ICU risk models learn from two different kinds of information at once. One is the patient's physiology: lactate, blood pressure, creatinine. The other is the care process: which labs were ordered, how often vitals were charted, how long since the last blood gas. The second kind is genuinely predictive, because a clinician who orders lactate every hour is worried. It also differs from hospital to hospital and from one patient group to another. Current models mix the two into a single score. A clinician looking at an alert cannot tell whether the patient is deteriorating or is simply being watched closely. A hospital adopting the model cannot tell which part of it will break on its own patients.
We propose to build ICU risk models with two explicitly separate channels. A physiology channel sees only measured values, and clinical prior knowledge (which direction each vital or lab moves risk) constrains how it may use them. A care-process channel sees only measurement timing and frequency. The model's risk is their sum, so each alert splits exactly into "physiology says" and "care pattern says." Our central claim is that this split matters in practice. Across hospitals and demographic groups, most of the failure in transfer and fairness should sit in the care-process channel. If so, a new site can recalibrate that channel alone with few labels, and the alert can tell the bedside clinician when a high score rests mainly on how the patient is being managed.
Why this gap is real
The tension is already in the literature. P-BiLSTM treats missingness masks as intentional clinical signal and shows they improve mortality prediction on PhysioNet 2012 (AUC 0.923 versus 0.906 for a plain BiLSTM). It evaluates one dataset and never asks whether that signal travels. MIMIC-IF audits twelve attribution methods on MIMIC-IV. It finds that attention weights fail remove-and-retrain checks (retrain without the top-attributed features and see whether accuracy drops). It also finds that attributions diverge across ethnic groups and that care itself differs by group: Black and Hispanic patients had shorter mechanical ventilation. Its work is a post-hoc audit and does not change the model. YAIB shows that preprocessing and local definitions across MIMIC, eICU, HiRID and AUMCdb often matter more than architecture. These papers motivate the proposal: they suggest the care-process signal carries institutional and demographic practice, but none isolates it.
Two papers constrain the design. Guo et al. found that invariance methods failed to beat plain training on pooled data across a 12-year MIMIC-IV window, because the shifting features were still predictive. We therefore do not penalize the care-process channel toward invariance. We keep it and make it separately adjustable. FairerOPTH supplies the guiding analogy. Routing ophthalmic diagnosis through a biological lesion bottleneck suppressed age and sex shortcuts without lowering accuracy. Our physiology channel plays the role of that bottleneck, but uses priors that are cheap to write down rather than 67 densely annotated lesion types. The monotonicity penalty comes from RMLP, which enforced irreversible risk trajectories in Alzheimer's disease. We apply the same idea to the direction of effect of each variable rather than to time.
Core Claim
The model's log-odds of an outcome for patient $i$ at time $t$ is
$$ \text{logit}\, p_{it} = f_\theta(v_{it}) + g_\phi(m_{it}) + h_\psi(s_i), $$
where $v_{it}$ are the most recent measured values with no timing information, $m_{it}$ are the measurement indicators, counts and time-since-last-measurement for each variable, and $s_i$ are static covariates such as age and sex. We keep $s_i$ because YAIB found they help almost everywhere. Here $f_\theta$ is a neural additive model with low-order interactions, trained with a hinge penalty whenever its partial effect goes against a clinically agreed direction. For example, rising lactate, falling mean arterial pressure and rising creatinine may only raise risk. The directions are taken from organ-failure scoring conventions, and each is documented. The function $g_\phi$ is unconstrained.
Because the decomposition is additive, it is exact by construction. It does not depend on a post-hoc attribution method that MIMIC-IF showed can be unfaithful.
The claim has three falsifiable parts. First, when a model trained at one site is applied at another, the miscalibration and AUROC loss should come mostly from $g_\phi$. Second, differences in subgroup performance and subgroup attribution should concentrate in $g_\phi$. Third, refitting only $g_\phi$ and an intercept on a small labeled sample from the target site should recover most of the transfer gap. Full fine-tuning on the same sample should need more labels to match it.
Research Program
We build all cohorts with the YAIB pipeline for in-hospital mortality, acute kidney injury and sepsis on MIMIC-IV, eICU, HiRID and AUMCdb, so cohort definitions match published numbers.
One leakage path must be closed. Carrying the last value forward lets the value channel infer how stale a measurement is. We therefore give $f_\theta$ only values, and we measure residual leakage with a probe that tries to predict $m_{it}$, and the source site, from $f_\theta$'s hidden representation. If the probe succeeds well above chance, the separation is not clean and we report it as such.
Faithfulness of each channel is checked with remove-and-retrain degradation, following MIMIC-IF, rather than assumed.
