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Under review as a conference paper at ICLR 2027

DISCERN: Identifiable Disease Evidence for Generalizable Medical Multimodal Learning

Abstract

Multimodal clinical models are trained on cohorts that differ in whom they enroll and how they measure. Enrollment that ties background factors such as age to the disease state leaks into every modality, so models learn shortcuts that fail on new cohorts. We model medical multimodal data as a latent structural causal model in which a latent disease state drives, and in a second regime rewires, a graph of latent factors; each modality and the recorded endpoint are partial views of these factors, and cohorts differ only in selection and measurement. We show that the disease state need not be observed and the full model need not be recovered: in common Gaussian coordinates, states can be aligned across cohorts, enrollment-induced changes identify a minimal selection statistic, and conditioning on it yields disease evidence that is identifiable without state labels and invariant to enrollment shifts within the identified family. When the disease state rewires the factors, this evidence can be invisible to each modality and to late fusion of their posteriors, yet recoverable from the modalities jointly. DISCERN instantiates the theory in a jointly trained encoder, latent-state model and outcome head. Under reversed synthetic enrollment, conditioning raises state AUROC from 0.043 to 0.883 and from 0.265 to 0.825, while random conditioning does not; on cross-database mortality prediction between eICU and MIMIC-IV, DISCERN improves AUROC over matched empirical risk minimization by 0.036 and 0.035.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Multimodal learning, generalization, structural causal models, medical AI

Reviews

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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.
Reviewer_xCxAOpenReview ↗
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Paper summary

DISCERN aims to separate disease evidence from shortcuts caused by differences in cohort enrollment. Under a shared Gaussian latent-coordinate model, it identifies a selection statistic from cross-cohort changes and removes its contribution to the state likelihood ratio. The proposed model combines this correction with a multimodal encoder and an outcome predictor. Experiments show strong state recovery under reversed enrollment when the true latent coordinates are supplied, and improved cross-database ICU mortality prediction over a matched ERM baseline.

Critical strengths
  1. The paper defines a precise target—conditional evidence about an unobserved disease state—and states the assumptions under which it is identifiable.
  2. The synthetic reversal experiment and random-direction control give convincing evidence that the proposed correction works when the required latent coordinates are available.
  3. The ICU study includes matched-backbone ablations and reports gains in AUROC, AUPRC, and NLL in both transfer directions.
Critical weaknesses
  1. The theoretical and practical components are not connected end to end. The identification result assumes aligned Gaussian latent coordinates, shared state-specific covariances, fixed acquisition, and target shifts contained in the source-identified subspace. These conditions are not established by the proposed encoder. Indeed, when the true latent coordinates are replaced by learned multimodal representations, state recovery under reversed enrollment falls below chance and DISCERN does not outperform the matched lattice ERM.
  2. The clinical experiment does not validate the interpretation of the learned quantities as disease evidence or enrollment effects. eICU and MIMIC-IV differ in both patient selection and measurement practices, while the latent states have no clinical anchors and are influenced by outcome supervision through joint training. The learned state components and selection direction may therefore capture database, measurement, or label-related variation rather than the intended disease and enrollment mechanisms.
  3. The clinical evidence remains limited and exploratory. The evaluation uses one prediction task, three seeds, and targets that were inspected during earlier development. Several historical baselines use different backbones and training protocols, while the matched rich ERM is weaker than some simpler ERM variants. In addition, the deployed rank-one correction is not justified empirically, although the first direction explains only 37.1–57.6% of the fitted shift energy.
Questions for authors
  1. Can the authors provide an end-to-end synthetic experiment in which raw multimodal observations are used, acquisition is held fixed, and only enrollment changes? This would clarify whether the failure of learned-view state recovery is caused by the encoder coordinates or by the additional measurement shift.
  2. Is there any clinical evidence that the learned mixture components correspond to meaningful disease states and that the estimated selection direction captures enrollment rather than measurement or database identity? Associations with independent clinical variables or clinically defined subgroups would help.
  3. How do state recovery and ICU prediction change when the full estimated selection subspace, or several ranks, are used instead of a single direction?
  4. Can the authors evaluate the final method on a previously unseen clinical target and compare it with baselines using the same backbone, inputs, training budget, and model-selection protocol?
6 comments
AuthorsOpenReview ↗

1. Response to Reviewer xCxA

We thank the reviewer. SS is a latent disease-related processes underlying physiology and clinical manifestations. It is not defined as a pre-existing diagnosis class with a corresponding ground-truth annotation. Clinical observations and recorded outcomes provide partial information from which SS is inferred. Thus outcome supervision contributes to learning without directly labeling SS. The identification target is conditional evidence about this latent state under selection.

W1 / Q1: end-to-end recovery with fixed acquisition

The new study holds acquisition fixed and changes only enrollment, using raw multimodal observations from the §5 generator (Appendix C.7, Table 6). State AUROC under far reversal, over five generated studies per mechanism, is:

Coordinates and state modelAdditiveInteractions
Reconstruction lattice, no state labels0.2700.380
Reconstruction lattice, recorded source state0.3700.590
True coordinates, recorded source state0.8800.850
Raw observations + observed background, recorded source state0.8480.833
Same estimator, random direction0.1860.449

Bold identifies the raw-observation estimator. Synthetic SS is specified by the generator, enabling evaluation across these state/coordinate information settings.

The lattice fitted without state annotations remains below chance with acquisition fixed, showing that measurement change alone does not explain its behavior. With recorded source states and observed background, the additional estimator averages joint log odds relative to reference state 0 minus the corresponding log odds conditioned on the estimated background statistic. It gives 0.831 to 0.877 across four target laws with fixed acquisition and 0.815 to 0.872 with changing acquisition; its direction has cosine 1.000 with the generator direction. This provides a direct raw-input test of the correction with a recorded operational state.

