acceptodds
Under review as a conference paper at ICLR 2027

BrainGenFlow: Modeling Longitudinal Progression via Residual Flow Matching and Gaussian Imputation

Abstract

Forecasting individualized brain trajectories from a single baseline scan is essential for prognosis and early intervention in neurodegenerative diseases, yet existing methods either operate on composite biomarkers or require sequences of follow-up visits at inference. We introduce BrainGenFlow, a two-stage framework that produces month-resolved, multi-region brain trajectories from a single scan and clinical covariates. The central design addresses cohort sparsity through Bayesian distillation: a deep kernel Gaussian process performs exact temporal imputation per region of interest, converting sparse irregular visits into dense monthly supervisory trajectories. We utilize these trajectories to train an autoregressive flow matching model through a new parameterization technique called Residual Flow Matching, to model the changes in the biomarkers directly. At inference, BrainGenFlow forecasts decade-long trajectories across 145 brain regions using only the baseline scan, without requiring access to longitudinal data. On long-horizon AD biomarker forecasting, our method achieves state-of-the-art performance with improvements that hold under leave-one-study-out evaluation. Furthermore, predicted regional rate-of-change align with established Alzheimer's disease progression pattern.

Primary area:
applications to neuroscience & cognitive science
Keywords:
generative models, neuroscience, time series, flow matching

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_wyn3OpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
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2
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Paper summary

Summary: The paper introduces BrainGenFlow, a two-stage framework for forecasting month-resolved trajectories of 145 regional brain volumes from a single baseline scan plus clinical covariates. Stage 1 fits one deep kernel Gaussian process (DKGP) per region of interest (ROI) on the training cohort, and its posterior mean is used to impute dense monthly trajectories over each subject’s observed follow-up. Stage 2 trains an autoregressive flow-matching model that predicts month-to-month residuals rather than absolute next states. It is conditioned on the current state, a GRU embedding of the generated history, and a baseline embedding applied via FiLM. Experiments on nine longitudinal cohorts report improved forecasting accuracy over statistical and neural baselines, generalization under leave-one-study-out evaluation, and associations between predicted atrophy rates and clinical progression groups.

Critical strengths
  1. The problem is clinically meaningful and well-scoped. Forecasting multi-regional trajectories from a single baseline addresses a useful setting with sparse, irregular longitudinal observations.
  2. The two-stage framework design is well-motivated. Temporal imputation provides the generative model with dense monthly trajectories to train on, enabling long-horizon forecasting from a single baseline scan at inference time.
  3. The evaluation is well-designed. The paper includes subject-level cross-validation, seven leave-one-study-out evaluations, persistence and statistical baselines, objective-matched deterministic residual predictors, and component ablations.
Critical weaknesses
  1. The improvement over the strongest baseline is not significant. The deterministic Transformer (0.2240) lies within the 95% CI of BrainGenFlow ([0.2079, 0.2255], Table 1). The headline improvements (26.8% over RNN-AD and 69.9% over TFM-ODE) are measured against baselines that perform worse than the no-change persistence baseline (0.2684). This suggests that these baselines may be under-tuned or poorly adapted. The “state-of-the-art” claim is not supported.

  2. A direct DKGP forecasting baseline is missing. Because the DKGP takes [x0; c; t] as input (Eq. 4), the trained teacher can in principle forecast a held-out subject directly from the baseline scan and covariates. However, this baseline-only DKGP forecast is not reported. Since Stage 2 is described as learning to reproduce the same dynamics “in an amortized form” (Section 4.1), the teacher is the most natural reference point. Without this comparison, it is unclear whether Stage 2 improves accuracy or only amortizes the GP.

  3. The decade-long forecasting claim needs more evidence.

Questions for authors
  1. What is the MAE of the DKGP teacher used directly as a single-baseline forecaster on held-out subjects, under the same protocol? Please also report per-fold results for the deterministic Transformer (Table 3 currently omits it) and a paired comparison with BrainGenFlow under comparable capacity and tuning budgets.

