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Primary publication: doi.org/10.1037/bul0000128

Publication text or primary record: affective-science.org/wp-content/uploads/2024/04/siegel-et-al-fingerprints-2018.pdf

Psychological Bulletin 144, 343–393; autonomic-reactivity meta-analysis. The 2024 directory is a hosting date, not the research date.

Refit a meta-analysis after deleting each study, comparing fitted effects, uncertainty and heterogeneity to the full fit. For fixed weights $w_i>0$, total weight $W$ and weighted effect $\hat{\mu }$, direct subtraction of the two weighted means gives $\hat{\mu }-{\hat{\mu }}_{(-i)}=w_i(y_i-\hat{\mu })/(W-w_i)$. Re-estimating heterogeneity additionally measures influence through the weights. This is a sensitivity diagnostic, not an automatic rule for removing discordant studies.

The logarithm of a risk ratio is zero at equal risks, negative when the first risk is smaller, and positive when it is larger. For independent binomial event counts $d_1,d_0$ from samples $n_1,n_0$, its usual delta-method variance estimate is $1/d_1-1/n_1+1/d_0-1/n_0$. This approximation requires nonzero counts; zero-event arms need another procedure. Log estimates are convenient for inverse-variance meta-analysis, and exponentiation returns to the risk-ratio scale.

Small, variable effects support a limited influence of facial activity on reported feeling; they do not identify a single feedback mechanism or establish that facial feedback is necessary for emotion. This conclusion separates the experimental contrast from its proposed explanation. Randomly assigning a facial task estimates the effect of that task, including every change the task produces. It does not automatically isolate sensory feedback from the face.

Nicholas A. Coles, Jeff T. Larsen and Heather C. Lench synthesized 286 effect sizes from 138 studies using a random-effects approach with robust variance estimates. Their overall estimate combined outcomes, so the more relevant result for experienced emotion is the emotional-experience subgroup: standardized mean difference $d=0.17$, with 95% confidence interval $[0.11,0.23]$. Affective judgments of stimuli had a larger estimate. The reported moderators included outcome type and properties of the eliciting stimuli. These are comparisons among existing studies, not randomized assignments of the proposed moderators.^[ref]

The distinction between outcome types is theoretically important. Rating a cartoon's objective funniness asks for an evaluative judgment about a stimulus; rating one's own amusement asks about experience. Either can change through inference, expectations or response interpretation. Treating both as direct measures of feeling would make the evidence seem more decisive about the facial feedback hypothesis than it is. Equally, a small average change in experience is compatible with a real contributory mechanism: emotion ordinarily has many inputs, so no single input need dominate.

The classic apparatus illustrates both the ingenuity and the ambiguity. Fritz Strack and colleagues in 1988 had participants hold a pen in ways that facilitated or inhibited smile-related activity, without explicitly instructing them to look happy. They reported differences in humor responses to cartoons. Avoiding an instruction to act happy reduces an obvious route through deliberate category labeling. It does not equate effort, discomfort, attention, interpretation of the task or the sensory consequences of the postures.^[ref]

A subsequent preregistered replication coordinated by Eric-Jan Wagenmakers and colleagues used 17 laboratories and 1,894 analyzed participants and did not reproduce the original difference. That directly limits confidence in the robustness of this particular procedure. It is not a test of every possible facial manipulation, and it should not be counted as evidence independent of a later synthesis that includes those replication studies.^[ref]

There are several possible causal routes. First, information generated by muscle activity or associated bodily changes might contribute to felt emotion. Second, a person might use their own posture as evidence when interpreting an ambiguous state: a self-inference route could be stronger when other emotional information is weak. Third, producing a posture might activate learned associations without an explicit inference. Fourth, the task might change breathing, effort, discomfort or attention. Fifth, demand characteristics might change the report while leaving experience relatively unchanged. Social responses to a visible face are another possible route in interactive settings, but cannot explain a truly isolated participant's immediate response through an actual partner's reaction. These alternatives are hypotheses, not findings established by the meta-analysis.

The logical problem can be stated without assuming that any route is absent. Write assignment as $X$, facial activity as $F$, sensory feedback as $M$ and the report as $Y$. The chain $X\to F\to M\to Y$ and a model with $X\to F$ plus an expectancy route $X\to D\to Y$ can produce the same association between assignment, movement and report. Randomization of $X$ removes preassignment confounding of its total effect, but does not randomize $M$ or eliminate $D$. Establishing causal mediation therefore requires additional interventions or justified assumptions, not simply a significant total effect.

