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Under review as a conference paper at ICLR 2027

Uncertainty-Aware Survival Distillation for Flexible Continuous-Time Relative Risk Models

Abstract

Clinical decision-making requires accurate individualized survival predictions and clinically interpretable characterization of their uncertainty. Prominent survival-distillation approaches typically provide only point predictions. Moreover, existing continuous-time distillation methods either rely on classical regression formulations that may not extend naturally to flexible machine-learning models or transfer relative-risk information without directly incorporating external survival probabilities. To address these gaps, we introduce BayCSD (Bayesian Continuous-Time Survival Distillation), an uncertainty-aware survival-distillation framework for flexible continuous-time relative-risk models, including deep neural networks. The framework introduces a censor-aware interval KL distillation criterion that compares teacher and student models, allowing external survival predictions to inform both nonlinear relative-risk functions and cumulative baseline hazards while retaining the original event and censoring times in the target likelihood. A generalized Bayesian update combines target-data fit, a borrowing-weighted distillation discrepancy, and a structural prior, propagating joint posterior uncertainty in the risk function and baseline hazard to individualized survival probabilities and restricted mean survival time. Controlled synthetic experiments characterize the benefits and limitations of borrowing under teacher compatibility and mismatch. Real-data pooled-reference benchmarks and kidney-alone-to-kidney–pancreas transfer demonstrate improved survival prediction relative to matched target-only learning, while pooled-reference analyses yield narrower posterior intervals at matched reference inclusion. BayCSD also compares favorably with existing survival-transfer approaches in the transplant application.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Survival Analysis, Knowledge Distillation, Transfer Learning, Bayesian Inference, Uncertainty Quantification

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.20 over 5 reviews, above 49% of the others.
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Paper summary

This paper proposes BayCSD, a survival prediction method that transfers information from an external teacher model to a student trained on a smaller target dataset. The method combines the target outcomes, teacher predictions, and a prior through a generalized Bayesian update. It preserves the original event and censoring times and produces uncertainty estimates for survival predictions. The authors evaluate the approach using synthetic experiments and real clinical datasets.

Critical strengths

1- The paper addresses a useful practical problem. When few events are observed in the target population, information from an external survival model can help improve prediction without requiring access to the original source records.

2- The method retains the original event and censoring times while borrowing information from teacher predictions at selected time points. This is a meaningful design choice, and the controlled comparisons help demonstrate its value.

3- The experiments show improvements over target-only learning on several datasets. In the kidney-to-kidney–pancreas transfer experiment, BayCSD also improves over the teacher and the compared distillation methods.

4- The authors investigate both compatible and mismatched teachers. I appreciate that they discuss how borrowing can reduce estimation variability but also introduce bias when the teacher does not match the target population.

Critical weaknesses

1- The main idea could be explained more clearly. Although the teacher and student are defined, their roles, training procedures, and implementation details are spread across several sections. A simple example would help explain how the generalized posterior uses teacher guidance and why this could improve target prediction.

2- The advantage over directly using the teacher needs clearer justification. In Figure 2, teacher-only predictions appear competitive with or better than BayCSD in the compatible and calibration-shifted settings, although BayCSD performs better under risk-function shift. This does not invalidate the method, but it raises the question of when its additional complexity is worthwhile. A comparison with simple target-data recalibration of the teacher would be helpful.

3- The uncertainty estimates are not consistently reliable under teacher mismatch. In Appendix Table 5, the nominal 95% intervals contain the true survival probabilities approximately 75.6% of the time under calibration shift, compared with 83.4% for the target-only model. The authors acknowledge that nominal coverage is not guaranteed. Nevertheless, narrower intervals alone do not establish better uncertainty estimates, which is important given the paper’s emphasis on uncertainty-aware prediction.

4- Comparisons with other transfer methods could be broader. The paper includes relevant baselines and controlled variants, but the broader comparison is concentrated in one real source–target application. Additional comparisons on the other datasets, or under different population shifts, would help establish the general usefulness of the method.

Questions for authors

1- Why does BayCSD not improve on teacher-only predictions under calibration shift in Figure 2? How would it compare with simply recalibrating the teacher using the target data?

2- How much of the predictive benefit comes from Bayesian posterior averaging rather than the teacher-guidance term? Could the authors compare against a single fitted model using the same objective?

3- How should users interpret the uncertainty intervals when the teacher is mismatched? Could the borrowing-weight selection be modified to consider interval reliability as well as predictive fit?

4- Do the improvements over other distillation methods hold across additional source–target settings?

5 comments

We thank the reviewer for the constructive comments and for recognizing the practical problem, the design of the controlled comparisons, and the analysis of compatible and mismatched teachers.

W1. How the generalized posterior uses teacher guidance. We thank the reviewer for this helpful suggestion. We agree that the teacher’s role and the student’s training procedure should have been explained together more clearly. The teacher is fitted once, outside the target analysis, and held fixed; BayCSD needs only its survival predictions for the target-training subjects at the comparison endpoints. The student is a Bayesian survival model fitted to the target data, whose posterior (Eq. 7) multiplies the target likelihood by a teacher factor and a structural prior on the student parameters. The target likelihood uses the original event and censoring times, while the teacher factor encourages agreement with the external predictions.

Eq. (8) gives this factor a simple reading. Suppose the teacher predicts that subject ii, event-free at τk−1\tau_{k-1}, fails within the next comparison interval with probability 0.10.1. Assume that this comparison is resolved by the observed follow-up, so Wik=1W_{ik}=1: the subject is followed to the interval endpoint or experiences an observed event within the interval. With η=10\eta=10, this comparison contributes the equivalent of one pseudo-event and nine pseudo-non-events for that subject and interval, in addition to the subject's actual observed outcome in the target likelihood. Equivalently, its teacher factor is proportional to pik(ϑ){1−pik(ϑ)}9{p_{ik}(\vartheta)\lbrace 1-p_{ik}(\vartheta)\rbrace ^{9}}, favoring student interval probabilities near 0.1 without forcing equality. These are algebraic contributions to the posterior, not additional observed patients or events.

Across included subject–interval comparisons, compatible teacher guidance can add information where sparse target events leave the model poorly determined; because the student's interval probability depends on both the risk function and the baseline hazard (Eq. 6), both components can be stabilized. The weight η\eta sets how many pseudo-observations the teacher contributes and is selected from the target data, with η=0\eta=0 recovering target-only learning. Joint posterior draws then provide individualized survival predictions and measures of their conditional uncertainty, rather than only a single fitted estimate. We have added this example to Section 3.3.

W2 / Q1. Teacher-only predictions and recalibration. We thank the reviewer for this helpful suggestion. We agree that the added complexity should be justified against both direct teacher use and simple recalibration, rather than by improvement over target-only learning alone.

In Figure 2, the compatible teacher is fitted to 50,000 subjects from the target law, and the calibration-shifted teacher is constructed by multiplying its baseline hazard by 1.5 while retaining its fitted risk function. Both therefore retain the same strong risk ordering. Although the calibration-shifted teacher's absolute survival level is shifted, it remains highly predictive, and the target data accordingly select an intermediate borrowing weight (median η^=75\widehat\eta=75, between 100100 under compatibility and 55 under risk-function shift). Because BayCSD compares conditional failure probabilities, which depend on both relative risk and absolute survival level, borrowing at this strength transfers the teacher's accurate risk ordering together with its shifted survival level, which the sparse target outcomes only partly correct.

These comparisons should also be read in light of the information each predictor uses and provides. The teacher is fitted to 50,000 source subjects, whereas BayCSD uses 200 target subjects ($\approx$51 events) and only the teacher's survival predictions for them. Used directly, the teacher provides point predictions that neither incorporate the target outcomes nor quantify uncertainty for target subjects. BayCSD learns a target model with posterior uncertainty, improves on target-only learning under all three teachers, and improves on the teacher when its covariate effects are shifted.

As suggested, we added target-data recalibration of the teacher (Appendix J), fitted to the same target cohort with the same continuous-time PWE likelihood, baseline partition and prior as BayCSD: (a) re-estimating the baseline hazard with the teacher log risk as an offset, and (b) additionally estimating a calibration slope on the teacher log risk. Both treat the teacher's risk score as known, so their posterior intervals reflect uncertainty in the baseline hazard (and slope) only. Results are in Table R1.

