acceptodds
Under review as a conference paper at ICLR 2027

Deep Variational Frailty Models for Survival Prediction Under Dependent Censoring

Abstract

Most survival models assume that censoring is uninformative about event time given observed covariates, an assumption that fails when unobserved factors drive both event and censoring times. Such dependence cannot be identified from right-censored data without structural assumptions. We propose the Deep Variational Frailty Model (DVFM), which jointly models event and censoring times through a shared latent frailty and nonlinear conditional decoders rather than a prespecified copula family. DVFM is trained with a -regularized censored-data variational objective and amortized inference. DVFM is neither an assumption-free identification method nor a test for dependent censoring, but a predictive model for settings where shared frailty plausibly explains the dependence. On synthetic and semi-synthetic benchmarks, DVFM matches the strongest dependent-censoring baseline and a Cox-Gamma frailty model on IBS and MAE, and outperforms four frailty-free models that assume independent censoring by 21-35% within a dataset. It also recovers subject-level frailty better than scalar frailty baselines, mainly on censored subjects, whose censoring times other models treat as uninformative. A matched ablation without the latent () shows that the latent drives the gains under dependence in synthetic data, while on semi-synthetic data its benefit is dataset-dependent: it lowers IBS on seven of twelve datasets, by 10-25% on four, and raises it by about 8% on two. On real data, where we predict time to death in ALS patients, the latent improves held-out log-likelihood.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Survival Analysis, Variational Autoencoders, Frailty Models, Dependent Censoring

Reviews

Among:
Shape:
1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_FpZdOpenReview ↗
Rating
4
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper introduces the Deep Variational Frailty Model (DVFM) for survival analysis under dependent censoring. It models event and censoring times through a shared subject-level latent variable, with neural conditional decoders and amortized variational inference. This provides an alternative to explicitly parameterizing their dependence through a copula.

The paper derives a censored-data variational objective, establishes identification of the frailty-effect distribution under a restricted multiplicative model with known hazard indices, and explains why the ELBO cannot distinguish observationally equivalent dependent and independent explanations. Experiments on synthetic data, semi-synthetic benchmarks constructed from 12 source datasets, and real ALS data evaluate prediction, joint-distribution recovery, latent recovery, and dependence calibration. The results show competitive predictive performance and improved latent recovery among censored subjects, while also exposing limitations under independent censoring and in dependence calibration.

Critical strengths
  1. A natural modeling alternative. Modeling event–censoring dependence through a shared unobserved factor is well motivated. Neural conditional decoders and amortized inference provide a coherent implementation of this approach, offering a worthwhile alternative to explicit copula modeling.

  2. Extensive experiments with useful empirical support. The experiments cover synthetic, semi-synthetic, and real data and assess complementary aspects of performance. Improved latent recovery among censored subjects suggests that explicitly modeling the censoring process can provide additional information. This systematic exploration is valuable even without uniform predictive superiority over strong copula-based methods.

  3. Careful treatment of theoretical scope and transparent reporting. The paper clearly explains dependent censoring, distinguishes restricted identification results from guarantees for the full neural implementation, and acknowledges that the variational objective cannot resolve observational equivalence. The authors report degradation under independence, mixed results against HACSurv, imperfect dependence calibration, and a nonsignificant joint-survival ISE difference. They also avoid interpreting improved real-data likelihood as proof of dependent censoring. This transparency increases my confidence in the findings.

  4. An informative analysis of learning under non-identifiability. Section 4 explains when the variational objective can favor a frailty-based explanation: its observed-data likelihood advantage must outweigh its additional variational gap, with regularization also affecting this preference. The authors clearly distinguish this inductive-bias argument from identification guarantees. This broader perspective also helps interpret how copula-based methods such as HACSurv and DCSurvival may learn useful dependence structures under their modeling assumptions, even without unrestricted identification guarantees.

Critical weaknesses
  1. The potential to learn covariate-dependent dependence remains insufficiently validated. The semi-synthetic benchmark keeps dependence strength constant across covariates, and individual posterior recovery using observed follow-up does not establish this capability for new subjects observed only through covariates. The restricted identification theorem does not provide such a guarantee either.

  2. The comparison with HACSurv does not isolate marginal flexibility from dependence modeling. HACSurv uses monotone neural marginal survival functions, whereas DVFM uses conditional Weibull distributions that become mixtures after marginalization. A controlled comparison would clarify which component accounts for the observed performance differences.

Questions for authors
  1. Could you clarify how the copula can vary with x at prediction time under the shared aggregate posterior in Equation (11), and whether this capability has been directly evaluated?

  2. Do you have an ablation that controls for marginal flexibility when comparing DVFM with HACSurv? Such evidence would help separate the contributions of marginal and dependence modeling.

  3. Could you report training and prediction times for DVFM, HACSurv, and Cox-Gamma frailty under comparable hardware conditions?

2 comments

Thank you for identifying the need for prospective dependence experiments, a marginal-flexibility control, and comparable timings. We performed all three analyses.

Weakness 1 and Question 1. Covariate-dependent dependence for a new patient.

A common mixing distribution allows dependence to vary with x because both conditional decoders take x and z jointly. Under the aggregate posterior in Eq. (11), the joint survival is

S(e,c∣x)=∫SE(e∣x,z)SC(c∣x,z)qagg(z) dz.S(e,c\mid x)=\int S_E(e\mid x,z)S_C(c\mid x,z)q_{\rm agg}(z)\,dz.

