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Under review as a conference paper at ICLR 2027

Testing Dependent Censoring via Mutual-Information Uncertainty and Deep Latent Imputation

Abstract

Learning a survival prediction model can be viewed as regression with the added complication of censoring. Each subject has a true event time and a censoring time , yet we only observe and . Many standard methods assume conditional independence , which may not hold in practice. Assessing this dependence is challenging, as for each subject we observe either or , but never both. To address this, for each we define indicator variables and , taking values in , where "?" denotes censoring-induced missingness. Using across multiple time points, we develop a model-assisted diagnostic for testing . Our statistic is the Conditional Mutual Information (CMI) uncertainty range, ΔIₜ = Iᵗₘₐₓ − Iᵗₘᵢₙ, defined as the width of the CMI values attainable over all feasible completions of the missing "?" entries. Here, Iᵗₘₐₓ and Iᵗₘᵢₙ are the corresponding maximum and minimum feasible CMI values. Under independence, ΔIₜ follows a characteristic null distribution, whereas dependent censoring induces structured deviations. To compute these bounds efficiently, we formulate the problem as a decomposable integer program and solve it exactly via a polynomial-time algorithm. To calibrate the statistic, we combine this uncertainty measure with a deep variational frailty model that imputes latent event and censoring marginals, followed by stratified permutation to generate a model-assisted null distribution under conditional independence. Synthetic experiments show calibrated behavior under independent censoring and increasing power for several dependent-censoring mechanisms, while real-data experiments reveal heterogeneous evidence of possible dependent censoring.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Dependent Censoring, Survival Analysis, Statistical Testing

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

The paper proposes a model-assisted diagnostic for conditional dependence between latent event and censoring times. It measures the range of mutual information over censoring-compatible binary completions at landmark times. A deep variational frailty model supplies one completed dataset for within-stratum permutations and a symmetric rank test. The paper establishes exact stratum-wise computation, oracle validity, and calibration-error bounds, and evaluates the method on synthetic and real survival data.

Critical strengths

S1. The statistic has a clear interpretation. It measures how much mutual information remains undetermined by the observations.

S2. The oracle calibration argument is sound under its assumptions. Reusing one compatible completion gives an error bound without a factor proportional to the number of permutations. Algorithm 2 correctly calibrates its Fisher score through symmetric ranks.

S3. The appendices discuss nonidentifiability, model-dependent calibration, and median saturation.

Critical weaknesses

W1. The real-data protocol does not establish practical reliability. Table 6 in the Appendix reports rejection summaries without baseline comparisons or model and stratification sensitivity analyses. Covariate and stratum counts vary across runs without a clear selection rule, so runs may test different conditional-independence hypotheses. Continuous covariates can also yield singleton exact-profile strata with no nontrivial permutations; if all strata are singletons, Algorithm 2 returns pglobal=1p_{\mathrm{global}}=1. Coarsening instead requires justified within-stratum invariance. These summaries describe behavior across runs, not detection accuracy or power. A clear conditioning target, stratification rule, and sensitivity analysis are needed to interpret the real-data rejections.

W2. The interpretation of rejection remains unresolved. The paper acknowledges observational equivalence but leaves the restricted model class behind "identifiable departures" unspecified. Theorem 3 bounds calibration error using error in the joint conditional completion law for the whole dataset; it does not show that DVFM fitting makes this error small. Under correct marginal specification, Proposition 3 establishes a correct null-compatible optimum, while allowing other completion laws to tie in observed likelihood. The paper needs to explain which assumptions let a rejection distinguish dependent censoring from imputation-model misspecification.

W3. The source of power needs clarification. Proposition 5 gives a population width of log⁡2\log 2 when the at-risk probability is 1/21/2. In a single stratum, selecting an observed-time median landmark separately for each dataset saturates the population raw maximum for both original and reconstructed distributions, removing the positive gap required by Theorem 2. Appendix H's grids for K=3,5,7K=3,5,7 include the median. Global landmarks need not be medians within every stratum, so power could arise from separation across strata or finer-scale behavior outside Theorem 2. The paper should clarify which mechanism drives its results.

W4. The experiments do not isolate the statistic's benefit or adequately characterize its scope. Synthetic evaluation fixes n=1000n=1000 and four covariates, leaving behavior across sample sizes, dimensions, and sparse strata unexplored. The copula baselines report single-seed p-values rather than rejection rates under a common replication protocol. Different generation conventions in Appendices C and C.1 also leave comparability unclear. A comparison that changes only the statistic, retaining the same DVFM fits and shared completions, would isolate the value of MI uncertainty. Appendix H provides a useful preliminary null check, but ten independent datasets per setting yield intervals too wide to confirm precise 5% error control.