  2. Please report horizon-stratified MAE (as in Table 10) for persistence, GAM, Det-Transformer, and the endpoint-pair flow, as well as LOSO results for at least the strongest baselines. Please also report an error metric on change from baseline, or a skill score relative to persistence.

  3. (Minor) Several abbreviations are used before they are defined, or are never defined:

2 comments
AuthorsOpenReview ↗

Response to review

We thank the reviewer for the careful review, and for recognizing the clinically meaningful, well-scoped problem and the well-motivated two-stage design. All neural results use the corrected evaluation (general comment).

Significance and the state-of-the-art claim

We agree with the reviewer. The Det-Transformer shares our framework (DKGP supervision, residual target) and replaces only the flow head, with roughly 3× the velocity network's parameters and the same training settings and validation split (at matched capacity, the MLP head reaches 0.2047). Per fold results are: Det-Transformer: 0.2019, 0.1995, 0.1997, 0.2074, 0.1989, BrainGenFlow: 0.2122, 0.2076, 0.2005, 0.2137, 0.2028. The Det-Transformer is slightly more accurate under five-fold (fold-paired, +0.0059 [+0.0013, +0.0104]), and the two are tied under LOSO (Table W2). We report the two as comparable in point accuracy, withdraw the 26.8%/69.9% comparisons, and narrow the "state-of-the-art" claim to published methods that forecast all 145 ROIs jointly from a single scan (TFM, RNN-AD, endpoint-pair flow; Table Z1 in the response to Reviewer zJda), all of which BrainGenFlow outperforms. Flow matching adds a calibrated predictive distribution: its 95% intervals cover 95.0–97.3% at every horizon (94.5–97.1% under LOSO), vs. 82.9% at 60–120 months for MC dropout on the Det-Transformer (Table M1 in the response to Reviewer Mswv).

On baselines below no-change: scan noise accounts for ~90% of no-change squared error in years 1–3, where most visits fall. RNN-AD and Deep Regression predict absolute volumes and stay below no-change even with DKGP supervision (0.2591, 0.3091; Table D1 in the response to Reviewer DeHU); TFM's next-state prediction compounds over the rollout (0.608 at best).

Direct DKGP baseline

We agree that the teacher is the natural reference. With the same conditioning, the DKGP (145 per-ROI models) reaches 0.1971, more accurate than BrainGenFlow overall (fold-paired, +0.0103 [+0.0057, +0.0149]). BrainGenFlow is more accurate in the first year (0.166 vs. 0.170); the DKGP leads from two years on. The DKGP uses exact inference conditioned on the full training cohort, which it must keep at prediction time. Stage 2 distills it rather than competing with it, and comes within about 5% of its MAE. What it adds: one joint model, no training data at inference, and uncertainty that grows with horizon. The DKGP's predictive SD is nearly constant (0.36–0.37), so it over-covers early (98.6% at 0–12 months) and is nominal only at 60–120 months. We will add it as a baseline and revise the description of Stage 2.

Decade-long forecasting

Every horizon bin has held-out subjects from all five folds: 1,231 subjects and 2,076 visits at 60-120 months (Table D2 in the response to Reviewer DeHU), and 1,101 subjects under LOSO. There, BrainGenFlow improves on no-change by 20.9%, with 97.3% coverage (97.1% LOSO). We will claim 120-month generation validated within observed follow-up, not uniformly accurate decade-long prediction.

Requested analysis

Horizon-stratified MAE with per-bin counts is in Table D2 (response to Reviewer DeHU).

Table W1. Skill relative to no-change (1 − MAE/MAE_no-change), five-fold, computed per fold and averaged. Endpoint-pair flow: one seed.

