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Variation in the underlying study effects, additional to sampling error. The usual normal random-effects meta-analysis models it by a between-study variance ${\tau }^2$. It can reflect effect modification, design differences or within-study bias; it is not automatically a biological treatment difference.

A weight $w_i=1/v_i$ gives more weight to a more precise estimate. In random-effects meta-analysis the variance of the corresponding marginal distribution is $v_i+{\tau }^2$, giving weight $(v_i+{\tau }^2{)}^{-1}$. A percentage weight divides the individual weight by the sum of all weights.

A meta-analysis combines statistical evidence from several studies addressing a common estimand. It may assume a shared effect or use a random-effects meta-analysis to represent between-study variation. Inverse-variance weighted means combine independent effect estimates when their variances are known or estimated; differences in study validity and effect modifiers require substantive assessment, not just weighting.

Meta-regression relates study effect estimates to study-level explanatory variables. A common random-effects meta-analysis extension is $y_i=\alpha +\beta x_i+u_i+{\epsilon }_i$, where $\mathrm{Var}(u_i)={\tau }^2$ and $\mathrm{Var}({\epsilon }_i)=v_i$. For log odds ratios, $e^{\beta }$ is a ratio of underlying odds ratios per unit of $x$. Few studies, correlated design changes and exploratory variable selection limit interpretation; a study-level association does not identify an individual-level causal effect. The interpretation of study-level predictors is also discussed in the Cochrane methods handbook, section 10.11.

Partial pooling estimates related local parameters jointly through shared hyperparameters. Each local Bayesian posterior balances its own likelihood function against a group prior distribution, with stronger shrinkage when its data are weak or the group variation is small. It lies between forcing all local parameters to be equal and estimating them independently. Random-effects meta-analysis is an important application.

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.

A fixed-effect meta-analysis models the studies as estimating a common underlying treatment effect. In a generic inverse-variance version, independent log odds ratios $y_i$ have approximate distributions $N(\delta ,v_i)$ and are pooled with weights $1/v_i$. The supplied forest plot instead has the Mantel–Haenszel pooled odds ratio weights: for event/nonevent cells $a_i,b_i,c_i,d_i$ and total $n_i$, the normalized weights are proportional to $b_i{c}_i/n_i$. They reproduce the printed percentages and yield a pooled odds ratio about $2.338$. This is still a common-effect analysis; the two weighting methods should not be silently identified.

A random-effects meta-analysis allows different true effects: $y_i\mid {\delta }_i\sim N({\delta }_i,v_i)$ with ${\delta }_i\sim N(\mu ,{\tau }^2)$. The between-study heterogeneity variance ${\tau }^2$ adds to sampling variance, giving marginal variance $v_i+{\tau }^2$. Its pooled estimate targets the mean of the study-effect distribution rather than one identical effect. Uncertainty about heterogeneity must also be considered.

A fixed-effect meta-analysis assigns inverse-variance weights. Using the unrounded within-study variance from part (b), this trial has $w=8$, so its percentage weight isUsing the printed rounded standard error of $0.35$ instead gives approximately $2.04\%$; the raw cell calculation yields the more precise answer.

For a random-effects meta-analysis, the corresponding weight and percentage weight areWith ${\hat{\tau }}^2=0.05$, its unnormalised weight is $40/7\approx 5.714$. The supplied sums of fixed-effect weights do not determine the denominator of the random-effects percentage; the individual $v_i$ are needed. Positive heterogeneity makes the weight distribution more even. Percentage weight measures the trial's contribution to a pooled mean with fixed weights; total influence can also involve re-estimation of heterogeneity.

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 random-effects meta-analysis allows differences in true treatment effects across countries and eligibility criteria. For trial $i=1,\dots ,6$, let $y_i$ be its estimated log odds ratio and $v_i$ its estimated within-trial variance. A usual approximate statistical model isindependently across trials, with $b_i$ independent of sampling errors. Here $\mu$ is the mean true log odds ratio in the population of comparable trials, and ${\tau }^2\ge 0$ is between-trial heterogeneity, not additional sampling error. Therefore $y_i\sim N(\mu ,v_i+{\tau }^2)$, and for a fitted heterogeneity value,One can estimate ${\tau }^2$ by restricted maximum likelihood or another justified method; $({\sum }_i{w}_i{)}^{-1}$ is a plug-in conditional variance and does not fully account for estimating heterogeneity. With only six studies that uncertainty matters. Different eligibility rules motivate this random effect but do not by themselves establish exchangeability or remove bias; known effect modifiers may warrant stratification or regression.

Use leave-one-study-out influence analysis: fit all six trials, then omit Cohen 1989 and refit both $\mu$ and ${\tau }^2$. Report $\hat{\mu }-{\hat{\mu }}_{(-C)}$, the corresponding change in the odds ratio, and changes in the confidence interval and heterogeneity. As a diagnostic with heterogeneity held fixed, writing $W={\sum }_i{w}_i$ givesThe fitted Cohen weight would be $(0.15+{\hat{\tau }}^2{)}^{-1}$ and $y_C=-1.95$. A precise but discordant trial can have large influence; refitting assesses additional influence through heterogeneity. The other five trials' data are absent, so a numerical six-trial influence assessment is not identifiable from the displayed table.