Interactions between x and z change both heads' responses to the shared frailty. The same mechanism applies under prior prediction, which we will use in the revision. In matched same-checkpoint comparisons, the median oracle IBS difference for aggregate-posterior minus Gaussian-prior prediction was +0.00004.

We tested step and smooth covariate-dependent frailty loadings using ten repeats with 10,000 subjects, ten covariates, and 50% censoring. At each new covariate profile, we estimated Kendall's τ\tau from 2,000 event-censoring pairs generated using fresh prior draws and x alone. The smooth-loading results were

x₁-2-1012
Generating τ, Monte Carlo.00.02.26.46.49
DVFM τ, median.15.18.29.39.42
HACSurv global τ.21.21.21.21.21

Generating values use 200,000 draws. DVFM recovered the increasing pattern in 9/10 repeats, with median correlation 0.93. For the step design, it ranked the higher-dependence stratum correctly in 10/10 repeats, with median estimates 0.21 and 0.41 against true values 0 and 0.50. Absolute dependence calibration remains imperfect, and 3/10 repeats produced negative-dependence solutions with comparable validation objectives. HACSurv used untuned pilot settings and had lower event IBS, 0.1024 versus 0.1140 on the step design and 0.1032 versus 0.1239 on the smooth design. The experiments directly support prospective recovery of dependence heterogeneity.

Weakness 2 and Question 2. Contribution of marginal flexibility and sharing.

We trained shared- and independent-latent variants with two separate decoder trunks, the same total latent budget of two, and matched training settings, splits, and seeds. Both retain Weibull-mixture margins. Shared heads receive both latent coordinates, while independent heads receive one coordinate each. Across four datasets, five scenarios, and ten seeds, this required 400 fits. Joint-survival integrated squared error (ISE) at τ=.50\tau=.50 was

DatasetIndependentSharedHACSurv
GBSG0.01560.01200.0385
METABRIC0.00720.00680.0063
SUPPORT0.01210.01200.0142
SEER liver0.01170.01260.0075

Independent mixture latents improved over the latent-free model on three datasets and tied on SEER liver, supporting the contribution of marginal flexibility. Sharing further improved GBSG joint ISE with a paired interval excluding zero and increased censored-subject frailty rank correlation by 0.09-0.18 on all four datasets. Joint-ISE gains were small on METABRIC and SUPPORT, and independence performed better on SEER liver. Per-margin latent dimensions differ between the two controls, and HACSurv also has a different marginal architecture. These differences limit exact attribution to individual components.

Question 3. Training and prediction costs.

Using four threads, warm-up, and three seeds on AMD EPYC 9655 CPU and NVIDIA L40S GPU hardware, median training seconds were

Training setDVFM CPU / GPUHACSurv CPU / GPUCox-Gamma CPU / GPU
GBSG, 4794.2 / 9.124.2 / 19.30.10 / 0.30
SUPPORT, 6,21051.8 / 108.3150.7 / 112.70.73 / 1.50
SEER liver, 7,00068.5 / 134.2341.3 / 234.70.82 / 1.54

For 1,000 SEER liver predictions, CPU times were 0.057 s for DVFM with cached aggregate posterior, 0.116 s for HACSurv, and 0.0003 s for Cox-Gamma. DVFM and HACSurv GPU times were 0.055 and 0.034 s. Defaults used float32 for DVFM and float64 for the others. Their SEER CPU epoch times were both about 0.34 s, with 200 DVFM epochs versus typically 550-1,000 HACSurv epochs. Cox-Gamma was fastest for CPU training and prediction.

Thank you for the clarification and the additional experiments.

Since the paper offers a natural and well-motivated alternative to copula-based modeling of dependent censoring, I maintain my rating and vote for acceptance.

I hope the final version will include the additional covariate-dependent dependence experiment. It demonstrates a potential advantage over HACSurv, even though the absolute dependence estimates remain imperfect.

Reviewer_LcdtOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes the Deep Variational Frailty Model (DVFM) for survival prediction under dependent censoring. A shared latent variable renders event and censoring times conditionally independent, while neural decoders parameterize their conditional Weibull distributions. An amortized encoder infers a subject-level latent posterior from covariates, observed follow-up time, and event status. Training uses a censored-data variational objective; prediction averages conditional survival curves over the aggregate training posterior.

The theoretical contributions establish identification of the frailty-effect distribution under a restricted multiplicative model with known hazard indices and sufficient covariate variation. They also show that, at β=1\beta=1, the population ELBO ties observationally equivalent dependent and independent candidates when both posteriors are represented exactly. These results explicitly do not establish identification of the unrestricted neural model.

Validation includes synthetic experiments, semi-synthetic experiments using 12 source datasets and four copula families, and a real-data experiment on PRO-ACT. DVFM achieves competitive predictive performance relative to HACSurv and Cox-Gamma frailty, and stronger recovery of the generating latent among censored subjects. On the real PRO-ACT dataset, DVFM achieves a higher estimated held-out observed-data log-likelihood than its no-latent counterpart. As the authors acknowledge, this supports improved modeling of observed follow-up rather than establishing dependent censoring. Since the latent variable also increases the flexibility of the marginal distributions, this comparison does not isolate the contribution of event--censoring dependence modeling.

