Do Pulse-Oximeter Errors in the ICU Follow Patients Home?

A pulse oximeter is the clip on a patient's finger that estimates blood oxygen by shining two wavelengths of light through the skin and comparing how much each is absorbed. It is a spectrophotometer, an instrument that infers a concentration from light absorption. Because melanin also absorbs light, the device overestimates oxygen saturation in patients with darker skin relative to the invasive reference measurement taken from arterial blood. A recent causal analysis of two intensive-care databases found that this optical error barely changes whether Black patients are put on a mechanical ventilator. It does keep them on the ventilator longer: 2.3 extra hours in eICU and 7.4 in MIMIC-IV (Path-Specific Effects for Pulse-Oximetry Guided Decisions in Critical Care). That study stopped at the ICU door. We do not know whether a few extra ventilator hours caused by a measurement artifact lead to tracheostomy, pneumonia, readmission, or death in the following year. Hours of ventilation are a surrogate endpoint, and a large literature warns that surrogate gains or harms often fail to carry over to hard outcomes (Sohal et al., Hu et al.).

We propose to estimate the long-term consequences of oximeter error by combining two retrospective cohorts that each have only part of the needed follow-up. eICU is large but ends at hospital discharge. MIMIC-IV is smaller but, as far as we know, links to post-discharge death records for roughly a year; this must be confirmed for the database version we use. The core idea is a "surrogate bridge." We estimate the oximeter-driven effect on the weaning process in the large short-follow-up cohort. We estimate how that weaning process affects one-year outcomes in the long-follow-up cohort. Then we test whether the combined estimate agrees with a direct long-term estimate computed inside MIMIC-IV alone. If the two agree, the bridge is a reusable way to extend short-window causal findings. If they disagree, we have concrete evidence that ventilator hours are an unsafe surrogate for this harm.

Core Claim

Oximeter bias acts through repeated weaning decisions: at each bedside check, a falsely reassuring reading can delay extubation. We therefore claim the right estimand is sequential, not a single average over the whole stay. We also claim the long-term effect can be identified by joining a short-follow-up cohort to a long-follow-up one, under an explicit surrogate assumption that can be tested. The assumption is that, conditional on measured baseline and ICU covariates, oximeter error affects post-discharge outcomes only through the ventilation and weaning trajectory.

This differs from the existing path-specific analysis in three ways. That analysis uses a static estimator. Its outcomes are confined to the stay. It treats the invasive arterial reference as available, even though arterial blood gas draws are sparse and are themselves clinical decisions, a limitation noted in the research file. We keep its mechanism, the effect of race on outcomes that runs only through the discrepancy $V = SpO_2 - SaO_2$ (pulse-oximeter reading minus arterial co-oximetry reading). We extend the outcomes past discharge and model the process over time.

Research Program

The first component rebuilds the cohort of the path-specific study in both databases: admissions with paired oximeter and arterial readings, and baseline confounders and clinical indicators defined the same way. This lets us reproduce the published in-stay effects (2.3 and 7.4 hours) before changing anything.

The second component replaces the static estimator with a marginal structural model. This is a regression fit on a reweighted population in which, at each time block of the ventilated period, the extubate-or-continue decision no longer depends on measured time-varying severity. Standard sequential inverse-probability weights multiply across time steps and tend to explode. We will therefore use kernel optimal weighting, which solves a convex program that directly minimizes covariate imbalance at every step while penalizing large weights (Optimal balancing of time-dependent confounders for marginal structural models). In a longitudinal HIV cohort, that method recovered a protective treatment effect where ordinary weighting gave high-variance, non-significant estimates.

Arterial draws are missing in many time blocks. We handle this with a separate weight for "an arterial draw happened in this block," modeled on the same covariates. The discrepancy is then estimated only where the reference exists, reweighted to the whole ventilated period.

For post-discharge follow-up in MIMIC-IV, patients are censored when the death-record linkage ends, and possibly earlier if linkage is incomplete. Censoring may be informative, since sicker patients may be transferred or lost. We therefore add inverse-probability-of-censoring weights, reflecting the concern about informative right-censoring raised in the limited-follow-up literature.

The third component is the bridge. In eICU, we estimate the oximeter-mediated effect on the full weaning trajectory, including time to extubation, reintubation within 48 hours, and tracheostomy. In MIMIC-IV, we estimate how that trajectory affects one-year mortality, readmission, and ventilator-associated pneumonia coded in later encounters. We compose the two estimates and propagate uncertainty by bootstrapping both cohorts jointly.

eICU spans many hospitals, while MIMIC-IV comes from one. The composition therefore also requires the trajectory-to-outcome relationship to transport across settings. We check this by reweighting MIMIC-IV to eICU's covariate distribution.

We choose propensity models by covariate balance rather than predictive accuracy. Balance is measured with the standardized mean difference, the gap between group means divided by their pooled standard deviation. This follows the finding in High-throughput target trial emulation for Alzheimer's disease drug repurposing with real-world data that selecting by prediction accuracy is suboptimal and that LSTMs did not reliably beat regularized logistic regression. Where the race-by-discrepancy strata overlap poorly, we will report overlap-weighted estimates alongside full-population ones. Overlap weighting down-weights patients with no comparable counterparts in the other group; Assessing racial disparities in healthcare expenditure using generalized propensity score weighting showed it raised the effective sample size in a sparse subgroup from 155 to 1,105. We will state that this narrows the target population rather than hide it.