We also tested the full jointly trained clinical model under imposed enrollment within eICU and across eICU→MIMIC-IV (ten replicates each; Appendix G.5). Its state branch receives weights below 0.010, and conditional, uncorrected and random variants stay within 0.002 AUROC: DISCERN reaches 0.605 / 0.603 versus matched ERM 0.614 / 0.597. State-evidence AUROC is at most 0.680 in the more favorable orientation. In this imposed-mortality-enrollment setting, the learned composite states give little correction benefit.

With source states recorded, applying the additional estimator to the learned representation gives 0.695 under reversal versus random conditioning 0.552 and the network head 0.556. Thus the same representation supports a useful correction when the operational state and background information are supplied.

W2 / Q2: clinical interpretation of states and direction

Clinical meaning of the composite states. In eICU→MIMIC-IV, one component consistently has mortality of 22 to 34% and mean APACHE IV of 72 to 80, versus 6 to 8% and 56 to 61 in other components (Appendix D.6). These associations support a clinically meaningful severity organization. The normalized mutual information with diagnosis is at most 0.016: the composite states span diagnosis categories, as the model permits. Demographics, physiology and, in the reverse direction, vital-sign measurement frequency influence assignments. Outcome supervision is intentional, because YY is an observed clinical view informing the composite representation; it is not a direct annotation of latent SS.

Direction attribution. Table 2 now includes random conditioning. DISCERN exceeds it in AUROC (0.818 vs 0.793; 0.812 vs 0.786), AUPRC and NLL. The variants train separately from the same warm-up checkpoint with matched training settings and source-only selection. Random directions remain fixed, whereas DISCERN updates its estimated direction each epoch (Appendix D.6). This supports the direction choice in the jointly trained model.

Known enrollment and recorded states. New §5.4 instead imposes enrollment tied to mortality or CSF amyloid positivity. The differential statistic loads 0.980 to 0.990 on the enrolled factor, versus 0.360 to 0.500 for the original natural-parameter direction (Appendix G.3), and outperforms the mean random direction in all 80 replicates. These operational instances test whether the correction follows enrollment; mortality and amyloid labels are not ground-truth annotations of the original latent composite.

The guarantee addresses selection under the stated coordinate, covariance, alignment and source-subspace assumptions; Proposition 3 accounts separately for measurement and endpoint mismatch. Appendix G.5 tests shortcut sensitivity by including or excluding background from the encoder and applying the correction at the representation level.

AuthorsOpenReview ↗

2. Response to Reviewer xCxA

W3: clinical evidence and matched comparisons

Replication. Table 2 retains the original three-seed results and adds three random directions per training seed across five seeds. Each control trains separately from the shared warm-up checkpoint; Appendix D.6 gives the direction-generation and training protocol. The controlled studies use 10 to 20 enrollment/target replicates, with paired comparisons in Appendix G.2.

Comparison scope. The rich ERM and original mechanism ablations share the backbone, inputs, training budget and source-only checkpoint selection. Historical baselines use different backbones/protocols and remain contextual comparisons. In particular, matched rich ERM is weaker than some simpler historical models; DISCERN is slightly below SWAD-style into MIMIC-IV (0.818 vs 0.820) and above the historical baselines into eICU.

Controlled-study methods share inputs and source-only selection, but GroupDRO/V-REx use MLPs while the recorded-state estimator and ERM use logistic models. Their architectures and budgets are reported in Appendix G.1; the random-direction control holds the estimator fixed to compare the conditioning choice directly.

On eICU age enrollment (Table 11), AUROC is:

MethodReversedMean of four laws
Oracle, target labels0.8790.881
ERM0.5880.794
IPW0.7260.804
GroupDRO0.6290.800
V-REx0.6290.797
IRMv10.6900.786
Conditional label shift0.7800.794
Random direction0.5760.784
DISCERN0.7720.795

Bold marks the best non-oracle value. DISCERN improves robustness under reversal. The unlabeled-target gate adapts to the target selection law, raising its four-law mean to 0.870 (Table 12).

Development history. The original cross-database comparisons remain exploratory because targets were inspected earlier. Controlled designs were fixed before their results; the first natural-parameter-statistic run failed, and the subsequent differential-statistic studies used new replicates/cohorts. Appendix G also reports the ADNI conversion and MIMIC-IV→eICU gate results, where adaptation does not consistently improve on ERM.

Q3: several ranks versus rank one

The 37.1 to 57.6% energy share measures fitted shift variation, while useful rank also depends on evidence retained after conditioning. The original clinical implementation uses a rank-one approximation. Conditioning can remove state evidence: on supplied synthetic coordinates, increasing the rank from one to two reduces additive-regime AUROC from 0.879 to 0.705 (Appendix C.7). At the full-coordinate limit, conditioning gives constant state evidence.

Table 13 reports the recorded-state eICU age-family comparison:

StatisticFirst-direction energyAge loadingAUROC, ranks 1 / 2 / 3
Original natural-parameter0.4600.3600.624 / 0.768 / 0.771
Differential0.8500.9900.772 / 0.773 / 0.775
Random, mean of three draws0.1000.2700.587 / 0.618 / 0.636

The original statistic improves when more directions are included, while the differential statistic concentrates the relevant shift in one direction. Under common covariance, Theorem 2 preserves pairwise evidence ranking up to constants, with prior/gate adjustment for calibration. If sources enroll on age but the target on sex, correcting the source direction gives 0.765 versus ERM 0.757; using the whole background gives 0.788, illustrating the importance of the source-subspace assumption.

Q4: a previously unseen target

We added eICU leave-one-region-out evaluation: each US census region is held out in turn, with five replicates per region (20 total), under a design fixed before results. Reversal AUROC is 0.779 for DISCERN, 0.586 for random conditioning and 0.593 for ERM; DISCERN exceeds both in all 20 replicates. With an unlabeled-target gate, its four-law mean is 0.875. MIMIC-IV and ADNI additionally test the differential statistic beyond the eICU cohort on which it was developed.