W5 (minor). The landmark illustration has incorrect labels. Figure 1's post-event EtE_t and post-censoring CtC_t should be zero, as its caption correctly states. Table 5 also marks the counterpart indicator as unknown at T=tT=t, contrary to Appendix H.2's no-ties boundary convention.

Questions for authors

Q1. How are covariates and strata selected, and do all runs test the same hypothesis? What calibrates the repeated-run Fisher combination, and how sensitive are real-data rejections to the completion model and stratification?

Q2. Which model restrictions make the null and alternatives distinguishable, and what supports accurate conditional completion by the fitted DVFM?

Q3. Does power reflect population separation across strata or finer-scale behavior? Results by landmark grid and the maximizing landmarks would help resolve this.

Q4. Could you provide a matched comparison of statistics and baselines, and characterize calibration across sample sizes and stratum sparsity?

7 comments

Thank you for the detailed comments. In the additional analyses below, we fix the DVFM latent dimension at eight and retain our implemented MI-width statistic, single completion, and p-value calculation. We make the conditioning target explicit, provide a concrete identifiable class, and add matched comparisons and independent-cohort calibration experiments.

Q1 and W1 Conditioning target and real data

Our target is E⊥C∣SE\perp C\mid S, where SS is a stated covariate profile. For NWTCO, the primary target uses study, stage, and central histology in their original categories. There are 4,028 patients and 16 exact strata, with 32--757 patients per stratum. We fix this target, the ten landmark quantiles from 0.15 to 0.85, minimum stratum size 20, and 200 permutations across all three prespecified fit/completion seeds. We also examine two explicitly different conditioning targets, using the same settings and eight latent variables throughout.

Conditioning targetStrataCoverageThree p-values
Study, stage, histology16100%1/201, 1/201, 1/201
Stage, histology8100%1/201, 1/201, 1/201
Primary plus age >37 months2998.83%1/201, 1/201, 1/201

Thus NWTCO remains flagged in every run without combining repeated-run p-values. The age cutoff is the covariate median; three profiles containing 47 patients are below the minimum size. Different targets test different conditional hypotheses and will be labeled separately. These results establish seed and target stability for the examined DVFM configuration, rather than real-data detection accuracy or robustness to all completion-model families. On the same primary cohort and target, Gaussian and Clayton bootstrap LRTs also give p=1/201p=1/201, while Gumbel gives p=180/201p=180/201; the bootstrap-calibrated maximum across the three gives p=1/201p=1/201.

We will remove the Fisher chi-square pooling across runs in Table 6. Seeds on the same patients do not create independent datasets. The Fisher score within an individual test is compared with generated reference scores, not a chi-square distribution. We will also distinguish the fixed-target analysis from the earlier exploratory feature settings.

For continuous covariates, grouping must be stated in advance. Constancy of the conditional event and censoring distributions within each group is a sufficient condition for preserving the original conditional null; otherwise the grouped analysis has its own target. Singleton or undersized profiles cannot provide usable permutation evidence. We report their exclusion and subject coverage, and report no result if no eligible stable stratum remains.

Q2 and W2 Model restrictions and completion accuracy

We replace the phrase ``identifiable departures'' with an explicit example. Within each fixed stratum, suppose EE and CC are conditionally independent exponentials with rates rMrM and (1−r)M(1-r)M, where M>0M>0 is shared frailty and 0<r<10<r<1. Write T=min⁡(E,C)T=\min(E,C) and δ=1{E<C}\delta=1\{E<C\}. The observed law identifies r=P(δ=1)r=P(\delta=1) and STS_T, and therefore identifies

P(E>e,C>c)=ST(re+(1−r)c).P(E>e,C>c)=S_T(re+(1-r)c).

Nonconstant shared frailty has no observationally equivalent independent member of this restricted class. The missing-time law is identified as well: for c≥t>0c\geq t>0,

P(C>c∣T=t,δ=1)=fT(rt+(1−r)c)fT(t).P(C>c\mid T=t,\delta=1) =\frac{f_T(rt+(1-r)c)}{f_T(t)}.

The derivation and extension to fixed, known Weibull shapes appear below. These structural restrictions explain when observed-law estimation can determine latent completion. They are not imposed merely by choosing eight latent variables, and independent proxies outside the class are not ruled out.

