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Under review as a conference paper at ICLR 2027

Aligning Data-Driven Predictors with Allocation: A Decision-Focused Approach to Survival Analysis

Abstract

Machine learning predictors have become essential tools for guiding automated decision making. However, a major misalignment persists: predictive models are typically optimized in terms of standard statistical metrics in isolation from the algorithmic tasks they inform. We highlight this incongruity in both theory and practice in the high-stakes domain of organ allocation. We demonstrate that any algorithm relying on (even near-perfect) survival predictors optimized for standard metrics—such as the Concordance index (C-index)—can yield arbitrarily poor outcomes when used for allocation, failing to guarantee utility better than a uniform random selection. To bridge the gap between survival analysis and policy optimization, we introduce a decision-focused learning approach based on optimizing normalized discounted cumulative gain (NDCG), a mainstay metric in information retrieval. We establish the utility of NDCG in survival analysis by proving that it translates to guarantees on the performance of allocation. Empirically, we develop a bootstrapping approach to optimize the NDCG of existing survival models. Unlike prior work, we also address the challenge of right censoring when evaluating NDCG. We show the aforementioned misalignment persists in historical heart transplant data from the US, and our method dramatically boosts the NDCG across a suite of survival models by 40-100%. We anticipate that our framework will find broader applications in decision making with predictions.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Survival analysis, decision-focused learning, organ allocation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_LobyOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
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1
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Paper summary

The paper studies the mismatch between conventional survival-prediction metrics and the utility of selecting a high-value transplant recipient. It gives worst-case examples showing that a high C-index alone need not imply good single-recipient allocation, connects NDCG to a position-weighted selection policy, and develops expected-years imputation and inverse-probability-of-censoring weighting (IPCW) for estimating discounted gains from censored outcomes. A second-stage gradient-boosted model combines regression on imputed survival labels with an NDCG-weighted ranking objective. Experiments use the UNOS heart-transplant registry, first with artificially censored observed-event records and then with the full registry.

The motivating problem is important. However, the current evidence more directly supports improved retrospective top-of-list survival ranking than improved organ allocation. The statistical interpretation of the estimated NDCG comparisons and the contribution of the ranking objective also need stronger justification.

Critical strengths

S1. The paper identifies a consequential mismatch between evaluation and use. Section 3.1 gives a simple, effective construction in which almost all pairwise comparisons are correct while the selected candidate is the worst one. This is an important warning against treating a global ranking metric as sufficient evidence for a top-selection decision. The focus on right-censored outcomes makes this more relevant than a generic learning-to-rank example.

S2. The empirical study includes useful controls and acknowledges nuisance-model limitations. The use of several survival-model families, two relevance estimators, cross-fitting, and the additional covariate-dependent censoring experiments in Appendix I is valuable. Appendix H.1 also provides the necessary regression-only and ranking-only controls. These components make it possible to assess which parts of the proposed framework are actually responsible for the gains, even though the interpretation needs revision.

Critical weaknesses

W1. Unbiased DCG estimation does not establish the claimed reliability of NDCG-based model comparisons, and the censoring experiments need to be reconciled with the assumptions. Section 4.2 correctly observes that two estimated NDCG values share a normalizer on a fixed dataset. This proves that their ordering equals the ordering of their estimated DCGs. It does not prove that this ordering matches the true DCGs or true NDCGs. Likewise, an upward bias in estimated IDCG does not by itself establish a downward bias in its ratio with an estimated numerator. The numerator and denominator are dependent, so a ratio argument needs separate justification. A twofold ratio of estimated gains is also not automatically a twofold ratio of true allocation gains.

This distinction matters most at the small values of k emphasized by the paper. In Table A10, IPCW model-selection accuracy at k=1 is approximately 55% at gamma=0, rather than uniformly reliable; EY is better, but remains imperfect. The positive EY biases in Table A9 also show that a generally negative NDCG bias is not an adequate description of the implemented estimators. Appendix I should therefore qualify the main-text claims, rather than be summarized as unconditional preservation of model rankings.

There is a further mismatch in Appendix F: for selected patients, the censoring time is drawn uniformly from [0, T*]. This construction depends on the event time and does not generally satisfy conditional independent censoring given the baseline covariates. Appendix I uses an appropriate alternative construction and is an important partial response, but it primarily reports estimator diagnostics. The headline bootstrapping gains should also be established under that assumption-compatible construction. Restricting the starting cohort to patients with observed events additionally changes the population and should not be treated as validation on a representative fully observed transplant cohort.