(W2 / Q1. Teacher-only predictions and recalibration continued)

Table R1. Teacher-mismatch simulation: BayCSD versus the teacher recalibrated on the target data (baseline only / baseline and slope). Means over 20 paired replicates.

Teacher regimeMethodC-index ↑\uparrowIBS ↓\downarrow
CompatibleTeacher only0.7640.174
Recal. teacher (baseline / +slope)0.7640.177 / 0.179
BayCSD0.7570.179
Calibration shiftTeacher only0.7640.193
Recal. teacher (baseline / +slope)0.7640.177 / 0.179
BayCSD0.7520.199
Risk-function shiftTeacher only0.6320.218
Recal. teacher (baseline / +slope)0.6320.210 / 0.210
BayCSD0.6640.210
  • Calibration shift is a pure baseline multiplier, exactly the family recalibration corrects. Recalibration removes the imposed baseline shift, so its fits coincide across the two regimes.
  • Risk-function shift. Recalibration uses the teacher score as its only risk input, so it cannot learn a target-specific risk ordering. BayCSD learns target-specific covariate effects and improves the C-index in 18/20 replicates (+0.032+0.032, 95% CI [0.023,0.041][0.023, 0.041]) at the same IBS. Recalibration also treats the teacher's risk function as known: its nominal 95% intervals contain the true survival probability for only 48–49% of predictions, compared with 82% for BayCSD.

These comparisons clarify when the additional complexity is worthwhile. Direct teacher deployment may suffice when the teacher transports well and point predictions meet the analytical goal. Recalibration is effective when the shift lies in its parametric family; BayCSD is most relevant when target adaptation requires learning covariate effects beyond a baseline adjustment or global slope, together with uncertainty in the adapted risk function and baseline hazard. The type of shift need not be specified in advance. In the KI-to-KP application, where the shift is genuine, BayCSD has lower mean IBS and higher mean CtdC_{\mathrm{td}} than both recalibrated KI teachers (Table 2). We have added the recalibrated KI teachers to Table 2 and the simulation comparison to Appendix J.

W3 / Q3. Interpreting the intervals under teacher mismatch. The intervals quantify the uncertainty that remains in the target survival model after the teacher's predictions are incorporated at the selected strength. The joint generalized posterior over the risk function and baseline hazard induces a distribution of individualized survival probabilities and RMST, whose spread reflects how sharply the target likelihood and the teacher's pseudo-observations together determine these quantities. Their practical value is to provide patient- and horizon-specific measures of estimation precision beyond a point prediction. Under teacher mismatch, however, this conditional precision should not be interpreted as accounting for all sources of prediction error.

Under teacher compatibility and a fixed borrowing weight, the generalized-posterior analysis accompanying Proposition 1 (Appendix B.3) gives the local posterior covariance n−1Hη−1n^{-1}H_\eta^{-1}, where Hη=HR+ηGH_\eta=H_R+\eta G combines the curvature HRH_R of the target-likelihood criterion with the curvature GG contributed by the teacher, and this uncertainty propagates through the student model to individualized survival probabilities and RMST. The borrowing weight is selected for target predictive fit, and the posterior at the selected weight quantifies the uncertainty that remains after borrowing.

How these intervals relate to the true survival probability depends on teacher alignment, and the theory identifies the two cases. Under compatibility, borrowing preserves the population center, and Proposition 1 and the accompanying posterior analysis (Appendix B.3) show that the local posterior covariance n−1Hη−1n^{-1}H_\eta^{-1} is no smaller than the sampling covariance of the fitted center, n−1Hη−1HRHη−1n^{-1}H_\eta^{-1}H_RH_\eta^{-1}. This explains the conservative truth inclusion observed under compatible borrowing (98.8%, Table 5; Appendix G.4.1). Under mismatch, borrowing displaces the center by −ηHR−1∇Q(ϑ0)-\eta H_R^{-1}\nabla Q(\vartheta_0) to first order (Eq. 12), where ∇Q(ϑ0)\nabla Q(\vartheta_0) is the gradient of the teacher–student discrepancy at the target parameter ϑ0\vartheta_0. This displacement is not contained in the posterior spread, so truth inclusion is governed by this displacement relative to the spread.

(W3 / Q3. Interpreting the intervals under teacher mismatch continued)

The two mismatch regimes show how target-guided selection acts on this balance. Under risk-function shift, strong borrowing from the shifted teacher worsens target predictive fit, so WAIC selects weak borrowing (median η^=5\widehat\eta=5), the displacement remains small, and inclusion stays close to target-only learning (82.1% versus 83.4%); recalibration, which treats the teacher's risk function as known, reaches only 48–49% (W2 / Q1). Under calibration shift, the teacher predicts well but carries a shifted survival level, so WAIC selects borrowing intermediate between the compatible and risk-function-shift regimes yet substantial enough to carry the shifted level, and cross-validation borrows as strongly as under compatibility and yields lower inclusion (66.5% versus 75.6% over ten replicates). This is the case in which predictive accuracy and interval accuracy diverge.

For users, a larger selected η\eta indicates greater reliance on the teacher's predictive information, and the target-only fit (η=0\eta=0), always part of the selection grid, shows how much of the interval reduction is due to borrowing. Because a shifted survival level is reflected in how well predictions are calibrated against observed target outcomes, incorporating censoring-adjusted calibration in the target population into the selection of η\eta, alongside predictive fit, is a natural extension.

Q2. Posterior averaging versus teacher guidance. To separate the contributions of posterior averaging and teacher guidance, we consider both the statistical role of the posterior mean and a direct comparison with a single fitted model. BayCSD predicts with the posterior predictive survival probability, Sˉη(t∣x)=EΠη[Sϑ(t∣x)]\bar S_\eta(t\mid x)=\mathbb E_{\Pi_\eta}[S_\vartheta(t\mid x)], which averages the survival curves implied by the posterior draws (Gelman et al., 2013). This summary has two statistical motivations. First, the posterior mean minimizes the posterior expected squared-error loss, which connects it to the Brier score underlying the IBS (Gneiting and Raftery, 2007). Second, because it averages over the parameter configurations supported by the posterior rather than relying on a single fitted configuration, its predictions are less dependent on any one configuration, which is particularly relevant for a neural risk function learned from few target events (Wilson and Izmailov, 2020). The single fitted model the reviewer describes is the joint MAP of the same generalized objective, which initializes each BayCSD fit (Appendix J); Table R2 compares the two at the same WAIC-selected η\eta.

Table R2. Single fitted model (MAP) versus posterior-mean prediction at the WAIC-selected η\eta in the teacher-mismatch simulation. Means (SD) over 20 paired replicates.

C-index ↑\uparrow (MAP)C-index ↑\uparrow (Posterior mean)IBS ↓\downarrow (MAP)IBS ↓\downarrow (Posterior mean)
Target-only Bayesian PWE0.566 (0.034)0.611 (0.030)0.239 (0.009)0.225 (0.009)
BayCSD, compatible0.762 (0.004)0.757 (0.009)0.176 (0.004)0.179 (0.005)
BayCSD, calibration shift0.737 (0.062)0.752 (0.019)0.201 (0.019)0.199 (0.007)
BayCSD, risk-function shift0.609 (0.050)0.664 (0.020)0.223 (0.013)0.210 (0.006)

The results are consistent with these motivations and show that the gains do not come from averaging alone. Teacher guidance substantially improves the single fitted model itself, most clearly under compatibility (MAP C-index 0.566→0.7620.566\to0.762; IBS 0.239→0.1760.239\to0.176). Posterior averaging adds further accuracy under weak borrowing, namely for target-only learning and under risk-function shift (C-index 0.609→0.6640.609\to0.664; IBS 0.223→0.2100.223\to0.210), and it makes predictive performance more stable across replicates under both mismatch regimes (C-index SD 0.062→0.0190.062\to0.019 under calibration shift and 0.050→0.0200.050\to0.020 under risk-function shift). Under strong compatible borrowing, the posterior concentrates and the two predictions nearly coincide. Teacher guidance thus improves the single fitted model itself, while posterior averaging can further improve accuracy and stability when borrowing is weak or the teacher is mismatched; the joint posterior in addition quantifies uncertainty in individualized survival probabilities and RMST.