Heterogeneity also has a limited interpretation. A simple random-effects meta-analysis writes $y_i=\mu +u_i+{\epsilon }_i$, with between-study variance ${\tau }^2$ and sampling variance $s_i^2$. Under independent errors the variance of $y_i$ is ${\tau }^2+s_i^2$. Nonzero ${\tau }^2$ means that true effects differ under the model; it does not specify whether the difference comes from sensory mechanisms, expectations, populations or measurement. Dependent estimates require further treatment, which is why a naive analysis counting every effect as an independent study is inappropriate. Small effects and noisy measurement also make individual studies unstable. Selecting a plausible moderator after a failed experiment is insufficient unless it predicts results in a new test.

Useful follow-up work would preregister a factorial design that varies actual facial activity separately from participants' beliefs about its emotional meaning, with matched effort controls and separate reports of felt state and stimulus judgment. Facial electromyography can verify the motor manipulation, but not certify its psychological mediator. A test of a sensory route also needs a defensible manipulation of that route that leaves the relevant alternatives adequately controlled. Masked hypotheses, automated instructions and timing measures reduce particular ambiguities rather than providing a universal guarantee. A necessary-role claim would require evidence that reducing the relevant feedback prevents an otherwise expected emotional response; an initiation claim requires an effect without the external emotional elicitor, while accounting for the task's own meaning.

The clinical interview produced far fewer events, so the trial may have had substantially less statistical power for that measurement than for the screening-scale threshold. Its intervention-versus-control difference is less striking: the crude event proportions are about $4.7\%$ and $7.3\%$, based on only 37 diagnoses altogether. A concise abstract may therefore have emphasized the more statistically convincing screening result. These are possible explanations, not evidence of the authors' motives.

Nevertheless, a prespecified primary measure should not disappear merely because its result is less favourable. Selective outcome reporting could make the evidence seem more consistent across primary measurements than it is. A reasonable abstract should at least acknowledge the clinical result and its uncertainty, while distinguishing a positive screen from a diagnosis. Limited space can justify brevity, but not a misleading implication that both primary measures provide the same evidence.

The unexpectedly low clinical prevalence also merits investigation, including the telephone interview's implementation, timing, recruitment and diagnostic definition. A meta-analysis of different studies is not automatically a like-for-like reference population; its higher pooled percentage does not by itself establish measurement failure in this trial.

Publication bias occurs when the availability or publication of a study depends on its results, for example their direction or statistical significance. The published studies then need not represent all studies meeting the review's eligibility criteria. This is different from unbiased studies simply having large sampling errors.

If mortality reductions favouring transfusion are more likely to be published than null or unfavourable findings, the observed log risk ratios will tend to be too negative and the pooled risk ratio too small. The apparent benefit will then be exaggerated. An ordinary meta-analysis interval ignores uncertainty about the missing evidence and may have poor coverage even if its sampling-variance calculation is correct for the studies included. The direction of bias depends on which results are preferentially made available; publication bias does not invariably favour a particular treatment.

Three distinct benefits of a meta-analysis are greater precision, an explicit synthesis of the effect, and assessment of variation across studies.

Combining compatible independent estimates can reduce the standard error, improve statistical power and provide more informative confidence intervals than individual small trials. A prespecified pooled estimate summarises the direction and magnitude of the evidence quantitatively, instead of informally counting statistically significant results. Finally, between-study heterogeneity and subgroup comparisons can reveal whether effects vary with populations or interventions, helping assess generalisability. These benefits require comparable estimands and an appraisal of study validity; pooling cannot repair systematic within-study bias.

Within-study bias is a systematic displacement of a study's effect estimate from its intended true effect because of its design, conduct, analysis or reporting. Examples include faulty allocation concealment, differential outcome assessment without suitable blinding, informative loss to follow-up, deviations from the intended treatment analysis, and selective reporting of outcomes or analyses. This differs from chance sampling error; the bias need not diminish as a study becomes larger.

It can shift a pooled meta-analysis effect and can create or obscure between-study heterogeneity. A random-effects meta-analysis accommodates dispersion, not systematic invalidity. Publication or non-inclusion of whole studies is a separate selection problem at the synthesis level.