W2. The experiments do not yet isolate a decision-focused ranking advance or validate the intended allocation use. Theorem 1 concerns one allocation with known nonnegative utilities and a specified true NDCG bound. At k=1, Corollary 1 is essentially the identity between selected-to-optimal utility and NDCG@1. It does not establish sequential allocation performance, transplant benefit, or how an estimated validation metric supplies a bound for a new donor-specific candidate set. Section 6 evaluates historical outcomes of recipients who actually received transplants, rather than alternatives for the same arriving organ. The relationship between graft survival, expected benefit relative to no transplant, candidate compatibility, and future allocation opportunities consequently remains untested. The claim that graft survival dominates life-years gained does not resolve these identification and decision-design issues.

The algorithmic attribution is also weaker than the headline improvements suggest. In Table A8, regression-only training achieves NDCG@1 of 0.468, compared with 0.494 for the hybrid loss and 0.288 for the original Cox model. Regression-only training is better than the hybrid at k=5, 10, and 50. Thus, much of the improvement may come from the imputed labels and the added boosted-tree model, rather than the ranking component. Learning to rank for allocation and NDCG-weighted boosted-tree training already have substantial precedents, including Kamran et al. (2024) and Burges (2010). Both are acknowledged by the manuscript; the issue is isolating the additional contribution here, not missing citations.

At minimum, the paper needs a broader matched regression-only comparison and a controlled donor-specific allocation experiment with known utilities. Without such evidence, the conclusion should be restricted to retrospective ranking. Section 6.2 should also avoid claiming statistically significant improvement across every survival model: Table 3 contains nonsignificant NDCG@1 comparisons, including the IPCW results for AFT and DeepSurv.

Questions for authors

Q1 — W1, theoretical clarification. What result, beyond cancellation of the common estimated denominator, supports preservation of true model rankings in Section 4.2? Can you state the estimand, distinguish expected from realized rankings, and provide either a comparison-error bound under explicit assumptions or a narrower empirical claim? Please also justify or remove the asserted general direction of NDCG bias.

Q2 — W1, essential experimental evidence. Can you report the baseline-versus-bootstrapped ranking gains under the conditionally independent censoring construction in Appendix I, alongside the Appendix F results? Please clarify the artificial-censoring fraction, nuisance-model fitting, and the evaluation population induced by selecting observed-event patients. This would determine whether the central gains persist in the setting covered by the assumptions.

Q3 — W2, contribution attribution. With the same pseudo-labels, boosted-tree architecture, tuning budget, and splits, how does the hybrid objective compare with regression-only training across all base models? Are its incremental NDCG@1 gains stable, and how should the stronger regression-only results at larger k in Table A8 affect the claimed benefit of ranking optimization?

Q4 — W2, decision relevance. What exactly forms a query/candidate set in training and evaluation, and how does it correspond to compatible recipients for one donor? Can a controlled allocation setting with known donor–recipient utilities establish the proposed metric's decision benefit? If that evidence is unavailable, would you limit the claims to survival ranking rather than improved transplant allocation?

3 comments
AuthorsOpenReview ↗

Author response (1/2)

We thank reviewer Loby for their review.

What result, beyond cancellation of the common estimated denominator, supports preservation of true model rankings in Section 4.2? Can you state the estimand, distinguish expected from realized rankings, and provide either a comparison-error bound under explicit assumptions or a narrower empirical claim? Please also justify or remove the asserted general direction of NDCG bias. The cancellation of the common IDCG denominator guarantees agreement between comparisons using estimated DCG and estimated NDCG. Our unbiasedness results establish that estimated DCG matches expected DCG. For IPCW with correctly specified censoring probabilities, a stronger conditional result holds: estimated DCG is unbiased for the realized DCG, conditional on the true outcomes and covariates.

This does permit a comparison-error guarantee. For two fixed model rankings with true DCG difference Δ>0\Delta>0 and an IPCW difference estimator with conditional variance bounded by VV, Cantelli's inequality yields that the probability that Δ^≤0∣T∗,X\widehat{\Delta}\leq 0\mid T^*,X is less than VV+Δ2\frac{V}{V+\Delta^2}. Thus, under conditional independent censoring, the probability of incorrectly comparing two models decreases as their true DCG difference becomes large relative to estimation uncertainty. We will add this clarification and distinguish realized from expected model comparisons explicitly.

