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Under review as a conference paper at ICLR 2027

CALIPER: Multimodal Disease Staging and Velocity Estimation from Clinical Snapshots

Abstract

Multimodal disease progression is often observed through sparse clinical snapshots rather than dense trajectories. Alzheimer's disease provides a canonical case, with amyloid (A), tau (T), and neurodegeneration (N) biomarkers measured irregularly and incompletely. Individuals at the same disease time may exhibit different modality-specific stages and velocities: a modality that is further advanced need not be changing faster. Comparing these changes also requires accounting for state-dependent response sensitivity and residual variation. We introduce Caliper, a generative framework for modality-specific staging and Fisher-calibrated population-velocity readouts from incomplete multimodal snapshots. An anchored observation model learns a shared disease clock, modality-specific stage offsets, and heteroscedastic emissions. A reverse Schr\"odinger bridge constructs endpoint-conditioned population currents and regime responsibilities from pseudo-ordered snapshots. Differentiating modality-stage maps along these currents yields model-implied local velocities, calibrated using the mean-response component of Fisher information. In model-matched simulations, Caliper recovers modality-stage ordering and relative calibrated speeds; matched ablations show higher mean relative-speed correlation and leading-modality accuracy with local Fisher scaling than with fixed or omitted scales. In ADNI and SCAN-linked NACC development data, the clock captures clinical severity, and imaging-and-age regime assignments achieve higher mean anchor-recovery accuracy than a same-anchor logistic reference. Matched ADNI follow-up comparisons show modality-pair-dependent ordering gains over uncalibrated stage speed. Caliper separates disease position from locally standardized change, enabling comparison of heterogeneous multimodal profiles at the same disease time.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Disease progression modeling, multimodal learning, clinical snapshots, Schrödinger bridges, Fisher information, heteroscedastic modeling, Alzheimer's disease

Reviews

Among:
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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 4 reviews, above 85% of the others.
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3
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Paper summary

Based on cross-sectional datasets about three modalities, i.e., Amyloid, Tau, and Neurodegeneration, CALIPER identifies subtypes and also the progression of these modality along a timeline for Alzheimer's disease.

Critical strengths

Estimating progression timeline from cross-sectional neurodegenerative disease datasets is challenging, but very useful for researchers and clinicians. Most of the time, datasets available are only sparsely longitudinal, and that's why many existing approaches such as EBMs focused on cross-sectional datasets. But most methods, using cross-sectional data, cannot output specific timelines for disease progression. This paper provides one of the few attempts (besides TEMPO) to achieve this goal.

References:

Hao, H., & Austerweil, J. L. (2026). TEMPO: Transformers for Temporal Disease Progression from Cross-Sectional Data.

Critical weaknesses

I identified two critical weaknesses of the paper.

Unclear and undefined terms

  • In the first few pages, the authors used many terms that are extremely hard to interpret. Just to name a few: "modality stages", "stage velocities", "response sensitivity", "residual variation", "local comparison", "progression direction", "statistical scale", "disease position", "calibrated local change", "latent state", "common clock", "modality-specific stage offsets", "reference regimes", "frozen representation", "endpoint-conditioned population currents", "regime responsibilities", "local stage velocities", "heteroscedastic emission model", "residual scales", "mean-response", "calibrated change", "fitted population field", "relative calibrated speeds", "development split", "shared disease clock", "disease coordinates", "local-encounter-level readout", etc.

  • LN 306-307: I also do not understand the experimental tasks: "modality-stage ordering", "relative calibrated-speed recovery", "endpoint assignment", "leading-modality accuracy". Note that I double checked, those terms have never been explained in sections before they appear and I don't think they are ever explicitly defined. Same is for terms of "modality-stage recovery", "relative information-speed recovery", and "endpoint-regime identification" in LN 324-325.

  • I also do not think "Local heteroscedasticity", and "Constant noise" are defined in the main text.

For the audiences, this makes it almost impossible to understand this paper.

Making sure the comparison is fair

The authors based their benchmarking results on synthetic datasets. However, the authors did not discuss whether the comparison with other methods (in Table 1) is fair. Many of these methods might have drastically different model assumptions than how the synthetic data is generated. The authors also failed to explain and disclose whether CALIPER "knows" any assumptions underlying data generation that are not available to the compared methods.

Questions for authors
  • What's your definition of modality? How's that different from "biomarkers"?

  • You said that previous methods didn't answer the question of "which modality is leading now?". But could you explain why this is an important question to answer in the first place? Why do we have to know this? Is it more important than knowing which biomarker will be impacted for this patient soon so we can prepare for the treatment or prevent it from being impacted?

  • Could you discuss why your synthetic data is as close to the real-world data as possible? For example, missing values.

  • Could you discuss whether it's fair to test the benchmarked methods on your datasets? Do these methods have the same underlying assumptions as your synthetic data? For example, EBM (Fonteijn et al., 2012) assumes that 1) biomarkers are either in healthy or pathological state, depending on how many biomarkers in this patient have become affected and the known biomarker-wise disease progression, and 2) participant disease stages are only nominal depending on how many biomarkers in this patient have become affected by the disease. Do these assumptions hold in your synthetic dataset generation method?

  • Relatedly, can you list assumptions that CALIPER has about the underlying synthetic data that are not known by other benchmarking methods?

References

Fonteijn, H. M., Modat, M., Clarkson, M. J., Barnes, J., Lehmann, M., Hobbs, N. Z., ... & Alexander, D. C. (2012). An event-based model for disease progression and its application in familial Alzheimer's disease and Huntington's disease. NeuroImage, 60(3), 1880-1889.

5 comments

We thank the reviewer for the careful and rigorous reading and for helping us identify the problems in our presentation. To answer the concerns in short: a modality is one imaging stream (amyloid PET, tau PET, or MRI-derived cortical volume), and a biomarker is one measured indicator within it; "which modality is leading now" asks which observed modality is changing the most relative to its own noise at the person's current position, not which biomarker will be impacted next; scan combinations in the simulation approximate the clinical frequencies, all methods received the same data and anchors, and we state where the generator favors CALIPER; finally, we revised the Introduction and Sections 4.1–4.2 to define the key terms, and we define every listed term under Weakness 1 (Part 3). The details follow, with the five questions first and then the two weaknesses.

Q1. Modality versus biomarker. We use modality for one stream of regional imaging measurements: amyloid PET, tau PET, or MRI-derived cortical volume as a proxy for neurodegeneration (the A, T, and N of the A/T/N framework; 31 regions each in the shared view). A biomarker is one measured indicator; regional tau uptake is one biomarker within the tau modality. An event-based model treats each biomarker as a separate event, whereas CALIPER assigns each modality one stage and compares modalities, not individual regional biomarkers.