To assess the fitted DVFM directly, we evaluated its conditional missing-time CDF against known conditional quantiles in 20 independent synthetic null cohorts of 2,000 subjects. We used 64 subjects per missing-time type per cohort, quantiles 0.1, 0.5 and 0.9, and 256 posterior draws. Mean absolute CDF error was 0.0313; the six type-by-quantile errors ranged from 0.0098 to 0.0498. Coverage of true central 90% conditional intervals averaged 88.3% for missing event times and 86.8% for missing censoring times. This directly examines latent completion rather than relying on observed likelihood alone. It is a diagnostic of accuracy, not an estimate of whole-cohort total variation.

The theoretical validity claim requires calibrated joint completion and exchangeable scoring. Our reference-only normalization and ranking are evaluated separately by the calibration experiments below; we do not claim that reducing latent dimension makes them inherit the exact symmetric-rank guarantee. This distinction keeps the theoretical assumptions and the evidence for the fitted procedure explicit.

Q3 and W3 Median saturation and the source of power

We agree that choosing each dataset's own median saturates the raw population maximum. The implemented statistic instead fixes the observed cohort's landmarks for all reference datasets and uses the largest absolute standardized width deviation within each stratum:

As=max⁡k∣Wsk−μsk∣σsk+ε,A_s=\max_k\frac{|W_{sk}-\mu_{sk}|}{\sigma_{sk}+\varepsilon},

where μsk\mu_{sk} and σsk\sigma_{sk} are reference means and standard deviations. An observed-data median need not be a reference median, and maximizing this standardized deviation is different from maximizing raw width.

The eight-variable analysis holds each fitted model, completion, and permutation stream fixed while varying only the landmark grid. The original ten-landmark grid remains primary; no grid was selected using these results. Entries are detections over 20 independent development cohorts.

DesignK=3K=5K=7K=1010 plus median
Shared frailty (3,3)20/2020/2020/2020/2020/20
Supplied Frank, θ=2020/2020/2020/2020/2020/20

For shared frailty, 272/320 standardized stratum maxima occur at quantiles at least 0.6, and 317/320 have negative deviations. Only 4/320 also maximize raw width. Adding the median selects it in only 16/320 strata and leaves the detection count unchanged. An early-only grid gives 1/20 detections and the median alone gives 19/20, identifying the importance of later landmarks in this fitted experiment. Frank gives 20/20 under both additional grids.

A population contrast can nevertheless exist within one stratum. In the shared-frailty class above, let L(u)=E[exp⁡(−uM)]L(u)=E[\exp(-uM)]. At a landmark tt, the original and independently permuted completed distributions have at-risk probabilities q1=L(t)>q0=L(rt)L((1−r)t)q_1=L(t)>q_0=L(rt)L((1-r)t) for nonconstant MM. At the population 0.15 quantile, q1=0.85q_1=0.85 and q0≥0.852>1/2q_0\geq0.85^2>1/2. The widths then satisfy W1=h(q1)<h(q0)=W0W_1=h(q_1)<h(q_0)=W_0, where hh is binary entropy. Thus a nonmedian downward contrast can supply population separation. This establishes a possible mechanism; it does not show that every fitted-model detection is explained by population separation. Completion-reference and finite-stratum effects also contribute, so we will restrict the corresponding power claim.

Q4 and W4. Matched comparisons and calibration

We isolate the statistic by replacing MI width with at-risk entropy, retaining the same eight-variable DVFM fit, completion, landmarks, permutations, normalization, and p-value calculation. LRTs use identical cohorts, Weibull margins, 200 bootstrap samples, and multistart fitting for observed and bootstrap data. Frank is excluded from fitted copula families. The maximum across Gaussian, Clayton, and Gumbel is bootstrap calibrated.

DesignMI widthEntropyGaussianClaytonGumbelMaximum
Independent null0/200/200/201/201/200/20
Shared frailty (3,3)20/2020/2015/2020/204/2020/20
Supplied Frank, θ=2020/2020/2020/2020/200/2020/20

Each row uses the same 20 development cohorts (2,000 subjects, four binary covariates); the null row is the prespecified first 20 cohorts, not the full calibration study. Width matches the strongest baseline rejection counts on both alternatives. Width and entropy make identical decisions here, so we claim no power advantage. MI width instead gives an exact uncertainty interval and minimax interpretation. At 5% at risk, event/censoring fractions (0.475,0.475) and (0.90,0.05) yield widths 0.5268 and 0.1985 nats, while at-risk entropy is 0.1985 for both. This illustrates the measured quantity, not additional power. After fixing the eight-variable configuration, we validated on fresh independent cohorts. Independent-Weibull null results were:

SubjectsCovariatesFalse rejections95% intervalMean coverage
200047/1003.4–13.7%100%
400042/202.8–30.1%100%
200060/200–16.1%99.42%

All binary covariates form exact profiles. Six-covariate coverage ranges from 97.25% to 100%; all cohorts yield finite results. Wilson intervals reflect cohort uncertainty. The earlier development result was 12/100 null rejections, distinct from fresh 7/100; we do not claim exact or uniform 5% calibration. Separate independent-frailty stress nulls yielded 18/20 and 14/20 false rejections at scales 3 and 1, showing dependence on completion and reference assumptions.

