Past exam of the mathematics course of the University of Cambridge / 2008 / iii / Paper 46 / 2

Treat the two retrieved sets of positive tests as independent binomial samples, each of size 500, and use a two-sided test at significance level $0.05$. The normal-approximation sample size for comparing two proportions, with equal numbers $n$ in each group, isFor $p_0=0.4$, $p_1=0.3$, this gives $n\simeq 355.94$, or 356 per group. Thus 500 positives in each period are sufficient for 80% power under these assumptions.

More explicitly, a pooled two-proportion test rejects whenwhere $\hat{p}$ pools the maximum-readout successes. At the proposed alternative, the difference has mean $0.10$ and standard deviation $\sqrt{0.45/500}=0.03$. The planning null critical difference is $1.96\sqrt{0.455/500}\simeq 0.0591$, giving approximate powerThis compares the readout percentage among positive tests. It assumes comparable measurement rules and independent observations; a change in that percentage alone does not identify its causal explanation or the prevalence of drug use in the full tested population.

Use equal individual allocation, a two-sided 5% test as in part (a), 80% power, complete four-week ascertainment and the supplied fatal-overdose endpoint. Then $p_0=1/200=0.005$, $p_1=0.7p_0=0.0035$, and $\bar{p}=0.00425$. Substituting into the sample size for comparing two proportions givesRounding upward for equal allocation givesThe corresponding expected endpoint counts are about 148 in the control arm and 103 in the active arm. The one-third eligibility proportion affects how many prisoners must be screened, not the number of eligible participants randomized; at full consent and eligibility ascertainment, roughly three times this randomized total would need screening. Loss to follow-up, nonadherence or a changed baseline mortality risk would require a separate design adjustment.

The wording needs an endpoint qualification. The supplied risk is death from overdose, and the proposed effect concerns preventing those deaths. It does not give the incidence of all overdoses. Thus the calculation above sizes fatal overdoses, the intended endpoint supported by the data. For a literal 30% reduction in all overdoses, the unknown baseline incidence $q$ must replace $0.005$ in the formula, with $p_1=0.7q$. This is the endpoint-specific rare-event sample size issue: the same fatal risk can coexist with many nonfatal rates. For example $q=0.005$ gives about 29525 per arm, whereas $q=0.05$ gives about 2838; knowing only the fatal rate cannot determine that latter sample size.

Use individual stratified randomization within each joint combination of prison and the three prespecified addiction-management categories. Within every joint stratum, use permuted-block randomization with equal numbers of active and control assignments in each completed block. This directly balances allocations within prison and within management category, rather than hoping that simple independent allocation will achieve both.

Run the allocation sequentially, since the availability and frequency of management categories change during recruitment. Completed blocks balance contemporaneously, so the expanding category is not assigned predominantly to one trial arm. Use varying block sizes and centrally protected allocation concealment to prevent prediction of future assignments. Incomplete final blocks allow a small residual imbalance, and an odd stratum total cannot be split exactly equally. If many joint strata are very sparse, a prespecified randomized minimization in clinical trials scheme can instead target the prison and management margins, retaining a random component. The analysis should account for the important design strata.

An ethical objection concerns the proposed saving of control-prison staff costs: the trial is explicitly based on individual informed consent, and institutional allocation does not justify omitting control participants' information, consent or appropriate outcome follow-up. These responsibilities remain in both arms. A cluster-randomized trial can sometimes be ethically defensible, but changing the randomized unit alone does not make those participant protections unnecessary.

The statistical objection is loss of independent information and potential prison-level imbalance. Outcomes within a prison may share baseline risks, management practices and release conditions, yielding positive intraclass correlation. For equal cluster size $m$, the usual exchangeable approximation gives design effect $1+(m-1)\rho$, so the individual-randomization calculation understates the sample required when $\rho >0$. There are also fewer independent randomized units, and prison-specific adoption of management practices can be unbalanced across arms. Thus randomizing prisons generally loses precision for this individually deliverable intervention, unless compensating design features and additional clusters are supplied.