Past exam of the mathematics course of the University of Cambridge / 2004 / iii / Paper 38 / 4

Let $n$ be the number allocated to each arm and test equality of the two reconviction probabilities, with a specified target difference as the alternative. For equal independent binomial arms, put $\bar{p}=(p_A+p_B)/2$, $\Delta =p_A-p_B>0$, $v_0=2\bar{p}(1-\bar{p})$ and $v_1=p_A(1-p_A)+p_B(1-p_B)$. Under the null the rejection boundary for ${\hat{p}}_A-{\hat{p}}_B$ is approximately $z_{\ast }\sqrt{v_0/n}$; under the planning alternative its mean is $\Delta$ and variance is $v_1/n$. statistical power 0.8 is obtained approximately by requiringThus the sample size for comparing two proportions iswhere $z_q={\Phi }^{-1}(q)$, $z_{\ast }=z_{1-\alpha /2}$ for a two-sided test, or $z_{1-\alpha }$ for a prespecified one-sided superiority test. With $p_A=2/3$ and $p_B=1/3$, this simplifies toFor illustration only, at $\alpha =0.05$ this gives 35 per arm, 70 total, for a two-sided test, or 27 per arm, 54 total, for a one-sided test. No unique numerical count is specified until alpha and sidedness are fixed. These are normal planning approximations; an exact requirement can be checked by summing the probabilities, from the two independent binomial distributions, of all tables in an exact test's rejection region and increasing $n$ until statistical power is at least 0.8.

This calculation detects a treatment difference when the effect equals the proposed target. It does not promise 80% statistical power to establish that the reduction is at least that target via a confidence bound when the true effect lies exactly at the target boundary. Such a different testing objective needs a separately specified null and planning alternative. Complete follow-up and ascertainment by intention-to-treat analysis are also required.

Now $p_A=2/3$, $p_B=1/2$, so $\bar{p}=7/12$, $\Delta =1/6$, $v_0=35/72$ and $v_1=17/36$. The same sample size calculation givesAt $\alpha =0.05$, the illustrative two-sided total is $2\times 137=274$; the one-sided total is $2\times 108=216$. The smaller difference needs roughly four times the size: its squared magnitude is a quarter of the previous one, while the variance factors change comparatively little.

The first 12 weeks are in custody and carry no stated overdose deaths. Thus the 26-week sentence-based window includes 14 weeks after release: the first two weeks followed by the next twelve. Interpreting the later probability conditionally on surviving the earlier interval givesHenceIf the two quoted frequencies instead use the same original cohort as their denominator, add the two marginal probabilities to get exactly 90 expected deaths. The conditional-survival calculation makes the denominator interpretation explicit; both conventions agree at the rounded precision of the quoted rates.

There is a time-window discrepancy in the printed request: the probabilities supplied concern 26 weeks after sentence, whereas this part asks about 26 weeks after release. The prison data specify only the first 14 post-release weeks. The literal release-based comparison is not numerically identified without further follow-up risks and a common time origin for both arms.

For the intended common 26-week sentence-based endpoint, plan specifically for a 12% relative reduction from $p_B=0.01$. Then $p_A=0.88p_B=0.0088$, $\Delta =0.0012$ and $\bar{p}=0.0094$. At 50% statistical power, $z_{0.5}=0$, so the rare-event collaboration size at half power isEach system contributes 10,000 participants per arm. ThereforeAt $\alpha =0.05$, this is five systems for a two-sided test, or four systems for a prespecified one-sided test. For the two-sided calculation the required size is approximately 49,681 per arm, giving a 100,000-participant collaborative design after rounding to whole systems.

The 12% planning reduction is not the reduction implied by part (c): $0.00898$ versus $0.01$ gives 10.2%. If one instead powers that calculated effect, the corresponding formula is $m=\lceil 1.80698576z_{\ast }^2\rceil$, giving seven systems at two-sided 5%. Rounding the first mortality estimate to $0.009$ changes the latter answer to eight systems, so it should not be silently substituted into the 12% calculation. All these counts assume independent individual outcomes and the common sentence-based window; the time-origin alignment of clinical endpoints is essential.

A trial can be well powered for a common reconviction outcome and poorly powered for a small difference in rare deaths. Failure to obtain a significant mortality comparison would not show that the treatments have equal safety. Participants' overall welfare cannot be reduced to reconviction alone: a decrease in that outcome must be weighed against possible loss of life.

Ethical randomization depends on clinical equipoise about the overall benefit-risk balance. Participants need voluntary informed consent that explains the uncertainty and possible mortality tradeoff; a criminal-justice setting demands particular care about coercion. The design should ascertain serious outcomes completely, use independent trial safety monitoring with prespecified stopping rules, and seek pooled safety evidence when an adequately powered mortality comparison needs collaboration. These principles are consistent with the research protections described in the Declaration of Helsinki.

A smaller efficacy trial is not automatically unethical, but deliberately avoiding adequate safety information is not a justification for it. A limited initial study needs a defensible scientific purpose, proportionate safeguards and an explicit plan for resolving serious-harm uncertainty; if evidence establishes an unfavorable net balance, continuing randomization merely to improve precision would not be justified.