Fresh detection counts were 20/20 for shared frailty (3,3), 7/20 for (1,3), 20/20 for supplied Frank, 18/20 for standard Frank (θ=20), and 17/20 for standard Gumbel (θ=6). Standard generators use uniform copula margins and Weibull times; supplied Frank has different margins and is reported separately. These cohorts are disjoint from matched baseline cohorts. All counts use p < 0.05 and are not power comparisons at matched true error rates.

Short derivation of the identifiable class

Within one stratum, ST(t)=E[exp⁡(−Mt)]S_T(t)=E[\exp(-Mt)] and P(δ=1∣M)=rP(\delta=1\mid M)=r. Conditional independence given MM gives P(E>e,C>c)=E[exp⁡{−M(re+(1−r)c)}]=ST(re+(1−r)c).P(E>e,C>c)=E[\exp\{-M(re+(1-r)c)\}]=S_T(re+(1-r)c). If MM is nonconstant, the two conditional survival functions are strictly positively correlated for positive e,ce,c, so EE and CC are dependent. Since the observed law already determines the joint law within the class, an independent member cannot reproduce it. Also,

P(C>c\mid T=t,\delta=1) =\frac{E[M\exp\{-M(rt+(1-r)c)\}]}{E[M\exp(-Mt)]},$$ which proves the completion formula. For fixed known Weibull shapes $k_E,k_C>0$, suppose the conditional survivals are $\exp(-rM u^{k_E})$ and $\exp(-(1-r)M v^{k_C})$. The observed event and censoring subdensities satisfy \$ \frac{f_1(t)}{f_0(t)}=\frac{r k_E}{(1-r)k_C}t^{k_E-k_C}, \$ identifying $r$. With $H(t)=rt^{k_E}+(1-r)t^{k_C}$, \$ P(E>u,C>v) =S_T\!\left(H^{-1}(ru^{k_E}+(1-r)v^{k_C})\right). \$ For $c\geq t$, let $z=H^{-1}(rt^{k_E}+(1-r)c^{k_C})$. The completion law is \$ P(C>c\mid T=t,\delta=1) =\frac{f_T(z)/H'(z)}{f_T(t)/H'(t)}. \$ The missing-event expression follows by symmetry. The restrictions must hold for the true and fitted distributions; this result does not assert that unrestricted DVFM training enforces them.
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Paper summary

This paper proposes an information-theoretic approach to verify the dependent censoring assumption in survival analysis. Most algorithms rely on the assumption that the event and censoring time are conditionally independent given the data, which may not true in practice, which can lead to biased estimation and incorrect analysis. To achieve that, the authors model the event and censoring time as ordered, discrete temporal landmark, and based on conditional mutual information to establish an estimator. From every possible completion of censored data, the maximum and minimum mutual information is recorded to form mutual information uncertainty range, which is claimed to follow characteristic null distribution if the discrete version of the data is independent, and exhibit structured deviation otherwise. To compute those minima and maxima, the authors used independent two-variable integer program in polynomial time for each stratum. To calibrate, the authors fit a deep variational frailty model to reconstruct latent event and censoring time on a conditionally-independent dataset generated by stratified permutation. They perform an empirical study on both synthetic datasets created from copula-based and frailty-based mechanism to conclude that the statistics can distinguish between conditionally dependent and independent censoring. Lastly, there are empirical experiments done on 7 real-world datasets which reveal various evidence of possible dependent censoring. Overall, this paper could be a significant contribution toward data and statistic-driven survival analysis.

Critical strengths

This work challenges the common assumption underlying many standard methods that the true event time and censoring time are conditionally independent given the observed data. It proposes a potential approach to testing this assumption. The proposed verification procedure is well-defined and supported by rigorous mathematical reasoning, which is presented in detail in the appendices.

Critical weaknesses

(1) Despite the rigorous mathematical reasoning, the positioning of this work within the existing literature is insufficiently developed. Although several methods for testing independent censoring are discussed, their limitations and assumptions are not clearly presented to highlight the improvements offered by the authors’ method. The proposed method appears to rely on fewer assumptions than previous approaches. Moreover, the role and novelty of one component, namely the Deep Variational Frailty Model, remain unclear in the current setting. The authors do not adequately establish the novelty of this component or provide appropriate references to support it.

