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Under review as a conference paper at ICLR 2027

SUBTRACE: JOINT AMORTIZED INFERENCE OF DISEASE PROGRESSION SUBTYPES AND TIMELINES FROM CROSS-SECTIONAL DATA

Abstract

Event-based models infer disease progression from cross-sectional biomarkers, but subtype extensions such as SuStaIn and Bayesian EBM subtyping (bebms) are computationally expensive and return only ordinal event sequences. We propose Subtrace, a simulation-trained Transformer for amortized subtype-aware disease progression inference. Given a cohort, Subtrace predicts subtype-specific continuous biomarker timelines, patient subtype assignments, and patient stages in a single forward pass. It does so by learning per-patient, per-biomarker abnormality evidence and fitting subtype timelines to that evidence at the predicted disease stage. Across nine synthetic experiments, Subtrace improves ordering and staging over bebms and SuStaIn. Most importantly, Subtrace scales favorably with dimensionality: with more biomarkers, ordering improves and normalized stage error decreases. Applied to ADNI and NACC, independently trained models recover similar Alzheimer's disease subtype patterns consistent with prior research. These results support simulation-trained amortized inference as a practical alternative to per-dataset MCMC for subtype-aware disease progression modeling. Code is available at https://gitlab.com/4peerreview/iclr2027_subtrace.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
disease progression modeling, event-based models, subtyping and staging, amortized inference, Alzheimer's disease, Transformer, cross-sectional data, synthetic data generation

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_rb6LOpenReview ↗
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Paper summary

The paper created a transformer&MLP based model for disease progression, that performs staging and subtyping. As opposed to SuStaIn, it uses deep-learning/transformers, continuous stages and several additional encoding steps. Validation is on simulated data with known ground truth as well as ADNI/NACC on Alzheimer's disease progression, a well known problem in medicine.

Critical strengths

Great use of transformer/deep-learning methodology for such a complicated problem involving rankings and hierarchical modeling.

Critical weaknesses

The model seems to be able to recover orderings better than SuStaIn esp with very large biomarker sets but the paper only goes up to 100. What would make the paper stronger would be to demonstrate it on real data with very large numbers of biomarkers where subtypes/heterogeneity is present. Some example datasets:

  • TADPOLE: spreadsheet of ~2000 biomarkers
  • UK BioBank
  • applying it to brain images where each voxel can become abnormal (e.g. amyloid/tau/FDG PET images from ADNI, can reach up to ~millions of voxels, each voxel here is considered a "biomarker").

In addition, which part of the model deals with strong correlation in the biomarkers? making the i.i.d assumption with correlated biomarkers can lead to spurious results. Did the simulations simulate correlated biomarkers? How and where?

Questions for authors

Intro: amyloid → MMSE → entorhinal volume → hippocampal volume — should change ordering to reflect a more Ad consensus from jack et al: Amyloid -> MRI measures (entorhinal/hippocampus) -> cognitive tests (MMSE, etc ..). I understand that some subtypes will not follow this, so the example should reflect the current understanding of the field.

Fig 1 is not intuitive at all. Please improve it. Add diagrams/plots, graphivs, ... make it more intuitive. An LLM generated diagram like that offers little intuition for people actually trying to understand it.

R^cohort_j,b ranks patient j within biomarker b. This does not make sense. By cohort you mean sub-type? Should it not be labeled R_b,k so biomarker b within cohort subtype k? Please fix in the paper and clarify.

Section 3.4 suggests that multiple parallel branches are used (likely just 2). It would be so much useful to see the entire graphical model of the architecture (add in appendix). A figure with the full algorithm pseudocode in appendix should be further added and with the parallel branches. And any key comments to help understand it.

In Eq 10, define zeta explicitly as a map that takes a subtype k and predicts a slot m.

What is the formula for the ordering cost? It's not included.

How can eq 10 be optimized on real ADNI data where we don’t know true sub-types? Are these inferred subtypes? If yes, this raises some concerns about identifiability and local minimas. How well does sub-type inference work in practice?

