A hospital risk score is built to change what clinicians do: flag a patient, start an intervention, escalate care. Yet these scores are trained on records in which clinicians already acted. A lab value measured after a vasopressor or dialysis session carries the fingerprint of that treatment. A model can therefore learn "this patient looks fine because someone already treated them," and it will look excellent in retrospective evaluation. The failure appears only when the score is used to change care.
Decision curve analysis (DCA) is the standard tool for judging whether a clinical score is worth using. It scores a model by its net benefit: true positives found, minus false positives weighted by the clinician's cost ratio, across a range of decision thresholds. DCA inherits this blind spot completely, because it is computed on the same historically treated data. We propose to borrow a tool from reinforcement learning to find and remove the leak. That tool is the inverse-dynamics model, a network trained to guess which action was taken from how the state changed. It was developed to separate what an agent controls from what it does not. We use it with the sign flipped. Features whose changes reveal the clinician's action are exactly the features through which the historical treatment policy leaks into a risk score. We then test whether removing or freezing them makes net benefit survive a change in treatment policy.
Core Claim
Our claim has three parts. First, a per-feature "action-revealing" score computed with multi-step inverse dynamics identifies which clinical variables are downstream of treatment. Second, risk models that rely on high-scoring features overstate net benefit under standard DCA, and the overstatement grows with how much the treatment policy shifts between training and deployment. Third, a model trained on features audited this way loses less net benefit under policy shift than the alternatives. The comparison holds the threshold interval fixed and covers models selected by AUC, by bounded proper scoring rules, or by simply deleting treatment indicator columns.
The novelty is not "feature selection evaluated with DCA." That is routine: the ARDS study Development of machine learning models for predicting acute respiratory distress syndrome:evidence from the MIMIC-III and MIMIC-IV selects 20 variables by filter and wrapper steps and applies DCA only after the fact. The novelty is using controllability as a diagnostic for when a decision curve can be trusted, and as the selection criterion that makes the curve robust.
Why the controllability literature applies, inverted
Controllability-based representation learning keeps only state features the agent can influence. Curiosity-driven Exploration by Self-supervised Prediction trains features solely to predict the action between consecutive states, so dynamics independent of the action are discarded. Guaranteed Discovery of Control-Endogenous Latent States with Multi-Step Inverse Models extends this to predicting the first action from a state $k$ steps ahead and proves identifiability under deterministic dynamics. Its AC-State model recovers a robot arm's position at 99.83% accuracy against video distractors, where autoencoders reach about 30%. Empowerment methods (Learning to Perceive the World Through Control: Empowerment-Based Representation Learning; Information Prioritization through Empowerment in Visual Model-based RL) reach the same separation from the forward direction. Factored world models do so by splitting the latent dynamics into controllable and uncontrollable parts (Denoised MDPs: Learning World Models Better Than the World Itself).
All of these keep the controllable part. We supply the method, but our goal is the complement. For the question "how risky is this patient if we do not intervene," the controllable part is contamination.
The closest conceptual precedent is Dichotomy of Control: Separating What You Can Control from What You Cannot. It shows that return-conditioned policies "count on luck" by conditioning on stochastic outcomes, and it fixes this with a mutual-information constraint that strips environment randomness from the plan latent. Our setting is its mirror image. A risk score "counts on the clinician" by absorbing the historical policy, and we strip action information from its inputs.
The motivating evidence for the gap comes from Reliable Decision Support using Counterfactual Models. It names the policy-sensitivity trap and shows that a standard supervised Gaussian-process risk score shifts by 0.083 across simulated treatment regimes, while its counterfactual model shifts by 0.001. That paper never evaluates net benefit and models a small, hand-picked set of variables. We take its diagnosis to a high-dimensional feature set and to the DCA metric that clinical papers actually report.
Research Program
The data are hourly ICU time series. Each state $x_t$ is a vector of clinical aggregates, and the actions $a_t$ are binary treatment signals: mechanical ventilation and vasopressors as extracted by MIMIC-Extract, plus dialysis where available.
For each feature $j$, we train a multi-step inverse model that predicts $a_t$ from the current state and the future trajectory of the features. The action-revealing score of feature $j$ is the information that feature's future change adds about the action, beyond the current state:
$$c_j = I\big(a_t ;\, x^{j}_{t+1:t+k} \mid x_t\big),$$
Here $x^{j}_{t+1:t+k}$ is feature $j$ over the next $k$ hours. We estimate $c_j$ as the drop in held-out action log-likelihood when that feature's future values are masked. Conditioning on $x_t$ is what separates "the action changed this feature" from "this feature's level prompted the action." That separation is valid only under the usual sequential no-unmeasured-confounding assumption also used in the counterfactual Gaussian-process work. We state this as an explicit limitation, not a solved problem.
Features with high $c_j$ get one of two treatments. They can be dropped. Alternatively, they can be frozen at their last value recorded before the first intervention in the prediction window. Freezing keeps their prognostic content while removing the treatment's imprint.
The risk model is then trained on the audited features. Its loss is the bounded Brier score of A Consequentialist Critique of Binary Classification Evaluation Practices, which that paper proves is linearly equivalent to integrated net benefit over a clinician-specified interval $[p_{min}, p_{max}]$. Model selection therefore targets the quantity DCA reports.
The analysis has a second product beyond the selected model: a leakage curve. It plots, for each model, the gap between retrospective net benefit and net benefit under a shifted policy, against the total action-revealing score of the features the model uses.
