Funnel plot 2026-10-07
A funnel plot displays study effect estimates against a measure of their precision, often standard error increasing down the vertical axis. Under a common-effect model, imprecise estimates spread more widely around the effect. Asymmetry is evidence of a small-study effect and can be consistent with publication bias, but it has other possible explanations.
Odds under at-least-one-positive selection 2026-10-14
For studies conditionally independent given the truth of one relationship, the event that at least one is positive has probability under the alternative and under the null. Its Bayes factor therefore gives the displayed posterior odds. For interior error probabilities these tend back to the prior odds . If power exceeds size, the Bayes factor decreases to one: the quotient of geometric sums is a weighted average of decreasing powers .
This result concerns the coarsened selection event. Full observed results instead multiply their individual Bayes factors, and concordant evidence can accumulate without this bound. It is a useful example of information discarded by publication bias.
Monoamine signalling contributes to mood regulation and to the actions of several antidepressants, but a universal “low transmitter causes depression” account is not established. Three propositions must be separated: a drug changes a molecular target; that change helps produce improvement; and the untreated disorder was caused by an opposite abnormality. Evidence for one proposition does not logically establish the next.
The monoamine hypothesis of depression developed from pharmacology. Monoamine oxidase inhibition reduces transmitter metabolism, while some tricyclic antidepressants inhibit transmitter reuptake; SSRI principally inhibit serotonin reuptake. Norepinephrine, serotonin and dopamine are distinct monoamines, acting through different receptors and pathways. The historical catecholamine proposal emphasized norepinephrine and already acknowledged the limitations of extrapolating from drug effects to disease mechanisms. Treating every low affective state as depletion of a single interchangeable brain substance is a substantially stronger claim.[ref]
The catecholamine hypothesis of affective disorders: a review of supporting evidence by Joseph J. Schildkraut. 1965 abstract and pp. 509–522: proposed catecholamine account and explicit limits on pharmacological extrapolation
Drug efficacy supplies evidence that manipulating these systems can matter. A 2018 network meta-analysis synthesized 522 double-blind trials in adults with major depressive disorder and found each included antidepressant more efficacious than placebo on its response outcome. This is evidence synthesis, not a direct assay of patients' transmitter levels. Average effects, trial selection, publication bias, blinding and symptom-scale outcomes limit interpretation, and not every patient benefits. Even a perfectly demonstrated effect would show that an intervention can change a pathological state, not that it reverses its original cause. A downstream compensatory mechanism can be therapeutically useful without being the initiating lesion.[ref]
Comparative efficacy and acceptability of 21 antidepressant drugs for the acute treatment of adults with major depressive disorder by Andrea Cipriani and others. Methods, Findings and Discussion: acute adult trials, response outcome and limitations
Measuring the proposed deficiency is itself difficult. Peripheral serotonin is not a direct measurement of release at a particular central synapse. Metabolites combine synthesis, release, reuptake and degradation; receptor or transporter imaging is not simply a concentration gauge. A difference observed after illness onset might be causal, compensatory, treatment-related or associated with physiological stress. Establishing a general deficiency would require convergent measures in appropriate untreated populations, temporal precedence and a relationship to well-defined symptoms, not merely one group-average biomarker.
Precursor depletion supplies a more informative intervention. In a double-blind crossover study, patients in antidepressant-induced remission underwent acute tryptophan depletion and a control condition. Fourteen of 21 experienced a transient depressive relapse after depletion, whereas control testing did not produce significant behavioural effects. This supports dependence of some maintained remissions on serotonin precursor availability. It does not show that all untreated depressed patients began with low serotonin, that depletion is sufficient to generate the full syndrome in everyone, or that norepinephrine and dopamine are irrelevant. The selected, previously treated sample is central to the causal question actually tested.[ref]
Serotonin function and the mechanism of antidepressant action by Pedro L. Delgado and others. Abstract and pp. 411–418: remitted sample, crossover control and 14/21 transient relapses
Time course also challenges a simple replenishment story. Initial transporter inhibition can occur before substantial clinical improvement. That discrepancy motivates slower receptor, circuit, learning and plasticity changes; it does not imply that early drug effects are absent. In a randomized placebo-controlled experiment, an acute dose of a norepinephrine reuptake inhibitor changed positive emotional processing in depressed participants before subjective mood or anxiety changed. Facial-expression judgments and emotionally valenced categorization and recall supplied behavioural readouts. These observations support an affective processing bias account: altered experience processing could accumulate into mood change. They do not establish that the measured early shift mediates every later clinical response.[ref]
Effect of acute antidepressant administration on negative affective bias in depressed patients by Catherine J. Harmer and others. Abstract; Methods and Results, pp. 1178–1184: randomized emotional-processing battery before mood change
Plasticity offers another candidate bridge between early pharmacology and delayed behaviour. In mice, preventing antidepressant-associated adult hippocampal neurogenesis blocked behavioural effects in particular experimental assays. The evidence included genetic and localized irradiation approaches. It supplies a mechanistic dependency within that model, rather than merely a correlation between a drug and cell proliferation. However, the assays are not human major depressive disorder, the interventions can have additional effects, and necessity for one behavioural endpoint does not establish either sufficiency or a universal human mechanism.[ref]
Requirement of hippocampal neurogenesis for the behavioral effects of antidepressants by Luca Santarelli and others. Abstract and pp. 805–809: interference with neurogenesis and model-specific behavioural effects
These alternatives refine rather than simply discard monoaminergic pharmacology. Serotonin or norepinephrine could regulate plasticity and learning within distributed neural circuits; baseline concentrations need not be uniformly low. Receptor sensitivity, pathway-specific activity and environmental experience could determine the effect of an intervention. Conversely, observing altered dopamine-related motivation would not prove that all anhedonia, cognitive slowing and sadness have one cause. Major depressive disorder groups multiple symptom patterns, so a mechanism associated with one dimension can be diluted or misleading when treated as a universal disease explanation.