Critical strengths

A useful joint modeling formulation that incorporates censoring into subject-level latent inference

The paper presents a joint modeling framework for event and censoring times, allowing information from the censoring process to contribute directly to the inference of a shared subject-level latent variable. The formulation is intuitive, and the censored-data likelihood and variational objective are clearly derived, making the proposed approach relatively straightforward to understand and implement.

The experimental results are encouraging, particularly for latent frailty recovery. On semi synthetic (i think) datasets derived from the three SEER cohorts, DVFM achieves Spearman correlations of 0.77--0.83 with the generating latent among censored subjects, compared with 0.58--0.66 for the Cox-Gamma baseline. These results are consistent with the usefulness of incorporating the censoring likelihood into subject-level latent inference.

  • Broad empirical evaluation with appropriate oracle metrics and explicit acknowledgment of limitations.}

The paper provides a comprehensive empirical evaluation, considering multiple metrics beyond concordance, including oracle IBS, MAE, joint-survival error, latent recovery, and dependence calibration. The use of synthetic and semi-synthetic data allows the authors to evaluate predictions against true event times, including for censored subjects, without relying on the independent censoring assumption. The repeated experiments, paired comparisons, and inclusion of a no latent ablation further strengthen the evaluation.

Another positive aspect is that the authors acknowledge the limitations of their results. For example, the improvement over HACSurv in joint-survival error is not statistically significant, and introducing the latent variable can negatively affect prediction on some datasets. The paper also clearly states that its theoretical identification guarantees apply only to a restricted frailty model, rather than the full neural formulation. This balanced discussion makes the findings more credible and informative, even when DVFM does not consistently outperform the baselines.

Critical weaknesses
  • The prediction procedure is not the marginal predictive distribution of the stated generative model, and its justification appears incorrect.

Equation (2) defines a model with the fixed prior p(z)=N(0,I)p(z)=\mathcal{N}(0,I). For fixed fitted parameters, the event-time survival function implied by that model is therefore

Sθ,Emodel(e∣x)=∫Sθ,E(e∣x,z) p(z) dz.S_{\theta,E}^{\mathrm{model}}(e\mid x) = \int S_{\theta,E}(e\mid x,z)\,p(z)\,dz.

However, Equations (11)--(12) replace p(z)p(z) with the aggregate training posterior qagg(z)q_{\mathrm{agg}}(z), and the paper states that prior sampling is valid only when qagg≈pq_{\mathrm{agg}}\approx p.

For the stated model, this reasoning is reversed: integrating against the prior gives its marginal predictive distribution regardless of whether the empirical aggregate approximate posterior matches that prior. Substituting qaggq_{\mathrm{agg}} changes the mixing distribution; it is not simply a Monte Carlo approximation to the same predictive quantity.

Using qaggq_{\mathrm{agg}} may be a useful data-dependent prediction procedure, and its construction from training data is not test-set leakage. Nevertheless, it needs to be justified as a distinct predictor rather than described as the marginal predictive distribution of Equation (2). This matters because the reported DVFM survival predictions use aggregate-posterior sampling, but no paired prior-versus-aggregate-posterior predictive comparison is reported.

Appendix G.5 further describes the PRO-ACT joint log-likelihood evaluation as an importance-weighted bound reducing to Equation (8) at K=1K=1, while the separate margin scores integrate over qaggq_{\mathrm{agg}}. The former appears to target the fixed-prior model, suggesting that the joint score and reported survival curves may evaluate different fitted distributions. The exact importance weights and the mixing distributions used for joint-survival and dependence estimation should therefore be made explicit. A paired prior-versus-aggregate-posterior sensitivity analysis on the same fitted models is needed to assess the practical consequences.

  • The central ablation does not isolate dependence modeling from increased marginal flexibility.

Removing the latent leaves a single conditional Weibull distribution for each margin, whereas including the latent produces mixtures of conditional Weibulls. Thus, the dz=0d_z=0 versus dz=1d_z=1 comparison changes both the capacity to model event--censoring dependence and the expressive power of the individual marginal distributions. Matching the remaining architecture and optimization settings does not eliminate this distributional difference.

The synthetic dependence sweep introduces a related confound: Equation (38) changes the shared loading λ\lambda to vary Kendall's τ\tau, but changing λ\lambda also changes the marginal distributions of event and censoring times. Consequently, the crossover in Figure 3 cannot by itself establish that the gains arise specifically from accounting for dependence rather than from better representing increasingly heterogeneous marginals. The semi-synthetic copula construction provides useful evidence with fixed event margins, but the model-class difference between the two ablations remains.

This distinction is consequential because the incremental benefit of the shared latent is heterogeneous: Table 7 reports a median within-dataset IBS disadvantage of only 1.3% for the no-latent model, although Appendix H.1 documents substantial gains on several datasets and losses on others. A control with comparably flexible but independent latent-variable marginals would more directly establish the value of coupling the two processes. Similarly, the event-only Cox-Gamma comparator does not determine whether a simpler joint shared-frailty model could achieve comparable latent recovery.

Questions for authors
  • Clarification and sensitivity analysis: Which latent mixing distribution defines the evaluated model?

How do you reconcile prediction under qaggq_{\mathrm{agg}} with the fixed-prior generative model in Equation (2)? Appendix G.5 describes the PRO-ACT joint log-likelihood evaluation as an importance-weighted bound reducing to Equation (8) at K=1K=1, while the separate margin scores use qaggq_{\mathrm{agg}}. Please provide the exact importance weights and confirm whether the joint score therefore targets the fixed-prior model. Which mixing distribution is used for the joint-survival and dependence estimates, and how are these evaluations reconciled with aggregate-posterior prediction?

