Doubly Robust Treatment-Timing Effects on Survival in Retrospective ICU Cohorts

Many of the hardest questions in hospital medicine are about when to start a treatment, not whether to start it. Examples include when to intubate a patient in respiratory failure, when to start vasopressors, and when to begin a biologic. Records of past patients, known as retrospective cohorts, contain large natural variation in timing. The textbook way to use that variation asks what would happen if every patient were treated at hour $t$. That question has no answer in the data, because for many patients at many moments the chance of being treated was essentially zero. Incremental Causal Effect for Time to Treatment Initialization sidestepped this by asking a gentler question: what if each patient's moment-to-moment chance of starting treatment were multiplied by a factor $\theta$, so that $\theta>1$ means sooner and $\theta<1$ means later? This "hazard-shifting" question is answerable from the data without assuming everyone could have been treated at every time. The paper's estimator, however, relies only on reweighting patients, and the authors state that it has high variance. They also flag a doubly robust version as open, and they tested it only on a single continuous one-year outcome (tender joint counts in 1,010 rheumatoid arthritis patients).

We propose to build and validate a doubly robust estimator of hazard-shift effects on right-censored survival outcomes, and to apply it to treatment-timing questions in MIMIC-IV intensive care records. "Doubly robust" means the estimate stays consistent if either the model of who gets treated when, or the model of how patients fare, is correct. A causal graph (a diagram of which clinical variables cause which) is used in two concrete places. It decides which parts of the evolving patient history enter each model. It also defines the set of defensible alternative graphs over which we test how much the answer moves. In short, the proposal gives clinicians an estimate of whether intubating somewhat earlier than usual changes 28-day survival, with honest confidence intervals, using records they already have.

Core Claim

The claim is that a doubly robust, cross-fitted estimator of the incremental hazard-shift effect on survival at a horizon $\tau$ will cut variance substantially relative to the weighting-only estimator. It will keep close-to-nominal coverage of confidence intervals in exactly the regime where the weighting estimator breaks down, which is delays ($\theta<1$) in patients with long exposure to a high treatment hazard. The estimator also stays valid when a graph-guided outcome model is misspecified but the treatment-hazard model is correct, and vice versa.

The target quantity is defined as follows. Let $\lambda(t \mid H_t)$ be a patient's natural hazard of starting treatment at time $t$ given their recorded history $H_t$, and let $T^{\theta}$ be the survival time that would occur if that hazard were replaced by $\theta\,\lambda(t \mid H_t)$. The estimand is

$$\psi(\theta) = P\left(T^{\theta} > \tau\right),$$

and its counterpart is restricted mean survival time up to $\tau$.

The reason reweighting alone struggles is visible in the weight it assigns. Consider a patient who has not started treatment by the end of follow-up $X$. Under the shifted regime, the likelihood ratio for that patient's observed treatment history is

$$W = \exp\left(-(\theta-1)\int_0^{X} \lambda(s \mid H_s)\,ds\right).$$

A patient treated at time $A$ gets the extra factor $\theta$, with the integral taken up to $A$. For $\theta<1$ this weight grows exponentially in the accumulated treatment hazard. In an ICU, where hourly hazards of intubation can be large for sick patients, a few individuals will then dominate the estimate.

The augmentation term adds a model of expected survival under the shifted regime. It is built from sequential outcome regressions over the history that the graph designates. When that outcome model is good, it absorbs most of the variance the weights create. When it is wrong, the weights correct it.

Research Program

Graph construction. We will write a clinical causal graph for each application, following the framing and identification steps of Step-by-step causal analysis of EHRs to ground decision-making. That paper builds a hand-constructed diagram and uses target-trial framing to avoid immortal-time bias for a baseline albumin decision in MIMIC-IV sepsis. We extend it from a single baseline decision to a treatment-initiation process unfolding hour by hour. The graph names three kinds of variables. The first is time-varying confounders that drive both initiation and death, such as oxygenation, respiratory rate, lactate, vasopressor dose and mental status. The second is variables affected by earlier care that must not be treated as baseline adjusters. The third is variables such as billing codes assigned at discharge, which cannot legally enter $H_t$ because they postdate $t$.

This matters because treatment-confounder feedback is the reason propensity matching fails in this setting. Addressing treatment switching in the ALTA-1L trial with g-methods: exploring the impact of model specification showed this in oncology with a graph of progression and switching.