Two useful approaches are risk-of-bias sensitivity analyses and explicit bias adjustment. First, appraise the relevant bias domains and compare the full synthesis with a prespecified synthesis restricted to studies with more credible methods, or stratify by those domains; discuss the resulting loss of precision and possible confounding of study characteristics. Second, if substantive information supports plausible bias magnitudes, use a bias-adjusted meta-analysis with uncertainty about those adjustments, and assess the effect across plausible values. Simply assigning a generic quality score or downweighting a study's sampling variance does not by itself remove its bias.

A network meta-analysis can offer three distinct benefits, assuming a connected treatment network and credible transitivity in network meta-analysis.

These are potential benefits, not guarantees: heterogeneous effect modifiers, inconsistent evidence, disconnected networks or imprecise rankings can defeat them.

Separating pupils by attainment is not, by itself, a reliable solution to individual differences. Benefits depend on whether the arrangement changes the instruction pupils receive, while costs can arise from restricted opportunities, inaccurate placement and persistent labels. Evidence distinguishes whole-curriculum separation from subject-specific and flexible grouping; it does not justify treating all forms as one intervention. Current achievement should also not be mistaken for a fixed measure of learning potential.

Streaming by attainment assigns a pupil to a group across much of the curriculum. Subject setting regroups pupils for a particular subject, allowing different placements in, for example, reading and mathematics. Within-class grouping creates smaller instructional groups inside a shared classroom and can be revised by task. These arrangements differ in exposure to peers, teachers, curriculum and opportunities to move. A finding about flexible mathematics groups therefore cannot automatically defend an enduring all-subject stream.

The favorable hypothesis is instructional fit. A narrower range of prior knowledge may let a teacher select examples, pace and support more accurately, while advanced pupils avoid unnecessary repetition. But the group label must actually change the lesson in a useful way. Separating pupils and then delivering the same unsuitable instruction supplies little reason to expect benefit. Nor does an appropriate lesson logically require fixed separation: formative assessment and flexible task allocation can address differences within a mixed classroom.

Robert E. Slavin's best-evidence synthesis distinguished assignment to self-contained ability classes, which lacked a general achievement advantage, from some subject regrouping and within-class mathematics arrangements with more favorable results. Its conditions emphasized reassessment and adapting the level and pace of teaching. The historical importance is the distinction between organization and instruction, not a timeless verdict that any arrangement called “grouping” works. A synthesis also inherits variation in the quality of its constituent comparisons.^[ref]

Saiying Steenbergen-Hu and colleagues' later second-order meta-analysis likewise separated forms of grouping. Across thirteen meta-analyses, between-class grouping showed little overall achievement benefit, while within-class grouping, cross-grade subject grouping and specialized arrangements had more positive average results. Acceleration was analyzed separately and should not be collapsed into ordinary attainment sorting. The evidence spans school ages and implementations, so its averages are not estimates of one particular primary-school policy. Reviews that share primary studies are also not independent replications to be counted as separate votes.^[ref]

These conclusions do not establish that tracking must harm low-attaining pupils in every setting. Esther Duflo and colleagues conducted a randomized tracking experiment in 121 Kenyan primary schools. In that context, tracking benefited lower-achieving pupils through better instructional targeting, despite the potential advantages of exposure to higher-achieving peers. The experiment provides a causal counterexample to a universal claim that mixed-attainment classes are always best. Its teacher incentives, curriculum and wider school conditions also limit transfer to a different education system.^[ref]

The Kenyan result helps distinguish two effects often conflated in discussion. Peer effects concern how classmates' skills or behavior influence learning; instructional targeting concerns what a teacher teaches to whom. They can act in opposite directions. A lower-attaining group might lose some peer opportunities yet gain a lesson that it can use. A different system could concentrate less experienced teachers or narrow tasks in the same group, producing a different outcome. The causal question is therefore the effect of the whole implemented arrangement, not a social label in isolation.

Placement creates further challenges. An assessment contains measurement error and reflects prior opportunity, language and familiarity with the task. Selecting pupils at one time point can therefore turn temporary performance differences into apparently stable categories. Even frequent movement on paper is insufficient if movement rarely occurs in practice. Researchers need placement histories and the material actually taught, not only the school's description of its policy. Comparing final scores of high and low groups is especially uninformative because initial attainment helped define those groups.