Please also report paired predictive results using the prior and aggregate posterior on the same fitted models. This would clarify whether the choice of mixing distribution materially affects the reported results.

  • Targeted validation: Does sharing the latent help beyond making the marginals more flexible?

How does DVFM compare with an independent-censoring control that gives the event and censoring margins separate, independent latent variables, retaining comparable marginal mixture flexibility?

For the synthetic study, can the benefit also be demonstrated when dependence varies while the marginal laws are held fixed? These comparisons would directly address whether the improvements attributed to the shared pathway come from dependence modeling.

  • Targeted validation: Does the latent-recovery advantage persist against a simpler joint frailty model?

The current Cox-Gamma comparator does not model the censoring process jointly with the event process. Can you compare against a simpler shared Gamma- or lognormal-frailty model in which the same latent affects both hazards, using the same observed data and held-out recovery metrics?

This would help determine whether the recovery advantage requires DVFM's neural formulation or is primarily explained by including the censoring likelihood.

Presentation Issues. The paper is generally clear and easy to follow. However, I find the organization of the experimental evaluation somewhat fragmented. Sections 5, 6, and 7 separately present the synthetic, semi-synthetic, and real-data experiments as three top-level sections. I would recommend consolidating them into a single Experiments section, with dedicated subsections for each experimental setting. This would provide a more coherent presentation of the empirical evaluation and make it easier to understand how the three studies complement one another.

3 comments
AuthorsOpenReview ↗

Wrong review

Dear Reviewer Lcdt,

Your review appears to concern a different submission ("RiCoTA," latent quantization for manifold-valued data) rather than our paper on survival analysis under dependent censoring. We have informed the AC. We would be glad to respond if you are able to provide a review of our submission.

Thank you for the updated review and careful reading. We ran experiments for both of your main questions.

Weakness 1 and Question 1. Prediction rule and mixing distributions.

You are right. Integrating against the prior p(z)=N(0,I)p(z) = \mathcal{N}(0, I) gives the marginal predictive distribution of the model in Eq. (2) by definition; qaggq_{\text{agg}} is a distinct, data-adapted predictor. We will correct the text.

We refit 600 semi-synthetic models and scored each checkpoint under both rules, using identical test subjects and matched Monte Carlo draws. Across 24 dataset-by-dependence comparisons, qaggq_{\text{agg}} minus prior changed oracle IBS by a median of +0.00004 (maximum +0.0011) and joint-survival ISE by a median of +2.1% relative (lower is better for both). The revision uses the prior for prediction.

  • Joint survival and dependence. Both integrate against the prior. For DVFM, the predicted joint surface averages SE(e∣x,z) SC(c∣x,z)S_E(e \mid x, z)\, S_C(c \mid x, z) over 500 draws z∼N(0,I)z \sim \mathcal{N}(0, I), and the encoder is not used. Appendix G.5 wrongly says "posterior samples", a wording error we will fix. Learned Kendall's τ\tau likewise uses prior draws.
  • PRO-ACT joint likelihood. Yes, it targets the fixed-prior model. With zk∼qϕ(z∣t,δ,x)z_k \sim q_\phi(z \mid t, \delta, x) and K=1,000K = 1{,}000, we report log⁡1K∑k=1Kwk\log \frac{1}{K} \sum_{k=1}^{K} w_k with wk=pθ(t,δ∣x,zk) p(zk)/qϕ(zk∣t,δ,x)w_k = p_\theta(t, \delta \mid x, z_k)\, p(z_k) / q_\phi(z_k \mid t, \delta, x), a lower bound on log⁡pθ(t,δ∣x)\log p_\theta(t, \delta \mid x) under p(z)p(z). Margin rows used qaggq_{\text{agg}} (differences from the prior at most 0.0002); the revision uses the prior throughout.

Weakness 2 and Question 2. Does sharing help beyond flexible margins?

Agreed: the dz=0d_z = 0 versus dz=1d_z = 1 comparison changes both dependence and marginal flexibility. We therefore trained shared and independent variants with two separate decoder trunks, the same total two-dimensional latent budget, and matched settings, splits and seeds. Shared heads receive both latent coordinates, while independent heads receive one each, so both keep Weibull-mixture margins. Four datasets, five scenarios and ten seeds gave 400 fits. At τ=0.50\tau = 0.50:

DatasetJoint ISE (shared / independent)Censored-subject Spearman (shared / independent)
GBSG0.0120 / 0.01560.66 / 0.48
METABRIC0.0068 / 0.00720.77 / 0.68
SUPPORT0.0120 / 0.01210.71 / 0.56
SEER liver0.0126 / 0.01170.83 / 0.69

Sharing improved censored-subject recovery on all four datasets, by 0.09 to 0.18. For joint ISE, the paired interval excluded zero on GBSG, differences were small on METABRIC and SUPPORT, and the independent variant did better on SEER liver. Your concern is partly right: independent mixture latents already improved joint ISE over the latent-free model on three datasets and tied on the fourth. Marginal flexibility explains part of the original ablation's gain, and the revision will attribute the gains accordingly.

On fixed marginals: we agree Figure 3 alone cannot separate the two. The semi-synthetic margins are fixed by construction, and both control variants have equally flexible margins, so the remaining difference is whether the latent is shared.

Question 3. A simpler joint shared-frailty model.