MonthsGAM (145 models)Det-TransformerEndpoint-pair flowBrainGenFlow
0–12−3.5%1.8%1.4%1.7%
12–245.2%6.6%5.1%6.1%
24–3611.3%11.5%8.1%10.2%
36–6017.3%14.2%8.1%11.0%
60–12029.6%25.6%19.5%20.9%
All15.1%14.2%10.1%11.7%

Since |(p − x₀) − (y − x₀)| = |p − y|, MAE is already a change-from-baseline error; Table W1 gives the skill score.

Table W2. LOSO MAE by held-out cohort (Det-Transformer: three seeds). Per cohort: 95% subject-bootstrap CI; mean: 95% t-interval across studies.

Held-out cohortNo-changeDet-TransformerBrainGenFlow
ADNI0.2485 [0.2418, 0.2549]0.2170 [0.2113, 0.2226]0.2178 [0.2121, 0.2234]
AIBL0.2634 [0.2362, 0.2930]0.2016 [0.1807, 0.2264]0.2075 [0.1877, 0.2316]
BLSA0.2366 [0.2294, 0.2440]0.1883 [0.1829, 0.1937]0.1817 [0.1760, 0.1876]
HABS0.1615 [0.1516, 0.1746]0.1407 [0.1325, 0.1519]0.1378 [0.1295, 0.1490]
OASIS0.2754 [0.2648, 0.2867]0.2591 [0.2481, 0.2715]0.2675 [0.2562, 0.2802]
PENN0.2379 [0.2156, 0.2616]0.2242 [0.2047, 0.2441]0.2278 [0.2074, 0.2494]
PreventAD0.1248 [0.1214, 0.1284]0.1121 [0.1095, 0.1147]0.1139 [0.1109, 0.1170]
Mean0.2211 [0.1693, 0.2730]0.1918 [0.1452, 0.2385]0.1934 [0.1442, 0.2427]

BrainGenFlow and the Det-Transformer are tied (paired over subjects, +0.0004 [−0.0000, +0.0009]; averaged over studies, +0.0016 [−0.0031, +0.0063]). BrainGenFlow improves on no-change for 79.0% of subjects (paired over subjects, −0.0308 [−0.0324, −0.0292]). GAM and DKGP LOSO results will be added in the revision, and Figure 3a updated.

Abbreviations. We will define all abbreviations at first use.

I thank the authors for responding to my concerns. I will discuss this with other reviewers and make a final decision. I dont have further question

Reviewer_zJdaOpenReview ↗
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Confidence
4
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Paper summary

The authors develop a model to forecast the progression of brain ROI measures in Alzheimer's disease. The framework uses a Deep Gaussian Kernel Regression to perform data imputation at every month (since brain imaging is sparse), which they then use as supervisory signal for a residual flow matching framework conditioned on the single initial brain image as well as clinical covariates. They evaluate on a combined dataset of ADNI, AIBL, and several other brain neuroimaging datasets and show ablation studies.

Critical strengths
  1. To solve the sparsity problem, the model uses suitable frameworks for data imputation such as GP regression
  2. The model uses recently developed residual flow matching techniques to perform the longitudinal prediction
Critical weaknesses
  1. I saw the results in Table 1, but I'm not convinced of how good those baselines are. Some methods such as Deep Regression are methods that the authors built themselves for the purpose of this study. While informative, it would have been great to compare against more SOTA baselines built by others and published in scientific papers (so far I could identify only RNN-AD). The authors themselves cite a variety of these models (Koval 2021, Abi Nader, ... Hong 2019, Gruffaz 2021, Tassopoulou 2022). Perhaps simpler, the authors could run their method against the TADPOLE dataset to predict ventricle volumes on the exact same subjects and using the exact training&testing data from TADPOLE. This would allow to see the performance of this method against the ~60 submissions already existing in TADPOLE
Questions for authors
  • The authos claim that "Koval et al. (2021a) proposed a Bayesian mixed-effects model (AD Course Map) that produces subject-specific biomarker trajectories and was validated as the strongest performer in the TADPOLE challenge (Marinescu et al., 2018), though it operates on low-dimensional inputs ". However, the winner of TADPOLE was team Frog from Genentech which used XGBoost, a gradient boosting method. It would help to clarify or be more specific.
3 comments
AuthorsOpenReview ↗

Response to review

We would like to thank the reviewer for the constructive review, and for recognizing DKGP regression as a suitable solution to the sparsity of longitudinal neuroimaging and residual flow matching as a fitting technique for longitudinal prediction. All neural results use the corrected evaluation (general comment).

