Who Else Needed the Ventilator? Conflict Graphs for Retrospective Cohorts Under Hospital Contention

Most studies that estimate treatment effects from hospital records assume that one patient's care does not affect another's. In a strained intensive care unit (ICU) that assumption is false in a specific, recordable way. When two patients need the same scarce resource during overlapping hours, such as a dialysis machine, a ventilator, or the one free bed, giving it to one delays or denies it to the other. A retrospective study of "early versus delayed treatment" then blends two different things. The first is what delay does to a patient's own biology. The second is what it costs to be the patient who lost the contest. We propose to rebuild this contention explicitly from timestamps as a conflict graph: a network in which each patient is a node and an edge joins two patients who competed for the same resource unit in the same window. That graph then lets us estimate two separate effects from observational data. One is the patient's own treatment effect. The other is the "displacement" effect of their competitors' treatment.

The opportunity exists because two literatures each hold half of the answer. The conflict graph design of Kandiros, Pipis et al. shows how to estimate direct and spillover effects when the conflict graph is known. It works only when the experimenter randomizes, and it has no way to adjust for patient covariates. Target trial emulation on electronic health records, as in Step-by-step causal analysis of EHRs, does careful confounder adjustment. It also lists "no interference" as an assumption it simply relies on. The two-sentence version of our proposal is this: build the conflict graph of who competed with whom from resource-use timestamps, then run a doubly robust observational estimator over that graph's neighborhoods. Doing so separates how a delay harms the delayed patient from what it costs when competitors are treated first.

Core Claim

In retrospective cohorts drawn from capacity-constrained periods, a resource-specific conflict graph supports estimates that no covariate-only analysis can deliver. Its central contribution is a displacement effect, meaning the change in a patient's outcome when their conflicting neighbors are treated more aggressively.

A secondary and more contestable claim is that the graph also removes confounding of treatment timing by queueing state. A reviewer could argue that a scalar occupancy covariate handles that confounding equally well, and we treat that argument as a serious competitor rather than a straw man.

The intended contribution is the estimand and the identification strategy, not a new solver. Prior conflict-graph work in medicine is not causal at all. The kidney-exchange clearing of Zhao and Dickerson uses the graph only to pack donor cycles, with deterministic transplant counts as weights.

Research Program

Graph construction. For each scarce resource class $r$, we form a vertex for every patient episode in which the patient was clinically eligible for $r$. Eligibility is defined by a pre-specified clinical trigger, for example meeting oxygenation criteria for intubation or a renal threshold for continuous dialysis. Two eligible episodes are joined by an edge when their eligibility windows overlap and they draw on the same physical pool, such as the same unit's machines or the same bed bank.

This is the abstraction that wireless scheduling uses. There, links sharing a clique cannot transmit at once and their airtime shares must sum to at most one (Effects of Interference on Wireless Mesh Networks). The clinical analogue is that patients in a clique of the conflict graph cannot all receive the resource at once. Pool capacity bounds the number treated in any clique, so a pool's capacity takes the place of the single airtime budget. The point of building the graph per resource, rather than per ward-day, is that contention follows the resource and not the floor plan. Two patients on one ward who need different devices do not compete. Two patients on different wards who share one dialysis fleet do.

Estimands. Let $W_i$ be patient $i$'s treatment indicator or treatment time, and let $N(i)$ be $i$'s neighbors in the conflict graph. We define a neighborhood exposure $A_i = \sum_{j \in N(i)} W_j / c_r$, which is the treated-neighbor load relative to the pool capacity $c_r$. The two target quantities are

$$ \tau_{\mathrm{dir}} = \mathbb{E}\left[Y_i(1, a) - Y_i(0, a)\right], \qquad \tau_{\mathrm{disp}}(a, a') = \mathbb{E}\left[Y_i(w, a) - Y_i(w, a')\right], $$

where $Y_i(w, a)$ is patient $i$'s potential outcome (28-day mortality) under own treatment $w$ and neighbor load $a$.

Neighbor load has thin support at high values. Fixing neighbor exposures at chosen levels would therefore violate positivity, the requirement that every patient type could plausibly receive every exposure level. Following Incremental Causal Effect for Time to Treatment Initialization, we instead define the displacement contrast through an incremental intervention: every neighbor's treatment-initiation hazard is multiplied by $\theta$. That paper uses this device to avoid exactly this positivity problem for a single patient's timing. Extending it to neighbors' hazards is our methodological addition.

Estimation. We extend the augmented inverse probability weighting (AIPW) estimator used in Step-by-step causal analysis of EHRs. That estimator combines a model of who gets treated with a model of outcomes, and remains consistent if either model is correct. Our extension uses a joint propensity for $(W_i, A_i)$, built from per-patient hazard models conditional on covariates and on the current graph state. The outcome regression takes $(X_i, W_i, A_i)$ as inputs.

The inverse-weighting component is the Horvitz–Thompson structure of the conflict graph design, with estimated propensities in place of designed ones. That paper's variance analysis shows variance scaling with the largest eigenvalue of the conflict graph, $O(\lambda(H)/n)$, rather than with maximum degree. Its proof relies on designed randomization, so we do not inherit the bound. We use it to motivate a dependence-robust variance estimator whose covariance terms are restricted to pairs within two hops in the graph. We will check its coverage in simulation rather than assert it.