The strongest conclusion available at the examination date is therefore conditional. Particular monoamine manipulations can alter affective processing and symptoms, and some treatment responses depend on monoaminergic function. The evidence does not identify a single brain-wide deficit that is necessary and sufficient for human depression. A useful successor account specifies transmitter, receptor, circuit, time scale and symptom, and tests how biological changes interact with learning and environment. This evaluation concerns explanatory evidence, not a recommendation to start, stop or choose a medication.
Past exam of the mathematics course of the University of Cambridge 2008 iii Paper 44 1 i Solution 2026-10-14
Consistent independent replications should strengthen confidence; contradictory results can weaken it. The change depends on the actual evidence. If of studies are positive and all labels are available, the posterior odds areFor the normal model, retaining the full independent statistics instead givesEach study multiplies the existing odds by its own Bayes factor. Reading a complete synthesis is therefore different from learning only that somebody obtained a positive result. Publication bias, dependence between studies and changes in study design must be accounted for before applying the independent-product formula.
Past exam of the mathematics course of the University of Cambridge 2013 iii Paper 32 1 c Solution Created 2026-10-03 Updated 2026-10-07
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.
Past exam of the mathematics course of the University of Cambridge 2013 iii Paper 32 1 d Solution Created 2026-10-03 Updated 2026-10-14
A funnel plot places each estimated log risk ratio horizontally and its standard error vertically, with the most precise studies at the top. Under a common-effect model without selective availability, less precise estimates should spread approximately symmetrically around the underlying effect. The plotted dashed limits are the pooled estimate plus or minus twice the standard error; they illustrate the expected sampling spread, not a test of publication bias by themselves.
Funnel plot of the ten transfusion trial estimates, with inverse-variance pooled effect and approximate sampling limits
. Details. The least precise estimates are mostly far to the left, whereas the most precise estimates are close to zero. The reported regression slope means that increasing the standard error by one unit is associated with a decrease of about in the estimated log risk ratio. Its 95% confidence interval excludes zero, and gives evidence against a zero slope under that regression model. This is evidence of a small-study effect: less precise trials report stronger apparent benefit.
There is evidence consistent with publication bias, but asymmetry does not identify its cause. Selective availability of favourable small studies is a plausible explanation. Genuine differences in patient populations, trial quality, interventions or effect modification could also generate the pattern, and there are only ten trials. The given outcome-on-error regression should be interpreted as specified; it is not automatically the original standardized-effect-on-precision form of an Egger test. The plot and slope justify investigating missing studies and sensitivity to selection, rather than concluding that publication bias has been proved.
Past exam of the mathematics course of the University of Cambridge 2013 iii Paper 32 1 e Solution Created 2026-10-03 Updated 2026-10-07
One method is trim and fill. Estimate the direction and extent of funnel asymmetry, temporarily trim the extreme studies on the overrepresented side to estimate a centre, and fill in mirror-image studies on the underrepresented side. Recompute the pooled effect using the observed and imputed studies. This estimates what the summary might be under a symmetry-based missing-study model. It can move an exaggerated effect towards the null, but genuine heterogeneity can violate its symmetry assumptions.
A second method is a selection model for publication bias. Specify how the probability of a result being available depends on quantities such as its value, direction or precision, and combine that mechanism with a model for the underlying study effects. If a study estimate has density and availability probability , its observed density is proportional to , with a normalizing factor accounting for unobserved results. Fit the model, or vary the selection probabilities over plausible scenarios, to obtain selection-adjusted effects. Such models make assumptions about evidence that is missing, so their results are particularly useful as sensitivity analyses. Neither method removes publication bias without assumptions about the missing studies.
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]
Longitudinal relations between children's exposure to TV violence and their aggressive and violent behavior in young adulthood: 1977–1992 by L. Rowell Huesmann and others. Childhood measures, adult interview/archival outcomes and adjusted longitudinal models
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.
Competing causal explanations for a prospective media–aggression association; arrows are hypotheses rather than estimated effects
. Details. 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]
Violent video game engagement is not associated with adolescents' aggressive behaviour: evidence from a registered report by Andrew K. Przybylski and others. Registered hypotheses, exposure classification and carer-reported aggression analyses
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]
Does playing violent video games cause aggression? A longitudinal intervention study by Simone Kühn and others. Randomization, two-month intervention, outcome battery and follow-up
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]
Metaanalysis of the relationship between violent video game play and physical aggression over time by Anna T. Prescott and others. Abstract and adjusted-effect analyses; prospective physical aggression
[ref]Do longitudinal studies support long-term relationships between aggressive game play and youth aggressive behaviour? A meta-analytic examination by Aaron Drummond and others. Study-quality analyses and discussion of the longitudinal association
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.
Trim and fill 2026-10-07
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.