We expect power to be the binding constraint. The MIMIC-IV cohort in the prior study has 4,897 admissions, and a mediated shift of a few hours may move one-year mortality by less than a percentage point. We will therefore pre-register a smallest effect of interest and report equivalence bounds. A tight bound near zero is a publishable answer: it would say the in-stay disparity, while real, does not propagate to mortality.

Baselines

The naive reference point is the unadjusted difference in one-year mortality between Black and White ventilated patients in MIMIC-IV. It mixes every pathway, oximeter-driven or not, and serves only to show how much adjustment moves the estimate.

The conventional epidemiological baseline is a Cox proportional-hazards model of one-year mortality with race, the discrepancy $V$, and the same confounders as covariates. It uses the same cohort and the same covariate set, with no tuning beyond standard spline terms for continuous variables. The prior studies in the file suggest regression can hide real differences. In MEPS, a conventional analysis gave $p = 0.122$ where overlap weighting found a \$2,386.84 gap with $p < 0.001$ (Liu et al.). We still include it because it is what most clinical papers would run.

The strongest existing competitor is the self-normalized doubly robust path-specific estimator of Path-Specific Effects for Pulse-Oximetry Guided Decisions in Critical Care, applied unchanged except that the outcome becomes one-year mortality in MIMIC-IV. It is the only published estimator designed for exactly this path. In that paper's semi-synthetic benchmark it had an error of 0.003 versus 0.024 for an X-learner. We run it with the same confounders, the same nuisance-model learners, and the same cross-fitting folds as our method, so that any difference comes from the sequential structure and the censoring and missing-reference weights.

Our method beats it if it does two things. First, on a semi-synthetic benchmark built from real MIMIC-IV covariates, with ground-truth sequential weaning delays and informative censoring, it achieves lower error and correct confidence-interval coverage. Second, on real data it gives confidence intervals that are no wider, or that differ in point estimate by more than the sampling noise shown in bootstrap comparisons.

We also run sequential inverse-probability weighting with logistic regression chosen by balance, with and without weight truncation at the 1st and 99th percentiles. This isolates what kernel optimal weighting adds.

Three ablations isolate the key ingredients. The first compares static versus sequential estimation with everything else fixed. The second drops the weights for missing arterial draws. The third compares the bridge estimate with the direct MIMIC-IV-only estimate.

Why not just…?

Why not just swap the outcome in the existing static estimator? This is the most serious threat. If weaning decisions in practice respond to a summary of the discrepancy rather than to readings block by block, the static estimator may be nearly as good and much simpler. The semi-synthetic benchmark settles this. We generate data under both a summary-driven and a block-driven weaning policy. If the static estimator matches ours under the realistic policy, and the real-data estimates agree, we will say so and recommend the static estimator plus censoring weights as the practical tool. The sequential model would then be kept only as a robustness check.

Why not just put race and $V$ in a Cox model of one-year mortality? A Cox coefficient on $V$ does not isolate the path from race through oximeter error. It is also biased when ICU severity is both affected by earlier ventilation and a driver of later weaning, which is the time-varying confounding problem that Optimal balancing of time-dependent confounders for marginal structural models documents for standard models. We report the Cox model anyway. The semi-synthetic benchmark shows how far it drifts from the truth when severity feeds back on itself.

Why not just multiply the 7.4 extra hours by a published estimate of mortality per ventilator hour? This back-of-envelope version is the surrogate bridge without the checks. It assumes the harm of an extra hour does not depend on why the hour was added. An hour added because the oximeter falsely reassured the team, in a patient who was otherwise ready for extubation, may carry a different risk than an hour added because the patient was sicker. Our direct MIMIC-IV estimate, compared against the bridge, tests exactly this. No reported per-hour mortality figure was found on Lacuna for this comparison, so the file gives us nothing to plug in. This is a further reason to estimate the trajectory-to-outcome link ourselves.

Why not just use truncated inverse-probability weights instead of kernel balancing? Given the result in High-throughput target trial emulation that simple balance-selected logistic models hold up well, this may suffice. It is included as a baseline. We will prefer it if its imbalance and effective sample size are comparable.

Proposed Experiments

We first replicate the published in-stay effects in both databases, within bootstrap uncertainty. No reported result was found on Lacuna for any post-discharge outcome of oximeter error, so beyond replication there is no external number to match.

We then build the semi-synthetic benchmark. It keeps real MIMIC-IV covariates and arterial-draw patterns and simulates weaning under summary-driven and block-driven policies, with informative censoring. On it we compare bias, root-mean-squared error, and confidence-interval coverage across all baselines and ablations.

On real data, the primary outcome is one-year all-cause mortality in MIMIC-IV. Secondary outcomes are tracheostomy, reintubation within 48 hours, and 30-day readmission.

Three decisive checks follow. The first is agreement between the bridge and direct estimates; a pre-registered disagreement threshold rejects the surrogate assumption. The second is a negative-control outcome that the oximeter pathway should not plausibly affect, such as post-discharge fracture diagnoses; a nonzero estimate there signals residual confounding. The third is a sensitivity analysis reporting how strong an unmeasured confounder would have to be to explain away any nonzero effect.

If the equivalence bound excludes any mortality effect larger than the pre-registered threshold, we report that the in-stay disparity does not propagate. If it does not exclude it, we report the size of cohort a definitive study would need.