.

Publication bias is the possibility that the studies available to read are an uneven sample: encouraging results may be more likely to appear than disappointing ones. Statistical adjustments do not reveal every missing study, but they help test whether a conclusion depends on assumptions about the available evidence. This review gives strong reasons to doubt large, general academic benefits.

A separate review by Jeni Burnette and colleagues, also published in a 2023 issue, emphasized differences among interventions. For academic achievement, its model combining targeted student groups with high implementation fidelity estimated d=.14. That is a conditional estimate for selected circumstances, not an overall effect for all students. Its prediction interval ran from −.08 to .35, which leaves substantial uncertainty about what a future intervention would achieve.

Do not count these reviews as two votes. They made different choices about which results to combine, and they answer different questions. “What is the overall benefit in stronger studies?” and “What benefit might occur in targeted groups with high-quality delivery?” can produce different estimates without either estimate applying universally.

The same journal issue carried the next round of the argument. In an exploratory reanalysis, Elizabeth Tipton and colleagues, including David Yeager, who led the 2019 national study, used every effect size in Macnamara and Burgoyne's studies rather than one average per study. They estimated a mean effect of 0.09 standard deviations, and 0.15 for students they classified as at risk. Their central criticism was methodological: when effects really vary, a meta-analysis should model where they occur instead of asking whether one overall effect exists. Tipton and colleagues, 2023.

Macnamara and Burgoyne replied that the reanalysis had changed effect sizes, the coding of moderators and which studies and subsamples were included, often without explanation. When they applied the multilevel approach Tipton and colleagues recommended to their own coding, they estimated 0.07 overall and essentially zero (d=−.003) among studies that changed students' mindsets and met the most best-practice criteria. Macnamara and Burgoyne's reply.

Both reanalyses put the average effect below a tenth of a standard deviation. The live disagreement is whether the larger effects reported for targeted groups are dependable or reflect weaker designs and selective reporting. That is the question a school needs answered for its own students before adopting a program.

What the newer review changes

A 2025 structured review by Carolina Gazmuri provides another skeptical assessment. Its strongest included evaluations showed tiny or zero academic effects, which adds to the case against spending substantial resources on the assumption that a mindset program reliably raises achievement.

It is not, however, a direct retest of every positive subgroup finding. Its rules on how full-sample and subgroup results were reported led it to exclude several prominent trials, including the 2019 national experiment, and the review was not preregistered. Nor does it settle every claim about learning, motivation, or whether abilities change.

A useful message is not automatically a useful program

Imagine a student who is struggling with fractions. Telling the student that learning is possible does not identify which step they misunderstand. A mindset exercise could change how they interpret the difficulty while leaving the difficulty itself unresolved.

That example does not prove that beliefs are irrelevant. It shows why an academic intervention needs an academic outcome. A school should know whether students learned more, not only whether they gave more encouraging answers afterward.

Small effects can matter when an intervention is inexpensive and reaches many people. The benefits may also be too small to justify training costs and classroom time, especially when delivery is weak. Neither “it costs very little” nor “the average effect is small” settles that calculation without a concrete program and a realistic comparison.

If you are considering a program for a school, ask for evidence on that program, with similar students and the outcome the school wants to improve. Look for a credible comparison group and an analysis specified before the researchers saw the data. A testimonial or a general citation to mindset theory does not answer those questions.

The practical position is modest: do not build an educational strategy around a promise that changing beliefs will produce large achievement gains. Treat a specific mindset intervention as something that must earn its place alongside the other demands on students' and teachers' time.

For a different approach to the learning question, see the evidence on retrieval practice. That research tests what changes when learners try to recall material, and it has its own limits on subjects, comparison activities, and later performance.

A short message, a different default or a simpler form can sound like an inexpensive solution to a large problem. The appeal is easy to understand. If a small design change could reliably move behavior, organizations could avoid much harder changes to the service, the incentives or the activity itself.

The evidence is less convenient. Some interventions produce useful changes, but results from published academic studies can create inflated expectations. A large comparison of government nudge trials found substantially smaller average effects than a comparison sample from academic journals. That finding supports skepticism about generic promises; it does not establish that every nudge fails. DellaVigna and Linos, 2022.

