Bedside risk models in the intensive care unit (ICU) now update a patient's predicted chance of death every hour. When that number changes, the natural question is why, and current explanation tools answer by pointing at whichever inputs moved. The problem is that in the ICU many of those movements are caused by clinicians. A blood pressure that recovers after a vasopressor is started, or a risk score that stays low because the model has learned that patients like this one usually get ventilated, both look like good news, and both get explained as good news. A clinician who reads "low risk, driven by stable pressure" and then holds back treatment can turn the prediction into a self-defeating prophecy. The effect a treatment has on risk cannot be read off observational data, because sicker patients get treated for reasons that are partly unrecorded.
We propose splitting each hourly change in predicted risk into two parts. One is the part attributable to the patient's own physiology. The other is the part attributable to treatments, and that part is estimated using an instrumental variable: a source of variation in who gets treated that is unrelated to how sick they are. Here that source is practice variation across hospitals and care units, which works like a quasi-random assignment of patients to more or less aggressive clinicians. The model also reports an "untreated" risk alongside the observed risk. That lets a clinician see when a low score is being propped up by expected rescue treatment. The treatment effect is kept to a small additive curve so it can be plotted and audited.
Core Claim
A dynamic mortality model can be built so that its explanation of each risk change, $\Delta_t = r_t - r_{t-1}$ where $r_t$ is predicted mortality risk at hour $t$, splits into a physiological component and a treatment component. The treatment component is corrected for unmeasured confounding by a control function estimated from practice-variation instruments. Concretely, we fit the risk on the log-odds scale as
$$\text{logit}\, r_t = g(h_t) + \sum_{k} \theta_k(s_t)\, A_{k,t} + \rho_k \hat{v}_{k,t},$$
where $h_t$ is the physiological history up to hour $t$, $g$ is a recurrent network, $A_{k,t}$ indicates whether treatment $k$ (vasopressors, mechanical ventilation) is active, and $\theta_k(s_t)$ is a small additive curve in a low-dimensional severity summary $s_t$ (for example SOFA and lactate). The term $\hat{v}_{k,t}$ is the first-stage residual: the part of treatment $k$ that the instrument and observed history do not predict. Entering it as a covariate absorbs the unmeasured reasons clinicians treated, and $\rho_k$ measures how strong that hidden selection is. The untreated counterfactual risk $r_t^{0}$ sets every $A_{k,t}=0$. The explanation of $\Delta_t$ then assigns $\sum_k \theta_k(s_t)\,\Delta A_{k,t}$ to treatment and the rest to physiology. The rest is further broken down across features with shifted-window integrated gradients.
What is new is where the attribution comes from. The treatment share of a risk explanation is identified by an instrument rather than by the correlations a network happened to learn. A nonzero $\rho_k$ also gives a direct, testable reading of how badly an uncorrected explanation would have misattributed the change.
Where This Sits
Three lines of work motivate the gap. Delta-XAI explains changes between adjacent predictions in online monitoring. Its SWING method integrates gradients along the patient's real recent trajectory to avoid impossible all-zero baselines. We reuse SWING for the physiological component. Its explanations are faithful to whatever the network learned, and that includes treatment-confounded shortcuts. Boosting the interpretability of clinical risk scores with intervention predictions names the self-defeating-prophecy problem and responds by forecasting 13 ICU interventions next to mortality as "intervention fingerprints." Those forecasts are associational, so they tell a clinician what usually happens, not what the treatment does. XMI-ICU tracks SHAP attributions over rolling windows and reports ventilation importance falling as death approaches. It cannot say whether that reflects biology or care withdrawal. Our proposal keeps the online-change framing of the first, answers the question the second raises, and targets the ambiguity the third leaves.
Two papers supply the causal machinery. The control-function approach of Wang et al. enters first-stage residuals into a nonlinear outcome model. We adopt it because two-stage least squares does not carry over cleanly to a logistic, recurrent risk model. Counterfactual Risk Assessments under Unmeasured Confounding uses quasi-random decision-maker assignment as an instrument, together with sensitivity bounds, for static credit risk. It shows that correcting for confounding reverses decisions for 10.1% of applicants. We carry its instrument logic into the ICU, and its bounding idea into our robustness analysis, and we move both from a single decision to hourly trajectories.