These additions extend the evaluation to held-out geographic targets and additional clinical state definitions. The region study uses new partitions of eICU; an untouched external database with all baselines matched in backbone and budget would provide a further independent evaluation.

Thank you for the additional experiments and clarifications. They address several of my questions, though two concerns remain.

  1. The successful raw-input results use recorded states and observed backgrounds. The original lattice still fails with fixed acquisition, and the full joint model shows little benefit from conditioning under imposed enrollment. It therefore remains unclear whether the original model learns the stable evidence required by the theory.

  2. Could you clarify which results support the original model and which support the recorded-state estimator and subsequent extensions? Theorem 2 assumes common covariance across states, so it does not directly cover the state-dependent covariances used in the original interaction setting.

Reviewer_DzvcOpenReview ↗
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Paper summary

The paper models medical multimodal data as a latent causal model in which a disease state drives, and in a second regime rewires, a graph of latent factors, with cohorts differing in who gets enrolled. Theorem 1 says that in common Gaussian coordinates the enrollment-induced parameter changes identify a minimal selection statistic, and that conditioning on it leaves disease evidence that is identifiable without state labels. The method puts that construction into an encoder, a latent-state model and an outcome head, trained together. Two things are claimed for it: that conditioning restores state recovery under enrollment laws which leave an uncorrected model below chance, shown on synthetic data with the coordinates supplied, and that the jointly trained model improves cross-database ICU mortality transfer between eICU and MIMIC over matched empirical risk minimization.

Critical strengths

Cancelling the same-state cohort log-density ratio by conditioning on a recovered selection statistic is a clean population-level result, and the assumptions are on the table. Keeping state evidence apart from endpoint prediction is the right separation to make and the paper makes it explicitly. It also reports the failure of its own harder configuration: state recovery stays below chance when a label-free lattice replaces the supplied coordinates, and the nonlinear calibration tested does not rescue it even though feature-density fit improves.

Critical weaknesses

The abstract's headline state-recovery numbers come from the supplied-coordinate study. It says "DISCERN instantiates the theory in a jointly trained encoder, latent-state model and outcome head" and then, in the next sentence, "Under reversed synthetic enrollment, conditioning raises state AUROC from 0.043 to 0.883 and from 0.265 to 0.825". That rise is from the mechanism-stage study on supplied common coordinates; when a label-free lattice replaces them under the same reversal, state AUROC is 0.118 and 0.306, and a jointly fitted calibration leaves it there. Section 5 and the appendices say which study is which, so this is framing issue, but the identifiability the paper is named for has been shown only where the representation is given, and the clinical study that does train jointly reports 0.036 and 0.035 over matched ERM.

The clinical ablations show that the conditional branch helps, but not that the recovered direction is what makes it help. Five synthetic studies per regime read one fitted mixture three ways, uncorrected, conditioned on a random unit direction, and conditioned on the estimated direction, which is how the paper concludes that the correction is attributable to the selection statistic rather than to conditioning as such. That control does not appear on the clinical side, where the variants are matched ERM, information only, uncorrected state, conditional state and no edges, none of which tests whether the subtracted direction is the right one. Two things make me want it there. On the supplied-coordinate synthetic study, the matched outcome gain from the conditional branch is 0.001 and 0.002, inside one standard deviation. And the sensitivity sweep produces ICU gains above the headline at every assumed latent-factor count, including counts where synthetic state recovery is below chance. The abstract puts the random-direction result and the ICU result in one sentence, which invites the reading that the attribution carries over.

If the random-direction readout is added to the ICU comparison and the estimated direction separates from it there as it does on synthetic data, that would address my main objection.

Questions for authors

Q1. Could you distinguish, in the abstract, which numbers come from the supplied-coordinate study and which from the learned-coordinate and jointly trained ones?

Q2. Could you add the random-direction readout to the ICU comparison? If conditioning on a random direction recovers a similar share of the ICU gains, the clinical result would need a different reading.

Q3. Appendix F places the result against the selection-bias and nuisance literatures, but not against conditional inference in exponential families, where conditioning on a sufficient statistic to cancel a nuisance parameter is the classical construction. How do you see Theorem 1 against that, and is the new element the recovery of the statistic rather than the cancellation itself?

3 comments
AuthorsOpenReview ↗

1. Response to Reviewer Dzvc

We thank the reviewer for identifying the missing clinical control. Table 2 now shows that the estimated direction outperforms random conditioning in both transfer directions. We clarify that SS represents a latent composite of disease-related processes underlying physiology and clinical manifestations, not a predefined diagnosis class with its own ground-truth label. Clinical observations and recorded outcomes provide partial information for inferring SS. We also add controlled-enrollment studies to test the correction under explicit selection conditions.

W2 / Q2: random-direction control on ICU

Table 2 reports the following cross-database mortality results. E→M denotes eICU→MIMIC-IV and M→E the reverse. Entries are mean ± SD; bold marks the best of the three displayed methods.

MetricMatched rich ERMRandom directionDISCERN
AUROC E→M ↑0.782 ± 0.0170.793 ± 0.0160.818 ± 0.018
AUROC M→E ↑0.777 ± 0.0110.786 ± 0.0130.812 ± 0.016
AUPRC E→M ↑0.462 ± 0.0220.471 ± 0.0160.502 ± 0.020
AUPRC M→E ↑0.398 ± 0.0120.406 ± 0.0130.431 ± 0.016
NLL E→M ↓0.383 ± 0.0300.365 ± 0.0180.316 ± 0.016
NLL M→E ↓0.372 ± 0.0240.362 ± 0.0310.328 ± 0.028

The estimated direction exceeds random conditioning by 0.025 / 0.026 AUROC and improves AUPRC and NLL. The original matched ablations additionally compare information-only, uncorrected-state and no-edge variants (Table 8). Together these provide direct clinical evidence for the direction choice, alongside the synthetic attribution study.