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Paper summary

BayCSD addresses survival prediction in a target population with few observed events when a stronger external model is available but its training records are not. It combines a continuous-time survival likelihood with a KL penalty comparing teacher and student conditional failure probabilities. The comparison intervals need not coincide with the student’s baseline-hazard intervals, allowing the method to borrow probability-scale information without grouping the original event and censoring times. A generalized-Bayesian formulation provides joint posterior estimates of the risk function and baseline hazard, from which survival probabilities and restricted mean survival time are calculated.

The evaluation includes simulations with compatible and mismatched teachers, three within-population benchmarks, and kidney-alone-to-kidney–pancreas transfer. The results generally support improved prediction over target-only learning. The evidence for useful uncertainty estimates is more qualified: borrowing narrows intervals, but their inclusion of the true survival probability can deteriorate when the teacher is miscalibrated.

Critical strengths

The method solves a specific modeling problem rather than adding an arbitrary distillation penalty. A teacher may report survival at a few horizons, while the target data contain exact follow-up times. BayCSD keeps those two representations separate and transfers information about both baseline risk and covariate effects.

The controlled comparisons are persuasive. The authors replace the distillation criterion and target likelihood separately while retaining the Bayesian student. On the transplant task, full BayCSD obtains IBS of 0.021424, compared with 0.023491 for risk-set distillation and 0.022989 for the grouped-likelihood variant. These experiments are more informative than simply showing that one complete system outperforms another with a different architecture and training procedure.

The treatment of uncertainty is more thoughtful than reporting narrower intervals as an automatic success. The analysis distinguishes posterior spread from the sampling variability of the fitted predictor, and the simulations explicitly show how teacher mismatch changes posterior centering. I also appreciate that the unfavorable truth-inclusion results are reported. They reveal a real limitation of borrowing rather than being hidden behind aggregate prediction scores.

Critical weaknesses

In Table 5, nominal 95% intervals achieve 75.57% truth inclusion under calibration shift after the borrowing weight has already been selected from target outcomes. The target-only model also undercovers, at 83.37%, but borrowing makes this particular result worse while improving prediction. Thus, target-guided weight selection does not reliably protect the uncertainty estimates from an inaccurate teacher. The authors acknowledge the conditional nature of their posterior; nevertheless, the reported interval reductions should not be interpreted as evidence of more trustworthy uncertainty under population shift.

The WAIC calculation needs a clearer methodological justification. Each subject affects the posterior through both its target likelihood and an outcome-dependent, masked distillation term. The reported correction uses only the posterior variance of the target log likelihood. It is therefore not clear that it estimates the relevant leave-one-subject-out predictive quantity for this generalized update. The cross-validation comparison provides useful empirical reassurance about prediction, but it does not examine whether the two selectors produce comparable interval accuracy. WAIC here should be treated as an empirically assessed heuristic unless a derivation is supplied.

The added value over simply adapting the teacher is not fully established. Direct teacher predictions are reported, which is good, but they already perform strongly: on SUPPORT, the teacher has better mean IBS and C-index than BayCSD. The within-population results therefore demonstrate recovery of external information more clearly than an advantage over using that external predictor. A teacher with its baseline hazard recalibrated on the target training data would be an informative comparator, particularly because baseline-calibration shift is one of the paper’s central examples.

The genuine population-shift evidence remains narrow. The kidney–pancreas cohort contains only 51 events, and the repeated cross-validation runs reuse the same recipients. The small repeat-level standard deviations show limited sensitivity to the chosen partitions; they do not establish uncertainty across new patient samples or centers. This matters particularly for the relatively small IBS improvement over the source teacher, from 0.021882 to 0.021424. Paired uncertainty for that difference would help distinguish a stable predictive advantage from a favorable mean ordering.

Questions for authors
  1. Does replacing WAIC with subject-level cross-validation improve truth inclusion, not just prediction, in the calibration-shift experiment? This would clarify whether the observed undercoverage primarily reflects weight selection or persists under the alternative selector already evaluated.

  2. How does BayCSD compare with the source teacher after target-only baseline recalibration? Such a comparison would help establish whether the transplant gains require learning a new flexible risk function or can largely be obtained by adjusting the teacher’s absolute survival scale.

3 comments

We thank the reviewer for the thoughtful assessment, in particular for recognizing the modeling problem BayCSD solves, the controlled comparisons, and the separation of posterior spread from sampling variability.

W1 / Q1. Interval accuracy under calibration shift and the role of weight selection.

We agree that narrower intervals alone do not establish more reliable uncertainty under population shift. In BayCSD, teacher predictions enter the generalized posterior as fractional pseudo-observations on the target subjects (Eq. 8), alongside the target likelihood, so the intervals quantify uncertainty given the target data and the teacher's information at the selected strength. When the teacher's risk ordering and absolute survival level are both correct (compatible teacher), this information concentrates the posterior around the right center: under compatibility, truth inclusion rises from 83.4% to 98.8% while interval width is roughly halved (Table 5). Thus, the target-only intervals already undercover, and compatible borrowing produces conservative inclusion in this experiment. Under risk-function shift, inclusion stays close to target-only learning (82.1%) with narrower intervals. Under calibration shift, the teacher retains accurate risk ordering and therefore remains highly predictive, so it is borrowed strongly; its shifted survival probabilities then move the posterior away from the target truth, and the selected borrowing strength determines how strongly this mismatch enters the update.

To examine the sensitivity of interval inclusion to weight selection, we evaluated truth inclusion under the subject-level five-fold cross-validation selector of Table 6 (Appendix J). Since cross-validation refits the model for every candidate weight, this comparison uses the ten replicates of Table 6; results are in Table R1.

Table R1. Truth inclusion and width of nominal 95% pointwise intervals after WAIC or five-fold cross-validation selects η\eta (teacher-mismatch simulation, the ten replicates of Table 6; averaged over the target event-time quartiles t25t_{25}, t50t_{50}, t75t_{75}).

Teacher regimeSelectorMedian η^\widehat\etaTruth inclusion (%)Width (10−210^{-2})
–Target-only (η=0\eta=0)083.554.7
CompatibleWAIC20098.823.7
Cross-validation20098.922.1
Calibration shiftWAIC12575.634.6
Cross-validation20066.530.2
Risk-function shiftWAIC382.043.3
Cross-validation10.579.741.2

Cross-validation does not improve inclusion: under calibration shift it selects even stronger borrowing than WAIC, and inclusion is lower (66.566.5% versus 75.675.6%). Both selectors target predictive accuracy and both favor a teacher that remains highly predictive, so the undercoverage reflects the teacher's shifted survival level rather than WAIC specifically. We have made explicit in the discussion of Table 5 that interval reductions are to be read together with teacher alignment.

W2. Justification of WAIC. We thank the reviewer for identifying this important distinction between the rationale for evaluating target prediction and the justification of the WAIC correction. The borrowing weight is selected for predictive performance on target outcomes, so each generalized posterior is evaluated with the target likelihood; the teacher KL term contributes to the posterior update but is not part of the target predictive density being evaluated. This parallels selecting the discounting parameter of a power prior by predictive criteria for the current data, such as DIC or LPML (Ibrahim et al., 2015). As the reviewer notes, a subject's follow-up also enters the distillation term through the resolved-comparison mask, so leaving out a subject removes both the subject's likelihood contribution and its masked distillation contribution, whereas the WAIC correction uses only the posterior variance of the target log likelihood. We therefore treat target-likelihood WAIC as an empirically assessed criterion for selecting the borrowing weight, with subject-level five-fold cross-validation, which refits the full update for each candidate weight (Appendix G.3.3), as the refitting-based check. The two selectors give similar predictive accuracy (Table 6): WAIC's IBS is within 0.005 of the best fitted candidate under every teacher. Cross-validation also does not improve truth inclusion under either mismatched teacher (Table R1, Appendix J). We have clarified this role of WAIC, with cross-validation as the refitting-based check, in Appendix D.