Q2. What "which modality is leading now?" asks. The leading modality is the observed modality whose measurements move the most along the population current, the direction in which snapshots move as the disease advances, in units of that modality's own noise at its current stage (Eq. 10 and the paragraph after it in Section 3.5). It is a population-level quantity read at the person's position, not the person's per-year rate (Table 3 caption). Each term is defined under Weakness 1 (Part 3).

Consider a person midway along the disease clock whose amyloid is far advanced (near its plateau), tau moderately advanced, and cortical volume still close to normal. Along the population current, a small step forward implies the following (illustrative numbers in the spirit of the simulation):

ModalityChange in raw unitsLocal noise SDChange in SD units
Amyloid PET+0.005 SUVR0.020 SUVR0.25
Tau PET+0.040 SUVR0.050 SUVR0.80
Cortical volume−150 mm³600 mm³0.25

Four questions have four different answers. Which modality is most advanced? Amyloid; this is stage, or burden, which staging methods report. Which has the largest raw change? Cortical volume, but the units are not comparable, and dividing by one pooled SD per modality gives an answer that depends on the pooled SD chosen, because noise itself varies with stage. Which will become abnormal next? Neurodegeneration; this is the ordering question of event-based models, a population sequence shared by everyone at this stage. Which is leading now? Tau: its movement is the largest relative to its own noise at this stage. Amyloid is most advanced but has stopped moving; volume moves a lot in raw units but within its noise.

Why this question matters clinically. Our framing follows the dynamic-biomarker model cited in Section 1 (Jack et al., 2010; 2013): amyloid, tau, and neurodegeneration markers become abnormal in sequence along sigmoid-shaped trajectories, so each marker's rate of change depends on where a person is in the course, and amyloid markers approach a plateau while tau and neurodegeneration markers are still changing. Two consequences follow. First, at a given visit the most abnormal marker is often no longer the one that is changing, so "which process is moving now" is the per-person form of the question that model answers for the population. Second, a marker carries prognostic information while it is still changing: in 1,431 participants from eight cohorts, baseline tau PET predicted subsequent cognitive decline better than amyloid PET or MRI (Ossenkoppele et al., 2021). A leading-modality readout generalizes this instead of assuming that tau is always the informative marker: it reports which observed modality is informative at this person's position, which is also the modality worth re-measuring at the next visit.

Reference not in the submission (Jack et al., 2010; 2013 are cited as in the paper)

  • Ossenkoppele R, Smith R, Mattsson-Carlgren N, et al. Accuracy of tau positron emission tomography as a prognostic marker in preclinical and prodromal Alzheimer disease. JAMA Neurol. 2021;78(8):961–971. doi:10.1001/jamaneurol.2021.1858

Q2 (continued). Why this question matters clinically.

Treatment decisions already turn on which process is active. In TRAILBLAZER-ALZ 2, donanemab slowed decline in the low/medium-tau population; in a post hoc analysis of the high-tau group, the difference on the primary outcome was smaller and not statistically significant; and participants who met pre-specified amyloid-clearance criteria were switched to placebo (Sims et al., 2023). Deciding whether a person is still in the window where amyloid-directed treatment helps, and what to monitor once amyloid has been cleared, requires knowing which process is moving now, not only which marker will become abnormal next. Finally, the AT(N) framework (Jack Jr et al., 2018) characterizes individuals by their biomarker profile rather than by a single stage, and individuals at the same clinical stage can carry different profiles; two people at the same point on the disease clock can therefore differ in which process is advancing. A population sequence cannot express this; an encounter-level readout can, and that is the gap CALIPER addresses.

Relation to "which biomarker will be impacted next". The two questions use different information and serve different decisions. "Impacted next" is a population ordering that gives everyone at a given stage the same next event (Fonteijn et al., 2012); "leading now" is read from one person's snapshot, without follow-up, and is what the treatment and monitoring decisions above require. Existing snapshot methods provide the first; CALIPER adds the second.

Q3. Realism and missingness. We sampled the seven A/T/N scan combinations at frequencies that approximate those in the clinical data (Eq. 56). For example, 41.4% had MRI alone and 11.3% had all three. This captures scan availability, while the reasons a clinician orders a scan lie outside the simulation. Masks are drawn independently of stage.

Q4–Q5. Benchmark fairness and shared assumptions. All methods had access to the same snapshots, masks, available ages, and training anchors, the participants whose reference-regime labels are visible. CALIPER received no true stages, speeds, noise scales, or held-out labels. The generator does give CALIPER a structural advantage by sharing its continuous clock, bounded modality-stage offsets, degree-six regional response curves, and independent Gaussian residuals. The speed target uses the Fisher scale CALIPER is designed to estimate. In contrast, the simulated progression paths were written as closed-form curves, not generated by the Schrödinger bridge that CALIPER fits, so that part of CALIPER is not matched to the generator.

EBM infers an ordering of biomarker abnormality events. The two assumptions you list do not hold in our generator: each regional measurement changes continuously with stage rather than switching between a healthy and a pathological state, and stage is continuous rather than a count of affected biomarkers. EBM also does not output modality-specific stages or speeds, so Table 1 evaluates it only on endpoint balanced accuracy, that is, whether the correct reference regime is identified, through a classifier trained on EBM stage and age.

Among the methods listed in Table 1, CALIPER had the highest mean in five of the six comparisons on stage correlation, relative-speed correlation, and leading accuracy across the two noise settings. These metrics and settings are explained under Weakness 1 (Part 3). In the sixth, stage correlation under constant noise, CALIPER reached 0.955 versus 0.960 for MoPoE-VAE. A within-model ablation isolates the contribution of calibration: the fitted model is kept fixed and only the scale used to compare modalities is changed. Under local heteroscedasticity, leading accuracy was 0.775 with the local Fisher scale, 0.737 with a fixed scale, and 0.633 without calibration. On 525 development-split real-data anchors, CALIPER's endpoint balanced accuracy was 0.748 versus 0.677 for same-anchor logistic regression (Appendix H.2).

Weakness 2: fairness of the comparison. Our answers to Q3–Q5 above state what all methods share, where the generator favors CALIPER, and how EBM was evaluated. The paper describes the simulation as assumption-matched (Section 4.2; Appendix D.1) and gives the shared baseline protocol in Appendix D.4. The dashes in Table 1 mark readouts that a method does not provide.

