Past exam of the mathematics course of the University of Cambridge / 2010 / iii / Paper 34 / 1

The odds ratio compares event odds, not event probabilities. Let group 1 denote the elective group and group 0 the reference group. Their fitted event probabilities are ${\hat{p}}_1=9/1515\simeq 0.00594$ and ${\hat{p}}_0=1215/75057\simeq 0.01619$. ThusThe risk ratio is similarly about $0.367$. The unadjusted observations show a lower adverse-event frequency in the elective group, rather than an increase. This is an association, not evidence that choosing the procedure prevents adverse outcomes. The direction is opposite to the reported adjusted odds ratio above one; the two analyses compare different populations or different conditional risks.

Zero observed events do not mean that the underlying event probability cannot be estimated. For independent observations having a common Bernoulli distribution, the binomial likelihood with no events is $(1-p{)}^{1515}$, maximized at $\hat{p}=0$. A zero-event binomial upper confidence bound shows the remaining uncertainty: the one-sided 95% upper bound solves $(1-p_U{)}^{1515}=0.05$, givingThus the point estimate is zero, but a nonzero mortality risk is compatible with the observations. This bound is an illustration under independent equal-risk sampling; clustered data or unequal risks require their own uncertainty calculation.

The empirical unadjusted odds ratio is also defined:Its log odds ratio is $-\infty$, so the ordinary normal approximation for a log-odds confidence interval is unavailable. Exact likelihood-based limits can still describe uncertainty; a specified continuity correction would instead yield a finite, method-dependent point estimate.

In an unpenalized logistic regression with a separate coefficient for elective exposure, every exposed death outcome is zero. Decreasing that coefficient toward $-\infty$ increases the exposed observations' likelihood contributions and leaves the reference observations unchanged. This is quasi-complete separation: there is no finite ordinary maximum-likelihood estimate of the exposure coefficient, even after adding background predictors. It is reasonable to say that the usual finite adjusted coefficient could not be fitted; it is too strong to say that no risk estimate or statistical information is possible. A specified penalized likelihood or Bayesian inference with proper coefficient priors can provide a finite adjusted estimate, whose dependence on the regularization must be reported.

Write the logistic regression aswhere $A=1$ denotes elective exposure and $x$ contains the measured background predictors. At fixed $x$, changing $A$ from zero to one changes the log odds by $\beta$, so the adjusted odds ratio is $e^{\beta }$. If $\hat{V}$ is the estimated coefficient covariance matrix, thenUse the clinic-cluster sandwich covariance matrix if that is how within-clinic dependence is allowed for. The interval is first calculated on the coefficient scale and then exponentiated; one does not add and subtract a standard error directly from the odds ratio. This is a large-sample Wald confidence interval; profile-likelihood limits are another option when the likelihood shape warrants them. If exposure interacts with background variables, there is no single common conditional odds ratio: its logarithm includes the corresponding interaction terms.

There is an apparent reversal, but not a mathematical contradiction. The crude odds ratio averages over the actual background distribution in each group, whereas the adjusted logistic regression compares groups at the same fitted background values. Strong confounding could make those distributions very different: for example, elective patients might disproportionately come from low-risk backgrounds or clinics, while the reference patients come from higher-risk backgrounds. The Simpson paradox can then reverse the marginal comparison even when every conditional comparison favours the same direction.

The noncollapsibility of the odds ratio can also make marginal and conditional odds ratios differ in magnitude. It does not, by itself, explain a sign reversal if both groups have the same covariate distribution and the common conditional effect has one sign: if $p(1,x)>p(0,x)$ for every $x$, averaging over the same distribution of $x$ still gives a larger exposed risk. A genuine reversal therefore requires differing background distributions, heterogeneous effects or another change in what is being compared. The observed reversal is a reason to investigate these issues, not proof of a programming error.

Using the reference event rate as the background-risk benchmark givesThis is the expected count if the elective group had the reference group's baseline risk and the procedure added no effect. It is substantially above the observed count, illustrating the importance of the background-risk comparison.

Similarity of background factors alone does not fix the elective group's event risk if the procedure itself changes it. If one additionally retained the reported common adjusted odds ratio $R=2.7$ and used $p_0=1215/75057$ as the common baseline risk, then conversion from odds to probability would giveThese are different assumptions: about 25 is the baseline/no-effect benchmark; about 64 includes an odds multiplier of 2.7.

As a rough rare-event calculation, divide the observed elective-group event count by the reported adjusted odds ratio:For a homogeneous illustrative risk, the exact odds conversion starts from $p_1=9/1515$ and givesThe corresponding baseline risk is about $0.22\%$, compared with $1.62\%$ in the observed reference group, roughly seven times lower. Thus taking the adjusted result literally implies exceptionally low background risk among the elective patients.

This is a diagnostic approximation, not an identified mean of potential outcomes obtainable from the aggregate table. A conditional odds ratio cannot generally be inverted at an aggregate mean: individual background risks are needed for outcome standardization. Interpreting the calculation causally also requires conditional exchangeability, the positivity assumption and a correctly specified outcome model. At very small risks the rare-event approximation makes the estimate of roughly three events useful for checking the plausibility of the adjustment.

The groups were not formed by randomization. Their background health, access to care, clinic, country and reasons for selecting a delivery method can predict both the method and the outcome, creating confounding and selection bias. Moreover, the label describing the reference delivery may be determined after labour: patients whose attempted nonoperative delivery develops a complication can move into an operative category, leaving a selected uncomplicated reference group. Comparing intended strategies would avoid treating this post-baseline classification as a baseline assignment.

A useful comparison would therefore align eligibility and follow-up time, compare intended delivery strategies among patients genuinely eligible for both, and account for sufficient pretreatment predictors. Logistic regression cannot create comparable patients where the positivity assumption fails or remove unmeasured confounding.

The displayed information does not establish increased maternal mortality caused by elective exposure. There are no observed deaths in that group, and the reported adjusted estimate concerns a composite adverse outcome, not death alone. A composite can show an association driven by nonfatal components without identifying a mortality effect.

If the logistic regression and its adjustment are correct, its confidence interval supports an adjusted association with the composite outcome. Calling that association a causal increase in risk additionally requires a defensible comparison group, adequate control of confounding, valid outcome classification and a well-defined intervention. The crude result is in the opposite direction, and the implied very low counterfactual baseline risk deserves examination. Conversely, zero deaths does not prove absence of harm. The justified conclusion is an association conditional on model and study assumptions, with mortality and morbidity distinguished.

A reversal this large calls for an audit, but the aggregate table cannot identify a particular error. Check the outcome and exposure coding, the reference category, the subset used in each analysis, missing-data exclusions, denominators, weights, and whether the reported coefficient actually corresponds to the intended comparison. Reversing an exposure contrast or exponentiating the wrong fitted coefficient would change the reported odds ratio. Conditioning on variables affected by delivery, or including inappropriate interactions, could also change the causal inference rather than merely improve precision.

Start by reproducing the crude odds ratio from an independent two-by-two calculation. Then fit progressively adjusted logistic regressions, recording how the coefficient and analysis population change; inspect within-clinic comparisons, sparse cells and separation. For an ordinary likelihood fit, check the fitted expected event count against the observed count and verify that changing only to cluster-robust standard errors leaves the fitted coefficients unchanged. A sandwich covariance matrix corrects uncertainty for clustered data; it does not by itself turn a crude odds ratio below one into an adjusted odds ratio above one. Adding clinic effects, using weights or changing the model can change the point estimate and must be distinguished from that variance correction.

Programming or reporting error is a possibility to check, not a conclusion proved by the reversal. Strong legitimate confounding remains another explanation.