Teacher expectations and children's interpretations of their placement are plausible additional pathways. A label can affect the challenge offered or the opportunities to demonstrate improvement; a child may interpret it as a statement of fixed worth. These are hypotheses requiring direct measurement rather than automatic explanations for every group difference. Self-concept, participation and belonging matter even when an average test score is unchanged. Conversely, a pupil may value appropriately demanding peers and tasks, so increased challenge should not be equated with social harm merely because it involves grouping.

A useful evaluation would randomize schools or classes to well-specified arrangements, measure baseline attainment before allocation and monitor curriculum, staffing and movement. It should retain an intention-to-treat comparison rather than excluding pupils whose placements changed. Multilevel analysis or appropriate uncertainty estimates are required when pupils share teachers or classrooms. Prespecified subgroup analyses can ask whether effects differ by starting attainment, while distributional outcomes show whether an average gain masks widening gaps. Longer follow-up is important because early curricular restriction may have consequences beyond an immediate assessment.

The relevant comparison should be equally credible. A well-resourced setting program compared with an under-supported mixed class does not identify separation alone as the active ingredient. Equally, a mixed class receiving no help to differentiate instruction is not a decisive test of responsive mixed teaching. Comparing arrangements under explicit resource and implementation conditions makes the evidence more useful for practice. It also permits testing whether flexibility and good assessment capture the benefit without committing pupils to permanent categories.

For primary education, where performance profiles and opportunities can change quickly, the most defensible principle is responsiveness. Grouping may serve a specific instructional purpose when it is revisable and tied to what the pupil needs to learn next. Its effects should be monitored rather than justified by a presumed innate hierarchy. Maintaining ambitious curriculum access and checking actual movement are safeguards whose value should be assessed alongside attainment, not assumed to follow from a policy name.

The research supports evaluating instructional fit, opportunity and flexibility rather than endorsing streaming or setting as default answers to individual differences. Broad between-class sorting has weak average support, while particular subject and within-class arrangements can help under specified conditions. A successful contextual experiment does not universalize the policy, and an overall null average does not make the content and quality of teaching irrelevant.

The evidence supports some prospective associations between violent media exposure and later aggression, but it does not establish a large, general causal effect on serious violence outside the laboratory. Aggression is behavior intended to harm; violence is its severe physical subset. Angry thoughts, physiological activation and an aggression-task score are not interchangeable with either. The relevant claim requires an exposure contrast, an outcome that captures harmful behavior in everyday life, and a design that distinguishes influence from selection.

Laboratory experiments can randomize immediate exposure, but a brief game followed by a noise-blast choice mainly tests a short-term response in an artificial setting. Competition, frustration, difficulty and expectations can differ between games as well as violent content. A statistically detectable laboratory effect therefore needs both construct validity and ecological validity before it supports a claim about everyday aggression. A plausible social learning mechanism supplies a hypothesis about acquiring aggressive responses; it does not by itself demonstrate that media caused a particular real-world outcome.

An important source of evidence is L. Rowell Huesmann and colleagues' follow-up from childhood television viewing to young adulthood. The study related violent television exposure at ages six to ten to later aggression, using follow-up interviews and archival information. Associations persisted after adjustment for measured childhood and family characteristics. Unlike a single laboratory task, the design addressed a long interval and outcomes beyond the immediate viewing session. It also tested exposure before the later outcome, making simple simultaneity an inadequate explanation.^[ref]

Temporal order is necessary but insufficient for causal inference. Earlier aggression may both encourage violent-media selection and persist into adulthood. Family conflict, peer environments or poorly measured dispositions may influence both variables. Adjustment for baseline aggression helps, but imperfect measurement leaves residual confounding, and including a variable in a model does not ensure that its causal role was correctly represented. Attrition can further change the composition of the observed follow-up sample. These limitations qualify the causal interpretation without making the association irrelevant.

Andrew K. Przybylski and colleagues provide a useful contrasting design: a registered report studied 1,004 adolescent–carer pairs, combining adolescent gaming information and independently rated violent content with carers' reports of aggressive behavior. The confirmatory analysis did not support the predicted positive relationship. Separating the exposure and outcome reporters reduced one source of common-method bias, while preregistration reduced flexibility in choosing an attractive analysis. The design was a cross-sectional study, however, so it did not estimate a randomized causal effect or settle effects of earlier exposure.^[ref]

A null finding constrains a claim under the measurements and precision of that study. It does not prove that every form of violent media has exactly zero effect on every child. Conversely, explaining away every null result after observing it makes a general hypothesis difficult to test. The useful question is whether a prespecified exposure–outcome prediction survives an adequately sensitive test, and whether any estimated effect is large enough to matter outside the measurement scale.