(2) The work is based on a "necessary condition," which states that dependent censoring exists in continuous-time data if the discretized version defined in the paper exhibits dependent censoring. However, independent censoring in discrete-time data does not necessarily guarantee independent censoring in continuous-time data. This distinction should be explicitly acknowledged as a limitation of the proposed method.

Questions for authors

(beside those in Critical Weakness) (1) It would be helpful to clarify the motivation and reasoning behind the use of the Deep Variational Frailty Model in Section 5.1, as well as whether this method is novel or has been introduced in previous studies. In comparison, the motivations and rationale in Sections 3, 4, and 6 are more clearly explained. (2) The assumptions and propositions presented in Section 5.2 require substantially more effort to understand compared to those in other sections. It would be helpful to improve the presentation by providing a more step-by-step explanation of how the assumptions, propositions, and theorems are connected, making it easier for readers to follow the reasoning.

2 comments

We thank the reviewer for the constructive comments. We will clarify the contribution of DVFM, strengthen the comparison with related work, and explain the scope and assumptions of our diagnostic more directly.

W1 and Q1. DVFM contribution, motivation, and related work.

DVFM is our proposed joint model for event and censoring times. It combines a shared latent frailty, two nonlinear conditional Weibull decoders, and an encoder using the observed covariates, time, and event indicator. The model assumes

E⊥C∣(X,Z),E \perp C \mid (X,Z),

which permits dependence between event time EE and censoring time CC given XX after the shared latent variable ZZ is integrated out.

DVFM supplies the missing times needed to construct the permutation reference. We retain each observed time and sample its missing counterpart above that time. One compatible completed cohort is then reused across within-stratum permutations. The MI bounds themselves are computed over all feasible binary completions and do not depend on DVFM.

We will make this contribution explicit in Section 5.1 while crediting the established frailty and variational-inference ideas on which it builds. In particular, Liu and Wang [1] study censor-dependent variational inference for survival models.

We will also clarify the assumptions of earlier approaches. Lee and Wolfe [2] use proportional hazards and additional follow-up of a subset of censored subjects. Czado and Van Keilegom [3] obtain identification under restrictions on parametric copulas and margins. Our diagnostic uses ordinary right-censored observations without additional follow-up or selection of a named copula family, but requires an appropriate completion law and valid within-stratum permutations. These are different assumptions; we do not claim universally weaker assumptions.

W2. Landmark dependence and continuous-time independence.

We agree that the implication is one-way. For the true indicators At=1(E>t)A_t=1(E > t) and Bt=1(C>t)B_t=1(C > t),

\Longrightarrow A_t \perp B_t \mid X \quad \text{for every }t.$$ Thus, dependence at a landmark implies continuous-time dependence. However, nonrejection on a finite landmark grid does not establish independent censoring. Full independence requires factorization at every pair of event and censoring thresholds, whereas our grid examines selected equal-time thresholds. We will state this limitation explicitly. We will also distinguish MI uncertainty from latent MI: a positive interval width alone is not evidence of dependence. Its use as a test statistic requires the stated calibration assumptions. **Q2. Connections between the construction and guarantees.** We will reorganize Section 5.2 around the following steps: 1. **Observed information:** The landmark observations define the feasible MI interval. The optimization results establish its exact computation and uncertainty interpretation. 2. **Completion and reference:** DVFM supplies one compatible completion. Within-stratum permutations construct the reference distribution, requiring invariance under those permutations for the stated conditioning target. 3. **Validity:** Theorem 1 requires joint null calibration and symmetric scoring. Its symmetric-rank guarantee does not by itself certify the implementation's reference-only normalization. We will align the algorithm description with the implementation and distinguish their guarantees. Proposition 3 establishes a null-compatible population optimum under its assumptions; it does not guarantee recovery by variational training. Theorem 3 describes how joint completion error affects calibration. 4. **Power:** Theorem 2 additionally requires separation of the actual statistic on the chosen landmark grid. Consequently, power is conditional on this separation and is not guaranteed for every dependent alternative. **References** [1] Liu and Wang (2025). Censor Dependent Variational Inference. ICML. [2] Lee and Wolfe (1998). A simple test for independent censoring under the proportional hazards model. Biometrics. [3] Czado and Van Keilegom (2023). Dependent censoring based on parametric copulas. Biometrika.

I appreciate the authors' efforts to address my concerns, particularly regarding the role of DVFM, the assumptions underlying the proposed method, and its limitations. Overall, I remain positive about the contribution of this work and will maintain my original score of 3.