The closest longitudinal instrumental-variable method is TIFM, from Instrumental Variable Estimation for Causal Inference in Longitudinal Data with Time-Dependent Latent Confounders. It learns substitute instruments from covariate history with an LSTM, which is a recurrent network with memory. It has been tested only on synthetic and climate data, for a single scalar treatment, with no explanation layer. We deliberately use observable, auditable instruments rather than learned latent ones, because a clinician can argue about whether "this hospital's vasopressor habit" is a fair lever but cannot argue about an LSTM state. TIFM enters as a competing instrument source. Two further papers constrain the design. The reluctant additive model of RAITR shows that treatment-effect curves stay readable when nonlinearity must earn its place under penalty, and we impose the same discipline on $\theta_k$. Safe and Interpretable Estimation of Optimal Treatment Regimes achieves interpretable ICU dosing by matching but explicitly assumes no hidden confounders. We relax exactly that assumption.
Research Program
The instruments come first, because the rest of the program depends on them. In eICU, a multi-center database, the main instrument for each treatment is the admitting hospital's leave-one-out rate of starting that treatment, computed among patients with a similar severity profile in the preceding year. In MIMIC-III and MIMIC-IV, which come from a single center, the instrument is the admitting care unit's recent initiation rate. Unit assignment is partly driven by bed availability. We report first-stage strength for every instrument. We restrict the study to two treatments, vasopressors and mechanical ventilation, because each treatment needs its own instrument. The literature already notes that multi-treatment instrumental-variable models become under-identified, and we do not claim to solve that.
The main threat is the exclusion restriction: hospitals that ventilate more may also differ in nursing or quality in ways that affect death directly. We attack this three ways. We adjust for hospital-level case mix and size. We use negative-control outcomes that treatment practice should not affect, such as in-hospital falls or length of stay before ICU admission. We report sensitivity bounds in the style of the counterfactual risk assessment paper, showing how large a direct instrument-to-outcome path would have to be to erase the estimated treatment effect.
The model itself is the equation above, trained end to end. The first stage is a logistic model of treatment on instrument, history summary, and hospital covariates, fitted with cross-fitting so its residuals are out-of-sample. The physiological network $g$ is the same LSTM used in the Delta-XAI codebase (AITRICS/Delta-XAI), which lets us reuse its MIMIC-III preprocessing and SWING implementation. The explanation shown to a clinician has three parts. The first is observed risk next to untreated risk over time. The second is the treatment share of each hourly change. The third is a SWING breakdown of the physiological share.
Baselines
The naive reference is a static admission score: APACHE IV on eICU and SAPS II and SOFA on MIMIC-III. It carries no explanation of risk changes at all. XMI-ICU reports APACHE IV at an AUROC of 69.9 for 24-hour mortality on eICU. Loreaux et al. report SAPS II at 0.76 and SOFA at 0.69 on MIMIC-III.
The strongest discriminative competitor is the XMI-ICU model: gradient-boosted trees (XGBoost) over rolling 6- to 24-hour summary windows, explained with time-resolved TreeSHAP. The paper reports an AUROC of 88.2 for 24-hour mortality and 92.0 for 6-hour mortality on eICU. We refit it on our eICU cohort definition with the same splits and the same hyperparameter search budget as our model, so the comparison uses identical data rather than borrowed numbers.
The strongest explanation competitor is an LSTM with treatments as ordinary inputs, explained by SWING. This isolates what the instrument adds, since the attribution method stays the same. On MIMIC-III we also run the multitask intervention-fingerprint LSTM of Loreaux et al., which reports a mortality AUROC of 0.82 on its 18,335-stay cohort; we replicate that cohort definition. Delta-XAI reports that SWING wins on 9 faithfulness metrics, but the file gives no individual scalar values, so no reported number was found on Lacuna for SWING faithfulness. We will compute those metrics ourselves.
Three ablations isolate the key ingredient. The first uses the same additive treatment structure with the control-function term removed, which amounts to assuming no unmeasured confounding. The second replaces our observable instruments with TIFM-learned latent instruments. The third replaces the point estimate with sensitivity bounds only.
Our model "beats" the baselines in a specific sense. First, its discrimination must stay within 0.01 AUROC of the refit XMI-ICU and LSTM models; we are not claiming better prediction. Second, on the semi-synthetic benchmark, where the truth is known, its treatment share of $\Delta_t$ must have lower error than every baseline. Third, in the hide-a-confounder test on real data, its treatment effect must move measurably less than the no-instrument ablation's.