W3 / Q2. Value relative to the teacher and comparison with the recalibrated teacher. In the pooled-reference benchmarks, the teacher is fitted to 13–70 times more records from the same population, so the teacher and the pooled-data fit mark the high-information end of the benchmark; as the reviewer notes, these benchmarks measure how much of that information is recovered from predictions alone. BayCSD approaches the teacher on SUPPORT, matches it on METABRIC and improves on it on OPTN KI (Table 1). The comparison with an adapted teacher is most informative under genuine population shift, so we recalibrated the KI teacher on each KP outer-training fold, using the same continuous-time PWE likelihood, baseline partition and prior as BayCSD: (a) re-estimating the baseline hazard with the teacher risk score as an offset, which adjusts only the teacher's absolute survival scale, and (b) additionally estimating a calibration slope on the teacher log risk. Both treat the teacher's risk score as known, so their posterior intervals reflect uncertainty in the baseline hazard (and slope) only. All predictors use the repeated cross-validation partitions and evaluation of Table 2 (Table R2).

Table R2. OPTN KI-to-KP: BayCSD versus the KI teacher recalibrated on the KP training folds. Means ±\pm SD across the five repeats of five-fold cross-validation of Table 2.

MethodIBS (10−310^{-3}) ↓\downarrowCtdC_{\mathrm{td}} ↑\uparrow
KI teacher21.882±0.00321.882\pm0.0030.7048±0.00230.7048\pm0.0023
Recalibrated KI teacher (baseline)22.007±0.02622.007\pm0.0260.7048±0.00230.7048\pm0.0023
Recalibrated KI teacher (baseline + slope)21.731±0.21121.731\pm0.2110.7048±0.00230.7048\pm0.0023
BayCSD21.424±0.047\mathbf{21.424\pm0.047}0.7379±0.0048\mathbf{0.7379\pm0.0048}

Baseline-only recalibration slightly worsens the teacher's IBS, and adding a calibration slope improves it modestly; both leave its risk ordering, and hence CtdC_{\mathrm{td}}, unchanged. BayCSD improves on both recalibrated versions in IBS and CtdC_{\mathrm{td}}, reflecting what global recalibration cannot provide: adaptation of the risk function to KP recipients under teacher guidance. In the simulation (Appendix J, Table 16), recalibration removes the imposed calibration shift by construction, since it is a pure baseline multiplier, whereas under risk-function shift it cannot change the teacher's ranking and BayCSD improves the C-index (0.664 versus 0.632). We have added these comparators to Table 2.

W4. Paired uncertainty in the OPTN comparison. We added a recipient-level paired bootstrap using the saved out-of-fold predictions. Each of 1,000 draws resamples KP recipients with replacement, stratified by event status, and the same draw is applied to every method and all five cross-validation repeats; metrics are computed exactly as in Table 2 (Table R3).

Table R3. Recipient-level paired bootstrap for the OPTN KI-to-KP comparison (1,000 draws). Entries are differences, BayCSD minus comparator, with 95% percentile intervals; negative Δ\DeltaIBS and positive ΔCtd\Delta C_{\mathrm{td}} favor BayCSD.

ComparatorΔ\DeltaIBS (10−310^{-3}) ↓\downarrowΔCtd\Delta C_{\mathrm{td}} ↑\uparrow
Target-only Bayesian PWE−3.66-3.66 [−5.76,−1.81][-5.76,-1.81]+0.100+0.100 [0.033,0.165][0.033,0.165]
KI teacher−0.46-0.46 [−0.92,−0.04][-0.92,-0.04]+0.033+0.033 [0.002,0.067][0.002,0.067]
DiSKD−1.00-1.00 [−1.69,−0.39][-1.69,-0.39]+0.050+0.050 [0.009,0.097][0.009,0.097]
Component-wise KL−2.36-2.36 [−3.80,−1.06][-3.80,-1.06]+0.056+0.056 [0.024,0.090][0.024,0.090]

The IBS improvement over the KI teacher highlighted by the reviewer has an interval excluding zero, as does the CtdC_{\mathrm{td}} improvement; the same holds for the comparisons with target-only learning and both distillation methods. These paired intervals quantify recipient-level variability in the held-out comparisons, with the fitted predictors held fixed, complementing the across-partition SDs in Table 2. They are reported in Appendix I.8 and summarized in Section 4.4.

Dear Reviewer y9ur,

Thank you again for your thoughtful and detailed review. We have provided additional analyses and manuscript revisions in response to your concerns.

In particular, we have added comparisons of interval truth inclusion under WAIC and cross-validation, clarified the methodological interpretation and limitations of WAIC, and further discussed uncertainty under teacher mismatch. We have also added comparisons with target-data recalibrated teachers and recipient-level paired bootstrap intervals for the kidney-to-kidney-pancreas transfer experiment.

We believe these additions provide important evidence for evaluating both the predictive benefits and limitations of BayCSD.

We would greatly appreciate it if you could review our responses and revised manuscript, share any remaining concerns, and reconsider your assessment.

Thank you for your time and consideration.

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Paper summary

The paper proposes a way to predict patient survival from a small dataset by "borrowing" predictions from a model trained on many other patients, and training the new model to agree with those predictions at a few chosen time points while still fitting each patient’s exact event time in the new dataset. Its main contributions are this training (matching) approach, a Bayesian formulation that produces a range of plausible predictions for each patient rather than a single number, and some theory on how "borrowing" affects accuracy and uncertainty when the existing model is right. It is validated on simulated data where each patient’s true survival probability is known. Also, on three real datasets where part of the data is held out to represent the external population, and on a transplant registry where a model trained on kidney-only recipients is used to help predict outcomes for kidney-pancreas recipients.

Critical strengths
  1. The paper addresses a practical problem of training a survival model on a small dataset by reusing predictions of a stronger model trained on larger, inaccessible data.
  2. Unlike earlier methods of this type, BayCSD provides a range of plausible predictions for each patient rather than a single estimate, and it studies when those ranges can be trusted, including showing how they fail when the external model is wrong (unfortunately, many results such as Table 5, Figures 7 and 8 are given in the Appendix).
Critical weaknesses
  1. I am generally not convinced this paper is of interest to the ICLR community, as it is a niche application of distillation and uncertainty quantification. It is not clear which parts of the methodology given in Section 3 are novel (e.g. Sec. 3.1), and how they relate to prior work (Bayesian borrowing and distillation exist in non-survival settings). The two Propositions given in Sec. 3.4 are only stated without motivation for why they are important/interesting.
  2. The experiments make the new method look stronger than the evidence supports. The main comparison (Table 1) is against a model fitted to the small dataset alone, which is expected to do poorly in this setting by design, so beating it is a low bar (the more informative comparison, simply using the external model as-is, appears only in App. Table 10, where it matches or beats the new method on two of the three datasets). In the kidney transplant study (Table 2) there are only 51 observed events, which limits what can be concluded, yet no confidence intervals or tests are given for the differences between methods, and the +- values shown capture only variation across data splits, not the uncertainty that comes from having so few events. The comparison with competing methods in Table 2 also mixes several differences at once: the new method uses a different underlying model, averages many predictions, and is tuned differently. The paper’s own controlled variants, which swap in the competitors’ criteria but keep the new method’s model, give mixed evidence on this: one beats its competitor on both measures while the other improves ranking but has worse prediction error than DiSKD, so part of the advantage may come from the modeling setup rather than the new approach. Also, the simulations (Figs. 2 & 6) tell the model the correct structure of risk over time, and in every mismatch case tested the external model predicts better than the new one, so the method is never evaluated in the one situation where the right answer would be to ignore the external model.
  3. The main text is not self-contained: much of the evidence for the paper’s claims sits in the appendix (e.g., the comparison against the external model alone in Table 10, the coverage results in Table 5, and the controlled-variant details in Appendix I.3, quite a nice Figure 10), while the main text spends space on material that could be shortened. The split between the two parts (main/appendix) is weak and should be rethought.
Questions for authors
  1. Three sentences of the abstract starting with "A generalized" and ending with "reference inclusion" are particularly poorly written, full of jargon and unclear. What do "target-data fit", "borrowing-weighted distillation", "structural prior", "pooled-reference", "matched target-only learning" mean? What is the true meaning behind the middle sentence of "Controlled synthetic experiments characterize the benefits and limitations of borrowing under teacher compatibility and mismatch"?
  2. Can you compare against recalibrating the external model on the new data, e.g. refitting only an intercept and slope on its predicted risk? This requires no more than the predictions BayCSD already uses and is the standard way to adapt an external model to a new population, so it would clarify how much of the gain over the target-only model comes from the proposed distillation rather than from a simple adjustment of the external model.
8 comments

We thank the reviewer for the careful reading and for recognizing the practical problem BayCSD addresses and its individualized uncertainty quantification.