What the large comparison found

Stefano DellaVigna and Elizabeth Linos assembled 126 randomized controlled trials, involving more than 23 million people, from two US nudge units. Unlike a collection of journal articles, the units' records included trials whose results had not necessarily been published.

The average effect in the nudge-unit portfolio was an increase of 1.4 percentage points, compared with 8.7 percentage points in the academic-journal portfolio. These are absolute differences in measured behavior, not relative percentage increases. The researchers examined differences in statistical power, intervention characteristics and selective publication as explanations for the gap. They estimated that selective publication in the academic journals, made worse by the low statistical power of many academic trials, explains about 70 percent of the difference; differences in the kinds of nudges tested account for most of the rest. Study and comparison.

This was a comparison between portfolios. It did not follow the same interventions as they grew from small experiments into large programs. So the result cannot show that making any particular intervention larger will reduce its effect by a fixed amount.

The practical warning still stands. An organization planning from the academic average of 8.7 percentage points would expect far more than one planning from the government-trial average of 1.4. The most visible results in a literature are not automatically a realistic forecast.

A percentage point is not a percent

Suppose, as a hypothetical example, that 20 percent of a group completes a form. An increase of 1.4 percentage points would bring completion to 21.4 percent. The relative increase would be 7 percent: 1.4 divided by 20.

For 10,000 people, that difference would correspond to 140 additional completions, if the same effect applied. Whether that is valuable depends on the cost of the intervention, the value of completion, possible harms and the alternative use of the resources. The calculation is an illustration, not a prediction from the study for a new program.

This is why “small” does not mean “worthless.” It is also why a small improvement cannot justify any cost. The relevant comparison is with what the organization could otherwise do, not with an imagined world in which the intervention costs nothing and has no alternatives. The lesson Read the evidence before the promise works through the same distinction with an invented example: a reminder that raises attendance from 20 to 22 percent.

Why the broader debate remains unsettled

A separate meta-analysis by Stephanie Mertens and colleagues combined research on choice-architecture interventions across several domains. The paper received a formal correction after problems were identified in its included observations and coding. The revised estimates did not change the pattern of results or the authors' conclusions. The correction is part of the paper's record, so any description of its findings should mention it. Original synthesis; 2022 correction.

Maximilian Maier and colleagues challenged the evidence for a pooled effect after adjusting for publication bias. The original authors' response acknowledged publication bias and unexplained variation while arguing for more differentiated research. These papers address a separate dataset and analysis from the nudge-unit comparison. Maier and colleagues; Mertens and colleagues' reply.

Publication bias means that results are not equally likely to appear in the visible literature. If striking positive findings are easier to publish than small or null findings, an average calculated from published papers can be too optimistic. Statistical adjustments try to address that problem, but they depend on assumptions. One adjusted average is not an experiment testing every intervention in every setting.

A 2025 second-order meta-analysis by Bo Hu and colleagues pooled 14 earlier meta-analyses, covering 1,638 studies. The pooled estimate was d=0.27, a small effect expressed in standard-deviation units. One bias-adjustment method, PET-PEESE, reduced it to d=0.004, essentially zero. Another, a robust Bayesian model-averaging approach, left it at about d=0.29. The authors also rated 12 of the 13 source reviews as low or critically low in quality under a standard appraisal checklist. Hu and colleagues, 2025.

That paper sharpens the problem rather than settling it. The included meta-analyses define “nudge” differently, their results vary enormously, and two of the 14 inputs are the samples described above: DellaVigna and Linos's academic-journal sample and their nudge-unit sample. Pooling weak reviews cannot produce a strong answer, and an average across defaults, reminders, social comparisons and simplified forms says little about any one of them. What it does show is how much the headline estimate depends on assumptions about the studies that never reached publication.

The site's article Do Nudges Work? What the Evidence Can Actually Tell Us takes the wider question. It adds a flu-vaccination text megastudy and a review of social norms messages, and sets out how to decide whether a nudge is worth testing.