We ran it. We extended the Cox-Gamma baseline so that one Gamma frailty multiplies both the event and the censoring hazard, each with its own piecewise-exponential baseline and linear predictor; the subject-level posterior stays in closed form. We used the same 12 semi-synthetic datasets at τ=0.50\tau = 0.50, four copulas, ten seeds and the same splits as Figure 6. Censored-subject Spearman correlation with the generating frailty:

ComparisonMedian difference across 12 datasets [95% bootstrap CI]Datasets where DVFM is better
DVFM − event-only Cox-Gamma+0.19 [+0.13, +0.28]11 of 12
DVFM − joint Cox-Gamma−0.05 [−0.11, −0.02]0 of 12

So the recovery advantage comes from sharing a latent between the event and censoring processes, not from the neural formulation, consistent with the control above. The comparison also suits the joint model, since the semi-synthetic margins are proportional-hazards fits, which it assumes. The two models (DVFM and the joint Gamma model) differ in what they can represent. Conditional on xx, the joint Gamma model implies a Clayton copula with τ=1/(1+2α)\tau = 1/(1 + 2\alpha), the same at every xx, so it cannot capture covariate-varying dependence, which DVFM recovers (see our response to kyMv, Weakness 5). It also assumes proportional hazards for both processes, which DVFM does not.

We will add the joint frailty model to Figure 6 and revise the recovery claim: DVFM improves on event-only frailty baselines, and the gain comes from the shared latent rather than the neural parameterization.

Presentation.

Yes, we will merge Sections 5 to 7 into one Experiments section. Thanks again.

This is useful to see, and i think reassuring, i am happy to increase my score to 3 and think overall this is a good contribution

Reviewer_kyMvOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This work proposes the Deep Variational Frailty Model to address dependent censoring in survival analysis by jointly modeling event and censoring times through a shared latent variable, without prespecifying a copula family. The framework combines nonlinear neural decoders with variational inference and examines identifiability under restricted assumptions. Experiments on synthetic and semi-synthetic datasets demonstrate effective subject-level frailty recovery and competitive predictive performance under dependent censoring. Results on real ALS data further show improved held-out log-likelihood, although the estimated dependence strength remains imperfectly calibrated.

Critical strengths

1 The paper addresses dependent censoring, an important and practically relevant challenge in survival analysis, with clear motivation and problem formulation.

2 The shared latent frailty framework jointly models event and censoring times without prespecifying a copula family, while enabling subject-level latent inference, offering a meaningful methodological contribution.

3 The theoretical analysis is carefully developed, distinguishing identifiability under restricted assumptions from general non-identifiability and clarifying the limitations of the variational objective.

4 The experimental evaluation covers synthetic, semi-synthetic, and real datasets, with matched ablations and subject-level frailty recovery analyses.

Critical weaknesses

1 The generative model assumes a standard Gaussian prior, whereas prediction marginalizes over the aggregated posterior. This introduces a potential inconsistency between the generative formulation and the prediction procedure. The authors should clarify the theoretical justification for this choice and compare the predictive performance of prior sampling and aggregated posterior sampling.

2 The identifiability theorem applies only to a restricted multiplicative frailty model under strong assumptions, including known cumulative hazards. However, the implemented DVFM allows both the shape and scale parameters of the Weibull distributions to depend on the latent variable, which does not necessarily satisfy these assumptions. The authors should clarify how the theoretical results relate to the actual model and what guarantees they provide for DVFM.

3 The paper emphasizes DVFM's ability to recover subject-level latent frailty. However, successful latent recovery on synthetic data does not establish identification of the underlying dependent-censoring mechanism in real data. Given the inherent non-identifiability of latent dependence structures, observationally equivalent models may yield different latent interpretations. The authors should more carefully distinguish latent recovery under a specified data-generating mechanism from identifying informative censoring in practice.

4 The predictive advantages over the strongest baselines remain limited. DVFM ranks second on IBS and MAE in the semi-synthetic experiments, its improvement over HACSurv in joint prediction error is not statistically significant, and its performance is comparable to that of Cox-Gamma. Moreover, introducing the latent variable does not consistently improve prediction across datasets. Given the additional model complexity, stronger evidence is needed to establish the practical advantages of DVFM over existing approaches.

5 The experiments do not sufficiently validate the model's ability to capture complex dependence structures. In particular, the paper highlights DVFM's flexibility in modeling covariate-dependent event–censoring dependence, but the semi-synthetic benchmarks use dependence strengths that remain constant across covariates within each dataset. Experiments with covariate-varying dependence and heterogeneous subject-level dependence structures would more directly support this claimed advantage.

6 The real-data evaluation provides limited evidence for improved survival prediction. On the ALS dataset, the reported gains are primarily based on held-out log-likelihood, with a substantial portion of the improvement arising from the censoring component. Since better observed-data likelihood does not necessarily imply more accurate prediction of the underlying event-time distribution, the current results are insufficient to establish DVFM's predictive advantages under real-world dependent censoring. Additional survival calibration analyses and broader external validation would strengthen the empirical evidence.

Questions for authors

See Weaknesses

3 comments

Thank you for your comments and feedback. Below we have addressed the weaknesses you have brought forward.

Weakness 1. Consistency of prior and aggregate-posterior prediction.