Some explanation is also needed to understand why the model needs all those levels of hierarchy. [xj,b, Rwithin j,b , Rcohort j,b , dj ] -> u -> h -> t -> s -> r … what happens if you were to simplify or merge some of those steps? What is being lost?

5 comments
AuthorsOpenReview ↗

Response to reviewer rb6L

Thank you for the feedback. Your question about correlated biomarkers led to the most important change in our revision.

Correlated biomarkers

In the submitted version, the simulator drew each biomarker independently once a participant's stage was fixed. Real biomarkers are not like that.

We measured the correlation that remains in ADNI after stage is accounted for, and regenerated the 12-biomarker data so that each participant's biomarkers are drawn jointly with this correlation. The simulated residual correlation is 0.144 against 0.138 in ADNI, and 65 of the 66 biomarker pairs are within 0.10 of their ADNI value.

We then retrained SUBTRACE and refit every baseline (n=450n = 450 test datasets):

τ\tau distance ↓\downarrowARI ↑\uparrowstage MAE ↓\downarrow
SUBTRACE0.163 →\to 0.1600.291 →\to 0.3630.943 →\to 0.905
BEBMS0.214 →\to 0.3160.270 →\to 0.1211.235 →\to 2.072
SuStaIn (GMM)0.299 →\to 0.3140.219 →\to 0.1761.827 →\to 2.044

SUBTRACE improves on every metric while every baseline degrades.

As for which part of the model deals with correlation: no part of SUBTRACE assumes independence. The evidence Transformer attends across all of a patient's biomarkers, and the model is trained on correlated data, so it learns how much co-occurring abnormality tells it. BEBMS and SuStaIn multiply per-biomarker likelihoods, so correlated biomarkers are counted as independent pieces of evidence.

We applied this only at 12 biomarkers. ADNI has these same 12 biomarkers, so the correlation is measured rather than assumed. No real cohort exists from which to measure a 100-biomarker correlation.

Larger biomarker sets on real data

  1. We trained and tested SUBTRACE on synthetic data with 2,000 biomarkers (Exp. 1, 50 test datasets): τ\tau distance 0.158, ARI 0.788, stage MAE 57 out of 2,000 stages (Appendix U).

  2. Applying SUBTRACE to TADPOLE is planned. We will post the results if we finish before the rebuttal deadline.

  3. A real cohort with thousands of biomarkers still has no ground-truth ordering, so such an analysis would be qualitative, as in Section 5.

Introduction example

It now follows Jack et al.: amyloid →\to entorhinal volume →\to hippocampal volume →\to MMSE.

Figure 1

We agree and have redrawn it around the central idea: the model answers "is biomarker bb abnormal for patient jj?" in two ways, from the data and from its own estimates of subtype timelines and stages, and assigns each patient the subtype for which the two answers agree.

RcohortR^\text{cohort}

"Cohort" here means the whole input dataset, not a subtype. Rj,bcohortR^\text{cohort}_{j,b} is patient jj's rank among all patients on biomarker bb. It cannot be computed within a subtype, because subtypes are not known yet at this step. We have clarified this in Section 3.2.

Full architecture and pseudocode

We added Appendix B with the complete architecture: the three parallel branches (router, ordering, and evidence), where they meet, and where each training loss attaches. Algorithm 1 gives the full forward pass as pseudocode.

ζ\zeta and the ordering cost

ζ\zeta is now defined as a one-to-one map that assigns each true subtype kk to a predicted slot m=ζ(k)m = \zeta(k). The ordering cost is now given as Eq. 10, so the matching equation is now Eq. 11.

Eq. 10 (now Eq. 11) on real data

Eq. 11 is used only during training, on simulated cohorts whose true subtypes are known. On ADNI nothing is optimized: the trained model is applied in one forward pass, so there are no per-cohort local minima. On held-out synthetic data, subtype accuracy is in Table 2: ARI 0.363 against 0.176 for the best baseline at 12 biomarkers, and 0.544 against 0.581 for SuStaIn (GMM) at 100. With five subtypes it reaches 0.415 against 0.236 (Appendix Q).

