Many clinical outcomes compete with one another. A patient in intensive care can be discharged home, transferred to another facility, or die. Whichever happens first ends the others. Models that predict the probability of each outcome over time, called competing-risk models, are routinely trained at one hospital and used at another, and they often fail there. This note argues that much of that failure has a specific, fixable cause. The competing outcomes are not equally "biological." The rate at which sick patients die given their physiology may be roughly similar across hospitals. The rates of discharge and transfer are driven by local bed policy, payer mix and documentation habits. Most current competing-risk models predict each outcome's cumulative probability directly, which ties all outcomes together. A local change in discharge practice then corrupts the predicted risk of death, even when nothing about mortality has changed.
We propose an interpretable competing-risk model that keeps the outcomes separate. It models each cause's instantaneous rate as a sum of readable per-feature curves. A small, penalized site-specific deviation sits on top of a shared curve, and the size of that deviation serves as an audit of where hospitals differ. At a new hospital, the outcomes that look biological are carried over unchanged. Only the outcomes driven by practice are refit, and this needs little local data. The interpretable structure is not decoration added afterwards. It is what tells us which parts of the model can safely travel.
Core Claim
Two quantities need to be distinguished. The cause-specific hazard is the instantaneous rate of one outcome among patients still at risk. The cumulative incidence function (CIF) is the probability of having experienced that outcome by time $t$. A model of cause-specific hazards transports better across institutions than a model of CIFs, provided it is additive and its per-site deviations are explicit.
The reason is arithmetic. The CIF for cause $k$ combines every cause's hazard through the probability of still being event-free. A shift in one competing hazard therefore moves every CIF. Our claim has three testable parts. First, when an additive cause-specific model is fit across sites, the site deviations concentrate in practice-driven causes (discharge, transfer) and in practice-proxy features. Second, freezing the shared curves for biological causes and refitting only the practice-driven causes at a target site gives better-calibrated CIFs than pooling or recalibrating a CIF-level model, at equal local sample size. Third, the deviation audit recovers shortcut features injected into semi-synthetic data.
Relation to Prior Work
Prior work falls into four groups, each playing a different role here.
The first group supplies the competing-risk models we must beat. All of them model CIFs or a joint time-by-cause distribution, and all were evaluated on random splits within one source. DeepHit outputs a joint softmax over time and cause. Neural Fine-Gray uses monotone networks on subdistribution hazards behind an embedding network its authors call uninterpretable. Deep Kernel Aalen-Johansen builds predictions from neighbouring patient exemplars, but its learned embedding could just as easily cluster patients by hospital. None of the three separates outcomes in a way that can be refit independently. We do, at the cost of giving up their unconstrained embeddings.
The second group supplies our method. ADHAM and DyS are single-event additive survival models with one small network per feature. ADHAM introduced decoupled training to stop correlated features from absorbing each other's effects, and DyS introduced smooth gates for feature selection. ADHAM's authors name competing risks as future work. We extend the additive form to multiple causes and add the site-deviation structure, which neither model has. PyDTS supplies the discrete-time cause-specific formulation and a synthetic event sampler. Its linear model is the natural lower rung of our comparison.
The third group motivates the transport question but constrains how we can attack it. Multi-Source Survival Domain Adaptation aligns representations adversarially, but only for single events. DRL-Cox obtains Wasserstein robustness guarantees that rest on convexity, so they do not extend to neural additive curves. We therefore do not claim worst-case guarantees. DiSKD is the closest work to ours. It transfers competing-risk knowledge from an external teacher to a local student without sharing raw data and improves on internal-only models in the transplant registry. However, both teacher and student are opaque, and the transfer is applied to the whole model rather than to individual causes.
The fourth group shapes our evaluation. Alberge et al. show that competing-risk models are badly miscalibrated on minority causes and that post-hoc Aalen-Johansen recalibration fixes this without hurting ranking. Their result is a serious alternative to ours, which we confront below. Their warning that some calibration metrics need long follow-up also limits which metrics we can use on short ICU stays.