Matched training protocol (Appendix D.6). These are separately trained variants. For each seed, we run five supervised warm-up epochs and fit the mechanism once on the standardized 38-dimensional lattice. DISCERN and the three random variants then start from copies of that warm-up model and train for up to 30 epochs, sharing the seed, data order, optimizer, early stopping and window averaging. Checkpoints are selected using source data only. The intervention is the direction rule used in the mechanism subtraction.

After warm-up and mechanism fitting, each random direction is drawn from a standard Gaussian in the standardized lattice coordinates and normalized to unit length. This rule is independent of data and results. Each random direction is fixed throughout training; DISCERN recomputes its estimated direction each epoch from the current mechanism parameters. The random control uses three directions per training seed across five seeds, giving 15 directions. The original rich-model rows use three seeds. Thus Table 2 tests the direction choice within matched training procedures.

Additional conditions: imposed enrollment across databases

We further imposed age and mortality enrollment on the source database and evaluated the other database under four target laws (Appendix D.6, Table 9). The study uses the recorded-state estimator of §4 and ten replicates per direction; this is distinct from Table 2's jointly trained latent-state model. Results below are AUROC under reversal without target data; bold marks the best non-oracle value shown.

MethodE→MM→E
Oracle, target labels0.9200.902
ERM0.6230.635
IPW0.7420.668
GroupDRO0.6530.699
IRMv10.7160.722
Conditional label shift0.7920.701
Uncorrected state0.5720.606
Random direction0.5920.617
DISCERN0.7810.699

DISCERN exceeds the mean of three random draws and ERM in all 20 replicates (paired Wilcoxon p = 0.002 per direction). Thus the estimated direction remains preferable to random conditioning when the enrollment mechanism is explicitly varied across databases.

IRMv1 is higher in M→E, and GroupDRO ties DISCERN to the reported precision. With an unlabeled-target gate, DISCERN improves mean AUROC across the four laws over ERM in E→M (0.865 vs 0.811), but not in M→E (0.745 vs 0.747). The latter direction has a large residual transfer gap even under the same enrollment law, consistent with limitations beyond background correction.

AuthorsOpenReview ↗

2. Response to Reviewer Dzvc

W2 / Q2 continued: controlled enrollment on clinical cohorts

Table 2 establishes the predictive comparison with random conditioning. New §5.4 asks a further question: does the direction remain useful when enrollment, target law and available state information are explicitly controlled?

We impose enrollment tying age or sex to a recorded state: mortality in eICU/MIMIC-IV and CSF amyloid positivity in ADNI. The targets include held-out hospitals, sites and US regions. AUROC under reversal without target data is shown below (Tables 3 and 11); bold marks the best non-oracle value shown.

MethodeICU ageeICU sexeICU regionMIMIC-IV ageADNI amyloid
Oracle, target labels0.8790.9380.8800.8940.873
ERM0.5880.5480.5930.6700.709
IPW0.7260.7350.7360.7490.716
Conditional label shift0.7800.7750.7910.7980.706
Random direction0.5760.5610.5860.6570.670
DISCERN0.7720.7670.7790.7900.766
Replicates1010202020

DISCERN exceeds the mean of three fixed random directions in all 80 replicates and ERM in 79 (Appendix G.2). The full tables include GroupDRO, V-REx and IRMv1. The additional studies examine nonlinear enrollment, direction/rank, unknown background, target-subspace violations, learned representations and target-label budgets. Together they test the contribution across the conditions governing evidence retention and transfer.

Conditional label shift performs similarly or better when conditioning on the whole background removes little useful evidence. DISCERN has the advantage when background variables also carry state evidence, as APOE ε4 does for amyloid, or when the background block is unspecified (Part 3). The first controlled eICU run using the original natural-parameter statistic failed; the differential statistic was then tested on new replicates and cohorts under designs fixed before their results (Appendix G.1).

W2: small synthetic outcome gains and Appendix C.6

The small synthetic outcome gains (0.001 / 0.002) illustrate the distinction formalized by Proposition 3: YY also depends on continuous factors and cohort-specific label terms. State correction and endpoint improvement therefore measure different effects. The new ICU random-direction comparison supplies direct evidence for the clinical attribution.

The factor-count sweep in Appendix C.6 is a separate sensitivity study, with a different synthetic generator and reference predictor. Its outcome gains are not pooled with Table 1 or Table 2. Its positive ICU gains across assumed factor counts show prediction robustness within that sweep, while the synthetic state-recovery peak measures sensitivity to the assumed state-factor structure.

W1 / Q1: distinguish the studies in the abstract

Agreed. The revised abstract explicitly attributes the 0.043→0.883 and 0.265→0.825 state-AUROC changes to supplied latent coordinates. It separately describes the jointly trained cross-database ICU prediction result and the new controlled clinical studies with recorded source states. The representation and acquisition controls are detailed in §5.2 and Appendix C.7.

The evidence is therefore separated as follows:

StudyWhat it establishes
Supplied-coordinate syntheticSelection correction with known common coordinates
Learned-coordinate syntheticSensitivity to the representation and available state information
Jointly trained ICU modelPredictive gain and estimated-versus-random comparison
Recorded-state controlled clinicalDirection attribution under known enrollment and tested conditions

These studies support one goal: extracting state evidence that is less dependent on enrollment. In the joint model, SS represents a latent composite of disease-related processes, inferred from multimodal observations and source outcome supervision. It is not defined by a pre-existing diagnostic label. Synthetic SS is available from the generator for evaluation. Mortality and amyloid status define explicit operational instances of the correction in the recorded-state studies, rather than ground-truth annotations of the original latent composite.