Why so many levels

We removed or simplified each step in turn (12 biomarkers, Exp. 1, n=50n = 50):

Variantτ\tau distance ↓\downarrowARI ↑\uparrowstage MAE ↓\downarrow
Full model0.1360.4990.845
No rank features (RwithinR^\text{within}, RcohortR^\text{cohort})0.1310.4900.906
Per-biomarker MLP instead of attention in t→st \to s0.1340.4890.858
One timeline pass instead of two0.1460.4750.746
No profile fit0.1340.4000.720
No seed-router loss0.1840.4180.857

The seed-router loss and the second pass help ordering, the profile fit helps subtyping, and rank features help staging. Attention in t→st \to s makes no measurable difference at 12 biomarkers, but at 100 it lowers stage MAE from 4.46 to 3.87 (Appendix R). u→hu \to h is only a learned embedding of the four input features. Removing h→th \to t (no subtype pooling) gives a single ordering for everyone, as in TEMPO; Appendix H shows what that costs. s→rs \to r is only a sigmoid.

Please see Figure 1, Section 3, Section 4, Tables 2 and 3, and Appendices B, F and R in the revised PDF.

Thank you for the clarifications and the paper improvements. I am happy to increase the score if I see results on a large dataset of real biomarkers, such as the TADPOLE runs that are in progress. To me that is the critical missing piece that would convince someone to actually use it.

AuthorsOpenReview ↗

SUBTRACE results on TADPOLE

Thank you for the suggestion. We trained SUBTRACE on TADPOLE (Marinescu et al., 2018), an ADNI-derived dataset, with 239 real biomarkers. Details are in the new Appendix N of the updated PDF.

Data source

TADPOLE's 1,907 columns come from imaging blocks measured in different subsets of participants. Of 1,631 baseline participants, FDG PET covers 646, amyloid PET 791, DTI 190 and tau PET none, so adding any of them would at least halve the cohort. We use all cross-sectional FreeSurfer measures plus MMSE, ADAS13 and RAVLT: 239 biomarkers and 1,595 participants with complete data.

Training

Just like what we did for the 12 ADNI biomarkers, in TADPOLE experiment, θ\theta and ϕ\phi come from the EBM Gaussian mixture fit (Young et al., 2014), and the simulated data reproduce the measured correlation between the 239 biomarkers (mean 0.1810.181 simulated vs. 0.1830.183 measured). We trained one Exp. 9 model (K=3K = 3) on 500 simulated datasets of 1,595 participants each, in about 2 hours on one GPU. We did not run the baselines, which already take 111–368 minutes per dataset at 100 biomarkers (Table 1).

On 50 held-out synthetic datasets:

τ\tau distance ↓\downarrowARI ↑\uparrowStage MAE$/B$ ↓\downarrow
100 bio, Exp. 90.1200.0850.036
TADPOLE, 239 bio, Exp. 90.2870.4610.041

Ordering error is higher because 62% of TADPOLE biomarkers barely separate CN from patients (separation below 0.50.5, against 8% at 12 and 9% at 100 biomarkers). On the clearly separated biomarkers, τ\tau distance is 0.1900.190.

Real TADPOLE results

1. Stage tracks diagnosis

Only CN/non-CN is input, so the order of EMCI, LMCI and AD is not imposed. Predicted stage (0–239), mean ±\pm SD:

SubtypeEMCILMCIAD
1101.0±43.2101.0 \pm 43.2148.1±50.3148.1 \pm 50.3178.6±40.5178.6 \pm 40.5
284.1±34.384.1 \pm 34.3119.6±43.2119.6 \pm 43.2158.0±47.6158.0 \pm 47.6
3113.5±45.8113.5 \pm 45.8155.1±42.2155.1 \pm 42.2176.4±35.5176.4 \pm 35.5

All 411 CN receive a predicted stage of 0. Stage rises monotonically within every subtype, tracking clinical severity.