Reference not in the submission (Jack Jr et al., 2018 and Fonteijn et al., 2012 are cited as in the paper)

  • Sims JR, Zimmer JA, Evans CD, et al. Donanemab in early symptomatic Alzheimer disease: the TRAILBLAZER-ALZ 2 randomized clinical trial. JAMA. 2023;330(6):512–527. doi:10.1001/jama.2023.13239

Weakness 1: undefined terms. We agree that the submission left many of these terms undefined and used more than one name for the same quantity. In the revised paper we made the following changes.

  • Introduction. It now defines modality, the disease clock and modality stage. We also replaced several of the terms you listed with plain descriptions. For example, “response sensitivity and residual variation” is now “how strongly the predicted regional means change with stage and how much the measurements vary around those means”; “local stage velocities” is now “each modality’s rate of stage change along the estimated population path”; “heteroscedastic emission model” is now “an observation model with stage- and group-dependent residual variance”; and “a statistical scale” is now “units of residual standard deviation”.
  • Section 4.1. We replaced the list of task names with definitions of the four measures: stage correlation, relative-speed correlation, endpoint balanced accuracy and leading-modality accuracy.
  • Section 4.2. We added definitions of local heteroscedasticity and constant noise, and removed the second list of task names (lines 324–325 of the submission).

The notation is listed in Appendix A. Below we define every term you listed. A term in parentheses is another name that the submission used for the same quantity.

Where a person is.

  • Shared disease clock (common clock, disease position, disease coordinate): one number that places each snapshot on a common timeline of the disease.
  • Modality-specific stage offset: how far one modality runs ahead of or behind the clock. It is bounded.
  • Modality stage: clock plus offset, that is, how far that modality has progressed.
  • Latent state: a learned summary of the available scans, from which the clock and the stages are computed.
  • Frozen representation: the fitted clock, stages and measurement model, which are held fixed in the later steps.

Which way the population moves.

  • Reference regime: a clinically defined endpoint group. Anchors are the participants whose clinical labels define these groups.
  • Endpoint-conditioned population current (fitted population field, progression direction): the average direction in which snapshots move from the early group toward one endpoint.
  • Regime responsibility: how strongly a snapshot belongs to each regime.
  • Stage velocity (local stage velocity): how fast a modality's stage changes along the current.

How modalities are compared.

  • Heteroscedastic emission model: the measurement model. It gives each measurement's average at a stage (mean response), how strongly that average changes with stage (response sensitivity), and its noise (residual scale, residual variation), which may vary with stage.
  • Statistical scale (Fisher scale): sensitivity relative to noise, that is, how well a small change in stage can be told apart from noise. Local means that it is computed at the person's own stage.
  • Calibrated change (calibrated local change, calibrated speed): stage velocity times this scale, so that each modality's change is in units of its own noise.
  • Leading modality: the observed modality with the largest calibrated speed. Relative calibrated speeds are each modality's share of the total.
  • Encounter-level readout (local encounter-level readout, local comparison): this summary for one visit.

Experimental tasks. In the submission, lines 306–307 and 324–325 named the same four tasks in two ways.

  • Stage correlation (modality-stage ordering, modality-stage recovery): are participants ranked correctly by each modality's true stage?
  • Endpoint balanced accuracy (endpoint assignment, endpoint-regime identification): is the correct reference regime identified?
  • Relative-speed correlation (relative calibrated-speed recovery, relative information-speed recovery): are the modalities' shares of calibrated speed recovered?
  • Leading accuracy (leading-modality accuracy): is the leading modality identified?

These tasks use simulated data because only there is the truth known.

Noise settings and data split. Under local heteroscedasticity, each region's noise changes with stage and reference regime. Under constant noise, it is fixed and everything else is identical. All methods are compared under both. The development split is the set of real participants kept out of training and used during method development.

We hope our answers resolve your questions. If anything remains unclear, please let us know; we would be very happy to continue the discussion.

Reviewer_Pk1YOpenReview ↗
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Paper summary

This paper learns a shared disease clock and modality stages from incomplete snapshots. An endpoint-conditioned bridge on the frozen representation supplies population currents, which induce stage velocities calibrated by mean-response Fisher scales. The resulting speeds are per unit of local bridge progress, not individual annual rates. Model-matched simulations achieve relative-speed correlations of 0.769/0.808, with matched output-ruler ablations supporting the calibration. An application involving 6,935 participants reports severity association, endpoint-reference recovery, and matched ADNI follow-up ordering, but reuses a previously inspected development split.

Critical strengths
  1. The estimand is carefully specified. The mean-response Fisher ruler expresses local changes in residual-standard-deviation units and explains why raw stage-speed comparison can depend on modality scale.
  2. The authors conduct relatively suffcient experiments.
  3. Matched ablations separate some component effects.
Critical weaknesses

1.The real-data evaluation reuses data inspected during development and lacks confirmation on an untouched test set. The generalizability of the clinical findings is therefore uncertain. 2.The full method is complex, but its gains over simpler controls are inconsistent. In particular, the added value of local velocity calibration remains unclear in real follow-up data.

Questions for authors
  1. Please clarify which design choices used TUNE results, including support-floor and reporting decisions? Are there existing results on data untouched by these choices?
  2. Please provide additional analysis: For the existing matched follow-ups, please provide participant-level paired difference intervals and effective sample sizes by modality pair for local Fisher, fixed Fisher, and standardized vectors. The current shared-participant cell distribution does not constitute independent replication.
  3. On the same learned representation, what is the paired endpoint-recovery gain over the latent-plus-age classifier in Figure 7? Together with the endpoint-secant/fixed-Fisher results, which observable objective demonstrably requires the full current-and-local-ruler combination?
5 comments

We thank the reviewer for the careful and rigorous reading. To answer the three questions in short: with the two design choices examined on TUNE (age adjustment and SA/NA support floor) unchanged, the submitted model gave similar results on 513 additional ADNI participants never used or inspected during development, and we added the external A4 trial (Section 4.3; new Appendix J); participant-level paired intervals and Kish effective sample sizes are in the tables in Part 2 (new Table 14); finally, the bridge is comparable to a latent-plus-age classifier on endpoint recovery (new Table 11) and additionally provides the population current, which contributes to A–N follow-up ordering (new Table 15).

Q1. How TUNE informed the design. We used the same 525 TUNE anchors to compare four configurations in Figure 7 (Appendix H.2). We varied whether reported group probabilities were adjusted for age and whether the SA and NA bridges used a floor on the terminal clock. The age adjustment uses age distributions estimated from TRAIN anchors to reweight the reported probabilities. The floor changes which intermediate snapshots can contribute to the SA and NA bridges and thus can change their estimated currents. We designated the configuration with both changes as the full model before comparing the four variants.