Ask what actually changed

The word “nudge” covers interventions with different demands and purposes. Prompting someone to finish a nearly completed task is a different challenge from keeping them at an activity they dislike or cannot fit into their life. A rise in initial enrollment does not, by itself, show lasting participation.

Before adopting an intervention, state the outcome that would make it worthwhile. If the purpose is attendance, count attendance rather than clicks on a reminder. If the purpose is sustained participation, include enough follow-up to observe it. If more activity at one location could simply displace activity from another, measure the broader outcome as well.

Those are design questions, not additional findings from the portfolio average. They guard against a common mistake: treating a change in the measured response as proof that the underlying problem was solved.

A 2025 working paper by Silvia Saccardo, Hengchen Dai and colleagues, not yet peer reviewed, shows that mistake in a real trial. It reanalyzes the full sample of a UCLA Health trial of text reminders for COVID-19 vaccination, which Dai and colleagues first reported from early data in 2021 with larger effects. Dai and colleagues, 2021.

In the full sample, the first reminder raised vaccinations at UCLA Health within four weeks by 2.8 percentage points. Vaccinations anywhere in California over the same four weeks, measured through the state registry, rose by only 1.0 point. The authors read that gap as spatial substitution: some people who would have been vaccinated elsewhere went to UCLA Health instead.

A separate comparison points to timing. Over eight weeks, the statewide effect shrank by half and was no longer statistically distinguishable from zero, which suggests the reminders partly moved vaccinations earlier rather than adding new ones. The same paper reports smaller effects among people with low baseline motivation to act. Saccardo, Dai and colleagues, 2025 working paper.

The site's Bad News for Nudges explains the broader concern about generic behavioral fixes. The productive response is to examine the person, behavior and setting closely enough to choose a plausible intervention, then test the outcome that matters. A familiar theory does not excuse a proposed solution from that work.

For a focused case in which both replication results and a retraction changed the evidence, see signing first and honesty.

Key sources

• DellaVigna and Linos (2022): RCTs to scale
• Mertens and colleagues (2022): The effectiveness of nudging, with its correction
• Maier and colleagues (2022): Publication-bias reanalysis
• Mertens and colleagues (2022): Reply on choice-architecture research
• Hu and colleagues (2025): Assessing nudge impact: a comprehensive second-order meta-analysis
• Saccardo, Dai and colleagues (2025): Scaling nudges, working paper

An anchoring effect occurs when a number influences a later numerical judgment. But the way the number enters the situation matters. Asking someone whether a quantity is above or below a suggested value is a different intervention from putting an unrelated number in the background.

Explicit numerical anchoring has strong replication evidence in studied estimation tasks. Claims that incidental numbers reliably change consumers' price estimates have a less secure record. Treating both as one psychological trick hides the distinction that matters when you try to use the research. Many Labs, 2014; Shanks and colleagues, 2020.

The number in the question

Consider a hypothetical estimate: how long is a river you know little about? Before asking for your best answer, one version of the question asks whether the river is longer or shorter than 500 kilometers. Another asks whether it is longer or shorter than 5,000 kilometers. The suggested number is an explicit reference point. The research question is whether the two groups then give different estimates.

The example shows how an anchoring task is built; the numbers are not results from a study. What matters is that the person has to consider the anchor while making the judgment. It is not just a number that happened to be visible somewhere else.

The Many Labs project tested four explicit numerical anchoring questions based on earlier work by Karen Jacowitz and Daniel Kahneman. The effects appeared consistently across the participating samples. The project also noted design and effect-size differences between original and replication studies, so the result does not show that every original magnitude was reproduced exactly. Klein and colleagues, 2014.

That is evidence for a recognizable procedure and outcome: a numerical comparison followed by an estimate. It does not yet show what happens to sales, negotiation outcomes or long-term behavior.

The number in the background

A more surprising claim is that an incidental number can influence what a consumer thinks something is worth. For example, a number in a restaurant's name might supposedly shift people's estimates of what a meal costs, even though the number says nothing useful about the food.