2. Stage predicts conversion to AD

We repeat the ADNI survival analysis: baseline EMCI/LMCI participants, conversions from TADPOLE follow-up visits and a Cox model with stage rescaled to the ADNI 0–12 axis. Hazard ratios:

StageAgeSexEducationAPOE4
1.31∗∗∗1.31^{***} (95% CI 1.25–1.38)0.990.831.001.76∗∗∗1.76^{***}

Each 1/12 of the disease course further along at baseline raises the rate of AD diagnosis by 31%, indicating stages SUBTRACE infers carry prognostic information. Notably, subtype also predicts conversion beyond stage (likelihood-ratio p=0.022p = 0.022): at the same stage, patients in different subtypes convert at different rates, so the subtypes are clinically meaningful. On ADNI's 12 biomarkers, no method's subtypes did.

3. The subtypes match Murray et al. (2011)

Murray et al. define three subtypes at autopsy by the ratio of hippocampal to cortical tangle counts:

  • limbic-predominant (hippocampus most affected; oldest, slowest decline)
  • hippocampal-sparing (cortex most affected; youngest, fastest decline)
  • typical (in between).

Each SUBTRACE subtype matches one of them on three lines of evidence: its ordering, its patients' measurements, and variables SUBTRACE never sees. The table gives the last two; volumes are mean zz-scores vs. CN, compared within the same diagnosis.

Subtype 1Subtype 2Subtype 3pp
Hippocampal volume, LMCI−1.44-1.44−0.61-0.61−1.36-1.362×10−162 \times 10^{-16}
Hippocampal volume, AD−1.90-1.90−1.26-1.26−1.70-1.701×10−51 \times 10^{-5}
Parietal volume, LMCI−0.32-0.32−0.44-0.44−0.66-0.665×10−45 \times 10^{-4}
Parietal volume, AD−0.43-0.43−0.82-0.82−0.82-0.828×10−48 \times 10^{-4}
Age (Murray: 86 / 73 / 79)74.771.874.56×10−96 \times 10^{-9}
Men (Murray: 31% / 63% / 45%)55%60%59%0.340.34
Conversion hazard ratio vs. Subtype 111.451.380.0220.022

Subtype 1 (31%) matches limbic-predominant AD. Its ordering, cognition, hippocampus/amygdala →\to entorhinal →\to lateral temporal →\to parietal →\to frontal, puts hippocampus first, parietal late. Its patients have strong hippocampal and least parietal atrophy, are the oldest, have the fewest men and convert slowest.

Subtype 2 (37%) matches hippocampal-sparing AD. Its ordering, cognition →\to parietal →\to lateral temporal →\to hippocampus/amygdala →\to entorhinal →\to frontal, puts parietal before hippocampus. Its patients have the least hippocampal atrophy at every diagnosis, are the youngest, have the most men and convert fastest.

Subtype 3 (33%) matches typical AD. Its ordering, cognition →\to hippocampus/amygdala →\to parietal →\to lateral temporal →\to entorhinal →\to frontal, puts hippocampus and parietal early. Its patients have hippocampal and parietal atrophy and fall in between on age, men and conversion.

Reviewer_8nG9OpenReview ↗
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Paper summary

This paper proposes SUBTRACE, a Transformer model for amortized subtype-aware disease progression inference. This model learns per-patient and per-biomarker abnormality evidence and predicts subtype timelines at a predicted disease stage. On the ADNI and NACC datasets, the proposed model recovers realistic AD subtype patterns consistent with existing research.

Critical strengths

• The proposed method is novel and jointly infers disease subtypes, stages and continuous biomarker timelines.

• SUBTRACE is significantly faster for inference than SuStaIn and BEBMS.

Critical weaknesses

• Performance heavily depends on the assumptions used to generate synthetic training data.

• Subtype assignment accuracy remains low, particularly with 100 biomarkers.