Our empirical evidence directly evaluates the preservation of true model rankings. Table 2 and Appendix I compare estimated model rankings against rankings computed from known outcomes, validating the accuracy of the estimators at identifying the correct ranking.

Can you report the baseline-versus-bootstrapped ranking gains under the conditionally independent censoring construction in Appendix I, alongside the Appendix F results? Please clarify the artificial-censoring fraction, nuisance-model fitting, and the evaluation population induced by selecting observed-event patients. This would determine whether the central gains persist in the setting covered by the assumptions.

Yes, of course, this is an addition we can immediately add. The artificial censoring fraction is explicitly reported in Table A4 and is 49.47%. The results from Appendix I are intended to validate the nuisance model estimates, and the results for the NDCG gain are nearly identical to the Section F setup. As described in Appendix F, we cross-fit nuisance models to separate nuisance estimation from the evaluation of predictive performance. We will include those results in the final version of the paper and we provide them here. They reinforce the benefit of our decision-focused approach.

PredictorFrameworkNDCG@1NDCG@5NDCG@10NDCG@FullC-Index
KMBase0.1120.1890.2170.8500.500
+ Ours0.2590.3430.3700.9010.639
CoxBase0.1290.2770.3070.8940.626
+ Ours0.5270.4080.4010.9020.640
AFTBase0.2810.2500.2680.8940.630
+ Ours0.4420.4050.4050.9010.639
DeepSurvBase0.2090.2340.2890.8960.631
+ Ours0.3090.3980.3780.9010.639
DeepHitBase0.1260.2300.2650.8940.628
+ Ours0.3810.3880.3980.9010.640
RSFBase0.3600.4420.4310.8980.619
+ Ours0.6740.5110.4820.9040.640
AuthorsOpenReview ↗

Author response (2/2)

With the same pseudo-labels, boosted-tree architecture, tuning budget, and splits, how does the hybrid objective compare with regression-only training across all base models? Are its incremental NDCG@1 gains stable, and how should the stronger regression-only results at larger k in Table A8 affect the claimed benefit of ranking optimization?

We already have the results of this ablation and provide them for the reviewer here. Our decision-focused approach is specifically to optimize NDCG; regression may unintentionally perform well at this task by minimizing predictive errors at the top of the ranking. We provide the ablation for regression only training across all base models below and hope this clarifies the reviewer’s concern. We will add this to the paper.

Predictoralpha = 0.3alpha = 1
KM0.4230.412
AFT0.5140.550
DeepHit0.5980.522
DeepSurv0.5930.447

What exactly forms a query/candidate set in training and evaluation, and how does it correspond to compatible recipients for one donor? Can a controlled allocation setting with known donor–recipient utilities establish the proposed metric's decision benefit? If that evidence is unavailable, would you limit the claims to survival ranking rather than improved transplant allocation?

We appreciate the reviewer's question and believe it is important to distinguish the optimization of the predictive component from the optimization of the entire sequential allocation process. We do discuss this distinction in the paper, and can elaborate on this challenge.

Our objective is not to provide an end-to-end guarantee for the entire sequential allocation process, but rather to establish the correct optimization objective for the predictive component used within allocation algorithms. Every sequential allocation policy ultimately relies on comparing feasible candidates at each donor arrival. Our results show that optimizing aggregate survival objectives such as C-index is fundamentally misaligned with this decision, whereas NDCG@1 directly aligns the predictor with the allocation objective.

The training queries are resampled groups of 256 historical transplant recipients, which is stated already in Section 5, Appendix E.1. We evaluate the resulting predictors on their ability to identify patients with high graft-survival outcomes. Our experiments establish improvements in survival ranking, while our theoretical results establish why this ranking objective is directly relevant to allocation.

In practice, the single allocation problem is a concrete component of sequential heart allocation. The waitlist is highly dynamic and patients continuously enter and leave the system, and other papers have already observed that the distribution of patient characteristics remains relatively stable over time (e.g., “Near-optimal dynamic matching via coarsening and application to heart transplantation”, ICML 2026). At each donor arrival, the allocation algorithm repeatedly encounters a similar prediction problem: identifying the highest-utility candidate from the current feasible set of patients, which is exactly what we address.

