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Paper summary
This paper proposes TTE-PFN, a pretrained network that uses labeled right-censored observations to predict survival distributions for new patients without further gradient-based training. Compared with SurvivalPFN, the main changes are training on known synthetic distributions rather than sampled outcomes, varying the context size, and using a broader synthetic prior. The paper provides theoretical results and comparisons with 28 methods on 115 datasets. However, I am not convinced that the chosen synthetic prior offers a reliable advantage over alternatives (e.g. power prior, emoirical Bayes, Bayesian or transfer learning alternatives). A clearer prior-selection procedure and a consistent evaluation protocol are needed.
Critical strengths
The benchmark and nemuerical studies are extremely extensive. The results suggest that all three proposed changes contribute, especially with the broader prior.
Critical weaknesses
- My main concern is the choice of synthetic prior, which needs stronger justification. The authors specify five generators with fixed mixture weights and particular distributions for covariates, effects, and censoring. How were these choices made, and how should a user judge whether they are suitable for a new dataset? The prior seems account for the largest improvement in the numerical evaluation, so its selection is central to the contribution. The leave-one-generator-out analysis is useful, but sensitivity to mixture weights, effect strengths, and censoring settings is also needed. Please clarify whether the prior was designed using separate development datasets or revised after examining benchmark results.
- The paper builds on survival-PFN. The added value over SurvivalPFN and simpler regularized methods remains unclear. The oracle and sampled-label objectives have the same population target, so the benefit of oracle supervision is mainly computational. Please distinguish the SurvivalPFN comparison from the controlled ablation that holds the new architecture fixed. In addition, the possibility that prior information improves small-sample prediction is not enough to justify this particular prior. Carefully tuned comparisons with simpler Bayesian, power prior, or empirical-Bayes survival models would help establish its value.
- The optimality result holds under the chosen prior. The error bound assumes posterior concentration and overlap between the target-task distribution and the training distribution, while retaining a prior-mismatch term. These results help describe possible errors, but do not show when TTE-PFN should outperform a local estimator or how to recognize a poor prior (i.e. how to prevent negative learning). Can the authors provide a practical check for prior–data conflict or identify settings in which the method performs worse?
- Recalibration is applied specifically for IBS and KM-Cal, although the appendix shows that it can worsen MAE-PO. Please evaluate the raw and recalibrated predictors separately on all metrics and allow comparable recalibration for competing methods.
- The marginal Kaplan–Meier censoring weights also need justification when censoring depends on covariates. In addition, the log-rank comparison of predicted medians and observed times does not measure patient-level discrimination: permuting predictions among patients leaves that statistic unchanged.
- Random splits provide evidence for prediction within a cohort. They do not show that historical patients provide an adequate context for future patients whose outcome relationships may change
- The output approximates a posterior-predictive distribution, not a posterior over survival functions. The reported calibration measures are useful, but do not establish uncertainty about the model from variation in patient outcomes. Predictive-interval coverage and width under small samples, heavy censoring, and prior misspecification would strengthen the evaluation.
Questions for authors
please see the weakness section
4 comments
R2 [W2]: (i) Contributions beyond SurvivalPFN. We agree that TTE-PFN builds on the amortized inference framework of SurvivalPFN. Our contributions focus on a theoretically motivated pretraining framework combining oracle distillation, context-size randomization, and a structurally diverse synthetic prior. As established in our analysis, oracle distillation and sampled-label supervision share the same population minimizer. The primary benefit of oracle supervision is therefore the reduction of gradient variance associated with label sampling, rather than a different population-level objective. Context-size randomization supports inference across varying amounts of labeled context, while the diverse synthetic prior aims to cover heterogeneous covariate effects and event-time distributions. We do not claim that the specific prior configuration is uniquely optimal, and we separately examine its sensitivity in our response to R1 [W1].