W1. Relevance, novelty and the role of the propositions. The proposed BayCSD addresses a learning problem that existing distillation and Bayesian borrowing formulations do not directly resolve: how to use an external model available only through survival predictions at selected horizons to support flexible continuous-time target learning and joint posterior inference when outcomes are censored and source records and corresponding source parameters are unavailable. The transplant application illustrates this problem; it does not define or restrict the methodology. Its relevance to machine learning lies in prediction-only transfer across different model representations, learning from partially observed outcomes, and understanding how transfer affects both prediction and uncertainty.

W1 (a). The survival-specific transfer problem. Censoring and continuous time create a substantive transfer problem. A censored observation does not provide a complete event-time label: it establishes only that the event has not occurred by the last observation. Moreover, a continuous-time hazard is an instantaneous rate, not a probability distribution to which ordinary classification-style KL can be directly applied. A teacher reporting survival probabilities at selected horizons also does not specify the complete continuous-time event-time density. The issue is therefore not that KL is undefined for continuous distributions, but that the complete teacher distribution needed for such a comparison is not supplied. Thus, neither treating censored follow-up as fully observed labels nor directly matching raw hazard outputs provides the required probability-based transfer mechanism. The methodological question is how to construct an appropriate teacher–student comparison while preserving the information in the target observations.

BayCSD addresses this through conditional interval-failure probabilities and a censor-aware comparison rule, while retaining the original event and censoring times in the target likelihood (Section 3.2). Crucially, the comparison partition governs only the resolution of teacher guidance; it does not determine the student’s likelihood or baseline-hazard partition. This separates the temporal representation of external knowledge from the temporal representation used for target learning. Unlike grouped-time approaches such as DiSKD, it does not require grouping the target observations onto the comparison grid. Unlike Cox risk-set distillation, its comparison retains information about both the covariate-dependent risk function and the absolute baseline survival scale. These distinctions determine what information can be transferred and what information is preserved—not merely the algebraic form of a penalty.

W1 (b). Novelty relative to distillation and Bayesian borrowing. The teacher-induced pseudo-prior provides a bridge from survival distillation to joint posterior inference. A central contribution of Section 3.3 is to convert teacher survival predictions into a structured fractional pseudo-likelihood, or equivalently a teacher-induced pseudo-prior when combined with the structural parameter prior. Equations (8)–(9) show precisely how each included teacher–student comparison contributes fractional event and event-free information. These contributions are coupled through the student’s continuous-time model, informing both its nonlinear risk function and baseline hazard; they are not independent beta priors assigned to unrelated interval probabilities.

This construction changes the inferential object from a distilled point estimator to a joint generalized posterior over target survival models. Posterior draws propagate uncertainty in both model components to individualized survival curves and restricted mean survival time, even when the teacher supplies only point predictions. The pseudo-count interpretation therefore has a substantive role: it identifies how external predictive knowledge enters inference, separates teacher borrowing from structural regularization, and explains how teacher guidance can stabilize learning when target events are sparse.

(W1 (b). Novelty relative to distillation and Bayesian borrowing continued)

These posterior summaries provide patient- and horizon-specific measures of model-based estimation precision that point predictions and aggregate accuracy metrics do not convey. For example, two patients may have similar predicted post-transplant event-free survival probabilities but different posterior interval widths. Reporting both the estimates and their intervals makes that difference in estimated precision explicit, rather than presenting both prognoses as equally certain. The value is to characterize uncertainty about the estimated survival probability within the fitted model, not to equate a narrow interval with a small prediction error. Accordingly, our evaluation examines interval width together with truth inclusion in simulations and with inclusion of estimated pooled-model predictions in Section 4.3, rather than treating interval narrowing alone as evidence of accuracy.

This also clarifies the distinction from existing Bayesian borrowing. Conventional historical-data power priors (Ibrahim and Chen, 2000) require access to the source likelihood, while posterior-to-prior transfer (e.g., Paolucci et al., 2023; Shwartz-Ziv et al., 2022) requires a source parameter distribution and correspondence for the transferred parameters. BayCSD instead constructs the borrowing contribution from teacher predictions evaluated on target subjects, without reconstructing source records or transferring a source parameter posterior. The generalized Bayesian framework of Bissiri et al. (2016) supplies the updating principle; BayCSD supplies the survival-specific probability construction, its connection to original-time learning, and the analysis of the resulting inference. Because the teacher contribution depends on target follow-up through the comparison masks, the teacher contribution is appropriately interpreted as a data-adaptive pseudo-prior rather than a conventional data-independent prior. The resulting uncertainty is conditional on the fitted teacher, comparison partition, and borrowing weight.

W1 (c). Role of the propositions. The theoretical results explain when borrowing helps and what its uncertainty means. The propositions answer concrete questions about this construction. Proposition 1 asks whether compatible teacher information improves estimation rather than merely forcing agreement with a teacher. Under the stated compatibility and regularity conditions, the teacher contribution adds positive-semidefinite curvature without displacing the population target or adding first-order score variability. This yields a reduction in the first-order sampling variability of the fitted model. The accompanying posterior analysis distinguishes this sampling variability from posterior spread—an essential distinction when interpreting uncertainty after distillation. The mismatch expansion in Eq. (12) then identifies the first-order direction and magnitude of borrowing-induced displacement as the borrowing weight increases from zero. Together, these results explain why informative borrowing can stabilize estimation, but stronger posterior concentration need not imply better centering under population shift.

Proposition 2 addresses a different question: does the interval-based comparison have a meaningful continuous-time interpretation, or does it depend arbitrarily on the chosen grid? Under its stated conditions, refinement of the comparison partition leads to a well-defined integrated-hazard discrepancy over observed follow-up. This establishes the continuous-time quantity approximated by the finite-partition criterion, without requiring refinement of the student’s baseline model or discretization of its target likelihood. Appendix B.5 further establishes convergence of the corresponding generalized posterior under its stated assumptions, connecting refinement of the comparison criterion to stability of posterior inference.

Section 3.1 specifies the target model and likelihood on which these developments operate; the methodological contributions are the transfer construction in Section 3.2, the prediction-to-posterior construction in Section 3.3, and their analysis in Section 3.4. The revised Section 3.4 now explicitly motivates these results, and the controlled variants in Section 4.4 separately examine the roles of probability-scale transfer and original-time likelihood learning within the same Bayesian student. Taken together, the contribution is a framework for prediction-only transfer and uncertainty-aware learning with censored continuous-time outcomes, rather than an application-specific predictor or a generic uncertainty calculation attached to an existing distillation method.

W2 (a). Comparators in the pooled-reference benchmarks. These benchmarks measure how much of the information in a large external dataset can be recovered when only the predictions of a model fitted to it are available. The teacher is fitted to 13–70 times more records from the same population (e.g., 6,998 versus 100 subjects in SUPPORT), so the teacher and the pooled-data fit (Table 10) mark the high-information end of the benchmark. The matched target-only learner isolates the contribution of the teacher's predictions, and the pooled-data fit provides the high-information reference for evaluating recovery: relative to target-only learning, BayCSD reduces reference survival RMSE by 55–72% and yields 43–73% narrower posterior intervals at the same 95% inclusion of the pooled-data reference, which direct use of the teacher does not provide.

We agree that these results demonstrate recovery of external predictive information, not general superiority over direct teacher use. For example, on SUPPORT the teacher has better mean IBS and C-index than BayCSD (0.2187 versus 0.2218 and 0.6185 versus 0.6060); on METABRIC their performance is similar, and on OPTN KI BayCSD improves on the teacher in both metrics (IBS 0.0313 versus 0.0334 and C-index 0.7716 versus 0.7671). When the teacher already transports well and only point prediction is required, deploying it directly may be preferable. We have added the teacher-only IBS and C-index results from Appendix Table 10 to the main comparison (Table 1) so that this limitation is visible alongside the target-only results. Inclusion here is measured against the pooled-data reference, the high-information proxy available in real data; truth inclusion is assessed in the simulations.