• There’s no quantitative evaluation against actual longitudinal disease progression.

Questions for authors

• Does SUBTRACE recover genuine disease progression dynamics, or does it primarily learn to invert the assumptions embedded in its synthetic training simulator?

• Why does SUBTRACE achieve strong ordering performance but relatively poor subtype assignment accuracy?

• Have the authors considered validating the predicted disease stages and timelines using longitudinal follow-up data from ADNI or NACC?

• Since subtype similarity differs between the 12- and 100-biomarker settings, how can the authors isolate the effect of increasing biomarker dimensionality?

• How should the predicted continuous event intervals be interpreted clinically without ground-truth temporal information?

1 comment
AuthorsOpenReview ↗

Reply to Reviewer 8nG9

We deeply appreciate reviewer 8nG9's feedback. Your review made our paper stronger and pushed us to do a quantitative analysis that we missed.

Performance depends on the synthetic training assumptions

We agree, and we said so in the Discussion section. Two things we would add here:

  1. This limitation applies to every method in this literature. SuStaIn (Young et al., 2018), DEBM (Venkatraghavan et al., 2019), SA-EBM (Hao et al., 2025), EBM GMM (Young et al., 2014), BEBMS (Hao & Austerweil, 2025) and EBM KDE (Firth et al., 2020) are all evaluated on synthetic data. And it is necessary rather than incidental: real cohorts have no ground-truth ordering or stage, so there is no other way to measure accuracy.

  2. We cover nine different generative assumptions (Section 4) that have theoretical support, and we evaluate on two real cohorts. Models trained on data from one assumption also perform well on data from the others (Appendix T). And our ADNI and NACC experiments (Section 5) show that SUBTRACE results are clinically meaningful and broadly in alignment with empirical literature.

Does SUBTRACE recover real dynamics, or just invert its own simulator?

Our cross-experiment analysis tests this directly: each of the nine models is applied to test data from all nine generators, and every model stays competitive off-diagonal. The nine models also recover broadly similar subtype orderings on ADNI (Figure 2). A model that had only learned its own simulator would not agree with eight others trained on different assumptions. And our real world experiments (Section 5) are the strongest evidence of this.

Low subtype accuracy at 100 biomarkers

The reviewer is right that ARI = 0.108 is poor, and looking into it we found a configuration error on our side rather than a model limitation. We had drawn the Mallows dispersion from U[0.01, 0.50] at both dimensionalities, but the same range does not give the same subtype similarity as the number of biomarkers grows: the per-step displacement does not depend on B, while the normalizer grows as B2B^2. At 100 biomarkers this made the subtypes nearly identical (mean pairwise Kendall distance 0.15, against 0.40 at 12 biomarkers), so subtyping there was close to vacuous and a low ARI was mechanical.

We have corrected the range to U[0.01, 0.10] at 100 biomarkers, regenerated the data, and refit every method. Mean pairwise Kendall distance is now 0.35 against 0.40. ARI rises from 0.108 to 0.544, against 0.581 for SuStaIn (GMM), which has far worse ordering, staging and control-stage calibration. Ordering and staging conclusions are unchanged. Please see the updated Section 4 and Table 2 in the revised PDF.

Why is ordering strong but subtyping weak?

Much of it is the configuration issue above. Beyond that, subtyping is genuinely harder: ordering pools evidence across the whole cohort, whereas subtype must be decided per patient from a single snapshot, and early-stage patients carry almost no subtype information.

Validating stages against longitudinal follow-up

A ground-truth ordering or stage cannot be obtained by observing a cohort over time, and we know of no method that recovers one from longitudinal data: SuStaIn is cross-sectional by construction, and TEBM (Wijeratne & Alexander, 2021) does not output subtypes. If the reviewer knows of such a method we would genuinely appreciate the pointer. We can therefore only validate indirectly, and we now do so in two ways.