None of the four configurations receives a participant’s CDR-SB, MMSE, clinical diagnosis (CN, MCI, or dementia), or APOE genotype when predicting their group. Diagnosis and cognitive scores help define the clinical reference labels and are evaluated separately in Table 2.

Are there existing results on data untouched by these choices? In simulation, yes. Table 1 and Figures 4–6 report results on held-out synthetic data. We used separate synthetic training and evaluation samples and scored predictions against known ground truth. No clinical TUNE participant or outcome entered those evaluations. Figure 2 describes APOE ε4 carrier frequencies in groups assigned by a separate random forest, and Figures 3 and 10–13 show selected cross-sectional profiles. These descriptive analyses used neither the clinical support floor nor the age-conditioned reporting rule, although their samples include TUNE participants. The submitted paper evaluated clinical endpoint recovery on TUNE anchors and hidden TRAIN labels, and follow-up ordering on TUNE. It did not report these outcomes on a clinical cohort held out throughout development (Appendix E.6).

Since submission, we have evaluated staging, endpoint recovery and follow-up ordering on 513 additional ADNI participants who were never used or inspected during development, with the submitted model and both choices unchanged (Appendix J of the revised paper). Of these, 119 met the clinical endpoint definitions and 160 had a matched follow-up for at least one modality pair. The clock reached CN–dementia AUC 0.848 [0.793, 0.896] (n = 284) and CN–MCI AUC 0.742 [0.687, 0.795] (n = 368), against 0.849 and 0.624 for MoPoE-VAE (Table 10). Endpoint balanced accuracy (n = 119) was 0.745 [0.669, 0.816] with both choices, 0.626 with the age adjustment alone, 0.467 with the floor alone and 0.409 with neither (Table 11). Follow-up ordering is in the second table under Q2 in Part 2 (Table 14). In the external Anti-Amyloid Treatment in Asymptomatic Alzheimer’s Disease (A4) trial, likewise never used in training or development (1,078 participants from both arms, 389 protocol-defined global CDR progression events), the clock had the highest concordance for progression among all methods (C = 0.617 [0.588, 0.645]; Table 10).

Q2. Participant-level paired intervals and effective sample sizes. Both tables below appear as Table 14 in the revised paper (Appendix J.4). The first table gives paired differences in ADNI follow-up ordering agreement on TUNE in percentage points [95% CI]. Positive values favor local Fisher. For each modality pair, we averaged differences across supported seed × regime cells and resampled participants 1,000 times, using the same draws for all seeds, regimes and readouts. Intervals are conditional on the fitted models and unadjusted for multiple comparisons. The Kish ESS range is across supported cells and applies to all three readouts, which share participant weights.

FeaturesPairNKish ESS rangeLocal − fixed FisherLocal − standardized vector
common31A–N7942.2–64.6−5.64 [−11.60, −0.07]+13.42 [+8.51, +18.89]
common31A–T6939.2–51.4+2.97 [+0.17, +6.15]+3.94 [+2.36, +5.62]
common31T–N2814.7–22.1+1.91 [−4.68, +9.29]−13.69 [−22.50, −5.15]
common31All12214.7–64.6−0.45 [−3.31, +2.33]+2.58 [−0.51, +5.77]
nativeA–N7945.2–64.8−2.27 [−4.86, +0.42]+15.21 [+10.00, +20.69]
nativeA–T6936.3–50.9+2.47 [−0.10, +4.92]+1.74 [+0.09, +3.79]
nativeT–N2815.6–22.7+0.84 [−7.63, +10.02]−6.19 [−14.31, +2.09]
nativeAll12215.6–64.8+0.34 [−2.78, +3.45]+3.75 [+0.51, +7.27]

Held-out ADNI participants. We repeated the comparison on the 160 held-out ADNI participants with matched follow-up (Q1). Differences are in percentage points [95% CI]; Kish ESS is the mean ± SD across supported cells.

FeaturesPairNKish ESSLocal − fixed FisherLocal − standardized vector
common31A–N9761.9 ± 4.2−2.90 [−6.07, +0.60]+9.48 [+4.68, +14.11]
common31A–T8248.1 ± 4.7+4.37 [+2.25, +6.45]+2.92 [+0.29, +5.28]
common31T–N3019.1 ± 2.3−1.50 [−7.92, +5.31]−1.93 [−6.89, +2.77]
common31All16046.7 ± 16.9+0.22 [−1.73, +2.19]+4.32 [+2.05, +6.66]
nativeA–N9754.4 ± 6.2−1.87 [−3.94, +0.01]+13.35 [+8.39, +18.15]
nativeA–T8241.4 ± 5.8+4.89 [+2.22, +7.57]−0.60 [−3.33, +1.96]
nativeT–N3015.9 ± 2.8+2.58 [−3.55, +9.48]−0.80 [−7.42, +6.93]
nativeAll16038.8 ± 16.4+1.82 [−0.39, +4.47]+4.33 [+1.61, +7.34]

Two patterns appear in both samples: local Fisher exceeds the standardized-vector readout for A–N, and the A–T difference favors local over fixed Fisher (held-out intervals exclude zero in both views). For A–N, the difference favors fixed Fisher in both samples (held-out intervals include zero). Pooled over pairs (rows labeled All), local Fisher is higher than standardized vectors in both samples, and the two Fisher scales are not separated.

Q3. Endpoint recovery and the contribution of the current and local ruler. On the 525 TUNE anchors, the bridge and the latent-plus-age classifier achieved nearly identical observed balanced accuracy (0.748 vs. 0.749). Both use the same frozen representation, and the classifier is trained directly on the four endpoint labels. The paired difference, bridge minus classifier, was −0.08 percentage points (95% CI −3.31 to +3.08). On the 196 hidden TRAIN labels, balanced accuracy was 0.745 and 0.767, respectively, with a paired difference of −2.19 points (95% CI −6.51 to +1.98). On the 119 held-out ADNI participants with endpoint labels, it was 0.745 and 0.710, with a paired difference of +3.51 points (95% CI −0.96 to +8.98; Appendix J.3, Table 11).