Why not just…?
Why not just show predicted interventions, as intervention fingerprints do? Fingerprints tell a clinician that a patient like this one usually gets vasopressors. They do not say how much risk the vasopressors are removing. That quantity is what separates "stable" from "sick but being rescued." The fingerprint probabilities inherit whatever unrecorded bedside judgment drove historical treatment. We keep fingerprints as a baseline, and the semi-synthetic benchmark, with its known effect, will show whether they carry the same information as an untreated risk. If they do, our added machinery is unnecessary, and we will report that.
Why not just feed treatments into the network and read their SWING attributions? This is the most natural alternative, and it is the direct ablation. A gradient through a network trained on confounded data measures the association the network learned. Sicker patients get treated, so that association can even carry the wrong sign, with treatment looking harmful. The fitted $\rho_k$ tells us directly whether hidden selection is present. If $\rho_k$ is near zero and SWING's treatment attributions match ours, this alternative is good enough in that setting.
Why not just assume the rich EHR record captures the confounders and use G-computation or matching? This is a real threat. If the recorded vitals, labs, and notes capture why clinicians act, adjustment without an instrument will match our estimates with less variance. Weak instruments also pull two-stage estimates toward the biased answer and inflate uncertainty. Parikh et al. state openly that their matching depends on no hidden confounders. The counterfactual-risk paper shows its conclusions flipping under modest hidden bias, with an apparent disparity vanishing at a factor of 1.69. The hide-a-confounder experiment settles the question empirically. We withhold a strong measured confounder, such as lactate trajectory or a note-derived frailty indicator, from all methods and check which method's estimate stays closest to the estimate made with it included. If the no-instrument ablation holds up as well, we will recommend it and report the instrument as unnecessary.
Why not just learn the instruments, as TIFM does? Learned instruments sidestep the search for a natural lever, but their validity rests on the "no single-cause" assumption. They are also opaque, which defeats the purpose of an auditable explanation. We run TIFM as an instrument-source ablation. If it matches practice-variation instruments on the semi-synthetic benchmark, that is informative. It still would not give a clinician an instrument they can scrutinize.
Proposed Experiments
The decisive experiment is semi-synthetic, because there is no ground truth for the effect of treatment on real patients. We start from real eICU and MIMIC-III physiology. We then simulate treatment assignment that depends on observed history, on a hidden severity variable derived from withheld features, and on the real hospital-level instrument. Mortality is simulated with known additive treatment effects $\theta_k$ of varying size. Varying the hidden-selection strength and the instrument strength traces out where our method wins and where weak instruments make it worse than naive adjustment. The primary metric is the error of the treatment share of $\Delta_t$ and of the untreated risk $r_t^0$ against the simulated truth. Secondary metrics are AUROC and calibration of $r_t$.
On real data, we run the hide-a-confounder test described above on eICU and MIMIC-III. We check first-stage strength and the negative-control outcomes for every instrument. We also do external transfer to MIMIC-IV, whose myocardial-infarction subset XMI-ICU uses for validation at a reported AUC of 80.0 with its top eight features.
A clinical plausibility check targets the self-defeating prophecy directly. It asks whether patients with low observed risk but high untreated risk, the "rescued" group, show high SOFA, lactate, and later escalation more often than patients whom the uncorrected model rates equally low. If the instrument-corrected untreated risk identifies this group better than intervention fingerprints or SWING-on-treatments, the central claim holds. If it does not, or if the instruments turn out weak across hospitals, the result is a clear negative finding about practice-variation instruments in ICU risk explanation.
References
- Delta-XAI: A Unified Framework for Explaining Prediction Changes in Online Time Series Monitoring
- Boosting the interpretability of clinical risk scores with intervention predictions
- XMI-ICU: Explainable Machine Learning Model for Pseudo-Dynamic Prediction of Mortality and Heart Attack in the ICU
- Insurance policy and cropping structure adjustment toward staple grains in China: implications for food system resilience and security
- Counterfactual Risk Assessments under Unmeasured Confounding
- Instrumental Variable Estimation for Causal Inference in Longitudinal Data with Time-Dependent Latent Confounders
- A reluctant additive model framework for interpretable nonlinear individualized treatment rules
- Safe and Interpretable Estimation of Optimal Treatment Regimes