Data. One constraint shapes the plan. To our knowledge, MIMIC-IV, the de-identified Boston ICU database used by both Step-by-step causal analysis of EHRs and the MIMIC-IV pipeline, shifts dates independently for each patient. If so, true cross-patient concurrency cannot be recovered from it, and this must be verified first. MIMIC-IV is therefore used as a covariate and outcome source for semi-synthetic studies, in which we simulate arrival schedules and capacity so that the true direct and displacement effects are known.

The real-data target is a cohort with real calendar time from a strained period. The natural candidate is the São Paulo COVID-19 cohort of Sternlicht et al.: 3,020 admissions in March–August 2020, of whom 592 were intubated. Using it requires a data-use collaboration. If access fails, the real-data component moves to an institutional EHR with true timestamps.

Baselines

The naive reference point is the published analysis itself. This is a multivariable Cox proportional hazards model, which relates delay to the rate of death over time, adjusted for the 4C mortality score. On the São Paulo cohort it reports an adjusted hazard ratio of 1.018 per day of delay from symptom onset (95% CI 1.005–1.03) (Sternlicht et al.). We will reproduce it on identical inclusion criteria. Our estimate counts as different from it only if the direct-effect interval for daily delay excludes the reproduced point estimate, or if the displacement interval excludes zero.

The strongest existing observational method is no-interference AIPW in the style of Step-by-step causal analysis of EHRs. That style includes a target-trial-aligned time zero, which avoids immortal time bias (crediting treated patients with survival time before treatment began, when they could not have died as "treated"). It also includes the paper's vibration analysis, which reruns the estimate across alternative analytic choices. That paper reports qualitative agreement with randomized-trial meta-analyses for albumin in sepsis and no numeric effect size. For interference-aware observational estimators on clinical data, no reported result was found on Lacuna. This baseline will use the same covariates, the same learners (random forests with an equal hyperparameter search budget), and the same cross-fitting folds as our estimator.

The serious competitor is the same AIPW with contemporaneous unit occupancy, divided by capacity, added as a covariate. This tests whether a single scalar measure of strain does everything the graph does.

Three further comparisons isolate the graph itself. First, we replace resource-specific edges with ward-day cliques, which tests whether fine structure matters. Second, we rewire edges at random while preserving each patient's degree, which tests whether the specific topology carries signal. Third, we run the Horvitz–Thompson-only version without the outcome model, which tests what double robustness adds. In semi-synthetic data, "beating" a baseline means lower bias and nominal 95% coverage at matched or smaller interval width.

Why not just…?

Why not just add hospital occupancy as a covariate? This is the real threat, and for the confounding half of the claim it may well be enough. If strain affects a patient only through total census, occupancy captures it and the graph adds nothing. The occupancy-adjusted baseline and the ward-day ablation exist to show this if it is true. What occupancy cannot provide is the displacement estimand. It summarizes how busy the unit was, not whether this patient's specific competitors were treated. The semi-synthetic arm will include a regime in which contention is unit-wide, where we expect occupancy to tie with our method, and a regime in which a device pool is shared across units, where we expect it to fail. If occupancy ties in both regimes, we will report that the graph's value lies only in the displacement estimand.

Why not just use cluster-robust standard errors or mixed-effects models by ward and week? These methods correct uncertainty for correlation within administrative clusters. They do not change the estimand, so the point estimate still assumes no interference. They also draw cluster boundaries that ignore pathways shared across units. The analysis in the conflict graph design indicates that dependence follows interference structure, not maximum group size. We test this directly by comparing interval coverage of clustered errors against our graph-restricted variance in simulations where the truth is known.

Why not just use occupancy as an instrument for delay? This is a natural econometric move, but it conflicts with the phenomenon under study. A crowded unit affects a patient through channels other than their own treatment timing, including the displacement channel we aim to estimate. That breaks the exclusion restriction, the requirement that an instrument affect the outcome only through the treatment. We will still run it in semi-synthetic data to show the size of the resulting bias when displacement is nonzero.

Proposed Experiments and Decisive Checks

The semi-synthetic study draws covariates and outcome models from MIMIC-IV episodes. It then simulates arrival processes at loads approaching and exceeding capacity, with displacement effects of zero, small, and large magnitude. We vary whether contention is unit-wide or confined to resource pools that span units. For every estimator we measure bias, root-mean-square error, and interval coverage for $\tau_{\mathrm{dir}}$ and $\tau_{\mathrm{disp}}$.

The proposal succeeds only under three conditions. First, the method must recover a planted displacement effect that all baselines miss. Second, it must not invent one when the planted effect is zero. Third, it must beat the ward-day ablation in the cross-unit regime.

On real data with true timestamps, we report direct and displacement effects for intubation timing. We pair these with two falsification checks. Patients who were never eligible for the resource, and so have no edges, must show a null "displacement" effect. As a placebo exposure, neighbors' treatments occurring after the index patient's outcome window must also show a null effect. If the real-data displacement estimate is null and the direct effect matches the reproduced Cox estimate, that is itself informative. It would suggest that published timing effects from the pandemic peak were not contaminated by contention.