Paediatric study design and bias — branching viva

Opening (candidate)

I would approach these three papers by first framing the question each addresses, then naming the design that fits it, and finally assessing the risk of bias with the matched tool. For the trial I would check the randomisation process and allocation concealment before trusting the large benefit, because a big effect from a poorly concealed trial is the signature of bias. For the case-control study I would weigh the appropriateness of the design for a rare outcome against the threat of recall bias and confounding. For the meta-analysis I would read the heterogeneity and the forest plot to judge whether the pooling across age bands is defensible. [2] [5]

Branch A — Allocation concealment and the exaggerated effect

Examiner: The trial reports a large, statistically significant benefit, but the methods are vague about how participants were allocated. How does that concern you? [5]

Candidate: It concerns me greatly, because allocation concealment is the design manoeuvre most critical to a trial's validity. Concealment hides each assignment until it is irreversible, preventing staff from steering certain patients toward the arm they prefer. When it is inadequate, the comparison between groups is corrupted at enrolment, because the groups may differ in prognostic factors. The empirical evidence is that trials without adequate concealment exaggerate the treatment effect by about 30 to 40 percent. So a large benefit from a trial whose allocation is vaguely reported is likely overstated, and I would read the effect down toward the null and rate the randomisation domain of RoB 2 as high risk of bias. [5] [7]

Branch B — The case-control study and the rare outcome

Examiner: The case-control study reports that children with the rare adverse event were more often exposed to the medication. Is the design appropriate, and what is its main threat? [3]

Candidate: Yes, the design is appropriate, because a case-control study starts with the outcome and works backwards, which makes it efficient for a rare event that a prospective cohort could not capture in practical numbers. Its main threat is recall bias, because parents of affected children search harder for a cause and may remember past exposures more thoroughly than parents of controls. The defence is to collect exposure data identically in cases and controls, ideally from records made before the outcome was known, and to blind interviewers to case status. I would also check for confounding by indication, because the medication may have been given for a condition that itself caused the event. [3] [4]

Branch C — Confounding versus effect modification

Examiner: The authors adjusted for several variables and found the association persisted. A colleague says they removed a true subgroup difference. How do you distinguish confounding from effect modification? [4]

Candidate: The two are distinguished by their response to adjustment and by their meaning. Confounding is a distortion of the comparison by a third variable, and adjustment removes the distortion and moves the estimate toward the null. Effect modification is a true biological difference in the effect across subgroups, and the correct response is to report it, not remove it. If adjustment changes the estimate toward the null, that suggests confounding has been removed. If the estimate differs across strata of a variable, that suggests effect modification, and the honest report presents the subgroup estimates rather than averaging them away. Adjusting away effect modification hides a real finding and is a serious error. [4] [6]

Branch D — The meta-analysis and heterogeneity

Examiner: The meta-analysis pools trials across neonatal, infant, and adolescent age bands and reports a single summary. Is that defensible? [6]

Candidate: I would be cautious. A meta-analysis is only as trustworthy as its component studies, and pooling trials across disparate age bands risks hiding heterogeneity that means the summary describes no real patient. I would read the heterogeneity statistic and the forest plot to judge whether the trials agree, and I would check that each component was appraised for risk of bias. If the age bands show different effects, the review should report the subgroups separately rather than offer a single average. A pooled estimate cannot create external validity or internal validity its component studies never had. [6] [2]

Branch E — Applying the evidence to a child

Examiner: Your patient is a neonate, and the trial was conducted in school-age children. Can you apply the result? [1]

Candidate: I would judge applicability explicitly using PICO concordance, and I would find a mismatch in the population, because neonates and school-age children differ in dosing, metabolism, and outcomes. I would downgrade the certainty for indirectness, acknowledge that the evidence is extrapolated, and weigh the developmental heterogeneity carefully. I would involve the family in shared decision-making, choose the reversible option where possible, and arrange close monitoring. I would also seek neonatal-specific evidence or registry data before treating the result as fully applicable. [1] [7]

Close

Confirm understanding with teach-back, leave a written summary of the design, the bias assessment, and the applicability judgement, name the next contact, and document the reasoning so it survives the moment and teaches the next clinician. [2] [7]