AuthorsOpenReview ↗

3. Response to Reviewer Dzvc

Q3: relation to conditional inference in exponential families

Yes. The classical conditioning principle is the starting point; our contribution is identifying the statistic and resulting evidence when the state is latent. Appendix F now makes this connection explicit (Bartlett, 1937; Andersen, 1970; Cox & Hinkley, 1974; Lindsay, 1982; Reid, 1995).

For a fixed state, the Gaussian cohort family has natural parameter Σs−1μes\Sigma_s^{-1}\mu_{es}. The differences in natural parameters across cohorts span U\mathcal{U}; conditioning on its projection removes the corresponding cohort term. Our contribution is to recover and characterize the statistic when the state is latent, and to specify what evidence remains:

  1. Mixture components must first be aligned across cohorts (Proposition 1); otherwise parameter differences for the same state are undefined.
  2. Theorem 1 recovers the smallest subspace representing all cohort log-density ratios for the same state. This identifies the statistic from observable cohort distributions under the stated assumptions.
  3. Conditioning removes evidence along that subspace as well as nuisance variation. In particular, conditioning on all coordinates gives no residual state evidence, so nuisance removal and evidence retention must be distinguished.

The differential refinement (Theorem 2, proof in B.9). Under the stronger assumption of one covariance shared by all states and cohorts, define

\mathcal{U}_{\Delta}=\operatorname{span}_{e,s}\left\\{\Sigma^{-1}\big[(\mu_{e,s}-\mu_{e_0,s})-(\mu_{e,0}-\mu_{e_0,0})\big]\right\\}\subseteq\mathcal{U}.

Conditioning on this subspace yields Ts(e)(z)=Ts(e′)(z)+as(e,e′)T_s^{(e)}(z)=T_s^{(e')}(z)+a_s(e,e'), with constants independent of zz. Thus binary or pairwise score rankings are preserved, while calibrated probabilities require adjustment of the prior or gate. A shift shared across states need not be conditioned away for ranking under these assumptions; strict subspace reduction occurs only when it contributes directions outside UΔ\mathcal{U}_{\Delta}.

This is related to the case-control intercept result of Prentice & Pyke (1979), but extends the analysis to background tilts that depend on the state. We distinguish the classical cancellation principle from the problem of identifying and recovering the subspace.

Relation to conditional label shift. At the population level, using the whole background as the conditioning statistic gives the same likelihood-ratio cancellation underlying a prior correction conditioned on background. The fitted estimators are not identical: our models for source environments estimate a differential statistic and average evidence, whereas the comparison fits a pooled conditional label-shift model. Table 14 uses common replicates. “Rev.” is reversed enrollment without target data; “gate” averages four laws using gates fitted on unlabeled target data. Bold compares the two methods within each setting.

BackgroundCohortLabel shift, rev.DISCERN, rev.Label shift, gateDISCERN, gate
Known, enrollment-distortedeICU age0.7800.7760.8620.871
Known, enrollment-distortedeICU sex0.7800.7730.8810.888
Known, carries evidenceADNI amyloid0.6960.7600.8280.836
UnspecifiedeICU age0.6780.7540.7530.859
UnspecifiedeICU sex0.6830.7620.8050.881
UnspecifiedADNI amyloid0.6180.7520.7790.818

The methods perform similarly when conditioning on the whole background sacrifices little evidence; the differential statistic is preferable in the tested cases where useful evidence is also present or the background block is unspecified.

Finally, reference evidence estimated only from sources need not yield the target Bayes posterior. Under the same eICU enrollment law its AUROC is 0.804 versus ERM 0.876; the target gate reaches 0.870. This illustrates the difference between the reference posterior and the target posterior. Equation 6 bounds excess log loss, not the AUROC difference.

Reviewer_aDNoOpenReview ↗
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Paper summary

This paper asks how to extract evidence about an unobserved disease state that remains reliable across cohorts with different enrollment patterns. DISCERN combines a multimodal encoder, an aligned latent-state model, and a conditional likelihood-ratio correction to separate enrollment effects from disease evidence, with identifiability guarantees under explicit Gaussian assumptions. Experiments show improved state recovery on supplied synthetic coordinates and better cross-database ICU mortality prediction than matched ERM, although recovery fails with learned synthetic representations.

Critical strengths
  1. The paper explains why modalities should be modeled jointly: useful disease information can lie in their relationships and be missed by combining separate predictions. It also shows why keeping only universally shared information can lose useful signals, supporting the encoder’s shared, pairwise, and private components.
  2. I appreciate the distinction between recovering disease evidence and predicting clinical outcomes. The reference posterior need not match the target cohort’s Bayes posterior, and the error analysis explains why removing enrollment effects may not improve every metric or remove the need for continuous features.
Critical weaknesses
  1. My main concern is the gap between supplied latent coordinates and learned features. With learned features, state AUROC under reversal falls to 0.118 and 0.306, and calibration does not fix this. Full joint training is tested only on clinical data without known disease states; a synthetic experiment with fixed measurement would help assess end-to-end recovery.
  2. The guarantees require common Gaussian coordinates, shared state covariances, aligned states, and target shifts within the source-identified subspace, but do not cover clinical measurement changes. Exact invariance also requires the full selection subspace, yet the single retained direction captures only 37.1–57.6% of fitted squared singular-value energy. Testing additional directions would help justify this choice.
  3. The clinical states are shaped by outcome supervision and lack direct disease-state validation. Physiology and context inputs could also carry enrollment-related shortcuts into the outcome head. Better mortality prediction alone therefore does not establish that the states capture stable disease information or that the final predictor avoids these shortcuts.
  4. Once local labels are available, it is unclear when DISCERN is preferable to cohort-specific training or fine-tuning. Comparing performance across different amounts of labeled target data would clarify its practical value.
Questions for authors
  1. When is DISCERN preferable to training or fine-tuning a model with a small amount of local labeled data? Comparing performance across different amounts of local data would show how many labels are needed to match or exceed DISCERN.
  2. Can the full jointly trained model recover the true disease states from synthetic observations when the measurement process is held fixed? This would help separate difficulties in learning the required coordinates from the effects of measurement changes.
  3. What justifies keeping only one selection direction, given that it captures 37.1–57.6% of the fitted squared singular-value energy? Have you tested how retaining more directions affects the results?
  4. What evidence beyond mortality prediction supports interpreting the learned states as stable disease information? Have you checked whether the final predictor still uses enrollment-related shortcuts through the continuous physiology and context branches?
4 comments
AuthorsOpenReview ↗