Baselines
The naive reference points are DCA's own defaults: "treat all" and "treat none." Any model must beat both inside the chosen threshold interval. Next comes the conventional clinical pipeline. It uses gradient boosting on a filter-plus-wrapper selected subset, reproducing the ARDS study's procedure. That study reports CatBoost at an AUC of 0.817 on 2,852 ICU patients, with LightGBM and XGBoost at 0.793 and logistic regression at 0.664. No net benefit number is reported; no reported result was found on Lacuna for net benefit on MIMIC-based ARDS or mortality prediction. For in-hospital mortality, MIMIC-Extract reports AUROCs between 0.85 and 0.90. We will reproduce that number as a sanity check before comparing anything.
The strongest competitor on our specific question is a model with the same architecture and the same bounded-Brier objective. Its features are chosen by a wrapper search that directly maximizes bounded net benefit on validation data. This is the obvious "optimize DCA directly" idea, and it isolates whether controllability adds anything beyond targeting the right metric.
A second strong competitor is the counterfactual Gaussian process of Schulam and Saria. It is run on the variable set it can handle, since it attacks the same trap through explicit causal modeling.
Three ablations isolate the key ingredient. The first removes only the raw treatment indicator columns, which is standard practice. The second removes features at random, matched to the count removed by our audit. The third uses a single-step rather than multi-step inverse model.
Fairness of comparison is enforced in three ways. All models share the same patients, prediction horizons, threshold interval, and hyperparameter search budget. Calibration is fit on the same validation split for every model. Recalibration on the deployment period is offered to every baseline as well.
Beating the strongest competitor means two things, judged on the semi-synthetic and simulated settings where the truth is known. Our method must show smaller loss in integrated net benefit under policy shift, with confidence intervals excluding zero across seeds. Its retrospective net benefit must also be no worse than one point per hundred patients below the competitor's.
Why not just…?
Why not just delete the treatment columns? This removes the direct record of the action but not its consequences. Mean arterial pressure after a vasopressor and creatinine after dialysis still encode what was done. The column-deletion ablation tests exactly this. If its leakage gap matches our method's, the inverse-dynamics audit is unnecessary, and we will report that.
Why not just recalibrate or re-threshold at deployment? Net benefit, calibration, threshold selection, and training objectives for algorithmic fairness in healthcare shows that preserving calibration and choosing thresholds afterwards beats constraint-based training for net benefit at a 7.5% statin threshold. This is a real threat. Recalibration repairs a uniform shift in predicted probabilities, but it cannot repair a ranking that placed treated-and-recovering patients below untreated sick ones. Every baseline gets deployment-period recalibration. If recalibrated baselines close the gap, our claim narrows to "rankings do not leak," and the experiment will say so.
Why not just optimize net benefit directly during feature selection? The bounded-Brier wrapper baseline is this idea. It is a threat whenever validation data share the training policy, because then a leaky feature genuinely improves validation net benefit. Our hypothesis is that it will select more action-revealing features than plain AUC selection, not fewer. The leakage curve tests this directly.
Why not just fit a full counterfactual model? That is the principled answer when it is feasible. The counterfactual Gaussian process models a few variables in continuous time with explicit treatment processes and was demonstrated on 428 patients. Our audit is a cheaper screen that works with any downstream learner. We expect it to be competitive in robustness rather than superior, and the experiments compare the two head to head on the variable set both can use.
Proposed Experiments and Decisive Checks
The first experiment is a simulator in the style of the treatment-regime study. A latent severity process drives a mix of observed signals. Some are untouched by treatment, some are pushed toward normal by treatment, and some are pure noise. A clinician policy treats when severity crosses a threshold. Because untreated outcomes are known, the true net benefit of the "treat when predicted risk ≥ $p_t$" rule can be computed under a new policy. Two checks are decisive here. First, $c_j$ must rank the treatment-affected signals above the others, scored by the area under the precision-recall curve for recovering them. Second, the net benefit loss under a change of regime must shrink as $c_j$-ranked features are removed, but not when random features are removed.
The second experiment is semi-synthetic. It uses real MIMIC-Extract covariates and actions with a simulated outcome injected into the treatment response. This tests whether the audit still finds the affected features when the correlation structure among them is realistic.
The third experiment uses real data with natural policy variation. We train on MIMIC-III and evaluate on the later admissions in MIMIC-IV. We also train on one care unit and test on units with different ventilation and vasopressor rates. Counterfactual net benefit is not observable here, so we report decision curves within the interval using briertools. We also report net benefit stratified by whether patients were treated in the prediction window.
The predicted signature of leakage has two parts. Leaky models do well on treated patients but lose net benefit on untreated ones when moved to a unit that treats less aggressively. Audited models should show a flatter stratified profile.
The whole proposal fails if any of three things happen: the simulator shows no relation between total action-revealing score and the leakage gap; column deletion matches our method; or recalibrated baselines erase the difference. Each outcome would still be useful, as evidence that retrospective decision curves on ICU data are more trustworthy than the policy-sensitivity argument suggests.
References
- Development of machine learning models for predicting acute respiratory distress syndrome:evidence from the MIMIC-III and MIMIC-IV
- Curiosity-driven Exploration by Self-supervised Prediction
- Guaranteed Discovery of Control-Endogenous Latent States with Multi-Step Inverse Models
- Learning to Perceive the World Through Control: Empowerment-Based Representation Learning
- Information Prioritization through Empowerment in Visual Model-based RL
- Denoised MDPs: Learning World Models Better Than the World Itself
- Dichotomy of Control: Separating What You Can Control from What You Cannot
- Reliable Decision Support using Counterfactual Models
- MIMIC-Extract: a data extraction, preprocessing, and representation pipeline for MIMIC-III
- A Consequentialist Critique of Binary Classification Evaluation Practices
- Net benefit, calibration, threshold selection, and training objectives for algorithmic fairness in healthcare