Past exam of the mathematics course of the University of Cambridge / 2019 / iii / Paper 207 (Statistics in Medicine)

The Directed acyclic graph has arrowsThe roots $\lambda$ and ${\rho }_G$ are independent under their prior distributions; $N$ is fixed. Equivalently, the joint distribution factorizes as

The mean condition gives $a/(a+b)=0.1$, hence $b=9a$. The Beta distribution variance is thenSince $0.02985^2=9/10100$, equating variances gives $10a+1=101$. Therefore

For each person, infection occurs with probability $\lambda$ and, conditional on infection, a GP visit occurs with probability ${\rho }_G$. Independent Bernoulli thinning therefore gives visit probability $\lambda {\rho }_G$. More explicitly, the probability generating function isThusand the likelihood is

By Bayes theorem, with respect to Lebesgue measure on $(0,1{)}^2$,The omitted constant includes the binomial coefficient and the normalizing constant of the Beta distribution; the uniform prior contributes only the support indicator.

Use the deterministic evidence-synthesis relationwith supportA uniform prior on this triangle has density $21_{\mathcal{T}}$. Conditional on the prevalences, model the independent surveys bywith the two counts conditionally independent and ${\pi }_2={\pi }_1+\lambda$.

Integrating the constant density $2$ across horizontal slices of the triangular support givesso ${\pi }_1\sim \mathrm{Beta}(1,2)$. For $z={\pi }_2={\pi }_1+\lambda$, the line segment at fixed $z$ has length $z$, and the transformation has unit Jacobian. Henceso

Extend the original Directed acyclic graph withThe existing arrows $\lambda \to I\to Y_G$ and ${\rho }_G\to Y_G$ remain. The survey sample sizes and $N$ are fixed design variables, while ${\pi }_2$ is a deterministic node satisfying ${\pi }_2={\pi }_1+\lambda$.

For parameters $({\rho }_G,{\pi }_1,\lambda )$ on $0<{\rho }_G<1$ and $({\pi }_1,\lambda )\in \mathcal{T}$, conditional independence givesThis is the joint posterior up to its normalizing constant.

Causal mediation analysis decomposes the total causal effect of an exposure into a pathway operating through a mediator and a pathway not operating through that mediator. Let $M(x)$ be the potential mediator under exposure $x$, and let $Y(x,m)$ be the potential outcome under exposure $x$ with mediator set to $m$. One conventional decomposition usesfor the natural direct effect, andfor the natural indirect effect. In words, the direct effect changes exposure while holding the mediator at the value it would naturally have under no exposure; the indirect effect changes only that natural mediator value while holding exposure fixed at one.

Taken at face value, the mediation analysis says that the rs8034191 allele raises lung-cancer risk mainly through a pathway not captured by reported cigarettes per day: the direct-effect odds ratio is $1.35$, whereas the estimated indirect-effect odds ratio through smoking intensity is $1.01$ and is compatible with no mediation. It does not show that smoking intensity has no causal effect on lung cancer. It concerns mediation of this genetic variant's effect through this measured mediator, and a weak variant-to-intensity association, measurement error, or mediation through smoking duration, inhalation, or nicotine exposure could make that indirect pathway appear small.

The significant additive-scale interaction and the association of the variant with cancer among smokers but not nonsmokers indicate effect modification: the joint effect of genotype and smoking exceeds additivity on the risk scale. Under adequate control of confounding and selection, that pattern supports a causal role for smoking in activating or amplifying the genetic pathway. Interaction alone is not proof that smoking is causal, because smoking was not randomized and the stratum-specific estimates can be affected by confounding, selection, and low power among nonsmokers.

The mediation estimate relies on several strong assumptions. Possible failures include mediator-outcome confounding, residual exposure-outcome or exposure-mediator confounding, and an exposure-induced mediator-outcome confounder. Smoking duration may itself be part of the causal pathway, making adjustment inappropriate. Self-reported cigarettes per day has measurement error and does not fully measure tobacco exposure. The case-control sampling can create selection bias; population stratification can confound the genotype relations; cancer may alter reported smoking; and the product-of-coefficients calculation can be inappropriate for a binary outcome because odds ratio effects are nonlinear and noncollapsible. Any of these can attenuate or distort the indirect effect.