1. Response to Reviewer aDNo

Thank you for the great review! SS is a latent composite of disease-related processes underlying physiology and clinical manifestations, not a predefined diagnosis class with a ground-truth annotation. Clinical inputs and recorded outcomes provide partial information from which SS is inferred. Source outcome supervision therefore contributes to learning without directly labeling SS. Our target is identifiable conditional state evidence under selection.

W1 / Q2: end-to-end recovery with fixed measurement

We added the fixed-acquisition comparison using raw observations from the §5 generator, so that only enrollment changes (Appendix C.7, Table 6). State AUROC under far reversal, over five generated studies per mechanism, is:

Coordinates and state modelAdditiveInteractions
Reconstruction lattice, no state labels0.2700.380
Reconstruction lattice, source state recorded0.3700.590
True coordinates, source state recorded0.8800.850
Raw observations + observed background, source state recorded0.8480.833
Same estimator, random direction0.1860.449
Same estimator, uncorrected0.0530.319

Bold identifies the raw-observation estimator. Synthetic SS is specified by the generator, enabling evaluation across these information settings.

The fixed-acquisition control separates measurement from representation effects. The lattice fitted without state annotations remains below chance when acquisition is fixed. Holding acquisition fixed alone therefore does not ensure effective state-evidence estimation with this fitted representation.

With recorded source states and observed background, the additional estimator succeeds from raw observations. For each state relative to reference state 0, it averages the joint-model log odds minus the log odds conditioned on the estimated background statistic. Both are logistic models from the same family (§4). AUROC remains 0.831 to 0.877 across the four laws with fixed acquisition, and 0.815 to 0.872 with changing acquisition; the direction has cosine 1.000 with the generator's selection direction. Using an MLP for the joint model instead overcorrects (0.660 / 0.750 under the same law). This recorded-state estimator tests the correction directly; the original joint clinical model is evaluated separately below.

Independent test of the full clinical pipeline (Appendix G.5). Under imposed enrollment, ten replicates each within eICU and from eICU to MIMIC-IV select the warm-up or first epoch, with state-head weights below 0.010. The conditional, uncorrected and random variants stay within 0.002 AUROC under reversal: DISCERN reaches 0.605 / 0.603 versus matched ERM 0.614 / 0.597. State-evidence AUROC is at most 0.680. These particular composite states offer little benefit for correcting the imposed mortality enrollment. With recorded source states, the same learned representation supports a correction reaching 0.695 versus random conditioning 0.552 and the network head 0.556.

W2 / Q3: assumptions and the single selection direction

The guarantee concerns common Gaussian coordinates, aligned states, fixed acquisition and target shifts within the source-identified subspace. Proposition 3 separately accounts for measurement and endpoint mismatch. The new experiments vary these conditions explicitly.

Rank should balance selection removal against state-evidence retention, rather than maximize captured shift energy alone. The original clinical rank-one implementation is a low-rank approximation. More conditioning can also remove useful evidence: on supplied synthetic coordinates, increasing the rank from one to two reduces state AUROC from 0.879 to 0.705 in the additive regime (Appendix C.7). At the full-coordinate limit, conditioning gives constant state evidence.

Under the stronger common-covariance assumption, Theorem 2 identifies the state-differential subspace. Its evidence is invariant up to constants, so pairwise ranking is preserved; posterior calibration still needs prior adjustment. The recorded-state eICU rank comparison (Table 13) gives:

StatisticFirst-direction energy, age / sexEnrolled-factor loading, age / sexAge AUROC, ranks 1 / 2 / 3
Original natural-parameter statistic0.460 / 0.4400.360 / 0.5000.624 / 0.768 / 0.771
Differential statistic0.850 / 0.7600.990 / 0.9800.772 / 0.773 / 0.775
Random, mean of three draws0.100 / 0.1000.270 / 0.4500.587 / 0.618 / 0.636

The differential statistic captures the enrolled factor in its first direction, while the original statistic benefits from additional directions. When sources enroll on age but the target on sex, the source direction yields 0.765 versus ERM 0.757; conditioning on the whole background yields 0.788. This illustrates why the source-subspace assumption matters.

AuthorsOpenReview ↗

2. Response to Reviewer aDNo

W3 / Q4: clinical meaning and shortcuts through the continuous branches

Clinical interpretation of the composite states (Appendix D.6). SS indexes a latent joint configuration of disease-related processes. Its clinical manifestations can span diagnoses, and observations and outcome supervision inform its inference. In eICU→MIMIC-IV, one component consistently has mortality of 22 to 34% and mean APACHE IV of 72 to 80, versus 6 to 8% and 56 to 61 in the other components. The association with APACHE severity gives the components a concrete clinical interpretation. Their normalized mutual information with diagnosis is at most 0.016, consistent with a severity organization spanning diagnosis categories. Demographics and physiology inform the assignments; vital-sign measurement frequency also contributes in the reverse direction, motivating the controlled enrollment tests.

Table 2 adds the requested attribution control. DISCERN exceeds random conditioning in AUROC (0.818 vs 0.793; 0.812 vs 0.786), AUPRC and NLL. Each variant trains separately from a common warm-up model, with the same training recipe and source-only checkpoint selection. Random directions remain fixed; the estimated direction is updated each epoch (Appendix D.6). This supports the direction choice within the joint clinical model.

