Past exam of the mathematics course of the University of Cambridge / 2026 / iii / Paper 207 (Statistics in Medical Practice)

Let $Y_s(1)$ and $Y_s(0)$ be the potential outcomes for the apprenticeship proportion at school $s$ if it is or is not converted to a UTC. The policy-relevant estimand is the average causal effectover the population of schools eligible for conversion. Ideally this would be identified by a Randomized controlled trial of conversion, or by an observational design that reproduces its exchangeability.

The raw difference is generally not a causal effect. Existing UTCs may differ systematically from non-UTCs in location, admissions, pupil composition, prior attainment, resources, and the local apprenticeship market. These are possible confounders of school type and outcome. The comparison also weights the 43 UTCs and roughly 3500 controls very differently from a clearly defined target population. Without conditional exchangeability, positivity, and consistency, the difference mixes the effect of UTC status with selection bias.

Matching in causal inference can improve the comparison by balancing measured pre-treatment covariates and restricting it to non-UTCs resembling UTCs. Under conditional exchangeability given the matching variables, adequate common support, and consistent treatment definitions, it can estimate an effect for the matched population.

It does not remove bias from unmeasured or poorly measured factors such as prior apprenticeship culture, catchment-area opportunities, selection of motivated pupils, or pre-conversion trends. Matching percentages also need not balance their nonlinear effects or interactions. The proposal is better than the raw comparison, but its causal interpretation still rests on untestable assumptions.

Using 50 controls per UTC can reduce sampling variance by averaging over more control outcomes. The gain has sharply diminishing returns because controls matched to the same UTC are not 50 independent treated-control contrasts.

The disadvantage is poorer covariate balance: the 50th-nearest school will usually be much less comparable than the fifth-nearest school, increasing residual confounding and changing the target population. A caliper or variable matching ratio should therefore prevent distant matches even if many controls are available.

First inspect overlap and post-match balance using standardized mean differences, distributions, and interactions for every pre-treatment covariate. Material imbalance or UTCs outside the control support shows that the design is extrapolating and cannot justify conditional exchangeability on those variables.

Second perform a negative control outcome analysis using apprenticeship outcomes from before conversion, or another outcome that UTC status could not yet affect. A nonzero estimated effect indicates remaining selection or differential trends. Neither diagnostic proves absence of hidden confounding, so a quantitative sensitivity analysis for unmeasured confounding is also useful.

If sex predicts apprenticeship uptake, extreme UTC sex ratios create both confounding and weak overlap. Matching only the aggregate percentage of boys may leave no genuinely comparable control, and an additive distance can hide a large imbalance in this influential variable. Sex may also be an effect modifier, so the UTC effect can differ across these unusual compositions. One should enforce close sex-ratio balance and estimate sex-specific effects before standardizing them to the intended policy population.

The average treatment effect is more relevant than the average treatment effect on the treated because the contemplated policy changes treatment status for schools that are presently non-UTC, not merely the 43 schools that selected into existing UTC status. More precisely, the ideal target would be the average effect among the candidate schools the minister might convert; if that population is represented by all eligible schools, it is the ATE. An ATT from existing UTCs answers a narrower historical question and may not transport to the policy targets.

The crude incidence-rate estimator isper person-month. This treats all 3000 person-months as susceptible time and assumes infection times are observed exactly, follow-up is complete, and each first infection is detected. In practice tests occur intermittently, so infection is interval-censored; latent, brief, or asymptomatic infections may also be missed.

Let $P(t)=e^{Qt}$ be the transition probability matrix of the four-state continuous-time Markov chain, and put $N=\{S,R\}$ for a negative test and $P=\{E,I\}$ for a positive test. Starting susceptible at time zero, the likelihood contribution isEquivalently, with indicator diagonal matrices $D_N,D_P$ and the susceptible basis vector $e_S$ it isThis sums over every hidden state sequence compatible with the three test results.

For transition-intensity vector $q$ and generator $Q(q)$, the expected infectious occupancy over three months from $S$ is the Markov reward model quantityInsert the fitted intensities to obtain $m(\hat{q})$, evaluating the matrix exponential and integral numerically if necessary.

If $\eta =(\log q_{SE},\log q_{EI},\log q_{IR})$ has estimated covariance $V$, calculate the numerical gradient $g={\nabla }_{\eta }m(e^{\eta })$ at $\hat{\eta }$. The delta method gives estimated variance $g^{T}Vg$ and the approximate confidence intervalSimulation from $N(\hat{\eta },V)$ followed by transformation through $m$ gives a useful asymmetric alternative.