(ii) Official SurvivalPFN comparison versus controlled ablation. We agree that the original presentation did not sufficiently distinguish the official SurvivalPFN comparison from the controlled ablation of our proposed components. We have therefore extended the factorial ablation to explicitly account for backbone architecture, as shown in Rebuttal Table 3 [https://anonymous.4open.science/r/TTEPFN/Table3.png ]. All eight combinations of oracle distillation (A), context-size randomization (B), and the diverse synthetic prior (C) are evaluated using the same two-way attention backbone. We additionally evaluate TTE-PFN with the TabDPT backbone while retaining all three pretraining components, and report the original SurvivalPFN separately.
The complete TTE-PFN achieves the best Overall average rank (4.07), closely followed by TTE-PFN (TabDPT) (4.10). In contrast, the original SurvivalPFN obtains an Overall rank of 7.23. This comparison suggests that the choice between the two backbones has a relatively small effect on aggregate performance in our evaluation, whereas the proposed pretraining framework yields substantial improvements even when using the TabDPT backbone. Within the controlled factorial ablation, removing the diverse prior causes the largest single-component degradation, increasing the Overall rank from 4.07 to 6.95, compared with 4.70 without context-size randomization and 4.26 without oracle distillation.
We have clarified the distinction between backbone-controlled ablations and the original SurvivalPFN comparison in the final version.
(iii) Additional comparisons with Bayesian and regularized survival models. We have conducted additional experiments comparing TTE-PFN against five alternatives: Bayesian Weibull AFT (BayesWeibullAFT, [1]), empirical-Bayes Weibull AFT (EB-WeibullAFT, [2]), power-prior Weibull AFT (PP-WeibullAFT, [3]), prior-projected Weibull AFT (PriorProj-WeibullAFT, [4]), and cross-validated CoxNet (CoxNet-CV, [5]).
As shown in Rebuttal Table 7 [https://anonymous.4open.science/r/TTEPFN/Table7.png ], TTE-PFN achieves the best Overall average rank (3.10) across 115 benchmark datasets, outperforming PriorProj-WeibullAFT (3.34), EB-WeibullAFT (3.43), PP-WeibullAFT (3.44), CoxNet-CV (3.72), and BayesWeibullAFT (3.94). TTE-PFN also achieves the best average ranks on five of the seven evaluation metrics, including MAE-PO, IBS, Harrell's C-index, Uno's C-index, and Log-Rank. The alternative methods remain competitive on calibration metrics, particularly PP-WeibullAFT on D-Cal and KM-Cal. These results demonstrate that TTE-PFN offers competitive overall predictive performance compared with simpler Bayesian and regularized survival estimators, rather than uniformly outperforming them on every metric.
We further investigate small-sample performance across 55 datasets at context sizes , without recalibration (Rebuttal Table 8 [https://anonymous.4open.science/r/TTEPFN/Table8.png ]). TTE-PFN achieves the best Overall ranks at (2.98), (3.01), and (3.10), providing direct empirical evidence of its competitive advantage in low-data settings. As the context size increases, simpler estimators become more competitive, with PriorProj-WeibullAFT ranking first at (3.20) and CoxNet-CV at (3.18). These findings suggest that the benefits of amortized prior-based prediction are particularly pronounced when labeled data are scarce, while locally fitted methods can become preferable as more observations become available.
We have incorporated these additional comparisons, implementation details, and a discussion of the relative strengths and limitations of prior-based and conventional survival estimators into the final version.
R3 [W3]: We agree that Theorem 1 provides a conditional error decomposition rather than a guarantee that TTE-PFN always outperforms locally fitted estimators. Importantly, the primary goal of our theoretical analysis is to decompose predictive error into amortization, prior coverage, and posterior concentration, thereby providing principled guidance for PFN design. Specifically, oracle distillation targets amortization error, the diverse synthetic prior aims to improve prior coverage, and context-size randomization supports learning across different cohort sizes. We acknowledge that these guarantees depend on posterior concentration and train--test overlap and may become uninformative under severe prior misspecification.