Thank you for the clarifications and additional experiments. Concerns remain about the claimed direction of NDCG bias, the completeness and stability of the regression-only ablation, and the link to allocation benefits, so I will maintain my score.

Reviewer_nfeiOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
3
Soundness
1
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Paper summary

The authors propose to adapt the metric of normalized discounted cumulative gain to the case of right censoring, to fill the gap between prediction and decision making with a survival outcome. They also propose an optimization procedure compatible with any base survival model and show on semi-simulated (artificial censoring) and real data the superiority of their approach.

Critical strengths

The identified problem is interesting and well justified. The proposed approach seems to improve the optimized metric compared to standard existing methods.

Critical weaknesses

A large part of the literature on this topic is ignored. The c-index is indeed not a good metric neither for optimization nor evaluation of survival methods (see Bahrini, Ghanem, Sebastien Razakarivony, Jean-François Dupuy, Valerie Gares, and Morgane Barbet-Massin. "When Can We Trust Survival Model Evaluation?." In Forty-third International Conference on Machine Learning. and Marius Lillelund, C., Qi, S., Greiner, R., & Fischer Pedersen, C. (2025). Stop Chasing the C-index: This Is How We Should Evaluate Our Survival Models. Manuscript submitted for publication. In The 39th Annual Conference on Neural Information Processing Systems (NeurIPS) https://doi.org/10.48550/arXiv.2506.02075). In particular the c-index is not proper, the notion of properness should be discussed in this contribution. Additionally, the authors mention the notion of calibration and state that "exploring how calibration can be used in cases where there is right censoring is an interesting direction for future work", but it is covered in Haider, H., Hoehn, B., Davis, S., & Greiner, R. (2020). Effective ways to build and evaluate individual survival distributions. Journal of Machine Learning Research, 21(85), 1-63.

There are also contributions about proper scoring rules for survival analysis Rindt, D., Hu, R., Steinsaltz, D., & Sejdinovic, D. (2022, May). Survival regression with proper scoring rules and monotonic neural networks. In International conference on artificial intelligence and statistics (pp. 1190-1205). PMLR. and Yanagisawa, H. (2023, July). Proper scoring rules for survival analysis. In International Conference on Machine Learning (pp. 39165-39182). PMLR. that should be considered here. And generally, the discussion between proper scoring rules and decision making is well-documented in machine learning.

Questions for authors

Can you evaluate your approach compared to other existing metrics, like the IBS, and also calibration metrics? this would really strengthen the contribution. And also explore the properness of the normalized discounted cumulative gain, as it would be a very strong property to have. And if the normalized discounted cumulative gain is not proper or strictly proper, maybe it could be extended to be?

3 comments
AuthorsOpenReview ↗

Author response (1/2)

A large part of the literature on this topic is ignored. The c-index is indeed not a good metric neither for optimization nor evaluation of survival methods (see Bahrini, Ghanem, Sebastien Razakarivony, Jean-François Dupuy, Valerie Gares, and Morgane Barbet-Massin. "When Can We Trust Survival Model Evaluation?." In Forty-third International Conference on Machine Learning. and Marius Lillelund, C., Qi, S., Greiner, R., & Fischer Pedersen, C. (2025). Stop Chasing the C-index: This Is How We Should Evaluate Our Survival Models. Manuscript submitted for publication. In The 39th Annual Conference on Neural Information Processing Systems (NeurIPS) https://doi.org/10.48550/arXiv.2506.02075). In particular the c-index is not proper, the notion of properness should be discussed in this contribution. Additionally, the authors mention the notion of calibration and state that "exploring how calibration can be used in cases where there is right censoring is an interesting direction for future work", but it is covered in Haider, H., Hoehn, B., Davis, S., & Greiner, R. (2020). Effective ways to build and evaluate individual survival distributions. Journal of Machine Learning Research, 21(85), 1-63. There are also contributions about proper scoring rules for survival analysis Rindt, D., Hu, R., Steinsaltz, D., & Sejdinovic, D. (2022, May). Survival regression with proper scoring rules and monotonic neural networks. In International conference on artificial intelligence and statistics (pp. 1190-1205). PMLR. and Yanagisawa, H. (2023, July). Proper scoring rules for survival analysis. In International Conference on Machine Learning (pp. 39165-39182). PMLR. that should be considered here. And generally, the discussion between proper scoring rules and decision making is well-documented in machine learning.