For the workflow component we design the alert so that it adds at most one line to an EHR risk display: the score, plus a flag when more than half of the score above baseline comes from the care-process channel. This follows the "unremarkable AI" principle in the human-centered CDSS review, which documents that dense point-of-care explanations add cognitive load. We evaluate the flag offline first, then in a small vignette study with ICU clinicians. We say plainly that this is not a live deployment. The same review notes that only 7 of 20 core studies were live, and ours would join the retrospective majority.
Baselines
The naive reference point is logistic regression and LightGBM on YAIB features, trained at the source site and applied unchanged at the target. YAIB reports mortality AUROC of 0.84 to 0.87 across datasets for its models. That range is the in-domain bar our model must stay within, at roughly 0.01 AUROC, to be acceptable.
The strongest competitor is a temporal deep model or gradient-boosted model trained on pooled multi-center data with missingness indicators included. In YAIB, eICU-trained models generalized better than single-center ones, and Guo et al. found pooled training matched or beat invariance methods. We run it with leave-one-site-out training, giving it the same features, the same hyperparameter search budget (equal trials per method) and the same compute. For reference on a different cohort, MIMIC-IF reports AUROC 0.955 and AUPRC 0.769 for IMV-LSTM on MIMIC-IV. That number is not directly comparable to YAIB's cohort, so we retrain IMV-LSTM in our pipeline instead of quoting it. To beat pooled training, our model must match its held-out-site AUROC within 0.01 and reduce at least one of two quantities: held-out calibration error, or the worst-subgroup AUROC gap.
For adaptation, the competitor is full fine-tuning and whole-model recalibration on $k \in \{100, 300, 1000\}$ labeled target stays. Our model wins if refitting only the care-process channel reaches equal AUROC and calibration with fewer labels.
Two ablations isolate the key ingredients. One removes the monotonicity priors while keeping the channel split, which tests whether clinical knowledge is what keeps site-specific practice out of $f_\theta$. The other keeps the priors but feeds timing into both channels, which tests whether the separation itself matters.
Why not just…?
Why not just drop the missingness indicators and impute? This is a real threat. If a model with no care-process channel transfers and is as fair as ours at equal held-out-site accuracy, our contribution shrinks to recommending exactly that. P-BiLSTM's ablation shows that removing the masks lowers accuracy in-domain, but it is silent on transfer. We run imputation-only models on every leave-one-site-out split and report the result either way.
Why not just train on pooled multi-center data? Guo et al. and YAIB both favor this, and it is our main baseline. It cannot, however, say which part of the score to adjust at a new site or how to explain an alert. The adaptation-efficiency experiment and the subgroup analysis show whether separation adds anything beyond pooling. If pooled training already removes the subgroup gap, we will report that.
Why not just fit a gradient-boosted model and group its SHAP values into physiology versus care-process features? This would give a similar diagnosis cheaply. But MIMIC-IF shows that attributions can be unfaithful and can diverge by subgroup. A post-hoc split also cannot be refit channel by channel. We compute this grouping anyway and check whether it agrees with our exact decomposition. If it agrees and recalibrating the full gradient-boosted model is as label-efficient as our channel refit, the architecture is not needed.
Proposed Experiments and Decisive Checks
The first check is transfer attribution. For each source-target pair, we compare how much $f_\theta$ and $g_\phi$ each contribute to the calibration shift, measured as the change in mean contribution among outcome-negative patients. The prediction is that $g_\phi$ dominates.
The second check is fairness. On MIMIC-IV and eICU we use ethnicity groups, and on all four datasets age and sex groups. We measure the subgroup AUROC gap and subgroup attribution divergence per channel. MIMIC-IF's ventilation-duration finding predicts that the divergence will concentrate in the care-process channel.
The third check is label efficiency. We plot held-out AUROC and calibration against $k$ for refitting only the care-process channel versus fine-tuning the whole model.
The fourth check is workflow. On held-out sites at fixed 80% sensitivity, we measure alerts per 100 patient-days. We also measure how often flagged alerts were true positives, compared with unflagged ones. In the vignette study, clinicians rate whether the flag changed their next action and how long they took to verify the alert.
The idea is refuted if any of three things happens. The care-process channel might not carry a disproportionate share of the shift. Dropping that channel might equal our model on every metric. Or channel-only recalibration might be no more label-efficient than full fine-tuning.
References
- Predicting ICU Mortality from Heterogeneous Clinical Events with Prior Medical Knowledge
- MIMIC-IF: Interpretability and Fairness Evaluation of Deep Learning Models on MIMIC-IV Dataset
- Yet Another ICU Benchmark: A Flexible Multi-Center Framework for Clinical ML
- Evaluation of domain generalization and adaptation on improving model robustness to temporal dataset shift in clinical medicine
- Fairer AI in ophthalmology via implicit fairness learning for mitigating sexism and ageism
- Learning the Irreversible Progression Trajectory of Alzheimer's Disease
- Human-centered design and evaluation of AI-empowered clinical decision support systems: a systematic review