W1. Comparison with published methods

We would like to clarify that the manuscript already compares with published methods, namely TFM, RNN-AD and the endpoint-pair flow (Δ-LFM supervision applied to our network; Table 1). Following the reviews, we add a fourth, the temporal deep kernel GP (DKGP). Each is adapted to forecast the same 145 regional volumes from a single baseline scan:

Table Z1. Five-fold MAE of published methods, mean [95% CI across folds] (lower is better). No-change: 0.2349 [0.2297, 0.2401].

MethodTypeMAE
TFM (Zhang et al., NeurIPS 2024)flow matching, next state0.6076 [0.4655, 0.7497] (best configuration)
RNN-AD (Nguyen et al., 2020), DKGP-supervisedrecurrent, absolute volumes0.2591 [0.2551, 0.2631]
Endpoint-pair flow (Δ-LFM supervision; Chen et al., ICLR 2026)flow, observed visit pairs0.2112 [0.2060, 0.2163]
Temporal DKGP (Tassopoulou et al., 2022; 2025)per-ROI DKGP, used directly0.1971 [0.1933, 0.2008]
BrainGenFlowresidual flow, one model0.2073 [0.2003, 0.2144]
  • TFM uses its official code, with the learning rate selected on validation. Its error comes from direct next-state prediction compounding over the 120-month rollout; predicting volumes rather than change is also a harder task, as shown by our residual vs. next-state ablation.
  • RNN-AD was retrained with its original settings, on observed visits (0.2964) and on our DKGP trajectories (0.2591); dense supervision improves it, but it predicts absolute volumes and stays below no-change, whereas BrainGenFlow improves on no-change at every horizon.
  • The endpoint-pair flow applies the published Δ-LFM supervision (pairs of observed visits) to our network.
  • The temporal DKGP is the method we use as BrainGenFlow's teacher. Its accuracy reflects exact DKGP inference conditioned on the full training cohort, which it must keep at prediction time, and it requires 145 separately fitted univariate models; we therefore report it as a per-region reference point rather than a like-for-like competitor. BrainGenFlow amortizes it into one model that needs no training data at inference, comes within about 5% of it (0.2073 vs. 0.1971), and keeps its intervals calibrated at every horizon (97.3% coverage at 60–120 months), whereas the DKGP over-covers at short horizons (98.6% at 0–12 months) and a deterministic head falls to 82.9% at 60–120 months.

Deep Regression and the deterministic heads are our own baselines and ablations (Appendix G), which isolate the residual target and the flow-matching head.

The other progression models cited address different settings from ours. AD Course Map (Koval et al., 2021) personalizes a small set of biomarkers from each subject's observed visits; Abi Nader et al. (2020) model progression at the population level; and the manifold models of Hong et al. (2019) and Gruffaz et al. (2021) need at least two acquisitions per subject at inference. None forecasts 145 regions from a single scan without changes that would make the comparison uncontrolled.

TADPOLE. We thank the reviewer for this suggestion. TADPOLE asks for monthly forecasts of diagnosis, ADAS-Cog13 and ventricle volume for ADNI rollover participants, made from all of each participant's data available before the deadline, with FreeSurfer-derived volumes. Our task differs in input (a single baseline scan), output (145 DL-MUSE regions) and cohorts (nine studies). A direct comparison would therefore require retraining on TADPOLE's data and changing the input protocol, so it would no longer test BrainGenFlow's setting.