The linear SEIR model with a constant susceptible-to-exposed intensity isAdding the four equations confirms conservation of population: $S+E+I+R=N$.

The separable equation $\dot{S}=-q_{SE}S$ with $S(0)=S_0$ has solution

Substitute part (ii) into $\dot{E}+q_{EI}E=q_{SE}{S}_0{e}^{-q_{SE}t}$. Multiplication by the integrating factor $e^{q_{EI}t}$ givesSince $E(0)=0$, integration and rearrangement yield

At an interior maximum, $\dot{E}(t)=0$, equivalentlyThusThis is positive for distinct positive rates. Its continuous limit when $q_{EI}=q_{SE}=q$ is $1/q$.

The $S\to E$ transition must be redefined. A constant $q_{SE}$ gives each susceptible the same external infection pressure even when no infectious person remains. For influenza, the force of infection should depend on the current infectious prevalence. The progression $E\to I$ and recovery $I\to R$ can retain rates $q_{EI}$ and $q_{IR}$.

With frequency-dependent transmission parameter $\beta$, the nonlinear SEIR equations are

While $I>0$, divide the susceptible equation by the recovered equation:Taking $R(0)=0$ and integrating givesAt the end of the epidemic $E_{\infty }=I_{\infty }=0$, so conservation gives $R_{\infty }=N-S_{\infty }$. Definingwe obtain the final size relation for an epidemic

Under the boundary null $p={\pi }_0=0.20$, rejection requires both $X_1>r_1$ and $X_1+X_2\ge r$. Independence of the two binomial distributions givesThe rejection event is increasing in $p$, so this boundary value is the supremum over the composite null $p\le {\pi }_0$.

Writing $v_H=p_H(1-p_H)$ and $v_L=p_L(1-p_L)$, Neyman allocation minimizes the variance $v_H/n_H+v_L/n_L$ at fixed total sample size and gives

Minimizing the expected failures $n_H(1-p_H)+n_L(1-p_L)$ at a fixed variance gives the ethically optimal ratioIt allocates more patients to the dose with the larger response probability.

Neyman allocation optimizes information and may allocate more patients to the arm whose Bernoulli variance is nearer its maximum at $1/2$. The ethical allocation instead favors the arm with higher response probability. They coincide only for special parameter values; in general ethical gain is purchased with some loss of precision relative to Neyman allocation.

Targeting the Neyman ratio asymptotically minimizes the standard error for a fixed total sample size, so it cannot be worse than a fixed 1:1 design when the target probabilities are known. Targeting the ethical ratio can increase the standard error because it optimizes failures rather than information, although it may still outperform 1:1 for some probabilities.

In response-adaptive randomization, the probabilities are estimated during the trial. Delayed outcomes, time trends, unstable early estimates, and random final arm sizes complicate logistics and inference; naive Wald standard errors may also ignore adaptation.

Since $X_j\sim \mathrm{Poisson}(n_j{\lambda }_j)$, the rate MLE has asymptotic variance ${\lambda }_j/n_j$. The delta method for the logarithm givesIndependence of the arms therefore yieldsUnder $H_0:{\lambda }_T={\lambda }_C=\lambda$, the asymptotic variance of the log rate ratio is

With equal allocation and true alternative rates ${\lambda }_T,{\lambda }_C$, the asymptotic variance isThe normal approximation requires $|\log R{R}_A|/\sqrt{V_A}\ge z_{1-\alpha /2}+z_{1-\beta }$. Hencerounded upward. Writing ${\lambda }_T=R{R}_A{\lambda }_C$ expresses it using a specified control rate and the target rate ratio.

If $U\sim \mathrm{Uniform}(0,1)$, the inverse transform sampling formulahas survival function $\mathbb{P}(T>t)=e^{-\lambda t}$ and hence the required exponential distribution.

Without censoring, every $v_i=1$ and $\mathbb{E}{T}_i=1/\lambda$. ThereforeThis is events divided by total person-time at risk.

The first two mechanisms are standard independent, noninformative censoring. The third relabels the event time itself and therefore is not independent censoring for the original latent event time; it is more naturally interpreted as assigning a cause in a competing risks model. The detailed calculations follow in the three subparts.