The evidence would be stronger with prospectively measured smoking before diagnosis, repeated measures of intensity and duration, objective biomarkers such as cotinine, and explicit modeling of cumulative exposure. The authors could use modern counterfactual mediation estimators suited to case-control data and binary outcomes, allow exposure-mediator interaction, report effects on interpretable risk scales, and perform sensitivity analyses for unmeasured mediator-outcome confounding and measurement error. Replication, ancestry adjustment, negative controls, and a Mendelian randomization analysis using additional smoking instruments with credible exclusion restrictions would help distinguish smoking-mediated effects from direct pleiotropic effects of this locus.

Let $Y_{it}$ be patient $i$'s QoL at visit $t$ and let $R_i$ be the last visit at which QoL is observed. The data are monotone missing-data pattern whenThus each patient contributes an observed prefix $(Y_{i0},\dots ,Y_{i{R}_i})$ followed by a missing suffix.

Let $A_i$ be treatment, $Y_i=(Y_{i0},\dots ,Y_{i,12})$, and $R_i\in \{0,\dots ,12\}$ the last observed visit. The missing at random assumption isfor every feasible $r$. Equivalently, each conditional dropout hazard may depend on treatment and observed QoL history but not on current or future unobserved QoL after conditioning on that history.

In this trial, MAR means that among patients assigned the same treatment who have the same recorded QoL trajectory up to a visit, the probability of dropping out next is unrelated to what their later QoL values would have been. Dropout may depend strongly on previous poor QoL, treatment assignment, and other observed history; MAR only rules out residual dependence on the unobserved outcomes.

MAR is plausible if clinic withdrawal is driven by recorded QoL, observed side effects, treatment, and other measured history. It is doubtful if patients leave because of an unrecorded deterioration, an imminent recovery, treatment toxicity not included in the analysis, or dissatisfaction that predicts their unseen 12-month QoL. The large dropout fraction makes such missing not at random mechanisms a serious concern, so MAR should be supported by rich predictors and sensitivity analysis rather than assumed without examination.

A missingness mechanism is ignorable for likelihood-based inference about the outcome parameter when the observed-data likelihood can be formed from the outcome model alone. The standard sufficient conditions are MAR and distinct parameters: the outcome-model parameter and missingness-model parameter have a product parameter space. The missingness indicators then carry no additional likelihood information about the outcome parameter once the observed outcomes are given.

Write the complete-data model as $p_{\theta }(y\mid a)$ and the missingness model as $q_{\psi }(r\mid y,a)$. Under MAR,Therefore the observed-data likelihood factorizes asWith distinct parameters, the first factor does not involve $\theta$. Maximizing or integrating the second factor therefore gives the same likelihood inference for $\theta$ as modeling the missingness process explicitly. Hence MAR plus distinctness makes missingness ignorable.

The monthly nurse assessments are auxiliary longitudinal outcomes observed even after clinic dropout. Investigators can include their histories, treatment, and earlier QoL in a multiple imputation model for missing 12-month QoL, or in a joint longitudinal model. Because the assessments predict disability and QoL, conditioning on them reduces residual outcome variance and makes each imputed value more informative, improving precision of the treatment-effect estimate. A prespecified covariate-adjusted or augmented inverse-probability estimator could use the same information.

The nurse measurements can also reduce bias by making MAR more credible: withdrawal may depend on unobserved clinic QoL, but that QoL is partly represented by the post-dropout disability assessments. They also permit diagnostics comparing inferred QoL trajectories with an independently recorded proxy and can support sensitivity analysis for departures from MAR. They do not by themselves prove MAR, because the rough score may omit reasons for dropout related to QoL.

Place discrete hazards $q_j$ at the ordered distinct event times $t_j$. If $d_j$ events occur among $r_j$ individuals at risk immediately before $t_j$, the nonparametric empirical likelihood isEquivalently, an observed event at $x$ contributes the probability mass at $x$, while a right-censored observation contributes the survivor probability beyond its censoring time. Maximization gives ${\hat{q}}_j=d_j/r_j$ and the Kaplan–Meier estimator

Left truncation means an individual is observed only conditional on surviving beyond an entry time $L$. Ignoring it overrepresents long survivors and creates survivorship bias. A subject with event or censoring time $X>L$ contributes its usual likelihood divided by $S(L)$; in risk-set form, that individual enters each $r_j$ only for event times satisfying $L<t_j\le X$.

The professors enter observation only when elected. Anyone dying before election cannot appear, so the birth-to-death sample is left-truncated at varying, outcome-related ages and is not an inception cohort from birth. Every listed professor was elected before age $60$ and survived to $60$, so all six are under observation from the common origin age $60$. The data can therefore estimate survival from age $60$ without delayed entry.