Endpoint assignment evaluates one output of the bridge. The bridge also estimates a population current at each position along each regime’s path. Figure 5 (Appendix G.2) tests whether that current and the local Fisher ruler help identify the fastest-changing modality and recover how each modality’s speed varies along a curved path. In this controlled experiment, the clock and stage coordinates and the Fisher scale are supplied, and the true instantaneous speeds are known. The full combination achieved 0.952 leading-modality accuracy and 0.936 within-modality speed correlation. Keeping the local ruler and replacing the current with the endpoint secant reduced these values to 0.805 and 0.776. Keeping the current and replacing the local ruler with fixed Fisher reduced them to 0.902 and 0.898. The full combination exceeded each control on both metrics in all five paired seeds.

In the main simulation with learned coordinates, the secant had higher leading-modality accuracy. The clinical follow-ups assess ordering over an observed interval and provide pair-specific evidence (Q2). There, local Fisher calibration raised ordering agreement over uncalibrated stage speed by 10.06 [5.68, 14.56]/10.57 [6.40, 14.77] points (common31/native) on TUNE and by 8.13 [3.39, 13.37]/8.60 [4.75, 13.07] points in the held-out participants (Table 13). With the ruler and regime weights held fixed, the bridge current exceeded the endpoint secant for A–N in the held-out participants by 11.79 [6.55, 16.73]/19.24 [13.13, 24.69] points (Table 15), as on TUNE; A–T and T–N did not favor the bridge. A–N follow-up ordering is therefore an observable objective to which both the calibration and the bridge current contribute.

We hope our answers resolve your questions. If anything remains unclear, please let us know; we would be very happy to continue the discussion.

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Paper summary

This paper proposes a generative framework for multimodal disease staging and population-level velocity estimation from incomplete clinical snapshots. The method learns a shared disease clock and modality-specific stages with heteroscedastic observation models, then constructs endpoint-conditioned population currents using a reverse Schrodinger bridge. A mean-response Fisher scale calibrates the induced stage velocities to identify the leading modality across amyloid, tau, and neurodegeneration measurements. Experiments on synthetic cohorts and ADNI/NACC data evaluate staging, endpoint assignment, and modality-specific progression readouts.

Critical strengths
  • The paper makes a meaningful distinction between disease stage and local modality-specific change. The utilization of a shared disease clock, endpoint-conditioned population currents, and Fisher-based calibration provides a principled framework for interpreting heterogeneous progression signals.

  • The experimental analysis is thorough, with synthetic recovery studies, matched component ablations, and clinical evaluations on ADNI/NACC. In particular, Fisher calibration improves relative-speed correlation from 0.513 to 0.769 under heteroscedastic noise, and the clinical regime assignment outperforms the same-anchor logistic reference.

Critical weaknesses
  • The clinical evidence for local Fisher calibration is less convincing than the simulation results. Although matched ADNI follow-up comparisons show gains over uncalibrated stage speed, the improvements depend on the modality pair, and local and fixed Fisher scales achieve similar mean ordering agreement. Moreover, the clinical evaluations reuse a development split previously inspected during method development, limiting the strength of the generalization claims.

  • The necessity of the reverse Schrodinger bridge is not sufficiently established in the complete pipeline. In the main simulation, a simpler endpoint-secant control achieves higher leading-modality accuracy than CALIPER (0.825/0.815 vs. 0.775/0.786 across the two noise settings). While the controlled path experiments show benefits from intermediate bridge constraints on curved paths, they use supplied coordinates and Fisher scales, leaving the advantage of end-to-end learning unclear.

Questions for authors
  • Why is the reverse Schrodinger bridge preferable to a simpler endpoint-secant velocity estimator in the fully learned setting, given the main-simulation leading-accuracy results?

  • In Table 1, CALIPER achieves substantially lower endpoint balanced accuracy than the same-anchor logistic baseline (0.648 vs. 0.765 under local noise), whereas Sec. 4.3 reports the opposite trend on clinical data. What explains this discrepancy, and how robust is the improvement to the age conditioning and endpoint-support adjustment?

4 comments

We thank the reviewer for the careful and rigorous reading. To answer the three concerns in short: the clinical gain from calibration is smaller than in simulation, but it recurred in 160 held-out ADNI participants never used in development (8.13/8.60 points; Section 4.3; new Appendix J, Table 13); we do not claim that the bridge is uniformly better than an endpoint secant, but it provides a regime assignment and a state-dependent current that a secant does not, and it had higher A–N agreement on held-out follow-up (new Table 15); finally, Table 1 and the clinical task evaluate different classification targets, and the clinical advantage recurred in 119 held-out participants (0.745 vs. 0.538; new Table 11).

W1. Clinical evidence for local Fisher calibration

We agree that the clinical gains are smaller than those in simulation. They are nevertheless present: on matched ADNI follow-up, local Fisher calibration raised ordering agreement over uncalibrated stage speed by 10.06/10.57 points (common31/native), and by 13.42/15.21 points over the standardized-vector readout for A–N (Section 4.3, Appendix H.3). The main constraint is the size of the follow-up sample. Only 79, 69 and 28 participants have matched intervals for A–N, A–T and T–N, each contributing one interval. With these numbers the comparison cannot resolve differences as small as that between local and fixed scales (−0.45/+0.34 points), and the T–N estimates are unstable. In simulation, where the truth is known and each replicate has 1,726 held-out participants, the local scale had higher relative-speed correlation than the fixed scale in all five paired seeds in both noise settings (Appendix G.1).

We have since applied the submitted model, without refitting, to 513 additional ADNI participants never used in development, and the results were similar (Appendix J of the revised paper). Among the 160 with matched follow-up (97/82/30 for A–N/A–T/T–N), calibration raised agreement over uncalibrated stage speed by 8.13/8.60 points (95% CIs 3.39 to 13.37 and 4.75 to 13.07; Table 13), and the A–N gain over standardized vectors recurred (+9.48/+13.35 points; CIs exclude zero). Local exceeded fixed Fisher for A–T (+4.37/+4.89; CIs exclude zero), as in the development split, but not for A–N (−2.90/−1.87) or overall (+0.22/+1.82; CIs include zero; Table 14). On real follow-up, the case for the local over the fixed scale is thus specific to A–T. On staging, the clock matched MoPoE-VAE on CN–dementia (AUC 0.848 vs 0.849) and was higher on CN–MCI (0.742 vs 0.624; Table 10). In the external Anti-Amyloid Treatment in Asymptomatic Alzheimer’s Disease (A4) trial, likewise never used in development (1,078 participants, 389 protocol-defined CDR progression events), the clock had the highest concordance among all methods (0.617; MoPoE-VAE 0.585; Table 10). Results not listed in this reply still come from the development split.

W2 and Q1. Bridge versus endpoint secant

We do not claim that the bridge is uniformly better than an endpoint secant. Our claim is that it fits the structure of this problem and provides quantities that a secant does not. Only the two ends of each path carry labels (PRE and endpoint anchors); the snapshots in between are unlabeled and cross-sectional. The two estimators differ in what they can represent.