Fixed administrative censoring $C=\tau$ is noninformative because it is unrelated to the random event time. The censored fraction isMoreover, $\mathbb{E}v=1-q$ andso the event-to-time ratio remains $\lambda$.

For an independent $C\sim \mathrm{Exponential}(\mu )$, censoring is noninformative andThe observed time is exponential with rate $\lambda +\mu$, while $\mathbb{E}v=\lambda /(\lambda +\mu )=1-q$. Thus

Independent relabelling gives $\pi =q$, $\mathbb{E}v=1-q$, and leaves $X=T$ with mean $1/\lambda$. Its ratio is therefore $\lambda (1-q)$ rather than $\lambda$. To retain event hazard $\lambda$, simulate the common occurrence time with rateand label it as the target event with probability $1-q$. This is equivalent to independent competing clocks with target-event rate $\lambda$ and censoring-cause rate $q\lambda /(1-q)$; their minimum has rate $\lambda /(1-q)$.

The Cox proportional-hazards model iswhere $h_0$ is an unspecified baseline hazard and $z_i$ indicates treatment. With no tied events, the Cox partial likelihood isEquality of the two hazard functions is $H_0:\beta =0$, testable with a likelihood-ratio, score, or Wald test from this likelihood.

Use each matched pair as a separate stratum with its own baseline hazard and fit one common treatment coefficient $\beta$. The Stratified Cox model partial likelihood multiplies the within-pair risk-set contributions, eliminating all pair-specific baselines. Test $H_0:\beta =0$ by the corresponding conditional score, likelihood-ratio, or Wald test.

A pair is informative only when its first observed exit is an event while both members remain at risk; later events after one member has left contribute a factor one. The uninformative pairs are therefore pair 5, with tied events at $(17,17)$, and pairs 10, 11, and 13, whose earlier observations are censorings: $(63+,278)$, $(89+,1083+)$, and $(141,138+)$. At $(140,140+)$ both are in the risk set immediately before time 140, so pair 12 is informative.

Among the nine informative pairs, the active patient fails first once and the placebo patient fails first eight times. The conditional partial likelihood is proportional tosoUnder $H_0$, the number of active-first failures is $\mathrm{Binomial}(9,1/2)$. The exact two-sided sign test hasso the data reject at the 5% level and favor lower hazard under active treatment.

Matching controls strong prognostic differences between patients and can greatly improve precision by making treatment comparisons within homogeneous pairs. It also protects against confounding when treatment assignment is not perfectly randomized globally.

Its disadvantage is loss of information: pairs with censoring before a comparison or tied outcomes contribute little or nothing, and the analysis cannot estimate the effects of pair-level matching variables. Poor matches and the logistics of paired enrollment can also reduce efficiency relative to a well-adjusted unpaired analysis.

With constant hazard $\theta$, observation $i$ contributesWriting $D={\sum }_i{v}_i$ and $T={\sum }_i{x}_i$, the log-likelihood is $D\log \theta -\theta T$, whose derivative is $D/\theta -T$. Hencethe number of events divided by total person-time.

Left truncation means that an individual enters observation only after a delayed entry time $L_i$ and is included only if the event time exceeds $L_i$. Earlier failures are absent from the dataset, so analysis must condition on survival to entry.

In the Kaplan–Meier estimator, replace the ordinary risk set at event time $t$ byThe product-limit factor remains $1-d_j/|R(t_j)|$, but only individuals who have entered and not yet exited contribute to its denominator.

Conditioning on survival to $L_i$ changes the constant-hazard likelihood contribution toThereforeusing only person-time accumulated after entry.

For period survival analysis over a calendar window, patients diagnosed earlier enter at the window's start only if still alive. Their survival times are left-truncated at the elapsed duration from diagnosis to that date, while follow-up is censored at the window's end. This estimates survival using mortality experience in the chosen recent period without pretending that earlier survivors were under observation from diagnosis.

There are seven deaths by day 28. Their total time plus 28 days from each of the ten later observations gives first-interval exposureAmong the ten observations beyond day 28, eight are deaths, and their exposure beyond 28 is

Under the two-rate alternative, maximize the piecewise-exponential survival model likelihood separately to obtain the estimates in part (i). Under $H_0:{\theta }_1={\theta }_2=\theta$, there are 15 deaths and 2200 days of exposure, so $\hat{\theta }=15/2200$. Twice the maximized log-likelihood difference isUnder the null this likelihood-ratio test statistic is asymptotically ${\chi }_1^2$.