Estimator derivation. We will derive the efficient influence function for $\psi(\theta)$ under right-censoring. Death before treatment ends the treatment process naturally, and administrative censoring is handled with a separate censoring-hazard model. In practice we will work in a fine discrete-time approximation, with hours as steps, where the derivation is a sequential augmentation of the likelihood-ratio weights above. The estimate is obtained by cross-fitting (nuisance models are trained on some folds and evaluated on others). We will prove the product-rate property: bias is controlled by the product of the errors of the treatment-hazard and outcome models. This is what allows flexible learners to be used without destroying valid inference.

Nuisance learners. We will compare three families of models for the treatment hazard, censoring hazard, and outcome regressions. The first is pooled logistic hazard models. The second is gradient-boosted trees. The third is an autoregressive sequence model in the style of Dynamic Survival Transformers for Causal Inference with Electronic Health Records, which feeds irregular hourly vitals and labs into a doubly robust estimator of restricted mean survival time but only for a treatment fixed at baseline. Our work supplies the time-varying treatment extension that paper leaves open, restricted to the specific and positivity-safe family of hazard shifts.

Robustness analysis. We will run a vibration analysis, in the sense of Step-by-step causal analysis of EHRs to ground decision-making. The estimate is recomputed across defensible alternative graphs (for example, whether a given lab is treated as a confounder or as a consequence of earlier care), history window lengths, and learners. ALTA-1L's range of cumulative hazard ratios from 0.38 to 0.73 across IPCW specifications shows why this is needed. Our hypothesis is that the doubly robust estimator's spread across specifications is much narrower than the reweighting estimator's. For latent confounding, we will add a simple bound in which an unmeasured variable is assumed to multiply the treatment hazard by up to a factor $\Gamma$.

Baselines

The naive reference point is a Cox model with treatment entered as a time-varying indicator, adjusted for baseline covariates. This is what most retrospective cohort papers would run. It does not target $\psi(\theta)$ at all, and it is biased under treatment-confounder feedback. Its role is to show the size of the gap between routine practice and a causal answer. It is fitted on the identical cohort, and the proposal beats it if its estimates on semi-synthetic data have lower bias.

The strongest existing competitor is the weighting estimator of Incremental Causal Effect for Time to Treatment Initialization, extended in the obvious way to survival by applying the same weights to a Kaplan–Meier or indicator-of-survival-past-$\tau$ outcome. We will give it every advantage. It gets the same treatment-hazard learners, the same cross-fitting, the same hyperparameter budget, and weight truncation at several percentiles, with the best truncation chosen on held-out semi-synthetic replicates. The paper reports point effects of a 1.23% decrease in tender joints at $\theta=2$ and a 1.51% increase at $\theta=0.2$, but no reported result was found on Lacuna for any hazard-shift estimator on a survival endpoint. There is also no reported variance or coverage figure for the weighting estimator to beat. We therefore set the bar ourselves. Beating it means at least a 30% reduction in root mean squared error at $\theta \le 0.5$ with 95% interval coverage within two points of nominal, while the truncated weighting estimator is either less accurate or under-covers.

The third baseline is a plug-in parametric g-formula. It fits models for how covariates and death evolve, then simulates patients under the shifted hazard. This is the natural competitor from Addressing treatment switching in the ALTA-1L trial with g-methods: exploring the impact of model specification. It has low variance but offers no protection when the outcome and covariate models are wrong. It gets the same learners and budget, and we beat it if we match its variance when its models are correct and have lower bias when they are misspecified.

For the nuisance-model component, the relevant reported numbers come from the same paper, on semi-synthetic MIMIC-III survival: DynST reached an MAE of 11.19, against 11.42 for a static transformer and 16.04 for a Cox oracle (Dynamic Survival Transformers for Causal Inference with Electronic Health Records). That tells us sequence models are worth trying as outcome regressions, not that they will win here.

Two ablations isolate the key ingredients. The first removes the augmentation term, which recovers the weighting estimator. The second replaces the graph-designated history with "all features available up to $t$", which tests whether the graph earns its place or whether a flexible learner fed everything does as well.

Why not just…?