The first was already in the submitted version: predicted stage increases monotonically across CN, EMCI, LMCI and AD within every subtype, even though the model only ever sees the binary CN/non-CN label. We have moved it from the appendix to the main text as Table 4.

The second is new, and follows the design of SuStaIn (Young et al., 2018, Table 3). Fitting to baseline cross-sectional data only, the baseline stage predicts later conversion to AD in all nine SUBTRACE models, with a hazard ratio of 1.4 to 1.8 adjusted for age, sex, education and APOE4, against 1.22 for BEBMS and 1.28 to 1.30 for SuStaIn on the same participants and the same stage axis. A hazard ratio above 1 means a participant further along at baseline is more likely to convert, so for the stage a larger value is better. Please see the updated Section 5.1, Table 5 and Appendix G in the revised PDF.

Interpreting the continuous event intervals clinically

Since SUBTRACE is applied to cross-sectional data, the continuous timeline in Figure 3 is relative, not absolute. Positions lie on the inferred disease axis rather than a calendar: a gap of 0.3 means roughly a third of the modelled disease course separates two events. Converting that to years would require longitudinal data, which no existing method achieves, and we make no such claim. Following the reviewer's point, the caption of Figure 3 in the revised PDF now says so explicitly.

Reviewer_RqWKOpenReview ↗
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Paper summary

This paper proposes SUBTRACE, a simulation-trained Transformer for jointly estimating disease progression subtypes, biomarker event timelines, and patient disease stages from cross-sectional observations. The method combines a seed subtype router, biomarker abnormality predictions, subtype-specific event ordering, and an iterative profile-fitting mechanism that couples the three prediction tasks. The papaer shows evaluation of SUBTRACE on nine synthetic experimental settings with 12 and 100 biomarkers, comparing against BEBMS, SuStaIn, and K-Means + TEMPO baselines. The reported results show substantial improvements in ordering accuracy and patient staging, while subtype identification remains weak comparatively. In addition, the method is applied to ADNI and NACC, where the inferred progression patterns are compared with existing knowledge of Alzheimer's disease.

Critical strengths

Jointly inferring disease progression orderings, subtype assignments, and patient stages is an important problem which is computationally challenging. Replacing computationally expensive per-dataset inference with an amortized model is a practically relevant direction. The method also explicitly attempts to couple the three prediction tasks instead of treating them as independent outputs. Also, the reported improvements over BEBMS and SuStaIn in ordering recovery are substantial, especially in the 100-biomarker setting. The experiments cover several simulation assumptions, and including architectural ablations and cross-experiment transfer evaluations is valuable. These results suggest that simulation-based amortized inference warrants further investigation.

Critical weaknesses

A major motivation of the paper is that SUBTRACE recovers continuous biomarker event timelines rather than merely ordinal event sequences. But the interpretation and identifiability of these continuous positions are unclear.

The model is supervised using event positions defined by a synthetic data-generating process. In Experiments 1–7, the underlying ground truth is ordinal, and continuous event-position predictions are evaluated against ranks. In Experiments 8–9, the ground-truth positions follow simulator-defined continuous distributions. It is unclear if the model learned meaningful temporal information or learned to reconstruct the particular latent representation imposed by the simulator.

Besides, I beleieve it is hard to assume that cross-sectional biomarker observasions do not determie the elapsed time between disease events without additional assumptions. The paper does not sufficiently explain what the relative spacing between predicted events represents in a real disease process or how those distances could be validated.



The experimental evidence does not convincingly establish the benefit of subtype-aware joint inference or the proposed architectural complexity.

First, subtype assignment performance remains weak. In the 100-biomarker setting, SUBTRACE achieves an ARI of only 0.108, below SuStaIn (GMM) at 0.169. Although the ordering results are substantially better, the limited ability to recover patient subtype memberships raises concerns about how reliably the predicted subtype-specific trajectories represent distinct disease progression patterns.