For $T=$ age at death minus $60$, the observations areThere are three distinct event times and hence three independent discrete hazards $q_2,q_7,q_{15}$. Their risk-set sizes are $6,5,3$, soThe maximum-likelihood estimates are ${\hat{q}}_2=1/6$, ${\hat{q}}_7=1/5$, and ${\hat{q}}_{15}=1/3$.

The estimated survivor function isuntil the last observed time. It first falls to at most one half at $t=15$, so

After correction, the records from age $60$ arewhere each pair is delayed-entry time and event or censoring time. The risk sets at event times $2,7,35$ all have size three. Thus the left-truncation-adjusted empirical likelihood isEach estimated event hazard is $1/3$.

The corrected Kaplan–Meier estimator is $2/3$ immediately after $t=2$ andimmediately after $t=7$. It first crosses one half there, so

Proton and Prune are censored after the estimated survivor curve has already crossed one half. Learning their later death times may add jumps in the far tail but cannot change the first crossing, so the nonparametric median remains seven years. An exponential distribution instead estimates one constant hazard from the total event count divided by total time at risk. Replacing censoring by observed later deaths changes both quantities and therefore changes the fitted rate and its median $\log 2/\hat{\lambda }$.

In a proportional hazards model, individual $i$ hasThe exponential term is the hazard multiplier relative to the baseline hazard $h_0$. With $h_0$ unspecified, the Cox partial likelihood multiplies, over event times, the failing subject's multiplier divided by the sum of multipliers in the current risk set. After estimating $\beta$, the Breslow estimator is

A Stratified Cox model uses a separate baseline hazard $h_{0s}$ for each stratum but a common $\beta$. Its partial likelihood is the product of within-stratum partial likelihoods, and a separate integrated baseline hazard is estimated in each stratum.

In a matched pair, the only informative comparison occurs while both members remain at risk. If the exposed member fails first, the pair contributes $e^{\beta }/(1+e^{\beta })$; if the unexposed member fails first, it contributes $1/(1+e^{\beta })$. A censoring as the first recorded time gives no informative failure comparison, and any later one-person risk set contributes one. With only two observations per stratum, each stratum supplies almost no information about its arbitrary baseline hazard, so a useful common integrated baseline-hazard estimate is generally unavailable.

Among the 12 pairs with control time first, the eight in which that first time is an event contribute $(1+\beta {)}^{-1}$ each. Among the eight pairs with treated time first, the four in which that first time is an event contribute $\beta /(1+\beta )$ each. Later events in one-eye risk sets contribute one. HenceDifferentiating the log likelihood gives $4/\beta -12/(1+\beta )=0$, and therefore

Without randomization, treatment side can be associated with prognosis. Always treating the left eye confounds treatment with systematic left-right differences; choosing the worse eye creates severe confounding by indication, baseline imbalance, and possible regression toward the mean. The within-patient comparison then no longer identifies a treatment effect without stronger adjustment assumptions.

A frailty random variable is an unobserved positive multiplicative risk factor. A proportional frailty model hasThe scale of $U$ is not separately identifiable from $h_0$: multiplying $U$ by a constant and dividing $h_0$ by it leaves the model unchanged. We may therefore normalize $\mathbb{E}U=1$, which lets $h_0$ represent the mean initial hazard multiplier and makes relative frailty interpretable.

If $U\sim \mathrm{Exponential}(1)$ and $h_0(t)=\lambda$, then the Laplace transform of $U$ givesThus $h(0)=\lambda$, while $h(t)\to 0$ as $t\to \infty$. Survivors become increasingly enriched for low-frailty individuals.

Letand use constant baseline hazard $h_0=m$. Define the two-point frailtyThen $\mathbb{E}U=1$, and the conditional rates are exactly $\gamma$ and $\beta$. The experimental-treatment population hasandSince standard treatment has hazard $\beta$, the population hazard ratio isAt zero,whereas for $\pi >0$,The treatment effect is therefore non-proportional and strengthens among later survivors as the high-rate subgroup is depleted. A trial should allow adequate follow-up, avoid relying only on a constant-hazard-ratio Cox model, and prespecify survival-curve, milestone-risk, restricted-mean-survival, or time-varying-effect analyses. Its power and interpretation will depend materially on follow-up duration.