David Shanks and colleagues tested incidental environmental anchors in three studies and did not find consistent effects on price estimates. In the second and third studies they also included standard numerical anchoring questions, for which they observed clear effects. Those standard questions asked about general-knowledge quantities, such as the population of Chicago, not prices, and the authors note that this rules out a direct comparison of the two effects' sizes. This was not a perfectly matched test showing that relevance alone explains the difference. Shanks, Barbieri-Hermitte and Vadillo, 2020.

The useful conclusion is narrower: under conditions that produced standard anchoring, these incidental-number procedures did not reliably produce the claimed consumer effect. The paper leaves open whether other circumstances could produce incidental anchoring. A null result in these studies is not proof that every unrelated number is powerless.

Why the distinction matters in practice

Imagine you are redesigning a pricing page. One proposal gives visitors a clear comparison with a relevant alternative. Another adds a large unrelated number because “anchoring works.” These proposals share a word, but they do not share an evidential foundation.

Even a relevant comparison introduces questions beyond the classic estimation tasks. Is the comparison accurate? Do visitors interpret it as useful information or as a sales tactic? Does it change the choice they make, or only an answer on a rating scale? Does it improve the decision from the customer's point of view?

The anchoring studies discussed here cannot answer all of those questions. To evaluate a pricing change, measure what it actually changes against an appropriate alternative. Do not use a well-replicated estimate shift as a substitute for evidence about purchases or customer benefit.

A field experiment on willingness to pay shows why. Tongzhe Li and colleagues asked adults to bid on gardening products using a slider whose starting price was set at random. In the original study, raising the starting price from the lowest anchor to the highest increased valuations by 31 percent. An overlapping team then ran a replication with 621 adults and far more statistical power. The estimated effect fell to 3.4 percent, with a 95 percent confidence interval from −3.4 to 10 percent, which rules out an effect as large as the original. Li, Weigel, Ferraro and Messer, 2025.

That replication does not show that numbers never move prices. It shows how a striking price result from an underpowered study can shrink sharply when tested again with enough participants, even in a similar setting run partly by the same researchers.

This is a general lesson for applied behavioral science: keep the procedure attached to the finding. “A number influenced an estimate in this task” is a testable claim. “Numbers can control decisions” has discarded the conditions that made the result meaningful.

What holds up

Explicit numerical anchors deserve a place in an account of how people make estimates. A meta-analysis by Dan Schley and Evan Weingarten, covering 2,601 effect sizes from five decades of anchoring research, supports the split this review describes. It found a large average effect when people compared a number before making a judgment, and that effect remained large after adjustment for publication bias. It found reduced or null effects for incidental anchors, for anchors that were random numbers and when incentives were present. Schley and Weingarten, 2026.

The replication record gives more support to the studied explicit-estimation procedures than to the particular incidental consumer-price claims tested here, or to large effects on what people will pay. It does not support one universal effectiveness rating for everything called anchoring.

Read the anchoring definition for the basic concept. The evidence review of nudges at scale follows the next practical question: how much should a research finding lead you to expect from a real intervention?

Key sources

• Jacowitz and Kahneman (1995): Measures of anchoring in estimation tasks
• Klein and colleagues (2014): Investigating variation in replicability
• Shanks and colleagues (2020): Do incidental environmental anchors bias consumers' price estimations?
• Li, Weigel, Ferraro and Messer (2025): Underpowered studies and exaggerated effects: a replication and re-evaluation of the magnitude of anchoring effects
• Schley and Weingarten (2026): Fifty years of anchoring effects: a theoretical reintegration and meta-analysis

Specific if–then plans can help people carry out intentions, but their average benefit is less certain and less uniform than familiar success stories suggest. A large review covering 642 independent tests found positive effects overall, with substantial variation and evidence of publication bias. Methods that adjust for that bias produced smaller estimates, and how much smaller depended on the method. The review also pooled behavior, cognitive performance, feelings and social judgments, so its overall result is not an estimate for behavior alone. Sheeran, Listrom and Gollwitzer, published online 2024.

Think of an implementation intention as a way to link something you intend to do with a situation you will recognize. It does not supply every missing ingredient of behavior. A plan cannot create time, access or a skill that a person lacks, and writing one does not show that the person wants the outcome enough to pursue it.