Nevertheless, a practical way to detect potential prior--data conflict is through held-out validation within the labeled context. Specifically, we can split the context into fitting and validation subsets and compare TTE-PFN against a locally fitted estimator such as CoxNet using censoring-aware predictive metrics. Cases where TTE-PFN performs substantially worse may indicate negative transfer and motivate selecting the local estimator instead.
We have clarified the purpose and limitations of our theoretical analysis and discussed this practical diagnostic in the revised manuscript.
R4 [W4]: We have extended the evaluation to all 29 methods under two consistent protocols: without recalibration (Rebuttal Table 1 [https://anonymous.4open.science/r/TTEPFN/Table1.png ]) and with the same context-based recalibration applied to all methods for IBS and KM-Cal (Rebuttal Table 2 [https://anonymous.4open.science/r/TTEPFN/Table2.png ]). The remaining five metrics are evaluated using raw predictions in both protocols, following the original evaluation setting.
Without recalibration, TTE-PFN ranks third overall (9.31), outperforming SurvivalPFN (10.97). With recalibration available to all methods, TTE-PFN achieves the best overall rank (8.42), ahead of CWGB (8.81) and SurvivalPFN (10.78). In particular, TTE-PFN's IBS rank improves from 8.01 to 6.02, while KM-Cal improves from 11.59 to 7.37. These results demonstrate that TTE-PFN remains competitive without recalibration and achieves the best aggregate performance under the matched recalibration protocol.
We have incorporated these additional comparisons and clarified the recalibration protocol in the revised manuscript.
R5 [W5]: (i) Censoring weights. Our evaluation follows the standard SurvivalEVAL implementation, using marginal Kaplan--Meier estimates consistently across all methods. We have clarified the underlying censoring assumptions and explicitly discussed the limitations of marginal censoring weights when censoring depends on covariates in the revised manuscript.
(ii) Log-Rank metric. We include the Log-Rank metric because it was used in SurvivalPFN, our closest baseline, and we follow the same evaluation protocol to ensure direct comparability. We agree that this metric measures cohort-level distributional agreement rather than patient-level discrimination. Importantly, our evaluation covers three complementary dimensions of survival prediction: predictive accuracy, discrimination, and calibration. Patient-level discrimination is evaluated separately using Harrell's and Uno's C-indices. We have clarified this distinction and revised the interpretation of Log-Rank in the manuscript.
R6 [W6]: We agree that random train--test splits primarily assess within-cohort generalization rather than prospective prediction under temporal distribution shifts. However, our primary objective, as formalized in Eq. (1) of the original manuscript, is to estimate the posterior-predictive distribution for new patients given a labeled context from the same underlying DGP. This is also the central setting of existing in-context survival prediction methods, including SurvivalPFN. Accordingly, we follow the widely adopted random-split evaluation protocol to ensure consistent and comparable evaluation across methods.
At the same time, evaluating temporal generalization is nontrivial, as it requires reliable temporal information and careful consideration of changes in baseline hazards, covariate distributions, and covariate--outcome relationships. We have clarified this limitation in the revised manuscript. We believe that extending in-context survival prediction to temporal distribution shifts represents an important and interesting direction for future work.
R7 [W7]: As formalized in Eq. (1) of the original manuscript, TTE-PFN approximates the posterior-predictive distribution , from which predictive survival functions and patient-level predictive intervals can be directly derived. While this distribution integrates over posterior uncertainty in the underlying DGP, it does not provide a posterior distribution over survival functions. One training-free approach to further characterize uncertainty in the estimated survival functions is context bootstrapping, which repeatedly resamples the labeled context and performs inference with the frozen TTE-PFN.
Regarding the suggested evaluation, our existing benchmark already covers challenging settings, with sample sizes ranging from to and censoring proportions from to across 101 real-world cohorts, as detailed in Table 3 of the original manuscript. Furthermore, we have added a synthetic case study in the Appendix (Rebuttal Figure 3 [https://anonymous.4open.science/r/TTEPFN/Fig3.png ]) examining pointwise context-bootstrap uncertainty bands across context sizes and censoring rates of , , , and . The results show that increasing context size generally narrows the uncertainty bands and improves agreement with the true survival function, whereas heavier censoring leads to greater uncertainty and larger prediction errors. Under extreme censoring, the bands may fail to contain the true survival function, highlighting the limitations of context bootstrapping as an approximate uncertainty assessment.