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Paper summary

This paper addresses the difficulty of testing the independent censoring assumption in survival analysis and proposes a model-assisted diagnostic framework based on conditional mutual information uncertainty. The authors represent the event and censoring processes as binary landmark states, construct a statistic from the difference between the upper and lower bounds of the mutual information over feasible completions, achieve exact computation through stratified optimization, and derive a closed-form formula for the upper bound. They further combine a deep variational frailty model, shared completions, and within-stratum permutation to construct a global test and provide guarantees of conditional validity and consistency. The experiments cover four types of copulas, shared frailty models, and seven real datasets. Under strong Gumbel dependence (θ≥6) and frailty dependence (α≥3), the detection rate reaches 100% over 10 repetitions; on the real dataset NWTCO, the detection rate reaches 90%. In the independent censoring calibration experiment, 60 datasets produced 4 false rejections, demonstrating the method's detection potential in some strong-dependence scenarios.

Critical strengths
  1. The research problem is important and has potential influence across models. Independent censoring is an important assumption for many classical and neural survival models. This paper focuses on its diagnosis and responds to a reliability issue that is prevalent in survival analysis. This makes the research value of the paper go beyond a single prediction model and is the main basis for supporting the paper's significance and potential impact.

  2. The paper proposes an uncertainty measure with clear meaning and exact computability, namely the feasible mutual information interval and its minimax error interpretation, providing a clear tool for characterizing the information insufficiency caused by censoring. The stratified two-variable optimization and the closed-form upper bound further make this measure operational. The combination of conceptual explanation and computational method is the most substantive methodological contribution of this paper and also provides a reusable foundation for subsequent research.

Critical weaknesses
  1. The connection between the conditional theoretical guarantees and the implemented DVFM remains insufficiently established. The paper explicitly acknowledges nonidentifiability, but does not specify a concrete model class in which the learned completion procedure satisfies the required calibration condition and retains power against meaningful alternatives. The existence of a null-compatible population optimum does not establish that variational training recovers an accurate conditional completion law. This gap limits confidence in interpreting rejections as evidence of dependent censoring rather than misspecification of the completion model.

  2. The empirical validation does not sufficiently resolve this calibration concern. Table 6 combines p-values from repeated runs on the same dataset using a Fisher chi-square reference distribution, without justifying its validity under their dependence. Meanwhile, the null-calibration study uses only ten independent datasets per setting, leaving substantial uncertainty about the false-positive rate. These limitations weaken both the real-data significance claims and the evidence that the implemented diagnostic provides reliable inference.

Questions for authors
  1. To which clearly defined model classes do the validity and power conclusions of this paper actually apply? How do these structural restrictions rule out independent proxies that have the same observed distribution as the dependent model, thereby making censoring dependence a testable object?

  2. For the DVFM training procedure actually used, what theoretical or experimental evidence supports the conditional completion accuracy required by the theorem? Can such evidence distinguish "good fit to the observed likelihood" from "accurate estimation of the conditional distribution of latent missing times"?

  3. What is the basis for the validity of using the Fisher chi-square distribution in Table 6 to pool p-values obtained from repeated runs on the same dataset? If the dependence among these runs is taken into account, or if this pooling method is not used, are the main real-data conclusions still supported?

5 comments

Thank you for recognizing the importance of the problem and the exact MI uncertainty interval. We address your questions by giving a concrete identifiable DVFM submodel, proving a separation result for MI width, and explaining how variational approximation affects conditional completion. We also report additional independence and near-independence checks and clarify the real-data conclusions without Fisher pooling.

1. Model class and meaningful alternatives

Identification within a DVFM submodel. Consider one covariate stratum and suppress xx in the notation. Let the two Weibull shape parameters equal one and let the event and censoring scale heads share the same positive function s(Z)s(Z). Thus, conditional on ZZ, the two times are independent exponentials with rate M=1/s(Z)M=1/s(Z). This is a nonempty submodel of our decoder: equal scale heads can still depend on ZZ, allowing genuine shared frailty. The restriction concerns both the true and fitted distributions; it is not an assumption that every unrestricted neural fit automatically satisfies it.

Write L(v)=E[exp⁡(−vM)]L(v)=E[\exp(-vM)] and T=min⁡(E,C)T=\min(E,C). Then

SE,C(e,c)=L(e+c),ST(t)=L(2t),S_{E,C}(e,c)=L(e+c),\qquad S_T(t)=L(2t),

and therefore

SE,C(e,c)=ST(e+c2).S_{E,C}(e,c)=S_T\left(\frac{e+c}{2}\right).