Research Program
We work in discrete time, with intervals $t = 1, \dots, T$. Let $h_k(t \mid x, s)$ be the probability that a patient with covariates $x$ at site $s$, still event-free at the start of interval $t$, experiences cause $k$ during it. We model it with a multinomial logit:
$$\operatorname{logit} h_k(t \mid x, s) = \alpha_{k,s}(t) + \sum_j \big[f_{kj}(x_j, \tau(t)) + g_{kjs}(x_j)\big].$$
Here $\alpha_{k,s}$ is a site- and cause-specific baseline. $f_{kj}$ is a shared shape network for feature $j$ and cause $k$, allowed to vary over a few coarse time bands $\tau(t)$ so that hazards can be non-proportional. $g_{kjs}$ is a site deviation. The deviations are penalized with a group penalty $\lambda \sum_{k,j} \lVert g_{kj\cdot} \rVert$, so that most of them are pushed to exactly zero.
The cumulative incidence follows from the hazards by the standard product-sum. If $S(u)$ is the probability of remaining event-free through interval $u$, then
$$F_k(t) = \sum_{u \le t} S(u-1)\, h_k(u),$$
with $S(0) = 1$. This formula makes the coupling explicit: changing any one $h_{k'}$ changes $S$ and therefore every $F_k$.
The fitted norms $\lVert g_{kj\cdot} \rVert$ form a cause-by-feature heatmap of cross-site disagreement, and that heatmap is the audit. For correlated feature groups we use ADHAM-style decoupled training, so that a deviation is not merely moved onto a correlated neighbour.
Deployment at a new site works as follows. We declare a set of transportable causes, either from the audit or a priori (death). Their shared curves $f$ and their baseline are frozen. For the remaining causes we refit $\alpha_{k,\text{new}}$, and optionally a small number of deviations, from local data. This needs far fewer local events than refitting the whole model, and in the limit it needs only interval-level event counts.
Baselines
The naive reference is a pooled model applied unchanged at the held-out site. We run it in two forms. One treats competing events as censoring, to reproduce the known overestimation of risk. The other is pooled cause-specific logistic regression from PyDTS. On the MIMIC-IV length-of-stay task, with discharge home, transfer and death as outcomes, PyDTS reports an AUC of about 0.65 with LASSO. This is the within-source number we expect to reproduce before any shift is introduced.
The strongest classical competitor is cause-specific Cox, or its discrete-time equivalent, with a site-stratified baseline that is refit at the target site. It already separates the causes and permits local refitting, so it isolates whether non-linear additive curves add anything. On synthetic quadratic effects, DeepHit reports $C^{td}$ of 0.755 against 0.578 for cause-specific Cox. That gap shows non-linearity can matter, but it was measured within a single source. We find no reported cross-site result on Lacuna for cause-specific Cox under competing risks.
The strongest flexible competitors are Neural Fine-Gray and DeepHit. Each is trained on pooled sites and then given the same local target data we allow ourselves. This is used in three ways: per-site Aalen-Johansen recalibration, fine-tuning of the full model, and distillation following DiSKD. We also include DKAJ with local recalibration as the interpretable competing-risk alternative. We find no reported cross-institutional competing-risk result on Lacuna for any of these models, so all numbers will be produced in our own runs.
Every method receives the same features, source sites, local target budget (measured in target events per cause) and hyperparameter search budget. Tuning uses leave-one-source-site-out validation only; the target site is never touched during tuning.
Two ablations isolate the key ingredients. The first removes the cause-selective freezing: everything is refit, or nothing is. The second removes the deviation penalty, which leaves an unpenalized per-site model. Beating the baselines means two things at the held-out site. The integrated Brier score and calibration error for the minority competing cause must be lower, with confidence intervals from site-level bootstrap. Death-cause $C^{td}$ must not be worse. Both must hold at local budgets of 50 to 200 target events. With unlimited local data, every method should converge, and we expect no advantage there.
Why not just…?