And also explore the properness of the normalized discounted cumulative gain, as it would be a very strong property to have. And if the normalized discounted cumulative gain is not proper or strictly proper, maybe it could be extended to be?

We thank the reviewer for highlighting the literature on proper scoring rules in survival analysis. We agree that these works deserve discussion, and we will add this discussion. However, we disagree that the absence of properness undermines the soundness or significance of our contribution. The central distinction is between evaluating the accuracy of survival distributions and evaluating the quality of the downstream decisions that those distributions inform. Our work complements this literature and we hope the reviewer is satisfied with our response below and will raise their score accordingly.

Proper scoring rules are an important statistical objective, but are distinct from the objective of our paper: determining whether a predictor can reliably identify the highest-utility candidate for allocation. NDCG is not a strictly proper scoring rule since it is invariant to strictly increasing transformations of predicted relevance scores. However, this is intentional: our decision problem depends on identifying the correct candidates, rather than recovering the correct survival distribution. This is precisely the point our paper makes.

Importantly, properness does not imply a guarantee on downstream allocation quality! Our theoretical contribution is to establish precisely such a connection for NDCG. To illustrate the distinction, consider the integrated Brier score (IBS) in the fully observed setting, where it is a proper scoring rule. Suppose there are NN patients, one of whom has true survival time ϵ\epsilon but is incorrectly predicted to survive for τ\tau years. All other N−1N-1 patients have true survival time τ/2\tau/2, which their survival distributions predict perfectly. The resulting IBS, normalized by the evaluation horizon, is at most 1/N1/N, approaching zero as NN increases. Nevertheless, a greedy allocation based on predicted survival selects the first patient, achieving only 2ϵ/τ2\epsilon/\tau of the optimal utility. This ratio can be arbitrarily close to zero.

Even an almost-perfect aggregate proper score cannot, by itself, guarantee that the best allocation is identified. By contrast, NDCG@1 directly captures this failure. Our point is that properness and allocation guarantees are different properties. The latter motivates our decision-focused metric and optimization framework.

We feel our work complements the cited papers rather than being subsumed by them. We will happily add this connection to our paper and cite all the provided papers; thank you for bringing these to our attention!

We will also revise our statement about calibration and cite the given work. The distinct direction relevant to our work is understanding how survival calibration can be leveraged to establish decision-specific allocation guarantees in a similar manner to NDCG. If the reviewer’s primary concern was to add the citations to these papers, we hope we have addressed that.

AuthorsOpenReview ↗

Author response (2/2)

Can you evaluate your approach compared to other existing metrics, like the IBS, and also calibration metrics? this would really strengthen the contribution.

Yes, of course. This is an addition we can immediately make to our paper. We report in the table below new results on the expected calibration error (ECE) for predicted RMST in the artificial censoring experiments. These results show that the improvements in NDCG achieved by our framework do not necessarily come at the expense of calibration (and in many cases, it improves), although the effect is model dependent and calibration is not explicitly optimized by our training objective. Regarding IBS, it requires a full predicted survival curve to evaluate. Our decision-focused model predicts a scalar RMST, which is sufficient for the ranking and allocation objectives we study. IBS is not directly applicable to the output of our framework. We will add this experiment and discussion to the paper.

PredictorBase+ Ours
Cox0.0090.012
DeepSurv0.0210.014
AFT0.0250.040
DeepHit0.0260.013
RSF0.0310.020
KM0.0830.033

Thank you for your answer. There is a huge body of literature on going from optimizing a model to decision-making, including in a health context, for which properness is key. The authors are right that it is not the only concept useful here, and they have focused on the clinical utility. Actually all of this is linked, and there are many useful references about that, like Van Calster, Ben, et al. "Evaluation of performance measures in predictive artificial intelligence models to support medical decisions: overview and guidance." The Lancet Digital Health (2025). A good metric for clinical utility is the net benefit, which was extended to survival analysis almost 20 years ago https://link.springer.com/article/10.1186/1472-6947-8-53. This could be a good baseline to include Regarding the link between properness and clinical utility, you may check Pfohl, Stephen, et al. "Net benefit, calibration, threshold selection, and training objectives for algorithmic fairness in healthcare." Proceedings of the 2022 ACM Conference on Fairness, Accountability, and Transparency. 2022. to see that actually the net benefit will be measured wrongly if the model is not well calibrated so indeed properness is not the same as building a clinically useful model, but it is a prerequisite. And this highlights another body of literature and baselines missing to this work, which again identifies a good problem, but entirely ignores existing parts of the solution.