W2 (b). Uncertainty in the OPTN comparison. We agree that the across-repeat SD does not reflect the limited number of KP events. We added a recipient-level paired bootstrap using the saved out-of-fold predictions. Each of 1,000 draws resamples KP recipients with replacement, stratified by event status, and the same draw is applied to every method and all five cross-validation repeats; metrics are computed exactly as in Table 2 (Table R1).

Table R1. Recipient-level paired bootstrap for the OPTN KI-to-KP comparison (1,000 draws). Entries are differences, BayCSD minus comparator, with 95% percentile intervals; negative Δ\DeltaIBS and positive ΔCtd\Delta C_{\mathrm{td}} favor BayCSD.

ComparatorΔ\DeltaIBS (10−310^{-3}) ↓\downarrowΔCtd\Delta C_{\mathrm{td}} ↑\uparrow
Target-only Bayesian PWE−3.66-3.66 [−5.76,−1.81][-5.76,-1.81]+0.100+0.100 [0.033,0.165][0.033,0.165]
KI teacher−0.46-0.46 [−0.92,−0.04][-0.92,-0.04]+0.033+0.033 [0.002,0.067][0.002,0.067]
DiSKD−1.00-1.00 [−1.69,−0.39][-1.69,-0.39]+0.050+0.050 [0.009,0.097][0.009,0.097]
Component-wise KL−2.36-2.36 [−3.80,−1.06][-3.80,-1.06]+0.056+0.056 [0.024,0.090][0.024,0.090]

All four paired differences have intervals excluding zero in both metrics. These paired intervals quantify recipient-level variability in the held-out comparisons, with the fitted predictors held fixed, complementing the across-partition SDs in Table 2. These intervals are reported in Appendix I.8 (Table 14) and summarized in Section 4.4.

W2 (c). Isolating the contribution of the method. The controlled variants are designed for exactly this purpose. Each retains the same student architecture, structural prior, posterior averaging and borrowing-weight selection procedure, and replaces a single component, so the comparison that isolates the method is between full BayCSD and each variant. BayCSD improves on both variants in both metrics (Table 2: IBS 21.4221.42 versus 23.4923.49 and 22.9922.99 (10−310^{-3}), and CtdC_{\mathrm{td}} 0.7380.738 versus 0.7250.725 and 0.7030.703, for the risk-set and grouped-likelihood variants, respectively). Comparing a variant with DiSKD or component-wise KL instead reintroduces the differences in the underlying model.

These results support the two design choices within the matched Bayesian PWE framework: replacing the probability-scale criterion mainly worsens IBS, while replacing the original-time likelihood worsens both metrics. They do not attribute the entire difference between complete systems to the distillation criterion alone. Architecture, posterior averaging, and tuning can also contribute, as the reviewer’s cross-system comparisons illustrate. The additional MAP-versus-posterior-mean analysis in Appendix J examines the role of averaging while holding the selected borrowing weight fixed: teacher guidance substantially improves the single fitted model itself (MAP C-index 0.5660.566 without borrowing versus 0.7620.762 with the compatible teacher).

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Paper summary

The paper introduces an distillation technique for survival models, which is trained on data that is not always available. Through a teacher model trained on a different dataset, paremeters are used in the training of a student model by the concept of borrowing. The work goes well into the mathematics and is supported by an extensive appendix. The work also provides some mathematical guarantees on the borrowing methodology to prove its validity. The method is then tested on simulated data and real datasets. The work is also tested under 3 different scenarios on how to provide the teacher-student interaction. The results show that the methodology is sound if appropriate parameters concerning the borrowing is set. The method works very well if the teacher model is trained from similar data (same covariate effects) and the same right censoring is used.

Critical strengths

[S2] The article is well written and has a clear problem statement with a clear goal. The conclusion is a clear and honest conclusion.

[S1] The paper is supported by a lot of mathematical explanations, which seem sound to me. The work also provides guarantees on the different aspects of the methodology (e.g. that there is always an information gain through the borrowing). The method is also tested in simulated data and real-data and even a realistic data transfer setup. This makes the study very complete.

Critical weaknesses

[W1] Although the paper is complete within the content, the work involves a lot of information that the reader has to go through. A lot of details about the setup, proofs and so on, are mentioned in an extensive appendix. This requires quite some effort in understanding the paper. Some results in the appendix, would fit more in the main article (e.g. table 6).

[W2] For me it is not really clear how the borrowing method works. What is actually borrowed and how do you select with part of the dataset or model is borrowed?

Questions for authors

[Q1] - In Table 2, the results for the transfer KI-to-KP are mentioned. There the external model (KI Teacher) is already performing very good, better than state of the art. The distilation with the BayCSD method shows only a marginal improvement towards the KI teacher. So, how important is it to already have a good teacher? Is it really worthwhile this complexity of the method when the KI teacher already shows good results?

[Q2] - The risk-function shifts alters the covariate effects. But how large was this difference between the teacher and student model. Does this depend on the type and/or nature of the parameter.

5 comments

We thank the reviewer for the positive assessment and constructive suggestions.

W1. Organization. We appreciate this suggestion and revised the paper accordingly. For Table 6, which compares WAIC with five-fold cross-validation for choosing η\eta, Section 4.2 states its conclusion directly: the two selectors give similar prediction accuracy: WAIC's IBS is within 0.0050.005 of the best fitted candidate under every teacher, and it is closer to that candidate than cross-validation under risk-function shift, where the borrowing path has a clear interior optimum. The revision adds that cross-validation does not improve interval coverage either (Appendix J). We kept the full table in the appendix for the detailed numerical comparisons, while summarizing its principal findings and providing a direct reference in the main text.

To make the method easier to follow, we have expanded the main-text explanations of how the comparison partition is chosen (Section 3.2), added a numerical example of how teacher predictions enter the posterior as pseudo-observations (Section 3.3), and clarified the question each proposition answers (Section 3.4). We have also defined the Linear, SimpleNN, and ComplexNN students in Section 4.2. The recalibrated KI teachers in Table 2 provide a main-text comparison with the simpler alternative of teacher recalibration, which does not attain BayCSD’s predictive performance in this application.

For supporting details that remain in the appendix, the main text provides explicit pointers to the censoring conventions (Appendix A.1), the PWE specification and priors (Appendices A.2 and C), borrowing-weight selection (Appendix D), and evaluation estimators (Appendix E). A new Appendix L lists the notation with the section in which each term is defined, and Section 3 points to this summary at the outset. These revisions are intended to reduce unnecessary navigation while retaining the detailed derivations and experimental specifications for readers who wish to examine them.

W2. What is borrowed. BayCSD borrows the teacher's knowledge expressed through individualized survival probabilities, rather than source observations or teacher parameters. Specifically, the teacher provides predictions for the target-training subjects at the comparison endpoints, and these predictions are held fixed during student learning. Survival probabilities provide a common basis for borrowing across models with different covariates, parameterizations, or architectures, without requiring parameter correspondence. The KL term encourages the student’s predictions to agree with the teacher’s, while the target likelihood allows the student to adapt to the observed target outcomes.

The teacher predictions are converted into conditional interval failure probabilities (Eq. 3): pikep^e_{ik} is the teacher's probability that subject ii, event-free at the start of comparison interval kk, fails within it, and Wik=1W_{ik}=1 when the subject's observed follow-up resolves this comparison. Each resolved subject–interval comparison contributes ηWikpike\eta W_{ik}p^e_{ik} fractional pseudo-events and ηWik(1−pike)\eta W_{ik}(1-p^e_{ik}) fractional pseudo-non-events (Eq. 8). These contributions form a structured fractional pseudo-likelihood, allowing external predictive information to enter the generalized posterior alongside the exact-time target likelihood and structural prior. The pseudo-counts describe the teacher’s contribution to the update.

Importantly, the student conditional failure probabilities depend jointly on the relative-risk function and cumulative baseline hazard (Eq. 6). Thus, borrowing on the probability scale informs both components, including the absolute survival scale that risk-set distillation normalizes away. No source-data subset or teacher parameter block is selected for transfer; the censor-aware mask WikW_{ik} determines which comparisons are included, and η\eta controls the overall borrowing strength. The mask is determined by observed follow-up, rather than by an assessment of teacher reliability for individual subjects or intervals.