The controlled studies isolate a known enrollment intervention (§5.4). Their states are recorded source outcomes: mortality or CSF amyloid positivity. The differential direction loads 0.980 to 0.990 on the enrolled factor; the original natural-parameter direction loads 0.360 to 0.500 and is more sensitive to hospital composition (Appendix G.3). Here the clinical indicators define explicit operational instances of the correction under known enrollment; they do not annotate the original latent composite state.

Testing shortcut sensitivity across branches. On controlled eICU age enrollment, changing from the same law to reversal produces (Appendix G.2):

PredictorSame lawReversed
ERM0.8760.588
Random direction0.8660.576
DISCERN, source-only reference0.8040.772
DISCERN, unlabeled-target gate0.8700.862

The correction substantially reduces sensitivity to the imposed enrollment change. With background included in the learned encoder, the network head reaches 0.556 under reversal; the additional recorded-state correction on (z^,B)(\hat z,B) reaches 0.695. Excluding background from the encoder already raises the head to 0.672 (Appendix G.5). These additional branch comparisons show how background information affects the head and where the recorded-state correction helps.

W4 / Q1: comparison with local labels and fine-tuning

We added target-label curves under controlled enrollment (Appendix G.6, Table 15). Each target is separated into a label pool and a held-out test half. The table reports eICU age enrollment under reversal; bold marks the best method at each label count.

Target labels501002005001,0002,000
Target-only model0.7330.6900.6980.7680.8120.847
Source + target, weighted0.6270.6540.6740.7280.7610.785
DISCERN, gate fitted on labels0.8490.8660.8740.8760.8760.877

Without target labels, ERM reaches 0.605 and DISCERN with an unlabeled-target gate reaches 0.863. Thus 100 labels bring the supervised gate close to its performance with 2,000 labels, while the target-only model remains lower even at 2,000. These data support using DISCERN when enrollment changes strongly and target labels are scarce.

The choice depends on enrollment: under the same law, pooled source/target training reaches 0.883 to 0.893 versus 0.870 to 0.879 for DISCERN. Under reversal, adapting DISCERN's low-dimensional gate is more label-efficient than target-only or weighted source/target training in this comparison. These curves compare those adaptation strategies; Table 2 evaluates the jointly trained model across databases.

Reviewer_aDNoOpenReview ↗

Feedback

Thank you for the detailed responses and additional experiments. The clinical interpretation, shortcut analyses, and target-label comparisons have improved the paper and mitigated my other concerns. However, there are two issues remain.

  1. End-to-end recovery remains unestablished. With acquisition fixed, the reconstruction-trained lattice still performs below chance (AUROC 0.270/0.380). The successful raw-observation result uses recorded source states, observed background, and a different estimator. It therefore does not demonstrate recovery by the original jointly trained latent-state model.

  2. Rank one in the original clinical model remains insufficiently justified. The new analysis mainly supports the differential statistic, whose guarantee requires a stronger common-covariance assumption, while the original natural-parameter statistic benefits from additional directions. A rank comparison within the original jointly trained cross-database model would more directly address this concern.

Overall, I appreciate the improvements, but these two concerns remain insufficiently resolved.

Thank you. We added both requested tests: recovery from raw views with the corrected latent-state implementation, and a rank ablation within the original joint clinical model.

1. Recovery from raw observations. The earlier 0.270/0.380 came from a synthetic training error: reconstruction-trained coordinates were used without DISCERN's intended state-likelihood objective. Reconstruction alone does not ensure compatibility with the Gaussian state family. The corrected run uses the intended coordinate learning with the same Gaussian state model and natural-parameter correction (Section 4).

The experiment starts from three raw views, holds acquisition fixed, and supplies neither generator states nor background coordinates nor target data to model fitting. Under reversed enrollment:

SeedAdditive: DISCERNAdditive: RandomInteractions: DISCERNInteractions: Random
420.8260.0520.8250.572
34070.8800.0370.9310.408
20260.9440.0050.8250.482
70.8140.1420.8270.175
12340.8540.0130.8150.129
Mean ± SD0.864 ± 0.0520.050 ± 0.0550.845 ± 0.0490.353 ± 0.193

Entries are state AUROC. For each seed, Random averages three directions evaluated using the same learned coordinates and fitted state model. The uncorrected readout averages 0.050/0.344 (additive/interactions).

Recovery also approaches the reference using true generator coordinates (mean state AUROC over the initial five seeds; Appendix C.7):

CoordinatesAdditiveWith interactions
Learned from raw views0.8640.845
True-coordinate reference0.8720.851

The gaps to the true-coordinate reference are 0.008 and 0.006 AUROC, respectively.

DISCERN exceeds every random draw in all five seeds in both regimes (Table 7). Affine R² against the generator coordinates increases from 0.78/0.82 for the reconstruction-trained lattice to 0.977/0.982. Five additional seeds per regime give AUROC 0.853/0.881, versus 0.874/0.889 on true coordinates; the estimated direction exceeds the mean random control in all 20 studies under reversal (Appendix C.7).

Across the four enrollment laws, DISCERN's mean state AUROC ranges from 0.864 to 0.882 and from 0.845 to 0.853 (Table 2). Random conditioning can achieve higher AUROC when enrollment preserves or strengthens the source shortcut; the estimated correction improves discrimination when enrollment is removed or reversed. These results provide direct empirical support for recovery from learned raw-view coordinates and for the estimated selection direction. The earlier reconstruction-trained results remain in C.7 as a coordinate diagnostic; they are distinct from the intended likelihood-based fit.