(i) Regime assignment. A secant does not assign unlabeled participants to regimes; the secant control in Appendix G.1 reuses the bridge's assignment. The bridge provides regime responsibilities for every unlabeled participant (Eq. 7).

(ii) Change along a path. A secant assigns one slope per regime and modality, so a modality's stage velocity is the same at every clock position. The bridge current is evaluated at the query's clock position (Eq. 8). On curved paths with supplied coordinates, the full bridge reached 95.2% leading accuracy versus 80.5% for the secant, with speed correlations of 0.936 versus 0.776 (Appendix G.2).

(iii) Individual state. Under a secant, all participants in a regime share the same stage velocities. The bridge current is evaluated at each participant's own state, so participants at the same disease time can differ.

(iv) Intermediate snapshots. A secant uses only the labeled PRE and endpoint anchors. The bridge also uses the unlabeled intermediate snapshots through its interior constraints (Eq. 6). In the same curved-path experiment, removing these constraints lowered leading accuracy from 95.2% to 87.8% and speed correlation from 0.936 to 0.890.

In that experiment the full bridge exceeded every listed control on both metrics in each of the five paired seeds (Figure 5). As the reviewer notes, it is a component-level test, because the coordinates and the Fisher scale are supplied.

In the main simulation, leading accuracy weights the three possible leaders by how often each occurs. When recall is instead averaged over the three true leaders with equal weight, the bridge reached 0.644 and the secant 0.592 under local noise, and 0.566 versus 0.482 under constant noise (bridge higher in 3 of 5 and in all 5 seeds, respectively). Always predicting amyloid gives 0.333 on this measure.

On real follow-up, with the ruler and regime weights held fixed, the bridge current exceeded the secant for A–N in the 160 held-out ADNI participants (+11.79 [+6.55, +16.73]/+19.24 [+13.13, +24.69] points, common31/native; Appendix J.4, Table 15), as in the development split. A–T and T–N did not favor the bridge (pooled over pairs: +3.67 [−0.86, +8.35]/+4.12 [−1.08, +9.25]).

Q2. Endpoint accuracy in simulation and in the clinical data

Table 1 evaluates recovery of the simulator's endpoint regime, whereas the clinical task evaluates assignment to operational reference groups whose definitions include age. The clinical advantage depends on the configuration. On the same 525 development anchors, balanced accuracy was 0.748 with both age conditioning and the endpoint-support adjustment, 0.669 with age conditioning alone, 0.399 with the support adjustment alone, and 0.328 with neither, compared with 0.677 for same-anchor logistic regression (Appendix H.2). The 119 held-out ADNI participants with endpoint labels gave similar results (Appendix J.3, Table 11): 0.745 [0.669, 0.816], 0.626, 0.467 and 0.409 in the same order, compared with 0.538 for same-anchor logistic regression (paired difference 20.74 points, 95% CI 10.12 to 31.26). The paired gain of both adjustments over neither was 33.68 points (95% CI 24.75 to 42.91). The difference in classification targets limits how far the ranking can be transferred across the two settings.

We hope our answers resolve your questions. If anything remains unclear, please let us know; we would be very happy to continue the discussion.

I thank the authors for their detailed rebuttal. Most of my concerns have been adequately addressed, particularly through the additional ADNI evaluation. I will maintain my current score of as weak acceptance.

We sincerely thank the reviewer for the valuable comments and for the prompt reply. We are glad that our response addressed most of the reviewer’s concerns.

Reviewer_sKNhOpenReview ↗
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Paper summary

The paper looks at multimodal disease staging from sparse, incomplete clinical snapshots, using Alzheimer's amyloid, tau and neurodegeneration imaging. CALIPER learns a shared disease clock and modality-specific stages with heteroscedastic emissions, fits a reverse Schrödinger bridge to get endpoint-conditioned population currents, and converts the induced stage velocities into comparable speeds with a mean-response Fisher scale. The authors test it on model-matched simulations with known stages and speeds, and on 6,935 participants from NACC and ADNI using clinical discrimination, anchor recovery, and a matched ADNI follow-up ordering analysis.

Critical strengths

The paper picks a real and underappreciated distinction. Where a subject sits on a disease clock is not the same as how fast each modality is changing, and a modality that is further along need not be moving faster. Separating position from locally standardized change is a useful way to frame multimodal progression, and the simulations show that good staging alone does not give good speed recovery. The VAE staging result with stage correlation 0.93 and relative-speed correlation near zero makes that point well.

The ablations on the output ruler are also well done. Holding the bridge fixed and swapping local Fisher, fixed Fisher and no calibration, with paired seeds, is the right way to isolate what the calibration contributes, and the authors report where it does not help.

Critical weaknesses

The central quantity, the calibrated leading modality, has no ground truth in real data, and the evidence for it is mostly from simulations generated under assumptions that match the model. In those simulations CALIPER is only a few points ahead of flow matching and MoPoE-VAE on relative-speed correlation (0.769 versus 0.738 and 0.686) with seed SDs of 0.03 to 0.12, and endpoint secants get higher leading accuracy than the full readout (0.825 versus 0.775). Endpoint balanced accuracy in simulation is 0.648, well below the same-anchor logistic at 0.765. So the claim that the full machinery, bridge plus Fisher scale, is needed is not established, and a much simpler baseline with a Fisher scale already looks competitive.

On the AD data the support is indirect. Staging performance is on par with or below MoPoE-VAE for CN versus dementia on ADNI, the best CN versus MCI result is not consistent across cohorts, and the evaluation split was previously inspected during method development, which weakens it as a test set. The ADNI follow-up ordering comparison is the closest thing to a real test of velocity, but it is descriptive, favors calibration for A to N and the opposite for T to N, and shows local and fixed Fisher as similar. The APOE and regime profile analyses are plausible but are consistency checks and could be produced by many models. The paper has many moving parts and design choices, so I could not tell which ones the real-data results actually depend on.

Questions for authors
  1. Is there any real-data setting with dense longitudinal follow-up where the predicted leading modality or relative speed can be compared to observed within-person change, using a held-out split that was not used for development?

  2. How much of the leading-modality accuracy in simulation survives when the data are generated from a process that does not match the heteroscedastic Gaussian emission model?

  3. Why does the bridge-based readout lose to endpoint secants on leading accuracy in the main simulation, and what does the bridge buy on real data that a straight-line current would not?