Why not just use stratified cause-specific Cox with a local baseline? This is the most serious threat, because it shares our central structural move. If it matches our model at the held-out site, the honest conclusion is that cause separation is what matters and that additive curves are needed only for the audit. We will report the result that way. The ladder of models, from linear to additive and from refitting nothing to selective refitting, is built to separate these two contributions. Our model can win on accuracy only where features have non-linear or time-varying effects. We will check whether such effects exist by inspecting the fitted shared curves.
Why not just pool sites and apply Aalen-Johansen recalibration per site? Alberge et al. show this repairs average calibration cheaply. However, it adjusts cumulative incidence as a function of time, not as a function of the covariates. If discharge policy at a new site shifts differently for different kinds of patients, for example elderly patients being transferred sooner, recalibration cannot correct it. Our semi-synthetic experiments inject exactly such covariate-dependent shifts, alongside covariate-independent ones. If recalibration wins in both cases, our claim fails.
Why not just fine-tune or distill a black-box competing-risk model at the new site? Fine-tuning and DiSKD-style distillation adapt every parameter. With few local events this is high-variance, and it gives no account of what changed. They are included at matched local budgets. Fine-tuning may win once the local data are large, which is expected and acceptable. The deciding experiment is the curve of target-site error against local sample size.
Why not just train on many sites and hope invariance emerges? Multi-site training does help with imaging artifacts (Harmon et al.). But differences in discharge and transfer practice are not noise that averages out. They are genuine differences in the competing outcome. Pooled ERM is included as the naive reference point to measure this directly.
Proposed Experiments
The first experiment uses semi-synthetic data with ground truth. We take the PyDTS event sampler and, separately, real covariates from SEER and MIMIC-IV. We simulate several "sites" that share a death hazard, have site-specific discharge or transfer hazards, and contain one site-correlated shortcut feature. We vary two things: whether the competing-hazard shift depends on the covariates, and the correlation between features. The audit is scored by how well the deviation norms recover the truly shifted (cause, feature) pairs, measured as area under the precision-recall curve. Transport is scored by held-out-site integrated Brier score and calibration of each CIF.
The second experiment uses real shifts. In MIMIC-IV length-of-stay, with outcomes home, transfer and death, we treat admission-era blocks and care-unit types as sites and hold each out in turn. In SEER breast cancer, with breast cancer, cardiac and other death as outcomes, the "sites" are the contributing registries, with leave-one-registry-out evaluation. Here we predict the reverse pattern: deviations should land on registry-level coding of cause of death rather than on discharge. In SRTR, with death versus graft failure, we use time periods as sites, mirroring the policy-shift setting of DiSKD so that the comparison with it is direct.
We report per-cause $C^{td}$, integrated Brier score, and Aalen-Johansen-based calibration. For the short ICU horizons, CR D-calibration is omitted, following the long-follow-up requirement noted by Alberge et al.
The decisive check is a joint test on the held-out MIMIC-IV care units. The audit must place most deviation mass on discharge and transfer rather than death, and freezing the death curves must beat stratified cause-specific Cox and recalibrated Neural Fine-Gray on minority-cause calibration at 100 local events. If deviations spread evenly across causes, the premise that some outcomes transport and others do not is false for this data, and the proposal reduces to an interpretable competing-risk additive model.
References
- DeepHit: A Deep Learning Approach to Survival Analysis With Competing Risks
- Neural Fine-Gray: Monotonic neural networks for competing risks
- Deep Kernel Aalen-Johansen Estimator: An Interpretable and Flexible Neural Net Framework for Competing Risks
- ADHAM: Additive Deep Hazard Analysis Mixtures for Interpretable Survival Regression
- Interpretable Prediction and Feature Selection for Survival Analysis
- PyDTS: A Python Package for Discrete Time Survival Analysis with Competing Risks
- Multi-Source Survival Domain Adaptation
- Distributionally Robust Learning in Survival Analysis
- Discrete Survival Knowledge Distillation for Competing Risks Analysis
- On the calibration of survival models with competing risks
- Artificial intelligence for the detection of COVID-19 pneumonia on chest CT using multinational datasets