What the plan adds

A goal states an outcome: “I want to keep better project notes.” An implementation intention links a cue to a response: “If the project meeting ends, then I will open the notes and write the next action before switching tasks.”

In this hypothetical example, the plan specifies a moment the person can recognize and an action they can perform. The response is more concrete than “be organized.”

The name matters because studies of planning do not always test the same thing. Some ask people to form an explicit if–then connection. Others ask them to choose a date and time. Still others combine planning with a separate exercise about goals and obstacles. These approaches may overlap, but evidence for one package does not identify the effect of every component.

The 642-test review distinguished contingent if–then plans from other planning formats. Benefits were generally larger for contingent plans, when participants were highly motivated, and when plans were rehearsed. Those patterns describe differences across the assembled studies; they do not provide a guaranteed formula for any individual. Sheeran, Listrom and Gollwitzer, published online 2024.

Children are a separate question. A 2026 meta-analysis by Jasmin Breitwieser and Tilman Reinelt, limited to children with an average age under 13, combined 52 effects from 42 studies involving 12,957 children. The pooled effect was g=0.31, a small-to-medium difference in standard-deviation units, with substantial variation across studies. The authors found signs of publication bias, but the adjustments disagreed: one method roughly halved the estimate, to 0.15, while a selection model put it at 0.38. The result supports testing if–then plans with children; it does not tell an adult program what to expect. Breitwieser and Reinelt, 2026.

A workplace flu-shot result and its size

A workplace vaccination study by Katherine Milkman and colleagues shows how a small change to a reminder can affect a concrete action. Employees received information about free workplace flu clinics. Some were also prompted to write down a date, or a date and time, for attending.

About one-third of the control group was vaccinated. The date-and-time prompt raised vaccination by an adjusted 4.2 percentage points relative to the standard reminder. The date-only prompt did not produce a statistically reliable increase. Milkman and colleagues, 2011.

This is a meaningful result from a specific situation: an available service, a short opportunity to use it, and a prompt attached to information that employees were already receiving. The intervention helped some additional people act. It did not make everyone comply, and it did not remove the need for the clinic itself.

The study also illustrates why a percentage-point gain can be worth having. A few additional actions per hundred people may matter when an intervention is cheap and the action has value. That is a different claim from saying a planning prompt radically transforms motivation.

Why another plausible planning prompt did not help

Mariana Carrera and colleagues later tested a scheduling prompt with 877 gym members. Participants in the intervention chose days and times to exercise over the next two weeks. They engaged with the planning task, but the study did not find an increase in gym attendance. Carrera and colleagues, 2018.

This result does not directly refute every if–then plan: choosing a schedule is not the same as forming a plan that links a cue to a response. It does challenge the broader assumption that asking people to plan when they will act is usually enough.

It also poses a practical question. Was the problem forgetting an intended action, finding a suitable opportunity, sustaining motivation, or something else? A reminder to decide on a time may address one of these obstacles while leaving the others in place. The comparison between the gym and vaccination studies does not isolate which difference explains their results. It shows why the successful example should not be carried into a new setting without testing.

The broader review also found that some outcome categories, including vaccination and voting, had uncertainty intervals consistent with no average benefit. A positive individual study and an uncertain category-level result can coexist. Sheeran, Listrom and Gollwitzer, published online 2024.

How to use a plan and test it

Start with an action that someone actually intends to take. Then ask what recognizable event could prompt it, whether the action is feasible at that moment, and what will count as completion. These are useful design questions. Answering them does not promise an automatic habit.

For example, “If I finish a customer call, then I will record the agreed next step before opening my inbox” gives the person a clear opportunity to act. But if the call system immediately routes another call, the plan may be impractical. Changing the workflow could matter more than strengthening the wording.

The same distinction applies to public programs. Asking someone to plan an appointment does not solve unavailable appointments or an inaccessible booking process. A planning prompt can be evaluated as one addition to a functioning service. It should not be used to explain away obstacles that the service creates.