Good observation, and based on our new results, we will use the Gaussian prior for as the main prediction method in the revised paper. In 600 refitted semi-synthetic models, each checkpoint was scored under both rules using identical test subjects and matched Monte Carlo draws. Across 24 dataset-by-dependence comparisons, qaggq_{\rm agg} minus prior changed oracle IBS by a median +0.00004 (maximum +0.0011) and joint ISE by a median +2.1% relative. Lower is better. On PRO-ACT, nine of ten splits had D-calibration p>0.05p>0.05 under either rule, and mean margin log scores differed by at most .0002. Joint observed-data likelihood already integrated against the prior, with the encoder used as an importance-sampling proposal.

Weakness 2. Identification with a shape-varying decoder.

Theorem 1 identifies the population law of two positive multiplicative frailty effects. It assumes known cumulative hazard indices, a common frailty-effect law across x, and an index range containing a nonempty open set. The submitted decoder estimates its hazards and lets frailty change both shape and scale. Applying the theorem requires additional restrictions beyond this architecture. The extension below allows shape-varying mixtures under explicit design assumptions.

Extension and proof.

Fix a clinical stratum ww and let dd be an additional observed covariate. Assume strictly positive event and censoring times. All candidate models use the same known time transformations a(e,w,d)a(e,w,d) and b(c,w,d)b(c,w,d). Each is jointly continuous in time and dd, increases from zero, and maps nonnegative time onto itself. Assume the conditional joint survival can be written as

P(E>e,C>c∣w,d)=Kw(a(e,w,d),b(c,w,d)),P(E>e,C>c\mid w,d)=K_w(a(e,w,d),b(c,w,d)),

where KwK_w is a continuous survival surface common across dd within the stratum. It may change freely with ww. We work on the conditional support of dd in each stratum for which the conditional law is defined. Since follow-up ends at T=min⁡(E,C)T=\min(E,C), the observed survival gives

P(T>t∣w,d)=Kw(a(t,w,d),b(t,w,d)).P(T>t\mid w,d)=K_w(a(t,w,d),b(t,w,d)).

Two models with the same observed law therefore agree at all such transformed pairs and, by continuity, on their closure. Equality almost everywhere in dd extends to its support by the same continuity argument. If the pairs are dense in the positive quadrant, the full joint survival and both margins are identified, with the margins obtained by taking one time down to zero. If all admissible surfaces are real analytic in the positive quadrant, a nonempty open subset of identified points suffices by the identity theorem. In Theorem 1 the surface is the Laplace transform of the frailty-effect law. Uniqueness of that transform gives the additional identification of that law.

A shape-varying example.

Suppose d>0d>0 is a known censoring-clock multiplier. Within ww, a reference pair (E0,C0)(E_0,C_0) has the same distribution across dd, and the actual times are E=E0E=E_0 and C=C0/dC=C_0/d. Then P(T>t∣w,d)=Kw(t,dt)P(T>t\mid w,d)=K_w(t,dt). If the support of dd covers all positive values, setting t=et=e and d=c/ed=c/e recovers Kw(e,c)K_w(e,c) for every positive pair. The reference Weibull shapes and scales may both depend on frailty. The observable multiplier and its exclusion from the reference law are extra design assumptions. Application to PRO-ACT would require establishing such a multiplier. The result identifies a population survival surface under the stated design.

We also tested the original multiplicative restriction with a global shape per margin and log-scale f(x)+gzf(x)+gz, while still learning the hazards. At true τ\tau = 0.75 the mean estimates were 0.52 for DVFM, 0.19 with the restricted decoder and penalty 0.1, and 0.26 with the penalty removed. At τ\tau = 0.50 they were 0.46, 0.43 and 0.50. At generating τ\tau = 0.50, the restricted variants had higher joint ISE than DVFM on all four semi-synthetic control datasets.

Weakness 3. Interpretation of latent recovery.

We agree. Synthetic recovery shows that inference recovers the latent when data follow our model; it does not show that the latent inferred on PRO-ACT reflects a real informative-censoring mechanism. As Section 7 states, the PRO-ACT gain shows a better fit to observed follow-up, not that censoring is dependent. On real data, the latent is a model-based summary, not a measured frailty.

This holds even within our model class, an instance of Tsiatis (1975). Fix xx, let Z∼N(0,1)Z \sim N(0,1) and R=1/2+tanh⁡(Z)/4R = 1/2 + \tanh(Z)/4.

  • Model A: given ZZ, E∼Exp(R)E \sim \mathrm{Exp}(R) and C∼Exp(1−R)C \sim \mathrm{Exp}(1-R), conditionally independent.
  • Model B: E,C∼Exp(1/2)E, C \sim \mathrm{Exp}(1/2), independent.

In both, T=min⁡(E,C)∼Exp(1)T = \min(E,C) \sim \mathrm{Exp}(1) and observed events and censorings each have density e−t/2e^{-t}/2 (in A since E[R]=1/2\mathbb{E}[R]=1/2), so the observed data are identical. Yet in A, SE(t)=E[e−tR]>e−t/2S_E(t) = \mathbb{E}[e^{-tR}] > e^{-t/2} by Jensen. By symmetry SC=SES_C = S_E, so SE(t)SC(t)>e−t=S(t,t)S_E(t)S_C(t) > e^{-t} = S(t,t): EE and CC are dependent in A but independent in B.

This does not contradict Theorem 1. Model A satisfies Assumption 1 with η(Z)=R\eta(Z)=R, ζ(Z)=1−R\zeta(Z)=1-R, but at fixed xx both indices equal tt, so their image is the ray a=ba=b rather than an open set (Assumption 3 fails). As in Remark 1, the data then identify only the law of U+VU+V, which equals 1 in both models.