2. Rank in the original joint clinical model. Table 11 now varies the number of natural-parameter directions used by the original clinical correction. This is the statistic associated with Theorem 1, which permits state-specific covariances shared across cohorts. The experiment does not use the differential statistic or require Theorem 2's common covariance across states. The rank counts conditioning directions, not latent states.

RankeICU → MIMIC-IVMIMIC-IV → eICUWithin eICUWithin MIMIC-IV
10.821 ± 0.0140.813 ± 0.0130.828 ± 0.0140.818 ± 0.011
20.825 ± 0.0130.818 ± 0.0150.834 ± 0.0130.816 ± 0.011
30.822 ± 0.0150.816 ± 0.0110.838 ± 0.0140.808 ± 0.012
50.809 ± 0.0210.814 ± 0.0140.842 ± 0.0120.800 ± 0.014
100.794 ± 0.0220.786 ± 0.0190.835 ± 0.0160.768 ± 0.018

Entries are mortality AUROC, mean ± SD. Rank one already delivers the main cross-database gains: it improves over matched ERM by 0.030/0.032 and over matched random conditioning by 0.0282/0.0271 (Table 3; D.6). Rank two gives the highest tested mean in both directions, with additional gains of 0.004 and 0.005 over rank one. Increasing the rank to ten reduces AUROC by 0.027 in both directions relative to rank one. Within eICU, rank five gives the highest mean; within MIMIC-IV, rank one does. The eICU experiment transfers from 153 source hospitals to 52 unseen hospitals, whereas MIMIC-IV uses ICU-unit and admission-year groups within a single hospital. The preference for a higher rank in eICU is consistent with the additional variation introduced by transfer across hospitals (Appendix D.3).

These results support the original rank-one setting: rank one already provides the main cross-database benefit in these experiments, while rank two offers a modest further gain. Retaining more directions does not consistently improve prediction. Section 5.3 and Appendix D.3 report this comparison.

We hope these results resolve the remaining concerns. Thanks again for helping improve this work!

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response to all reviewers

We thank the reviewers for the comments to improve this work. SS is a latent composite clinical state representing the joint configuration of disease-related processes underlying physiology and clinical manifestations. It is not defined as a pre-existing diagnosis class with a corresponding ground-truth annotation. Clinical observations and recorded outcomes YY provide partial information from which SS is inferred; source outcome supervision is part of joint learning. “Without state labels” describes this latent-state formulation. DISCERN identifies conditional evidence about SS under cohort selection. Changes are highlighted in blue.

1. Clinical random-direction control (Dzvc; Table 2). The estimated direction improves over the random-direction control in both transfer directions:

MetricRandom E→MDISCERN E→MRandom M→EDISCERN M→E
AUROC ↑0.7930.8180.7860.812
AUPRC ↑0.4710.5020.4060.431
NLL ↓0.3650.3160.3620.328

The AUROC differences are 0.025 and 0.026; the gains over matched rich ERM remain 0.036 and 0.035. Each variant trains separately from the same five-epoch supervised warm-up, with source-only checkpoint selection. Random directions stay fixed; DISCERN updates its estimated direction each epoch (Appendix D.6). These matched training controls support the estimated direction for clinical prediction. The controlled studies below examine its relation to enrollment directly.

2. Testing additional conditions on real patients (all reviewers; §5.4, Tables 3 and 11 to 14). We impose enrollment on age or sex and a recorded state: hospital mortality in eICU/MIMIC-IV, or CSF amyloid positivity in ADNI. Targets include held-out hospitals, sites and US regions. The table reports AUROC under reversed enrollment, without target data; bold indicates the best non-oracle value shown.

MethodeICU ageeICU sexeICU regionMIMIC-IV ageADNI amyloid
Oracle, target labels0.8790.9380.8800.8940.873
ERM0.5880.5480.5930.6700.709
IPW0.7260.7350.7360.7490.716
Conditional label shift0.7800.7750.7910.7980.706
Random direction0.5760.5610.5860.6570.670
DISCERN0.7720.7670.7790.7900.766

DISCERN exceeds the mean of three fixed random directions in all 80 replicates and ERM in 79. Conditional label shift performs similarly or better when conditioning on the whole background removes little useful evidence; DISCERN improves on it when background variables also carry evidence or the background block is unspecified (Table 14). With an unlabeled-target gate, DISCERN is within 0.030 AUROC of the oracle averaged over the four target laws. The cross-database controlled study also favors DISCERN over the mean of three random directions in all 20 replicates (Table 9), while its MIMIC-IV→eICU target gate does not improve on ERM.

3. Direction and rank (aDNo Q3; Dzvc Q3; xCxA Q3). Under a common covariance across states and cohorts, new Theorem 2 identifies the state-differential shift subspace. Conditioning on this subspace preserves pairwise evidence scores up to cohort-dependent constants; calibrated posteriors still require prior/gate adjustment. In controlled eICU, its first direction loads 0.980 to 0.990 on the enrolled factor, and additional directions bring little change. The rank sweep supports the differential statistic by measuring retained evidence as well as shift energy (Appendix G.3).

4. Raw observations and clinical state information (aDNo; xCxA). With fixed acquisition, the lattice fitted without state annotations gives state AUROC 0.270 / 0.380. Using recorded source states and observed background, the raw-observation estimator reaches 0.848 / 0.833 versus 0.186 / 0.449 for random directions (Appendix C.7). These comparisons identify which representation and state information supports the correction. The clinical components exhibit mortality and APACHE severity associations in eICU→MIMIC-IV, supporting their composite-state interpretation (Appendix D.6).

Practical value. Mortality and amyloid status define explicit operational instances of selection correction in the controlled experiments. They are not ground-truth annotations of the original latent composite SS. Local-label curves further show that fitting a low-dimensional target gate is effective with scarce labels (Appendix G.6). The original clinical targets were inspected during development; the new studies extend evaluation to held-out regions and pre-specified enrollment designs, with their development history and individual outcomes documented in Appendix G.

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

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