Past exam of the mathematics course of the University of Cambridge / 2009 / iii / Paper 41 / 1

Use separate randomization lists for women with and without a self-reported history of depression. Within each stratum, the central service could assign intervention and control in a $1:1$ ratio using randomly permuted blocks, preferably with concealed and varying block sizes. This is stratified randomization; the internet service can retain allocation concealment because the recruiting staff do not know the next assignment.

History is plausibly prognostic for the outcome. Keeping its distribution similar between arms reduces the risk of a chance imbalance in that important baseline factor and can improve precision. It also allows a comparison within each history stratum. Stratification does not guarantee balance of every other covariate, and staff must not be allowed to choose assignments. The regression model can retain history as a baseline covariate, respecting the design.

Specify the expected control-group event probability at the chosen follow-up time, the intervention probability or smallest clinically important absolute reduction to detect, the primary test's significance level and whether it is one- or two-sided, the desired statistical power, and the allocation ratio. Statistical power is the probability of rejecting the null hypothesis under that specified alternative; its complement is the Type II error probability.

For two independent binary-outcome groups, these probabilities determine the response variances needed by the sample-size calculation. Also specify how much loss to follow-up is anticipated when converting the required evaluable sample into a recruitment target. Here the design is balanced and the stated primary significance level is $0.05$. A target statistical power such as $80\%$ or $90\%$ and the anticipated event probabilities cannot be recovered from the sample size alone, so they should not be invented. The recruitment inflation allows for attrition rather than changing the target effect.

The primary outcome addresses the main prespecified question; the secondary outcomes involve several additional comparisons. Testing each at $0.05$ would increase the chance of at least one false positive across them. The smaller secondary significance level makes their individual tests more conservative, reducing multiple testing problems.

This is a design distinction between confirmatory and additional outcomes, not a claim that secondary outcomes are intrinsically less important. A level of $0.01$ per secondary test does not by itself establish a particular bound on the familywise error rate unless the whole testing plan and number of tests are specified. Likewise, having two primary measurements still needs a clear prespecified reporting and multiplicity strategy.

The research nurses should be unaware of each woman's randomized allocation. Blinded outcome assessment reduces the possibility that knowledge of receiving peer support changes how questions are asked, how answers are interpreted, or how a clinical diagnosis is recorded. It is especially useful for interview-based and partly subjective outcomes.

The mothers and volunteers would generally know whether calls took place. A mother might mention her volunteer, or a nurse might infer allocation from the conversation or consult records revealing it. This can break assessor blinding even when the allocation list is hidden. Standardized outcome interviews, separate intervention records and asking participants not to disclose allocation can help. Outcome assessment blinding is distinct from allocation concealment at recruitment, and does not prevent participants' own awareness from affecting reported symptoms.

Let $Y_i=1$ indicate a depressed outcome and $C_i=1$ indicate the control arm. A logistic regression could specifywith $x_i$ containing prespecified baseline characteristics, including the stratification factor. Fit the coefficients by maximizing the likelihood for independent Bernoulli random variables ${\prod }_i{p}_i^{Y_i}(1-p_i{)}^{1-Y_i}$. For equal covariate values the control-to-intervention odds ratio is $e^{{\beta }_C}$. Thus an estimate ${\hat{\beta }}_C=\log (2.1)$ produces the quoted adjusted ratio. An ordinary Wald confidence interval is obtained by exponentiating the endpoints of the coefficient's confidence interval.

The raw control-to-intervention odds ratio, using the actual counts, isUsing only the quoted percentages gives about $2.05$, so both versions are approximately $2.1$. The printed $14\%$ is not the usual whole-percentage rounding of $40/297\simeq 13.47\%$; using the counts avoids that small numerical inconsistency. The reversed intervention-to-control ratio is about $0.475$.

The apparent surprise is a coding issue: with depression as the adverse outcome and intervention relative to control, protection would give an odds ratio below one. A ratio above one is favourable if the comparison is control relative to intervention, as above, or if the outcome has been recoded as absence of depression and intervention is compared with control. Both comparison and outcome must be specified. The adjusted ratio need not equal the crude one, even in a randomized trial: covariate adjustment and noncollapsibility of the odds ratio can change an odds ratio. Their close numerical values here do not prove that the regression adjustment was unnecessary.

There was no clear documentation of initiation for $349-328=21$ women, givingThese women may not have received the intervention, although missing documentation is not proof that no contact occurred. Documentation of initiation also does not establish completion or full adherence.

Under intention-to-treat analysis, women retain their randomized arm regardless of actual uptake. Removing nonadherent women would condition on a post-randomization characteristic and could destroy the comparability created by randomization. The resulting estimand is the effect of offering the intervention under the trial's actual adherence pattern. Keeping nonadherent women in their arm does not itself solve missing-outcome problems: the reported 12-week denominators are smaller than the randomized totals, so the outcome analysis still needs an appropriate strategy and assumptions for losses to follow-up.

The number needed to treat is the reciprocal of the absolute reduction in the 12-week adverse-outcome risk. Using the counts rather than rounding the percentages first givesThis means about nine high-risk women would need to be offered the intervention to prevent one additional screen-defined case over that follow-up, under the trial's comparison. It is not a lifetime quantity or automatically an estimate for clinical-interview diagnoses. Calculating from the rounded difference $25\%-14\%$ gives approximately nine but need not give the same integer rounding; the exact counts explain the reported value.

For a confidence interval, first construct an interval for the difference between the two independent event proportions, allowing for binomial distribution sampling uncertainty. If both risk-reduction endpoints are positive, take their reciprocals and reverse their order to obtain an NNT interval. A bootstrap can instead resample women within their randomized controlled trial arms and transform the resulting risk-difference distribution. If the difference interval includes zero, the NNT confidence set extends through infinity and can include harm as well as benefit; it is not an ordinary bounded interval. The raw-outcome interval also relies on the missing-outcome assumptions discussed above.

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.