In the revision, we will restate the claim that the model "reports who it infers to have been informatively censored" as conditional on the shared-frailty assumption, and add this example to Section 4.

Weakness 4. Predictive gains and additional complexity.

The paired joint-ISE ratio versus HACSurv was 0.91 (95% CI 0.82–1.02, p = 0.12). With prior prediction, frailty improved IBS on seven of twelve semi-synthetic datasets, including four gains of about 10–25%, but worsened it by 7–8% on SEER brain and liver. DVFM and Cox-Gamma differed by under 1.5% in paired IBS and MAE at τ=0.50\tau=0.50. The added evidence concerns censored-subject inference. Across 12 datasets, frailty rank correlation exceeded Cox-Gamma on 11, with one tie and median gain 0.19 (95% bootstrap interval 0.13-0.28). A 400-fit control retained mixture margins and matched latent and network budgets. Sharing increased censored-subject rank correlation by 0.09-0.18 on all four datasets. Joint-ISE gains were clearest on GBSG, small on METABRIC and SUPPORT, and reversed on SEER liver. These results identify sharing's contribution beyond flexible margins and its limited predictive benefit.

Weakness 5. Direct validation of covariate-dependent dependence.

We added two synthetic designs in which the frailty loading depends on a covariate: a step at x1=0x_1 = 0 (true τ\tau from 0 to 0.50) and a smooth loading l(x)=1.3586 logistic(2x1)l(x) = 1.3586\,\mathrm{logistic}(2x_1), calibrated so the full loading gives τ=0.50\tau = 0.50. Each design uses ten independently generated cohorts of 10,000 subjects, ten covariates and 50% censoring. For a new patient, DVFM's τ^(x)\hat\tau(x) uses covariates alone: we draw 2,000 event–censoring pairs from the fitted decoder at xx with z∼N(0,1)z \sim \mathcal{N}(0, 1), the prior-based prediction rule we adopt in the revision (see Weakness 1).

Smooth design, x1x_1−2−1012
True τ(x)\tau(x)0.000.020.260.450.49
DVFM τ^(x)\hat\tau(x), median over 10 repeats0.150.180.290.390.42
HACSurv τ^\hat\tau (one global value)0.210.210.210.210.21

DVFM's τ^(x)\hat\tau(x) rises with x1x_1 in 9 of 10 repeats (median correlation with the true curve across the five profiles: 0.93). In the step design, it assigns higher dependence to the correct stratum in 10 of 10 repeats (medians 0.21 and 0.41, against true values 0 and 0.50); HACSurv returns 0.18. True values are computed by numerical integration.

This variation is possible even though the mixing law of ZZ does not depend on xx (Reviewer FpZd, Q1). For two independent subjects at the same xx, Kendall's τ\tau is E[sign(E1−E2) sign(C1−C2)]E[\mathrm{sign}(E_1 - E_2)\,\mathrm{sign}(C_1 - C_2)]. Given both frailties, the two signs are independent, so τ(x)=EZ1,Z2[mE(x;Z1,Z2) mC(x;Z1,Z2)]\tau(x) = E_{Z_1, Z_2}[m_E(x; Z_1, Z_2)\, m_C(x; Z_1, Z_2)], where mjm_j is the conditional mean sign. The law of ZZ is fixed, but mEm_E and mCm_C vary with xx through the decoder. This holds for any continuous decoder, including one in which zz changes both Weibull shape and scale.

Absolute levels remain imperfect. The fitted curve is compressed (0.15 to 0.42 against 0.00 to 0.49), overestimating weak and underestimating strong dependence, consistent with Figure 3(d). We will state the claim accordingly: DVFM recovers the direction and ordering of covariate-varying dependence, not its magnitude. We will include the results in the revised version.

Weakness 6. Real-data calibration and external validation.

We compared both models on the same ten splits, using prior prediction for the latent model.

Held-out PRO-ACT resultNo latentShared latent
D-calibration statistic, mean (SD)14.9 (5.5)8.0 (4.1)
Splits with D-calibration p > 0.056/109/10
Error against Kaplan-Meier curve0.00050.0059
Event-margin log score-4.268-4.208
Censoring-margin log score-2.758-2.558
Joint observed-data log score-7.026-6.732

The latent model had a lower D-calibration statistic on nine splits and higher event, censoring and joint log scores on all ten. The joint score uses an importance-weighted lower bound for the latent model. The larger margin-score gain was on censoring. The latent-free model's average survival curve was closer to Kaplan-Meier on every split. Both calibration diagnostics rely on censoring assumptions, and the separate margin scores treat censoring as independent. The evidence supports improved fit to observed follow-up on PRO-ACT. Validation in an independent clinical cohort and accuracy for unobserved event times remain open.

Reviewer_SGkbOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes the Deep Variational Frailty Model (DVFM), which jointly models event and censoring times through a shared subject-level latent variable. It uses neural networks to parameterize conditional Weibull distributions and variational inference to estimate latent posteriors. The authors discuss identifiability under a restricted model and evaluate DVFM on synthetic data, semi-synthetic benchmarks constructed from 12 source datasets, and real PRO-ACT data. The results show competitive predictive performance, although the benefits of the latent variable vary substantially across datasets.