7 comments

We thank the reviewer for the careful and rigorous reading. To answer the main concerns in short: no follow-up data entered fitting, and the follow-up results were similar in 160 held-out ADNI participants never used in development (Section 4.3; new Appendix J); under heavy-tailed and skewed noise, mean leading accuracy changed by at most 1.40 points (Section 4.2; new Appendix G.4); the endpoint secant in Table 1 reuses the bridge's regime assignment and is not a bridge-free method; on held-out data the clock is above, or within 0.004 of, the best baseline on every outcome (new Table 10); finally, each step of the pipeline produces one quantity that the final readout requires.

Q1. Longitudinal validation

We thank the reviewer for this question, which points to precisely the problem CALIPER is designed to address: dense multimodal follow-up is rarely available at the scale needed to fit trajectories. In ADNI and NACC, each modality is repeated only a few times per participant, years apart. No follow-up measurement entered fitting; the model was trained on index snapshots only, and follow-up scans were reserved for evaluation.

The frozen model uses baseline information alone to predict which modality of a pair will change faster, and we compare this ordering with the observed within-person change over one matched interval per participant and pair. The submission reported this for 122 ADNI participants of the development split. We have now repeated it, without refitting or any change of settings, on 513 additional ADNI participants who were never used or inspected during development; 160 of them had a matched follow-up for at least one modality pair (Appendix J.1 of the revised paper). The results were similar (Table 12): agreement (common31/native) was 65.4%/73.9% for A–N (97 participants), 64.8%/60.4% for A–T (82) and 58.4%/57.6% for T–N (30), against 61.2%/71.3%, 69.8%/70.9% and 55.8%/54.4% in the development split (79, 69 and 28 participants). In the Anti-Amyloid Treatment in Asymptomatic Alzheimer’s Disease (A4) trial, a second held-out cohort, the clock computed from baseline MRI had the highest concordance with subsequent clinical progression among all methods (C = 0.617; Table 10). Validation across successive intervals within individuals remains open.

Q2. Leading accuracy under non-Gaussian emissions

We thank the reviewer for this question, which prompted a new robustness experiment. We repeated the Table 1 simulation under symmetric heavy-tailed noise (Student-t with 5 degrees of freedom) and right-skewed noise (skew-normal with shape +5), refitting CALIPER with its Gaussian observation model under each noise law. Within each seed, we matched the conditional means and variances and kept the true leaders, masks, anchors and split fixed. Across the five original seeds and ten additional seeds, mean leading-modality accuracy was 79.46% under Gaussian noise (77.50% on the original five seeds, as in Table 1), 78.96% under Student-t noise and 78.06% under skew-normal noise. Mean paired changes were −0.50 points (95% CI −1.97 to +0.97) and −1.40 points (−2.96 to +0.16). These experiments address noise shape with the latent progression process held fixed. They are reported in Appendix G.4 of the revised paper.

Q3. Why the secant scored higher, and what the bridge adds

The endpoint secant in Table 1 is not a bridge-free method. It replaces only the slope and keeps the regime selected by the bridge and the local Fisher scale (Appendix G.1). On its own, a secant joins the PRE anchors to one regime's endpoint anchors with a single slope per modality. It therefore has no path between the two ends: it cannot place an unlabeled intermediate snapshot along a regime's course, and it cannot say which regime that snapshot belongs to. The bridge provides both. It builds each regime's path through the unlabeled intermediate snapshots (Eq. 6), and each snapshot's regime responsibility is the share of path density that passes through its state (Eq. 7).

In the main local-noise simulation, the endpoint secant had higher leading accuracy than the bridge (82.5% vs. 77.5%). Leading accuracy weights the three possible leaders by how often each occurs. When recall is instead averaged over the three true leaders with equal weight, the bridge reached 0.644 and the secant 0.592 under local noise, and 0.566 versus 0.482 under constant noise (bridge higher in 3 of 5 and in all 5 seeds, respectively). Always predicting amyloid gives 0.333 on this measure. When the local direction varies along a curved path (Appendix G.2, with supplied coordinates and Fisher scale), the full bridge reached 95.2% leading accuracy versus 80.5% for the secant with the same regime assignments, and it exceeded every listed control in each of the five paired seeds (Figure 5).

Q3 (continued). Bridge versus secant on real follow-up

On real follow-up, we compared the two currents with the ruler, regime weights and follow-up intervals held fixed. The table gives bridge-minus-secant differences in ordering agreement for the 160 held-out participants, in percentage points [paired 95% CI] (Table 15 in the revised paper):

PairNcommon31native
A–N97+11.79 [+6.55, +16.73]+19.24 [+13.13, +24.69]
A–T82−1.36 [−5.60, +3.13]−5.03 [−9.99, −0.25]
T–N30−0.74 [−14.65, +12.76]−3.33 [−18.51, +12.56]
All pairs160+3.67 [−0.86, +8.35]+4.12 [−1.08, +9.25]

The bridge had higher agreement than the secant for A–N in both feature views, with intervals that exclude zero, as in the development split (+5.7 and +14.3 points). A–T did not favor the bridge and T–N was imprecise in both samples. We therefore limit the real-data claim to pair-specific differences, which now also hold in participants who were not used in development.

Response to the listed weaknesses

Margins over flow matching and MoPoE-VAE. In Table 1, CALIPER has the highest mean relative-speed correlation in both noise settings (0.769 and 0.808) and the smallest seed-to-seed SD among methods with a speed readout (0.031 and 0.013); the largest SD quoted in the review (0.125) is flow matching's. The ranking is unchanged on the common set of evaluable queries (Appendix G.3). These baselines do not define calibrated speeds: their entries rely on PROFILE or decoder-tangent readouts that we added so that a comparison was possible (Appendix D.4). The component claim rests on the matched ablation, in which local Fisher exceeded fixed and omitted rulers in all five paired seeds in both settings (Appendix G.1).

Endpoint accuracy in simulation. The same-anchor logistic is a discriminative classifier trained for endpoint labels, whereas CALIPER's regime assignment is used to select the reference current. The simulation speed metrics are computed with the estimated regime (Appendix D.6), so CALIPER's relative-speed and leading-modality results already include the effect of regime errors. On real data, regime assignment reached balanced accuracy 0.748 versus 0.677 for the same-anchor logistic on development anchors (Appendix H.2), and 0.745 [0.669, 0.816] versus 0.538 [0.430, 0.648] on 119 held-out ADNI participants (paired difference 20.74 points, 95% CI 10.12 to 31.26; Table 11).