Longer experiments strengthen a different part of the argument. Simone Kühn and colleagues randomized adults with little recent gaming to a violent game, a nonviolent game or no gaming for two months, with later testing. They did not find the predicted increase in aggression across their outcome battery. Exposure occurred beyond a brief laboratory session, which improves the relevance of the manipulation. Yet many endpoints were questionnaires or experimental tasks, rather than observed assaults, and the modest adult sample cannot settle small effects in children. The violent and nonviolent games also differed in more than violent content.^[ref]

The distinction between naturalistic exposure and naturalistic outcome is crucial. A home-based intervention can establish a change in a laboratory score without demonstrating everyday harm; a real-world outcome can be valuable even when its exposure is assessed in an observational study. No single study here simultaneously supplies perfectly isolated content, prolonged exposure, representative participants and high-quality measurement of rare violence. Triangulation should ask whether the different weaknesses plausibly explain a pattern, rather than counting positive and negative papers as votes.

Meta-analysis helps estimate that pattern, but pooling does not repair a shared design limitation. Anna T. Prescott and colleagues combined 24 prospective studies with over 17,000 participants. They found a small positive association between violent-game exposure and later physical aggression after baseline adjustment; estimates decreased when available additional covariates were included. Aaron Drummond and colleagues' later meta-analysis emphasized weak associations and their sensitivity to study quality. The disagreement makes inclusion rules, measurement and analytic decisions central to interpretation.^[ref][ref]

Even a small, reproducible association would not automatically identify a small causal effect: a consistent confound can also replicate. On the other hand, limited statistical power means an individual nonsignificant experiment need not contradict a small association. Effect sizes and uncertainty should therefore be compared on compatible outcome scales. Publication bias and selective analysis can favor alarming positive findings, while insensitive measures can hide genuine effects; both possibilities require evidence rather than assertion. The available studies also concern particular media, populations and time intervals, so their conclusions should not be extended automatically to all violent content.

The strongest next tests would preregister longitudinal exposure contrasts, measure baseline behavior carefully, obtain outcomes from independent sources and retain participants across follow-up. Where ethical and practical, randomization to matched content would separate violent imagery from competition and frustration. Everyday aggression and severe violence would be analyzed separately. By the examination date, large causal claims about real-world violence exceeded the evidence; small or context-dependent effects on aggression remained possible and required better identification. This conclusion takes the positive prospective findings seriously while keeping their causal and behavioral scope explicit.

The most useful change is often to make a former outgroup part of an inclusive “we” while preserving a secure subgroup identity; no category arrangement is best independently of context and outcome. Prejudice is an evaluative attitude toward people because of group membership, stereotypes concern attributed group characteristics, and discrimination concerns treatment. A reduction in liking differences between small laboratory groups is therefore evidence about one component of prejudice, not automatically about durable equality in behavior.

Social categorization establishes who counts as an ingroup or outgroup. If favorable treatment follows the ingroup boundary, changing that boundary can extend favorable treatment to people previously excluded. But categorization also supports recognition, continuity and shared experience. Erasing a socially meaningful identity may threaten the very people an intervention is intended to include. The best test therefore asks both whether the new representation improves attitudes and whether it preserves enough identity for its benefits to generalize beyond the immediate encounter.

Decategorization encourages seeing an interaction partner as a distinctive person rather than merely an outgroup representative. It can weaken reliance on a stereotype and make personal information available. Its weakness is transfer: a liked individual may be treated as an exception while prejudice toward the broader outgroup remains unchanged. It is therefore most convincing when participants later respond more fairly to unfamiliar outgroup members, not merely when they like the person they just met. Individuation is a useful part of contact, but it need not supply a new inclusive group boundary.