Besides, in Appendix E, the true subtype orderings are substantially more similar at 100 biomarkers (mean Kendall's W = 0.893) than at 12 biomarkers (0.512). Consequently, good ordering recovery might be achievable even without accurately distinguishing the underlying subtypes. It is true that this does not invalidate comparisons but it makes it difficult to determine how much of SUBTRACE's strong high-dimensional ordering performance reflects genuine recovery of subtype-specific structure.

Also, I find the choice of learned baselines insufficient to isolate the proposed architectural contribution. K-Means + TEMPO is a decoupled clustering-and-ordering pipeline, but, as I understand ,it is not equivalent to a simpler jointly trained neural model with subtype, ordering, and etc. I think doing this comparison to establish if the proposed evidence-profile fitting and two-pass refinement are necessary.

Questions for authors
  1. What assumptions make the relative distances between predicted biomarker event positions identifiable from cross-sectional data?

  2. Given the high similarity of true subtype orderings in the 100-biomarker setting, how would SUBTRACE compare against a simple baseline that estimates one common ordering and uses it for all K subtypes? Can the authors demonstrate that the method recovers genuinely distinct subtype-specific progressions, rather than a largely shared ordering?

  3. Can the authors compare against a simpler jointly trained multi-output Transformer with the same training data and supervision? Also, can they clarify the provenance of corrected synthetic experiments and the incomplete high-dimensional baseline results, and provide the exact checkpoints and generation configurations used to produce Table 2? These would help determine whether the reported improvements are attributable to the specific proposed method and are independently reproducible.

7 comments
AuthorsOpenReview ↗

Reply to reviewer RqWK

Thank you for the careful review. Several of the numbers it questions have changed in the revision because we found and fixed a configuration error, described below.

Continuous event positions

The event positions are relative, not calendar time. They lie on the inferred disease axis: a gap of 0.3 means roughly a third of the modelled disease course separates two events. We make no claim about years, and the caption of Figure 3 now says so explicitly.

Whether the model learns real spacing or only the simulator's can be tested only where the true spacing is known, which means simulated data. This holds for every method in this area, since real cohorts have no ground-truth ordering. In Experiments 8–9, where the simulated event times are continuous and unevenly spaced, SUBTRACE recovers them with an event-position MAE of 1.87 and 1.68 at 12 biomarkers (random: 3.52) and 15.3 and 16.9 at 100 (random: 31.7) (Appendix P). On ADNI, the spacing should be read as a hypothesis from the model, not a measurement.

Subtype accuracy at 100 biomarkers

The ARI of 0.108 came from a configuration error on our side. We drew the Mallows dispersion from U[0.01,0.50]U[0.01, 0.50] at both dimensionalities, but the same range does not give the same subtype similarity as the number of biomarkers grows: the per-step displacement does not depend on BB, while the normalizer grows as B2B^2. At 100 biomarkers this made the subtypes nearly identical (mean pairwise Kendall distance 0.15, against 0.40 at 12 biomarkers), which is the high Kendall's WW of 0.893 you noted.

We corrected the range to U[0.01,0.10]U[0.01, 0.10] at 100 biomarkers, regenerated the data, and refit every method. Mean pairwise Kendall distance is now 0.35 and mean WW is 0.62. SUBTRACE's ARI rises from 0.108 to 0.544, against 0.581 for SuStaIn (GMM), which has far worse ordering (τ\tau distance 0.396 vs. 0.169) and staging. Ordering and staging conclusions are unchanged (Table 2).

A single shared ordering

We ran this comparison on the 12-biomarker test data (450 datasets). We applied TEMPO, which assumes a single subtype, to the whole dataset and used its one ordering for all three subtypes:

τ\tau distance ↓\downarrow
SUBTRACE0.160
TEMPO, one shared ordering0.255

SUBTRACE is better in every one of the nine experiments, so it recovers a distinct ordering for each subtype rather than a common one. A shared ordering also cannot assign patients to subtypes, whereas SUBTRACE reaches an ARI of 0.363 at 12 biomarkers, twice the best baseline (0.176).