Why not just truncate or stabilize the weights of the existing estimator? Truncation is cheap and may well get most of the variance reduction. That makes it the most serious threat to this proposal. Its cost is bias of unknown size that grows exactly when many patients carry extreme weights, as with long exposure at $\theta<1$. The semi-synthetic experiment settles this directly by plotting bias, variance and coverage against truncation level for the weighting estimator next to the untruncated doubly robust one. If some truncation level matches our estimator across $\theta$, we will report that and shift the contribution toward the survival extension and graph-based robustness analysis.

Why not just emulate a target trial comparing "intubate within $k$ hours of meeting criteria" against "later", using cloning and censoring with a grace period? This is the established epidemiological design, and it answers a clinically legible question. Its problem is that fixed-deadline strategies still require every eligible patient to have had a real chance of treatment within the window. In ICU data that fails for patients with contraindications or do-not-intubate preferences. Incremental Causal Effect for Time to Treatment Initialization proves that deterministic timing targets are not identified without positivity (every patient having a nonzero chance of each treatment option). We will still run a grace-period emulation on the same cohort as a comparator. Agreement in direction would be reassuring. Divergence concentrated in low-hazard patients would show where the positivity problem bites.

Why not just run a Cox model with time-varying treatment, or propensity score matching at baseline? Both condition on, or ignore, variables that earlier care has changed. Addressing treatment switching in the ALTA-1L trial with g-methods: exploring the impact of model specification shows the practical size of this error: the ITT hazard ratio of 0.81 understated benefit by 10 to 45 percentage points relative to g-methods. The semi-synthetic experiment quantifies the bias of the naive Cox model against known ground truth, so this argument does not rest on analogy.

Why not just learn the graph from data with dynamic structure discovery? Methods such as Directed Acyclic Graph Structure Learning from Dynamic Graphs and Dynamic Causal Structure Discovery and Causal Effect Estimation assume linear or smoothly evolving effects and have only been tested on synthetic, social-network or district-level data. Abrupt events like intubation break those smoothness assumptions, and the methods assume no hidden common causes, as the file's discussion of unmeasured confounding notes. We use the graph only to restrict histories and to generate alternative specifications. Discovery can be tried later as one more alternative graph inside the vibration analysis.

Proposed Experiments

Semi-synthetic study. The first experiment follows the design of Dynamic Survival Transformers for Causal Inference with Electronic Health Records. Real MIMIC-IV adult ICU covariate trajectories, preprocessed with An Extensive Data Processing Pipeline for MIMIC-IV, are kept as they are. We then simulate an initiation hazard and a death hazard from a known model encoded in the clinical graph, including treatment-confounder feedback in which initiation changes the next hours' oxygenation. Because the model is known, $\psi(\theta)$ can be computed exactly by simulation for $\theta$ from 0.2 to 5. We vary three stressors: the strength of the treatment hazard, which controls near-positivity problems; which nuisance model is deliberately misspecified; and the censoring rate. The metrics are bias, root mean squared error, 95% interval coverage and interval width, averaged over at least 200 replicates.

Real-data analysis. The second experiment uses MIMIC-IV patients with acute hypoxemic respiratory failure. The treatment is time from meeting a respiratory-failure definition to invasive ventilation, and the outcome is 28-day survival and restricted mean survival time. A second, separate analysis uses vasopressor initiation in sepsis, the population studied in Step-by-step causal analysis of EHRs to ground decision-making. The primary result is the curve of $\psi(\theta)$ with confidence bands, alongside its spread across the vibration grid of graphs, windows and learners.

Decisive checks. Three checks decide whether the proposal works. The first is semi-synthetic: the doubly robust estimator must hold nominal coverage when exactly one nuisance model is misspecified, while the weighting estimator under-covers or widens sharply at $\theta<1$. If best-tuned truncation matches it, the variance claim fails. The second is a negative-control test on real data. We shift the initiation hazard of a treatment that plausibly has no short-term effect on 28-day mortality, and the estimated effect should be indistinguishable from zero. The weighting estimator's wider intervals should make this check less informative for it than for ours. The third is a directional consistency check. Sternlicht et al. found that each day of delay in mechanical ventilation from symptom onset increased mortality in COVID-19. Our respiratory-failure estimates at $\theta<1$ should therefore not show a clear survival benefit from delay. If they do, and the result survives the graph variations and the $\Gamma$-bound, we will report it as a finding rather than explain it away. Otherwise it points to an error in the cohort definition.