Time-Varying Confounding With Competing Events

Why Longitudinal Treatment Creates a Special Problem

In a longitudinal study, treatment may be chosen repeatedly as a participant’s health evolves. A health measure recorded after an earlier treatment can both influence the next treatment and predict a later event. If the earlier treatment also affects that health measure, it is a time-varying confounder affected by prior treatment. This treatment-confounder feedback makes ordinary regression adjustment difficult: the measure needs to be accounted for when estimating the effect of later treatment, but adjusting for it in a conventional outcome regression can remove part of the effect of earlier treatment.

Competing events make the target a risk under a strategy, not simply a rate among people who remain event-free. A participant who experiences the competing event can no longer experience the event of interest first. The causal contrast therefore depends on how each treatment strategy changes both the event of interest and the competing event, as well as the evolving covariate history among those still at risk.

The focus here is the total risk contrast between treatment strategies. It is not the risk in a hypothetical world where the competing event is eliminated. Treatment assignment, covariate measurement, and event timing must be ordered clearly: covariates used to choose \(A_t\) are measured before \(A_t\), and once either event occurs, subsequent treatment decisions do not apply.

Assumptions for Causal Risk Estimation

A g-method does not by itself make observational data causal. Identification requires substantive assumptions, stated here for measured treatment and covariate histories:

• Consistency and well-defined strategies. If a participant follows regime \(g\), their observed event history equals the potential event history under \(g\). Treatment versions grouped under one value must be sufficiently well defined for this equality to be meaningful.
• Sequential exchangeability. At each decision time, conditional on measured history available before treatment, treatment assignment is independent of the potential future event and covariate histories under the regimes being compared. In practical terms, there are no unmeasured common causes of treatment decisions and subsequent outcomes after conditioning on that history.
• Positivity. Every treatment required by a regime has positive probability within each history that occurs under the regime. If, for example, nearly all participants with severe symptoms receive treatment, data may not support estimating the outcome they would have had untreated.
• Correct time ordering and measurement. Relevant confounders are measured before the treatment decisions they confound, and event type and timing are recorded adequately. A covariate measured after an event cannot be used as a pre-event treatment confounder.
• Appropriate handling of censoring. If loss to follow-up occurs, censoring must be independent of future potential outcomes conditional on the measured history used in the analysis, or be addressed with an appropriate censoring model. The examples below assume complete follow-up.

These assumptions extend the exchangeability, positivity, consistency, and censoring conditions used for causal risk estimation to a sequence of treatment decisions. They are not verified merely because a fitted model converges or produces plausible estimates.

Two-Period Competing-Risk G-Formula

Consider a two-period setting. At baseline, treatment \(A_0\) is assigned. During the first period, either the event of interest or the competing event may occur. Among those event-free at the second decision, \(L_1\) is measured and treatment \(A_1\) is assigned. During the second period, either event may occur. Let \(g=(a_0,a_1)\) be a sustained strategy, assigning \(A_0=a_0\) and, if the participant remains event-free, \(A_1=a_1\).

Write \(S_1^{a_0}=1\) for being event-free after the first period under \(A_0=a_0\). Let \(q_{1,0}(a_0)\) be the probability of the event of interest in period one under \(a_0\), and let \(q_{1,1}(a_1,l)\) be the period-two probability of the event of interest among those event-free with \(L_1=l\), under \(A_1=a_1\). Then the cumulative risk under \(g\) is:

The formula adds two mutually exclusive ways to experience the event of interest by the end of period two: having it in period one, or surviving event-free through period one and having it in period two. In the second term, the covariate distribution is the distribution that would arise under the first treatment \(a_0\), among those still event-free. This is precisely why simply fixing or conditioning away \(L_1\) does not generally estimate the total risk under a treatment strategy.

In longer follow-up, the same logic is applied recursively: at each time, average the event probabilities and next covariate distributions under the treatment specified by the regime, while removing from the risk set those who have already experienced either event. The competing-risk g-formula is this sequential standardization over the histories that would occur under the intervention.

Calculating Risks Under Sustained Strategies

Suppose a hypothetical data source supports the following conditional probabilities. “Survival” in period one means remaining free of both event types through that period. Each period-two row describes mutually exclusive period-two outcomes among people who survived event-free through period one.

The assumptions must be considered alongside this computation. The conditional probabilities need to identify the relevant potential outcomes through sequential exchangeability; both strategies must be possible in the histories they generate; treatment and events must be consistently defined; and the measured symptom distribution must correspond to the right time and risk set. If these conditions fail, the arithmetic still describes a model-based standardization, but it need not identify the causal risk contrast.

Why Ordinary Adjustment Can Change the Target

A standard regression that includes \(L_1\) as a covariate can help control confounding of the later decision \(A_1\), but it does not automatically recover the total effect of a sustained strategy. In particular, plugging in one common \(L_1\) distribution for both strategies removes the way the first treatment changes that distribution. The g-formula instead uses \(P(L_1\mid S_1^{a_0}=1)\) separately under each strategy.

For illustration, if the \((1,1)\) period-two outcome probabilities from the example were averaged using the \(L_1\) distribution under \(A_0=0\), the result would be \((0.800)(0.060)+(0.200)(0.120)=0.072\). Combining that with the \((1,1)\) first-period risk and survival gives \(0.080+(0.800)(0.072)=0.1376\), not the strategy-specific risk \(0.1568\). This calculation is not a claim that every adjusted regression equals 0.1376. It demonstrates that changing the covariate distribution changes the standardization target; a conventional conditional model needs an explicit, appropriate causal procedure to yield the desired total risk.

Diagnostics, Alternatives, and Limitations

The g-formula and inverse probability weighting are both g-methods, but they rely on different models. The g-formula models outcome and covariate distributions and then standardizes under a specified regime. Weighting models treatment assignment (and often censoring) and creates a weighted pseudo-population in which measured treatment history is balanced, subject to correct models and positivity. A marginal structural model can summarize weighted risks across strategies. Doubly robust approaches combine components, but “doubly robust” does not remove the need for well-defined interventions, adequate overlap, and at least one correctly specified nuisance-model component under the method’s conditions.

Useful checks include examining treatment probabilities across covariate histories, inspecting the range and upper tail of weights, and comparing weighted covariate balance before and after weighting. For the g-formula, inspect fitted probabilities for impossible values, compare model-predicted covariate and event distributions with observed distributions, and check whether important nonlinearities or interactions have been omitted. Extreme weights signal that some histories contribute disproportionately; truncation may reduce variance but introduces a bias-variance trade-off and changes the estimator. Report such choices and assess sensitivity to them.

Neither method is a cure for unsupported extrapolation. If no patients with a particular symptom history receive one treatment, the corresponding counterfactual risk is not learned from the data without additional assumptions. Model misspecification can also distort either approach: a flexible outcome model may still extrapolate poorly, while a treatment model may predict probabilities near zero and create unstable weights. With few events, especially few competing events, estimates can be imprecise even when the method is correctly specified.

A common mistake is to adjust for every available covariate in a single outcome regression and assume that this necessarily controls confounding. The reasoning is that a variable associated with treatment and outcome must be included as an ordinary covariate. The correction is to inspect its timing and causal role: if it is affected by earlier treatment, it can be both a confounder of later treatment and part of the earlier treatment’s effect pathway. Use a method that respects the longitudinal treatment and covariate history, and state the target regime and competing-event treatment explicitly.