Reviewer_HsCgOpenReview ↗
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Informativeness
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Paper summary

The paper argues that survival models used in organ allocation are trained and selected on statistical metrics such as the C-index, in isolation from the allocation task. It shows that a predictor with near-perfect C-index can, in the worst case, yield poor allocations, or no better than random selection. To resolve this, they propose an approach based on normalized discounted cumulative gain (NDCG) and prove that NDCG@k bounds the utility of a top-k selection rule. They propose two estimators of NDCG under censoring, and a bootstrapping training method. On the UNOS heart transplant registry, this raises NDCG@1 by at least 40% under artificial censoring.

Critical strengths
  • The central claims are investigated in detail: (1) C-index is not a good predictor of usefulness for the chosen task, (2) The estimators are checked against ground truth under artificial censoring.
Critical weaknesses
  • The link to allocation is only theoretical. In practice, graft allocations would be allocated sequentially, which the paper does not address with experiments, nor does it measure realized utility. This is an issue for a paper that claims to bridge the gap between standard survival approaches and a clinical (real-life) setting.

  • The hybrid loss adds little over plain regression. In the ablation (Table A8, Cox only), LightGBM trained with squared error alone (α = 1) reaches NDCG@1 0.468, against 0.494 for α = 0.3. The puts into question the claim that alpha=0.3 "consistently outperforms". There is no statical analysis of this result in Table A8.

Questions for authors
  • Can the authors do some experiments to simulate a "realistic" organ transplant usecase with sequental allocation, compatibility constraints, measuring e.g. waitlist mortality?
1 comment

We thank reviewer HsCg for their review. We hope to address their concerns below, and encourage the reviewer to increase their score if they are satisfied with our response.

The link to allocation is only theoretical. In practice, graft allocations would be allocated sequentially, which the paper does not address with experiments, nor does it measure realized utility. This is an issue for a paper that claims to bridge the gap between standard survival approaches and a clinical (real-life) setting. Can the authors do some experiments to simulate a "realistic" organ transplant usecase with sequental allocation, compatibility constraints, measuring e.g. waitlist mortality?

We do discuss this distinction in the paper, and can elaborate on this challenge. Our objective is not to provide an end-to-end guarantee for the entire sequential allocation process, but rather to establish the correct optimization objective for the predictive component used within allocation algorithms. Every sequential allocation policy ultimately relies on comparing feasible candidates at each donor arrival. Our results show that optimizing aggregate survival objectives such as C-index is fundamentally misaligned with this decision – EVEN in the static setting – whereas NDCG@1 directly aligns the predictor with the allocation objective.

In practice, heart allocation is indeed sequential, but the waitlist is also highly dynamic. Patients continuously enter and leave the system, yet other works have observed that the distribution of patient characteristics remains relatively stable over time (e.g., “Near-optimal dynamic matching via coarsening and application to heart transplantation”, ICML 2026). At each donor arrival, the allocation algorithm repeatedly encounters a similar prediction problem: identifying the highest-utility candidate from the current feasible set of patients, which is exactly what we address.

The hybrid loss adds little over plain regression. In the ablation (Table A8, Cox only), LightGBM trained with squared error alone (α = 1) reaches NDCG@1 0.468, against 0.494 for α = 0.3. The puts into question the claim that alpha=0.3 "consistently outperforms". There is no statical analysis of this result in Table A8.

Here in this rebuttal we provide the reviewer with the NDCG@1 results from this ablation study which we will add into the appendix of the paper. Note that we did not perform this ablation with RSF due to its intensive training time. Only the NDCG@1 of AFT did not increase using the fixed α=0.3\alpha = 0.3. Our decision-focused approach is specifically to optimize NDCG; regression may unintentionally perform well at this task by minimizing predictive errors at the top of the ranking. That does not undermine the significance of our approach. Note, everything but the improvement for KM is statistically significant.

Predictorα = 0.3α = 1
KM0.4230.412
AFT0.5140.550
DeepHit0.5980.522
DeepSurv0.5930.447

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