For data-adaptive borrowing, we fit the student at candidate values of η\eta from a prespecified grid containing zero and select the value minimizing target-likelihood WAIC (Appendix D). This selects the overall influence of teacher guidance according to predictive fit to the target outcomes; η=0\eta=0 recovers the target-only model.

Q1. Value of BayCSD when the teacher is strong.

We thank the reviewer for this important question. We agree that the benefit of borrowing and the incremental value over direct teacher deployment should be distinguished more clearly.

Useful borrowing depends on whether the teacher provides information relevant to the target population, not simply on its performance in the source population. An imperfect teacher can still help: in Appendix J, the orthogonal teacher performs worse than target-only learning but retains two correct covariate blocks, and weak borrowing yields a modest improvement. With the reversed teacher, WAIC selects η=0{\eta=0} in all 20 replicates, recovering target-only learning (Table 17). These results demonstrate adaptive downweighting in the studied settings, rather than guaranteed protection against negative transfer under arbitrary teacher mismatch.

If the teacher transports well and point predictions suffice, direct deployment may be an adequate choice. If the discrepancy is limited to the baseline hazard or a global risk-score slope, target-data recalibration is a relevant, simpler alternative; our added simulation confirms its advantage under pure baseline shift (Appendix J, Table 16).

BayCSD is intended for settings where sparse target outcomes must support a flexible target-specific risk function using external predictions, without access to source records or corresponding teacher parameters. It retains the exact target event and censoring times and uses the teacher’s survival probabilities to inform both covariate effects and baseline survival. This permits adaptation beyond baseline or slope recalibration.

In KI-to-KP transfer, BayCSD also improves upon direct KI teacher prediction (Table 2): IBS decreases from 21.882 to 21.424 (×10−3\times10^{-3}), and CtdC_{\mathrm{td}} increases from 0.7048 to 0.7379. We acknowledge that the IBS improvement over this strong teacher is modest, although its recipient-level paired bootstrap 95% interval excludes zero ([−0.92,−0.04]×10−3[-0.92,-0.04]\times10^{-3}; Appendix I.8). Moreover, the added baseline and baseline-plus-slope recalibration comparisons do not attain BayCSD’s performance in either metric in this application, supporting the value of adaptation beyond these simpler updates.

BayCSD additionally produces joint posterior summaries for individualized survival probabilities and RMST. These provide patient- and horizon-specific measures of model-based estimation precision that a point prediction alone cannot convey. Joint posterior draws propagate uncertainty in both the risk function and baseline hazard to the survival probability or RMST of interest. For example, two patients may have similar predicted post-transplant survival probabilities but substantially different posterior interval widths. Reporting the estimates together with their intervals makes this difference in estimated precision explicit, rather than presenting both predictions as equally certain. Such information can support more cautious interpretation and communication of individualized prognosis, particularly when the posterior spans a broad range of survival probabilities. These summaries provide an explicit characterization of conditional uncertainty that complements predictive accuracy. Their interpretation should be accompanied by assessment of teacher–target compatibility and predictive validation, because posterior concentration does not itself rule out prediction bias. We therefore view flexible target adaptation and patient-specific uncertainty characterization as complementary reasons for the added complexity, with the value of borrowing assessed against direct teacher use, recalibration, and target-only learning in the intended application.

Q2. Magnitude and nature of the risk-function shift. The target generating model uses covariate-block weights (0.6,0.8,1.0)(0.6,0.8,1.0), whereas the risk-shifted source uses (0.6,0.8,−0.1)(0.6,0.8,-0.1) (Appendix G.1, Eq. 75). Thus, the third block, involving four of the twelve covariates, changes both sign and magnitude, while the other two block weights and the baseline generating mechanism remain unchanged. The resulting source and target population log-risk functions have a correlation of approximately 0.630.63 under the simulated covariate distribution.

Yes, the effect depends on the type of parameter change and how it alters predictions over the target covariate distribution. For example, the separate calibration-shift experiment multiplies the baseline hazard by 1.5, changing absolute survival probabilities while preserving risk ranking. In contrast, the block-weight shift changes the covariate-dependent risk function and can alter the ordering of subjects’ risks.

More generally, since BayCSD borrows survival predictions rather than teacher parameters, the relevant teacher–target mismatch is expressed through discrepancies in conditional failure probabilities. Eq. (12) characterizes the local borrowing-induced displacement:

ϑη⋆−ϑ0=−ηHR−1∇Q(ϑ0)+o(η),η↓0,\vartheta_\eta^\star-\vartheta_0 = -\eta H_R^{-1}\nabla Q(\vartheta_0)+o(\eta), \qquad \eta\downarrow0,

where ϑ0\vartheta_0 is the target parameter, ϑη⋆\vartheta_\eta^\star the population center under borrowing weight η\eta, HRH_R the curvature of the target-likelihood criterion, and ∇Q(ϑ0)\nabla Q(\vartheta_0) the gradient of the teacher--student discrepancy at ϑ0\vartheta_0. The displacement depends on the resulting probability-scale discrepancy and the local target-likelihood curvature, rather than simply the numerical magnitude of an individual parameter change.

Ethics. SUPPORT and METABRIC are publicly available datasets; we use their processed versions released with DeepSurv (Katzman et al., 2018). The multiple myeloma TT2 and TT3 data used in the added analysis are publicly available through the MAQC-II study. The OPTN data are de-identified registry records obtained through a data request to the Organ Procurement and Transplantation Network, subject to applicable data-use requirements. The cohort construction is described in Appendix I.1.

The standard OPTN acknowledgment and disclaimer were omitted for double-blind review and will be restored in the camera-ready version. We have added a data-availability statement to the revised PDF.

Reviewer_s5w9OpenReview ↗
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Paper summary

The paper considers survival distillation based on a Bayesian framework under a continuous time scale for relative risk models. Under teacher compatibility, local information augmentation and the posterior-sampling covariance (which is smaller than that based only on a student model) are characterized. The first-order displacement under teacher mismatch and the integrated-hazard limit under comparison-partition refinement are also characterized. Empirical results show that the proposed BayCSD provides desirable results in terms of efficiency and robustness.

Critical strengths
  • The paper provides a framework that does not require discretization of continuous survival times.
  • The proposed BayCSD shows superior performance in the empirical results.
Critical weaknesses
  • Although a continuous time scale can be accommodated, partitioning of time is still required for distillation. Guidelines on how to construct these intervals, and on their impact, are somewhat lacking.
  • The main manuscript is not carefully written. Many terms are not clearly defined, or are defined in the Appendix without any reference to where the definitions are.
Questions for authors
  • More details should be provided on how the time interval is partitioned to construct the comparison intervals. The impact of its refinement (including its limit) is investigated theoretically (Equation (12)) and, to a certain degree, empirically (Appendix G.4.2). However, its implementation is still not clear. Please provide more detailed guidelines on how to construct the intervals.
  • This is related to the previous comment. The conditional probabilities (Equation (3)) are based on a Bernoulli distribution. Does this mean that each interval should contain at most one event?
  • The authors used a piecewise-exponential baseline hazard. Further details are needed on how to determine the number and lengths of these pieces.
  • Figure 2 provides empirical results under teacher compatibility for various teachers. Under calibration shift, BayCSD does not perform better than Teacher only. Can the authors explain these findings?
  • The definitions of many terms are omitted. Some definitions can be found in the Appendix, but the main text does not point to them. In general, the manuscript is clearly written, but these omissions made it difficult to read.
4 comments

We thank the reviewer for the constructive comments and for recognizing that BayCSD avoids discretizing continuous survival times, as well as its empirical performance. We address the questions below.

W1 / Q1. Construction of the comparison partition. The comparison partition determines the temporal resolution of the teacher–student probability discrepancy. Its cutpoints need not coincide with those of the student’s baseline-hazard partition. Importantly, the target likelihood retains the original event and censoring times regardless of the comparison partition. Thus, partitioning is used to construct probability comparisons for distillation, not to group the target observations in the likelihood.