When evaluating a prompt, measure the intended behavior. Did the appointment happen? Were the notes completed? Did attendance change? A well-written plan, a favorable survey response and confidence that the plan will help are not interchangeable with action. Compare the prompt with what people would otherwise receive, including any reminders or support already in place.

Implementation intentions remain a reasonable tool for helping people follow through on feasible goals. The evidence favors modest, context-sensitive expectations. Use the plan to make an intended action more concrete, then check whether the action changes. The research does not support treating planning as a substitute for motivation, resources or a workable environment.

People who spread practice across separate sessions generally remember more of the material later than people who pack the same practice into one session. This spacing effect has a broad research base, especially for learning and remembering verbal material. The harder questions are how far apart the sessions should be, how much of the benefit carries over to a particular subject, and what happens when the outcome is real performance rather than a memory test. Cepeda and colleagues, 2006.

The evidence supports coming back to material over time, including in ordinary classrooms. It does not support one revision timetable for everyone. And a large school trial of one branded spaced-learning program found no improvement in exam results.

Spacing changes the timing of practice

Suppose you have four opportunities to review the same material. You could hold them back to back on one afternoon, or spread them across several days. Spacing is about that choice. A fair comparison also gives both groups comparable material and practice, so that extra time or additional teaching cannot explain the result.

Spacing is different from retrieval practice, which concerns trying to produce information from memory. It is also different from interleaving, which changes the order in which different kinds of material or problems appear. A study routine can combine all three, but a gain from the combined routine does not reveal the contribution of each part.

This matters when choosing educational software. A flashcard program may vary the time between reviews, require recall and provide immediate corrective feedback. Evidence for the spacing effect makes its review schedule worth examining. It does not compare that product with every other way of studying.

A substantial record of repeated findings

A major 2006 review by Nicholas Cepeda and colleagues assembled 317 experiments on distributed practice in verbal recall. The results supported spacing, but how well it worked depended on two intervals: the gap between learning sessions and the time before the final test. Longer retention goals generally called for longer gaps. Cepeda and colleagues, 2006.

Later experiments by Cepeda and colleagues tested learning across different gaps and retention periods. They found that increasing the gap could initially help and then hurt performance. So more spacing was not always better. Cepeda and colleagues, 2009.

For a learner, this means the deadline matters. Preparing to use information tomorrow is a different problem from retaining it for several months. You still have to decide when you will need the knowledge, and check whether you can retrieve it.

A popular rule of thumb says gaps should expand: review after a day, then a few days, then a week. A 2021 meta-analysis by Alice Latimier, Hugo Peyre and Franck Ramus compared expanding with equal gaps between retrieval practice sessions across 54 effect sizes and found almost no difference (g = 0.034). Spacing retrieval practice, rather than massing it, did help (g = 0.74 after correction for likely publication bias). Latimier, Peyre and Ramus, 2021.

A recent replication shows why the details matter

In 2025, John Rogers, Tatsuya Nakata and Ming Ming Chiu reported an online conceptual replication of Cepeda and colleagues' 2009 vocabulary experiment. Participants learned Swahili–English word pairs in two sessions and completed a recall test after a ten-day delay. The study compared massed practice with five different gaps.

The result depended on the analysis. In the unadjusted comparisons, only the two-day condition significantly outperformed massed practice. After adjustment for prior and training performance, all five spaced conditions did. The authors interpreted the results as supporting the earlier spacing finding, while discussing differences between online and laboratory research. Rogers, Nakata and Chiu, 2025.

That adjustment needs care. It included accuracy during the second training session, after the spacing gap. Spacing could itself affect that accuracy, so the more positive adjusted result is not automatically stronger evidence of spacing's overall benefit. Only 222 of 569 recruits completed the experiment, and completion was lower in the longer-gap groups, adding uncertainty about how comparable the remaining groups were. Rogers, Nakata and Chiu, 2025.

So the replication supports spacing, with a qualification; it does not simply reproduce every original result. It also separates two questions: whether separating sessions helps, and whether one particular gap is best. Evidence for the first does not automatically settle the second.