We have incorporated this case study into the revised manuscript and clarified the distinction between posterior-predictive uncertainty and context-bootstrap uncertainty, including the limitations of the latter under heavy censoring.
References
[1] Ibrahim J G, Chen M H, Sinha D. Bayesian survival analysis[M]. New York: Springer, 2001.
[2] MacKay D J C. Bayesian interpolation[J]. Neural computation, 1992, 4(3): 415-447.
[3] Ibrahim J G, Chen M H. Power prior distributions for regression models[J]. Statistical Science, 2000: 46-60.
[4] Schmidli H, Gsteiger S, Roychoudhury S, et al. Robust meta-analytic-predictive priors in clinical trials with historical control information[J]. Biometrics, 2014, 70(4): 1023-1032.
[5] Simon N, Friedman J H, Hastie T, et al. Regularization paths for Cox's proportional hazards model via coordinate descent[J]. Journal of statistical software, 2011, 39: 1-13.
Thank you for your careful review and constructive feedback. We sincerely appreciate your recognition of the extensive numerical evaluation and your thoughtful suggestions regarding the synthetic prior, theoretical guarantees, and evaluation methodology. We apologize for the delayed response, as we conducted extensive additional experiments to thoroughly address your concerns. Your comments have helped us identify several aspects that required further clarification and empirical validation. We will provide point-by-point responses below.
R1 [W1]: (i) Prior design and selection. Our synthetic prior was designed to cover diverse survival DGPs rather than optimize performance for any particular dataset. The five generators provide complementary structures: Tree and DeepMLP capture different nonlinear interactions, \texttt{Narrow} emphasizes strong covariate effects, and Parametric and Bernstein broaden the range of conditional event-time distributions. All generators provide analytically available conditional distributions for oracle distillation. Importantly, we used separate held-out synthetic development tasks for model development and hyperparameter selection (Lines 1339--1342 of the original manuscript). None of the 115 benchmark datasets was used to tune the prior or select the reported model configuration.
(ii) Additional sensitivity analyses. To further assess the impact of prior specification, we have conducted three additional sensitivity analyses varying generator mixture weights, effect strengths, and censoring settings, each evaluated using five independent random seeds. The configurations and results are reported in Rebuttal Tables 5 [https://anonymous.4open.science/r/TTEPFN/Table5.png ] and 6 [https://anonymous.4open.science/r/TTEPFN/Table6.png ], respectively.
For mixture weights, the uniform configuration achieves the best Overall rank (2.70), followed by interaction-light (2.77) and our original configuration (2.99). Notably, the original configuration achieves the best ranks on MAE-PO and both C-indices, indicating trade-offs across predictive metrics. For effect strengths, the original configuration (1.96) performs close to the strong-effect variant (1.93), while the weak-effect variant performs worse (2.12). Similarly, for censoring settings, the original configuration (2.33) performs close to the heavy-censoring variant (2.25), whereas the light-censoring variant performs substantially worse (2.95).
Importantly, these analyses were conducted after fixing the original prior and were not used to reselect the reported configuration. The results confirm that prior specification affects predictive performance and that our original configuration is not universally optimal. Since future datasets are unknown, our objective is to construct a broadly applicable prior rather than select weights optimized for the evaluation benchmark.
(iii) Prior suitability for new datasets. For a new cohort, potential prior--data conflict can be assessed through held-out predictive performance and calibration within the labeled context, including comparisons with locally fitted estimators such as CoxNet. Such diagnostics can help identify settings where the fixed prior may be unsuitable, although they do not provide formal guarantees against negative transfer. We have incorporated the sensitivity analyses and clarified the prior development protocol, its limitations, and opportunities for more adaptive prior selection in the revised manuscript.