The comparison partition is constructed within the time range where teacher survival predictions are available (Appendix A.1). When predictions are reported at selected horizons (e.g., 1-, 3-, and 5-year survival), these horizons can define the comparison intervals. The continuous-time student is evaluated at those same teacher-reported endpoints, and Eq. (3) converts both sets of survival probabilities into conditional interval-failure probabilities. This accommodates differences between the teacher’s reporting grid and the student’s temporal representation without requiring interpolation of the teacher predictions or alignment of the student’s baseline-hazard cutpoints with the teacher grid.

When predictions are available throughout follow-up, the construction rule is specified before fitting:

  • Synthetic studies: K=20K=20 endpoints on a fixed grid (Appendix F) or at quantiles of the target training cohort's observed follow-up times (Appendix G.1).
  • Pooled-reference benchmarks: K=20K=20 endpoints τk=(k/20)1.5 τ\tau_k=(k/20)^{1.5}~\tau over the dataset-specific prediction horizon τ\tau (365 days for SUPPORT and OPTN KI, 120 months for METABRIC), which places shorter intervals early in follow-up, providing finer comparison resolution in that period where the hazard changes fastest and most subjects remain at risk (Appendix H).
  • OPTN transfer: K=12K=12 monthly intervals over the one-year outcome window, shared by all interval-based methods (Appendix I.2).

Regarding its impact, Proposition 2 (Eq. 13; Appendix B.5) establishes convergence to an integrated-hazard discrepancy as the comparison partition is refined. Appendix G.4.2 further examines K=5,10,20,40K=5,10,20,40 while keeping the student model unchanged. Prediction and posterior-interval summaries are stable from K=10K=10 onward (IBS: 0.1854, 0.1852, and 0.1853 for K=10,20,40K=10,20,40).

In practice, we recommend first fixing a clinically relevant horizon supported by the teacher, using the available teacher horizons or a modest prespecified grid, and checking sensitivity to a coarser and a finer grid when the teacher can provide predictions at the required endpoints. Any data-derived cutpoints should use the training data only. When teacher predictions are limited to a few reported horizons, those horizons provide a natural comparison grid; a finer distillation grid is not required merely because the student is a continuous-time model. We have added the construction details to Section 3.2 and these recommendations to Appendix A.1 of the revised PDF.

Q2. Bernoulli formulation. Each Bernoulli outcome is defined for an individual subject: whether a subject who is event-free at the start of an interval experiences the event within it. In the time-to-first-event setting considered here, each subject contributes at most one endpoint event over follow-up (for example, a death in a mortality analysis). However, multiple subjects can experience their respective events within the same interval. An interval can therefore contain any number of events across subjects, and there is no restriction on interval length imposed by this Bernoulli formulation. Interval width nevertheless determines how much temporal detail is available for distillation (W1 / Q1).

Q3. PWE baseline partition. The number and lengths of PWE intervals balance temporal flexibility against estimation stability, particularly when observed events are sparse. In the real-data settings, we allocate finer resolution early in follow-up, where baseline risk may change more rapidly, and use longer intervals later to avoid estimating excessive hazard parameters with limited event information. For example, OPTN uses cuts at 7, 14, 30, 60, 90, 180, and 270 days (Appendix I.2), while the pooled-reference benchmarks use seven cuts at fixed fractions of their respective prediction horizons (Appendix H). Gamma priors further regularize the baseline rates, with prior expected cumulative-hazard increments proportional to interval lengths (Eq. 49).

For controlled simulations, the teacher-mismatch experiment uses the known four-piece baseline structure of the data-generating model (Appendix G.1), while the student-capacity experiment deliberately varies baseline complexity (Appendix F). All matched target-only and BayCSD fits retain the same baseline specification. The baseline cutpoints need not coincide with the comparison endpoints. These are reproducible experimental specifications rather than an established optimal partition rule. For a new application, we recommend a parsimonious baseline partition chosen from clinical time scales and training-data support, considering both the observed event counts and follow-up exposure within candidate intervals, followed by a training-only sensitivity assessment of baseline complexity. Specifically, coarser and finer baseline partitions can be compared while keeping the distillation comparison grid fixed, so that sensitivity to baseline complexity is assessed separately from sensitivity to the resolution of teacher guidance. We have added this recommendation to Appendix A.2.

Q4. Calibration shift in Figure 2. BayCSD indeed remains slightly behind direct teacher prediction in this setting. The calibration-shifted teacher is constructed from a model fitted to 50,000 source subjects generated from the target law. Multiplying its baseline hazard by 1.5 preserves the learned covariate effects and risk ordering, so it remains a strong teacher despite the shift in absolute survival probabilities. With only 200 target subjects (approximately 51 events), WAIC still selects an intermediate borrowing weight for this teacher (median η^=75\widehat\eta=75, between 100100 under compatibility and 55 under risk-function shift). The probability-scale discrepancy transfers both its useful risk ordering and its shifted survival level, which the sparse target outcomes only partly correct.

The added recalibration comparison clarifies this case: under calibration shift, IBS is 0.177 for baseline recalibration, 0.193 for the unmodified teacher, and 0.199 for BayCSD (Appendix J, Table 16). Thus, when the teacher’s covariate effects transport well and only its baseline needs adjustment, simple recalibration can be preferable. Under calibration shift, BayCSD nevertheless improves on target-only learning in all four metrics (C-index, IBS, survival RMSE and predictive deviance), raising the C-index from 0.611 to 0.752. Under risk-function shift, by contrast, recalibration uses the teacher score as its only risk input, so it cannot learn a target-specific risk ordering, and BayCSD attains a higher C-index than both the teacher and the recalibrated teacher (0.6640.664 versus 0.6320.632). BayCSD’s additional flexibility is most relevant when adaptation requires changes to the target risk function beyond a baseline adjustment.

W2 / Q5. Definitions. We thank the reviewer for this concrete feedback. We have revised the presentation in the following three ways, with additions highlighted in blue in the revised PDF:

  • Definitions in the main text. We have added or clarified the construction of the comparison partition (Section 3.2); the teacher hazard hie(t)=−dlog⁡Sie(t)/dth_i^e(t)=-\mathrm{d}\log S_i^e(t)/\mathrm{d}t and Qn,mQ_{n,m}, the criterion in Eq. (5) on the mm-th partition of a refining sequence, in Proposition 2; and the Linear, SimpleNN and ComplexNN students in Section 4.2.
  • Pointers to supporting details. The main text now directs readers to the relevant appendices for the censoring conventions (Appendix A.1), the PWE realization and identification constraints (Appendix A.2), structural priors and posterior computation (Appendix C), borrowing-weight selection (Appendix D), and evaluation estimators (Appendix E).
  • Notation summary. A new Appendix L (Table 20) lists the main notation and terminology together with the section and equation in which each is defined, and Section 3 points to it at the outset.

We appreciate the reviewer’s suggestion, which has helped us identify where clearer definitions and more explicit cross-references were needed.

I thank the authors for their additional efforts in clarifying the construction of comparison and baseline partitions of time intervals, the Bernoulli formulation, and the definitions throughout the manuscript as well as for adding the recalibration comparison,. The revised manuscript is much clearer. However, these clarifications do not change my overall evaluation of the paper’s contribution, and I will keep my original score.

We thank the reviewer for acknowledging the clarifications and improvements in the revised manuscript.

We respect the reviewer’s overall assessment, but would appreciate some clarification regarding the remaining concerns about the paper’s contribution.

In the original review, the main concerns focused on the construction of the comparison and baseline partitions, the Bernoulli formulation, the calibration-shift results, and the clarity of definitions. We have addressed these points individually through detailed explanations, additional experiments, and revisions to the manuscript.

Since the original review did not identify a specific concern regarding methodological novelty or the significance of the contribution beyond these issues, we would appreciate it if the reviewer could clarify which aspects of the contribution remain insufficient. This would help us better understand the remaining concerns and facilitate a more informed assessment during the final discussion.

Thank you again for your time and consideration.

Comments on the paper

1 comment

Dear Reviewers,

As the discussion period is approaching its end, we would greatly appreciate it if you could review our responses and the revised manuscript, and share any feedback or remaining concerns. We would be happy to provide further clarification if needed.

Thank you for your time and consideration.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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