The observed distribution of TT therefore determines the entire joint distribution within this class, without assuming known marginal survival functions. If MM is nonconstant, the covariance of exp⁡(−eM)\exp(-eM) and exp⁡(−cM)\exp(-cM) is strictly positive for e,c>0e,c>0, so the two times are dependent. Independence within this class requires constant frailty. An independent member cannot reproduce the observed law of a nonconstant-frailty member, since the displayed identity would then give the same joint law. This directly excludes the independent proxies in your question within the stated class, while leaving the general nonidentifiability result intact.

Separation of MI width. This class also supplies meaningful alternatives for the statistic actually used. At a landmark tt, the observed and ideal independent-reference at-risk probabilities are

q1=L(2t)>q0=L(t)2,q_1=L(2t)>q_0=L(t)^2,

where strict inequality follows from Var⁡(exp⁡(−tM))>0\operatorname{Var}(\exp(-tM))>0. Whenever q0>1/2q_0>1/2, the population MI width is h(q)h(q), where h(q)=−qlog⁡q−(1−q)log⁡(1−q)h(q)=-q\log q-(1-q)\log(1-q). To see this, every feasible binary marginal has survival probability at least qq, so its entropy is at most h(q)h(q). Completing all ambiguous observations as (0,0)(0,0) attains this upper bound. By symmetry, each before-landmark observed category has mass (1−q)/2(1-q)/2. An independent feasible completion attains zero: its off-diagonal probabilities are both q−q\sqrt{q}-q, which are at most (1−q)/2(1-q)/2. Hence

ΔIobserved=h(q1)<h(q0)=ΔIreference.\Delta I_{\mathrm{observed}}=h(q_1)<h(q_0)=\Delta I_{\mathrm{reference}}.

This is a strict population gap. In a single stratum, the first population 15% quantile landmark has q1=0.85q_1=0.85 and q0=0.852>1/2q_0=0.85^2>1/2, so such a landmark is already included in our grid.

The implementation uses the absolute standardized difference, so a downward gap can produce rejection. More specifically, with one retained stratum and BB references, every reference standardized score is at most B−1B-1. If the observed score exceeds this bound at a retained landmark, the implemented p-value equals 1/(B+1)1/(B+1). The bound follows because the BB centered reference values have zero sum and their squared standardized values sum to at most BB; the subsequent rank calculation then places the observed score above every reference. This is a sufficient detection condition for the existing calculation, without changing the statistic or p-value rule. It requires an accurate completion reference and a landmark that passes the variance filter; it is not a claim of power against every alternative.

2. Completion accuracy and independence checks

A direct link to the missing-time law. The preceding identification result also identifies the required completion. Let fTf_T be the density of TT. For an observed event at time tt and c>tc>t,

P(C>c∣T=t,δ=1)=E[Mexp⁡{−M(t+c)}]E[Mexp⁡(−2Mt)]=fT((t+c)/2)fT(t).P(C>c\mid T=t,\delta=1)=\frac{E[M\exp\{-M(t+c)\}]}{E[M\exp(-2Mt)]}=\frac{f_T((t+c)/2)}{f_T(t)}.

The first equality follows by weighting the frailty distribution by the observed likelihood Mexp⁡(−2Mt)M\exp(-2Mt); the second uses fT(t)=2E[Mexp⁡(−2Mt)]f_T(t)=2E[M\exp(-2Mt)]. The formula for a missing event time is identical after exchanging EE and CC. Thus, within this class, two models with the same observed distribution cannot imply different conditional completion laws. This is stronger than merely establishing the existence of a null-compatible optimum.

What variational training must achieve. Let O=(X,T,δ)O=(X,T,\delta), let p0p_0 denote its true density, and let pp and qq denote the fitted model and encoder, with the covariate distribution held fixed. For the ordinary ELBO, corresponding to the final KL weight of one used in training,

E0log⁡p0(O)−ELBO⁡(θ,ϕ)=D+G,E_0\log p_0(O)-\operatorname{ELBO}(\theta,\phi)=D+G,

where

D=KL⁡(p0(O)∥pθ(O)),G=E0KL⁡{qϕ(Z∣O)∥pθ(Z∣O)}.D=\operatorname{KL}(p_0(O)\|p_\theta(O)),\qquad G=E_0\operatorname{KL}\{q_\phi(Z\mid O)\|p_\theta(Z\mid O)\}.

This follows by substituting the exact posterior into the ELBO and taking expectation. It separates observed-distribution error from posterior approximation error.