Critical strengths
  1. It is natural way of using a shared latent frailty to model dependent censoring, rather than forcing a predefined copula family. it is clear and well-motivated. It’s straighforward to handle the classic non-identifiability problem in survival analysis, and framing it as a deep variational model with amortized inference is a solid technical contribution. 2.The experimental evaluation is thorough and clear. The authors go out of their way to prove their points: fully synthetic data with known ground truth, semi-synthetic data with real covariates but simulated outcomes (allowing for oracle metrics), and a matched dz=0 ablation. They also explicitly admit where the model fails (e.g., dependence calibration is uncalibrated, and gains are dataset-dependent), which is refreshing.
Critical weaknesses
  1. The predictive gains over the strongest baseline (Cox-Gamma frailty) are basically negligible. Table 7 shows DVFM and CG Frailty are within 1-2% of each other on IBS and MAE. While DVFM beats the independence-assuming models by 20-30%, those are somewhat strawman baselines in a paper specifically about dependent censoring. If the complex deep generative model doesn't clearly beat a classical empirical-Bayes frailty model, the practical value is limited.
  2. The prediction mechanism feels a bit clunky. Using the "aggregate posterior" from the training set to predict for a new patient (Equation 11/12) means you have to encode the entire training split every time you want to make a prediction. For large datasets (like SEER with 80k+ patients), this seems computationally prohibitive for real-time clinical deployment, and it's unclear why a simple prior or a learned population-level distribution wouldn't work just as well.
Questions for authors

1.Predictive distribution and evaluation targets. Should the aggregate-posterior prediction in Eqs. (11)–(12) be interpreted as a post-training empirical adaptation of the prior? With identical fitted parameters, how do prior and aggregate-posterior integration compare on oracle IBS and joint-survival ISE in representative settings? Please also clarify which mixing distribution is used in the real-data joint-likelihood evaluation and how it relates to the aggregate-posterior predictor. 2.The specific contribution of the shared latent variable. On representative datasets, could you add a control using separate, independent latent variables for event and censoring times, retaining comparable mixture flexibility in both margins?

1 comment

Thank you for your comments and feedback. Below we have addressed the weaknesses and your two questions.

Weakness 1. Practical value beyond Cox-Gamma.

The paired IBS and MAE differences from Cox-Gamma in Table 7 are within 1.5% at τ\tau = 0.50. DVFM's additional contribution is inference about censored patients and a joint dependence model that can vary with covariates. Extending Figure 6 to all 12 semi-synthetic datasets, DVFM improved censored-subject frailty rank correlation over the Cox-Gamma posterior on 11/12, with one tie and a median gain of 0.19 (95% bootstrap interval 0.13 to 0.28). Among censored subjects placed in DVFM's top frailty quarter, a median 67% belonged to the generating top quarter, versus 25% by chance. Against CoxPH residuals, the outcomes were four wins, four ties and four losses. These findings support recovery of a known simulated latent, with the strongest comparison against Cox-Gamma.

Weakness 2 and Question 1. Prediction rule, evaluation targets and deployment cost.

Yes, qaggq_{\rm agg} can be interpreted as a post-training empirical adaptation of the mixing distribution. It averages the training patients' variational posteriors. Averaging exact posteriors over model-generated follow-up recovers the prior, while finite-data variational estimation introduces approximation error. We refit 600 semi-synthetic models and scored each checkpoint using the same test subjects and matched Monte Carlo draws under both mixing rules. Across 24 dataset-by-dependence comparisons, the median oracle IBS change for qaggq_{\rm agg} minus prior was +0.00004 (maximum +0.0011). The median relative joint-survival ISE change was +2.1%. Lower is better for both. We will use the Gaussian prior for as the main prediction method in the revised paper.

The submitted survival curves, event-time inference and separate margin scores used $q_{\rm agg}$. Joint ISE, learned τ\tau and the real-data joint observed-follow-up likelihood integrated against the prior. The encoder supplied the importance-sampling proposal for the IWAE likelihood estimate. Prior-based prediction aligns these quantities with the same generative mixing law.

At 10,000 training records, building qaggq_{\rm agg} once took 0.05 s on CPU and 0.11 s on GPU (L40S). Single-patient latency was 12 ms with caching versus 49 ms with rebuilding on CPU, and 52 versus 129 ms on GPU. Prior prediction requires only the new covariates and a fixed number of latent draws, making its cost independent of the training cohort size.

Question 2. Independent-latent control with mixture margins.

We trained shared and independent variants with two separate decoder trunks, the same total two-dimensional latent budget, and matched settings, splits and seeds. Shared heads receive both coordinates, while independent heads receive one coordinate each. Both retain Weibull-mixture margins. Four datasets, five scenarios and ten seeds gave 400 fits. At generating τ\tau = 0.50, the results were

DatasetJoint ISE (shared / independent)Censored Spearman (shared / independent)
GBSG0.0120 / 0.01560.66 / 0.48
METABRIC0.0068 / 0.00720.77 / 0.68
SUPPORT0.0120 / 0.01210.71 / 0.56
SEER liver0.0126 / 0.01170.83 / 0.69

Sharing improved censored-subject recovery on all four datasets by 0.09-0.18. Both models use survival up to censoring. Sharing additionally lets the density of censoring at that time update the event-related frailty. For joint ISE, the paired interval excluded zero on GBSG, differences were small on METABRIC and SUPPORT, and independence did better on SEER liver. Independent mixture latents already improved joint ISE over the latent-free model on three datasets and tied on the fourth, demonstrating the contribution of marginal flexibility.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.