Recategorization instead makes a common superordinate category salient. In the common ingroup identity model, the former outgroup is represented as part of a larger ingroup. Samuel L. Gaertner and colleagues experimentally compared ways of representing interacting participants, including one-group, two-group and individualized arrangements. The results supported a benefit of an inclusive group representation. This is a causal test of a manipulated social arrangement, although the arrangement may change cooperation and expectations together with perceived membership.^[ref]

The distinction between labels and social structure matters. Simply giving participants a common name need not change their expectations about how others will treat them. Shared tasks, balanced interaction and a credible common goal can make the inclusive identity psychologically meaningful. Conversely, if the “common” category is implicitly defined by the dominant subgroup's norms, minorities may experience it as an instruction to assimilate. A successful intervention must therefore assess whose identity is being recognized, rather than taking average category salience as a sufficient explanation.

John F. Dovidio and colleagues extended the experimental evidence beyond evaluations. After forming two three-person groups, they manipulated an inclusive versus separated representation and measured evaluations, self-disclosure and helping. The inclusive arrangement produced more favorable intergroup responses, with perceived group unity statistically accounting for part of the pattern. Helping is a stronger behavioral extension than an attitude rating alone. However, statistical mediation does not itself prove that perceived unity was the uniquely causal mediator: the manipulation could change additional processes alongside it.^[ref]

Dual identity retains the subgroups within the inclusive category. Participants can represent themselves as members of distinct departments within one university, for example. This can combine a shared membership with recognition of meaningful difference. It may also preserve the connection between a positive encounter and the original outgroup, helping the benefit transfer beyond a single partner. The proposal is conditional: constantly emphasizing a hostile division without a credible common category could reinforce the boundary rather than soften it.

Matthew J. Hornsey and colleagues tested subgroup and superordinate-category salience in two university-based experiments, with 178 and 135 participants. Bias was lowest when both identities were salient and highest when the superordinate category alone was emphasized. The design is a useful challenge to an unconditional recommendation to erase subgroups. Its theoretical implication is that an inclusive representation can work better when it accommodates distinctiveness. The precise ordering still needs to be evaluated in the population and relationships being studied.^[ref]

Crossed categorization offers another possibility: someone may be an outgroup member on one dimension but an ingroup member on another. This weakens a perfectly aligned “us versus them” division when the shared dimension is valued. It does not guarantee inclusion, because people can prioritize one division or reserve the strongest exclusion for those who share neither membership. Thus the number of visible categories is less important than how they organize expected similarity, belonging and cooperation. Which categorization works best must be an empirical question about those relationships.

Intergroup contact provides a wider evidential context. Thomas F. Pettigrew and colleagues' meta-analysis of 515 studies and 713 independent samples found that contact generally related to lower prejudice, with supportive conditions such as equal status and cooperation enhancing the relationship. This broadens the evidence beyond a single laboratory manipulation. It does not rank categorization strategies directly, and much contact is assessed in observational studies: less prejudiced people may seek it out. Contact can supply an opportunity for category change without establishing that category change alone produced every improvement.^[ref]

A strong comparison would assign otherwise similar cooperative encounters to decategorization, common identity and dual identity conditions. It would measure perceived inclusion and identity threat, then test attitudes and consequential treatment of unfamiliar group members after a delay. Separate subgroup analyses would reveal whether an apparent average benefit concealed a cost to the less powerful subgroup. These measurements make “works best” refer to generalization, persistence and behavior rather than to an immediate favorable rating.

An inclusive identity that preserves legitimate subgroup distinctiveness is a well-supported candidate, especially where identity threat would undermine simple assimilation. Decategorization and crossed categorization remain useful under appropriate conditions. The evidence favors changing how membership supports inclusion, with cooperative and equitable interaction, rather than expecting a verbal relabeling to remove prejudice on its own.

Publication bias arises when the availability of studies depends on the results, such as their significance, magnitude or direction. A meta-analysis of the available studies can then differ systematically from one including all eligible evidence. Funnel plot asymmetry can motivate investigation but does not establish this mechanism; heterogeneity and other small-study effects can also cause asymmetry.

A selection model combines a distribution for all study results with a probability $\pi (y)$ that a result becomes available. The observed distribution is reweighted by this probability and renormalized. Assumed or estimated selection mechanisms permit sensitivity analysis of a meta-analysis, but unavailable results generally prevent a fully assumption-free correction.

Trim and fill estimates missing studies from funnel plot asymmetry by trimming extreme studies to locate a centre and filling in counterparts on the less represented side. The adjusted meta-analysis includes these imputed estimates. Its interpretation depends on a symmetry model for missing evidence; it is not a guarantee that genuine publication bias has been removed.