Whether the full machinery is needed, and what each result depends on. The pipeline has several steps because each step produces one quantity that the final readout requires. The observation model gives the disease clock and a stage for each modality (Table 2, Table 10). Its stage-dependent noise gives the Fisher ruler, which makes speeds comparable across modalities: removing the ruler lowers relative-speed correlation from 0.769 to 0.513 (Appendix G.1; Table 13). The bridge gives the endpoint regime and the population current (Appendix G.2; Tables 11 and 15); for regime assignment, age conditioning and the support floor raise balanced accuracy from 0.328 to 0.748 on development anchors (Figure 7) and from 0.409 to 0.745 in the held-out participants (Table 11). No step leads on every metric, because the design balances these targets instead of maximizing one. Methods that lead on one readout fall short on another: in Table 1, FA + LR has the highest endpoint accuracy (0.867) with relative-speed correlation 0.654, and VAE staging reaches stage correlation 0.925 with relative-speed correlation 0.177. None of the baselines, as originally designed, provides the set of quantities CALIPER targets: a disease clock with a stage for each modality, endpoint regimes, population currents, and calibrated speeds; their stage, regime and speed entries come from readouts that we attached (Appendix D.4, E.5). Each component is ablated one at a time in Appendix G.1, G.2 and H.2–H.4, and on held-out data in Tables 11 and 13–15.

Response to the listed weaknesses (continued)

Staging relative to MoPoE-VAE. Table 2 uses the development split, so we repeated it on the 513 held-out ADNI participants and on the external A4 cohort, with the submitted model unchanged. The table compares the clock with the best of the 13 baselines on each outcome (estimates [95% CI]; all methods are in Table 10 of the revised paper):

OutcomenCALIPER (clock)Best baseline
Held-out ADNI: CN vs dementia AUC2840.848 [0.793, 0.896]MoPoE-VAE, 0.849 [0.800, 0.892]
Held-out ADNI: CN vs MCI AUC3680.742 [0.687, 0.795]Anchor LR, 0.645 [0.591, 0.697]
Held-out ADNI: CDR-SB ρ1350.472 [0.333, 0.592]MoPoE-VAE, 0.465 [0.338, 0.570]
Held-out ADNI: MMSE −ρ1270.468 [0.320, 0.603]MoPoE-VAE, 0.472 [0.329, 0.599]
A4: CDR progression C1,0780.617 [0.588, 0.645]Static FA, 0.606 [0.577, 0.637]

The clock is higher than every baseline on three of the five outcomes and within 0.004 of the best baseline on the other two. These results are similar to those from the development split, where the clock also had the highest ADNI CN–MCI AUC (0.730). MoPoE-VAE reached 0.624 for CN–MCI and 0.585 on A4. A4 enrolled cognitively unimpaired participants whose baseline CDR-SB and MMSE were concentrated near the limits of both scales, so we report how well baseline MRI scores predicted subsequent global CDR progression. Following the trial protocol, progression required a global CDR score > 0 at two successive assessments, or at the final observed assessment, during the double-blind phase.

Follow-up ordering. The table gives the difference in ordering agreement between local Fisher calibration and uncalibrated stage speed, in percentage points [95% CI] (Table 13 in the revised paper):

PairFeaturesDevelopment splitHeld-out ADNI
A–Ncommon31+19.10 [+10.13, +28.09]+19.66 [+12.27, +27.24]
A–Nnative+22.98 [+15.24, +29.81]+21.63 [+15.64, +27.95]
A–Tcommon31+15.77 [+11.35, +20.27]+13.15 [+7.66, +18.02]
A–Tnative+12.12 [+8.58, +15.60]+9.85 [+6.23, +14.02]
T–Ncommon31−9.61 [−20.19, +1.65]−15.53 [−28.21, −3.44]
T–Nnative−4.11 [−14.89, +5.33]−9.24 [−18.80, +1.25]
All pairscommon31+10.06 [+5.68, +14.56]+8.13 [+3.39, +13.37]
All pairsnative+10.57 [+6.40, +14.77]+8.60 [+4.75, +13.07]

In both samples, calibration raised agreement for A–N, for A–T and overall, with intervals that exclude zero; T–N remained the exception, as in the paper (Appendix H.3). Relative to the standardized-vector readout, the A–N gain also recurred (+9.48 [+4.68, +14.11] and +13.35 [+8.39, +18.15] points held-out; Table 14). Local and fixed Fisher remained similar overall on real follow-up (+0.34 [−2.78, +3.45] points in the development split and +1.82 [−0.39, +4.47] held-out, native features), although local was higher for A–T in both samples; the advantage of the local ruler over the fixed ruler is shown in simulation, in all five paired seeds.

APOE and regime profiles. We agree that these analyses are descriptive and do not test the speed readout. They are nevertheless independent support for the endpoint regimes: APOE was not used in training, anchor definition or preprocessing, yet the assigned Y-AD and O-AD groups have higher APOE-ε4 carrier fractions than the SA and NA groups, preserving the gradient of the clinically defined anchor groups (Figure 2). Evidence about modality ordering comes from the matched within-person follow-up comparisons above.

We hope our answers resolve your questions. If anything remains unclear, please let us know; we would be very happy to continue the discussion.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Global response

Dear Reviewers and Area Chair,

We sincerely thank all reviewers for their valuable comments. We are glad that our responses addressed most of the reviewers' concerns, and their comments have made the paper better. We have uploaded the revised PDF to OpenReview, with changes highlighted in teal. We made the following clarifications and additions.

Clarifications

  • Terms and measures (Introduction; Sections 2, 4.1 and 4.2). We defined several terms that could be misunderstood (modality, disease clock, modality stage, endpoint regime and leading modality), as well as the four simulation measures and the two noise settings, and clarified how CALIPER differs from earlier methods.
  • Follow-up evidence (Abstract; Section 5). We now state the follow-up evidence separately for each modality pair.

Additions

  • Held-out evaluation (Sections 4.1 and 4.3; Appendix J). We applied the submitted model, without refitting, to additional ADNI participants never used in training or development and to the external A4 trial, and repeated the staging, endpoint-assignment and follow-up analyses. The results were similar to those on the development split.
  • Paired comparisons (Appendix J.3–J.4). We added the endpoint-assignment ablation on held-out participants, participant-level paired comparisons of the output rulers with effective sample sizes, and a comparison of the bridge current with the endpoint secant.
  • Robustness to non-Gaussian noise (Section 4.2; Appendix G.4). We repeated the main simulation under heavy-tailed and skewed noise with the Gaussian observation model unchanged; leading-modality accuracy changed little.

If any questions remain, we would be happy to discuss them.

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