A simpler jointly trained model

Our ablation already contains this comparison. The "no profile fit" variant is a jointly trained multi-output Transformer with the same training data and the same supervision, but reads subtypes directly from a classification head instead of coupling them to ordering and staging:

ARI, 12 bio ↑\uparrowARI, 100 bio ↑\uparrow
Full model0.4990.658
Joint model, no profile fit0.4000.374
One timeline pass instead of two0.4750.594

Removing the profile fit costs subtyping at both sizes, and more at 100 biomarkers. Removing the second pass costs ordering (τ\tau distance 0.136 →\to 0.146 at 12 biomarkers, 0.137 →\to 0.159 at 100). See Table 3 and Appendix R, which also ablates the seed-router loss, the rank features, and attention in the ordering branch.

Reproducibility

All our code, including the data-generation configurations, is at https://gitlab.com/4peerreview/iclr2027_subtrace. Training with it reproduces our models, up to run-to-run variation from training randomness. We will release the trained model checkpoints upon publication.

Please see Section 4, Tables 2 and 3, and Appendices P and R in the revised PDF.

Thank you to the authors for the detailed rebuttal and additional experiments. I appreciate the efforts to address my concerns, particularly the corrected experimental configurationsand additional longitudinal analysis.

However, after reviewing the revised manuscript and the responses to the other reviewers, I still have some concerns.

  1. Continuous timeline interpretation: While the authors clarify that event positions represent relative disease progression, their identifiability and clinical meaning remain unclear. Also raised by Reviewer 8nG9, it is difficult to determine if the model recovers genuine disease progression or primarily learns the assumptions embedded in the synthetic data generators.

  2. Real-world validation: The new longitudinal analysis provides useful evidence for staging, but does not directly validate the inferred subtype-specific trajectories. Especially, the reported subtype assignments does not show significant association with conversion at K=3. This leaves me unconvinced about the clinical relevance of the inferred subtypes.

  3. Experimental assumptions: I also share Reviewer rb6L's concerns regarding biomarker correlations. Although the authors have improved the 12-biomarker simulations, the 100-biomarker experiments still use different assumptions, making it difficult to isolate the effect of dimensionality. The additional scalability experiments are encouraging but remain synthetic.

Overall, I recognize the computational advantages and the improvements made during the rebuttal. Nevertheless, I believe the central concerns about the validity and interpretation of the inferred disease progression remain insufficiently addressed.

I therefore maintain my rating of 2 (weak rejection).

AuthorsOpenReview ↗

Response to the follow up

Thank you for the follow-up.

Continuous timeline

From cross-sectional data alone, the absolute spacing of events is not identifiable for any method. Spacing is only defined relative to how patients are distributed along the axis, which is why we interpret it as relative progression and test it only on simulated data.

To test whether SUBTRACE recovers spacing from the data rather than from its training assumptions, we use the cross-experiment results (Appendix T). Models trained on Exps 1–7 only ever see evenly ranked event times. Applied to Exps 8–9, where the true spacing is continuous and uneven, they still recover it: event-position MAE 2.1–3.0 against 3.52 for random at 12 biomarkers, and 17.9–25.2 against 31.7 at 100. Matching the generator helps (1.68–1.87 at 12), but recovery does not depend on it.

Subtypes and conversion

Predicting conversion is not what SUBTRACE, SuStaIn, BEBMS, or any event-based model is designed to do. And we never claim SUBTRACE is able to do it.

These models estimate the order in which biomarkers become abnormal and how far each patient has progressed. A subtype describes a different order, not a faster or slower course, so there is no reason it should predict conversion. We include the survival analysis only as an external check on stage, following SuStaIn (Young et al., 2018). Consistent with this, no method's subtype predicts conversion at K=3K=3, including SuStaIn.

100 biomarkers

We agree, and we do not claim an effect of dimensionality. The paper states that the two settings differ and does not compare across them (Section 4).

No real cohort exists from which to measure a 100-biomarker correlation, so we treat 100 and 2,000 biomarkers as stress tests of scalability.

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