Under a correctly specified independent Weibull null, the decoder can ignore ZZ, and the exact posterior equals the Gaussian prior, which our encoder can represent. Thus a population ELBO solution within ε\varepsilon of the optimum satisfies D+G≤εD+G\leq\varepsilon. More generally, if the empirical ELBO differs uniformly from its population value by at most ee, optimization is within oo of its empirical optimum, and the true model's best variational approximation gap is aa, then

D+G≤a+o+2e.D+G\leq a+o+2e.

Indeed, compare the fitted empirical objective with the true-model candidate and apply the two uniform-error bounds. Here a=0a=0 for the independent null just described. Under dependent frailty, the posterior need not be Gaussian, so aa must be retained.

For a fixed stratum of positive probability, within the identifiable submodel, bounded frailty rates and convergence of the observed-law error imply convergence of the model-implied conditional completion law at observations with positive density. A proof is available directly from the formulas above: convergence of STS_T identifies the limiting frailty distribution through its Laplace transform; bounded rates give pointwise convergence of the conditional densities, and their normalization gives convergence in total variation. The positive scale floor in the decoder bounds the frailty rate in this exponential submodel. This connects accurate fitting to accurate completion under explicit structural conditions. Training for a specified number of epochs alone does not establish these conditions or error bounds.

Effect on the unchanged diagnostic. Conditional on the observed cohort and fitted parameters, let gig_i be the encoder's KL error relative to the fitted exact posterior for subject ii, and let did_i be the total-variation error of the completion law obtained using the fitted exact latent posterior and the implemented conditional time sampler, relative to the true missing-time law. Product coupling, Pinsker's inequality and data processing give ∣Pfitted(reject∣O)−Poracle(reject∣O)∣≤min⁡{1,(∑igi)/2+∑idi}.|P_{\mathrm{fitted}}(\mathrm{reject}\mid O)-P_{\mathrm{oracle}}(\mathrm{reject}\mid O)|\leq\min\{1,\sqrt{(\sum_i g_i)/2}+\sum_i d_i\}. The oracle here means using the true conditional missing-time law with exactly the same downstream calculation. There is no factor BB, because all references reuse one completed cohort. This bound applies to the implemented score and ranks. A nominal-level conclusion additionally requires calibration of that same oracle calculation; the symmetric-rank theorem alone does not establish it. For growing cohorts, the joint error in this bound must be controlled, rather than only the error for a single subject.

Completion accuracy.

We directly evaluated the fitted conditional distribution of missing times in 20 independently generated null cohorts of 2,000 subjects. For each cohort, we examined 64 subjects per missing-time type at the true conditional quantiles 0.1, 0.5, and 0.9, using 256 posterior draws. The mean absolute CDF error was 0.0313; the six mean type-by-quantile errors ranged from 0.0098 to 0.0498. Fitted missing-time draws fell within the true central 90% conditional intervals in 88.3% of event completions and 86.8% of censoring completions. These checks directly assess the latent missing-time distribution and provide evidence beyond goodness of fit to the observed likelihood.

Null calibration.

After fixing the latent dimension at eight, we evaluated fresh, independently generated cohorts with conditionally independent Weibull event and censoring times. We retained the implemented MI-width statistic, one shared completion, ten landmark quantiles from 0.15 to 0.85, 200 permutations, and the original p-value calculation. All binary covariates were retained as exact profiles, with minimum stratum size 20.

SubjectsCovariatesFalse rejections at p<0.05p<0.0595% interval
200047/1003.4–13.7%
400042/202.8–30.1%
200060/200–16.1%

Each denominator counts independently generated cohorts, with a separate DVFM fit for every cohort. The intervals are 95% Wilson intervals. Mean subject coverage was 100%, 100%, and 99.42%, respectively, and every cohort produced a finite result. The main validation therefore extends the null assessment to 100 independent cohorts, directly addressing the uncertainty arising from only ten datasets per setting.

3. Fisher pooling and the real-data conclusions

We agree that the usual Fisher chi-square reference is not justified for repeated analyses of the same patients. We will remove the pooled p-values and significance claims based on them from Table 6. This concerns aggregation across runs; individual-run results remain unchanged. Within a run, the implementation compares its Fisher-type aggregate with generated reference scores rather than a chi-square distribution.

Without pooling, NWTCO remains the dataset most frequently flagged: 9 of the 10 reported runs reject, compared with 5 for METABRIC and 2 for COVID. These counts describe recurrence across analyses, not an additional calibrated dataset-level test. The conclusion that NWTCO produces the strongest recurring diagnostic signal among these datasets remains supported. We will state this as model-assisted evidence and remove the stronger significance claim based on pooling.

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

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