Classrooms, mathematics and professional learning need their own evidence

Most spacing research comes from laboratories, often with word lists. Classroom evidence is thinner. A 2025 meta-analysis by Rhys Mawson and Sean Kang included only studies run in classrooms with material students would have learned anyway, and compared sessions at least a day apart with massed practice of equal study time. Across 22 studies (31 effect sizes, more than 3,000 learners), spaced practice did better (d = 0.54, 95% confidence interval 0.31 to 0.77). Results varied widely between studies, and too few studies were available for a full analysis of why. Mawson and Kang, 2025.

A program sold as spaced learning is a different test. In England, the Education Endowment Foundation funded a trial of SMART Spaces, a branded revision package for GCSE chemistry, in 125 schools with 14,098 pupils. Teachers delivered six scripted revision lessons in the three weeks before the exams: two different lessons, each taught three times on separate days. Each lesson covered three different blocks of content in 12-minute episodes, separated by ten-minute breaks for activities such as juggling. Pupils therefore met the same content three times, with at least one night's sleep between repetitions. Compared with schools' usual revision, the program made no detectable difference to the chemistry exam score (effect size −0.01, 95% credible interval −0.17 to 0.12), a result the evaluators rated as high security. EEF evaluation, 2023.

These results do not contradict each other. The meta-analysis compares spaced with massed study of the same material for the same time. The trial compares a whole package, squeezed into the last weeks before an exam, with whatever revision schools already did, which the evaluators note may have included looser forms of spacing. They judged that the null result “is unlikely to be due to ‘leakage’”, meaning control schools copying the approach, because 43% of control teachers said they knew very little or nothing about spaced learning. As the evaluators say, it is not definitive evidence for or against spaced learning in general. It is strong evidence that this package, delivered this way, did not raise exam results.

A 2025 meta-analysis focused on mathematics learning. Across 27 spacing studies, it found a positive average effect. Benefits varied, and the estimated effect was smaller for studies embedded in courses than for studies of material taught in isolation. Murray, Horner and Göbel, 2025.

That average does not mean every classroom procedure improves when spaced. In a separate 2025 study, Julia Krauspe, Mirjam Ebersbach, Anne Ludwig and Florian Scharf gave 213 fourth graders spaced or massed practice in long multiplication during regular lessons, with practice time held constant. Eight weeks later, spacing made no detectable difference, and Bayesian analyses supported the null result. One null result does not erase a positive literature, but it prevents the average from becoming a promise about every lesson. Krauspe, Ebersbach, Ludwig and Scharf, 2025.

A 2026 review in medical education also found benefits on knowledge tests from spaced-repetition interventions. Those interventions included different formats, such as flashcards and repeated questions. The results concern the studied learning programs and knowledge outcomes; they do not isolate a pure timing effect or show improved patient outcomes. Maye and Hurley, 2026.

Together, these findings point toward building spaced review into teaching, while leaving room for evaluation in each subject. Remembering vocabulary, carrying out a calculation and responding correctly during a professional task are related educational goals, but they are not identical outcomes.

What this means for a course or study routine

A sensible starting point is to build return visits into the schedule. Instead of treating a chapter or training session as finished once it has been covered, arrange later opportunities to use its important content. The precise schedule can follow the course, the learner's performance and the time at which the material will be needed.

For example, a workplace course might revisit an important procedure in later scenario exercises. To learn whether the change helped, assess the procedure after a meaningful delay and compare it with the previous format. If the new course also adds practice time, better explanations and feedback, describe it as a changed training program. Do not attribute the entire difference to spacing.

A student can also divide review across several sessions without assuming that a particular sequence of one, three and seven days is scientifically optimal. In studies of spaced retrieval practice, expanding gaps showed no general advantage over equal ones. If later practice shows that the material has been lost, that is useful information for adjusting support and review. A schedule should serve learning, rather than become a target that takes priority over it.

Spacing is a strong candidate for improving how learning opportunities are arranged. The evidence is clearest when the claim stays attached to its comparison and outcome: separated practice often improves later retention relative to concentrated practice. A specific calendar, app, course redesign or claim about professional performance still needs evidence of its own.