Q1. The TADPOLE winner

We acknowledge that the sentence was imprecise. TADPOLE's overall winner was team Frog, a gradient-boosting method, and no single submission was best on all three targets. Koval et al. (2021) report that AD Course Map predicts cognitive decline more accurately than the 56 methods benchmarked in TADPOLE. We will revise the sentence in both the introduction and related work:

"Koval et al. (2021) proposed AD Course Map, a Bayesian mixed-effects model of subject-specific biomarker trajectories, and reported that it predicts cognitive decline more accurately than the 56 methods benchmarked in the TADPOLE challenge (Marinescu et al., 2018), whose overall winner was a gradient-boosting method; it operates on low-dimensional inputs."

Thank you for the additional analyses and clarifications, which have now addressed my concerns. I have increased my score to a 4 (clear accept).

AuthorsOpenReview ↗

Reply to Reviewer zJda

We sincerely appreciate the reviewer’s positive reassessment and are glad that our rebuttal has addressed their concerns.

Reviewer_MswvOpenReview ↗
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2
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3
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3
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Paper summary

The paper forecasts how 145 brain regions change month by month over up to ten years, starting from a single baseline MRI scan and a few clinical variables. It works in two stages. First, a deep kernel Gaussian process fills in each training subject's sparse visits to create dense monthly trajectories. Second, a flow matching model is trained on these trajectories to predict the month-to-month change rather than the next state, and is rolled out step by step at test time. Experiments on nine cohorts report lower error than several baselines, and the paper also reports leave-one-study-out results and the predicted atrophy patterns.

Critical strengths

The task is useful: it forecasts many brain regions over a long horizon from a single scan. The data are large and come from many cohorts, and the leave-one-study-out evaluation is a good test of generalization.

Critical weaknesses
  1. The most important baseline is missing. The Gaussian process in stage one already takes the baseline scan, the clinical variables and time as input. It can therefore forecast a new subject's trajectory from a single scan by itself. The paper uses it only to create training targets and never tests it as a forecaster. Without this comparison, it is unclear what the second stage adds. The same question applies to the generative part: a plain deterministic Transformer reaches almost the same error, 0.2240 vs. 0.2167, with overlapping intervals. The model is also judged only by average error and never by the quality or calibration of its samples, so there is little evidence that flow matching is needed.
  2. The large improvements come from weak baselines. RNN-AD, Deep Regression and TFM all do worse than simply predicting no change. TFM's error is almost three times that of the no-change baseline, which suggests these baselines were not set up properly. The headline gains of 26.8% and 69.9% are measured against these baselines. Against reasonable ones, such as GAM, the endpoint-pair flow and the deterministic Transformer, the gain is small. Predicting the change instead of the next state is a common choice in forecasting, so presenting it as a new technique overstates the contribution.
Questions for authors
  1. How well does the stage-one Gaussian process forecast from a single baseline scan, under the same protocol as Table 1?
  2. Why do RNN-AD, Deep Regression and TFM perform worse than predicting no change? How were they tuned?
  3. Does the model's sample spread give useful uncertainty? If not, what is the advantage over a deterministic model?
1 comment
AuthorsOpenReview ↗

Response to review

We thank the reviewer for the thoughtful review, and for recognizing that forecasting many brain regions over long horizons from a single scan is a useful task.

All neural results use the corrected evaluation (general comment).

W1. The stage-one DKGP as a forecaster

Used directly from the baseline scan and covariates, the DKGP (145 per-ROI models) reaches 0.1971 vs. 0.2073 for BrainGenFlow (fold-paired difference +0.0103 [+0.0057, +0.0149]). Its advantage comes from long horizons: BrainGenFlow is more accurate in the first year (0.166 vs. 0.170), the two are equal at 12–24 months, and the DKGP leads from two years on. What Stage 2 adds:

  • One joint model instead of 145 univariate ones; exact DKGP prediction also needs the training cohort's data at inference, whereas BrainGenFlow does not (0.055 s per subject for 120 months).
  • Horizon-dependent uncertainty. The DKGP's posterior predictive SD is nearly constant (0.36–0.37), so its intervals over-cover at short horizons (98.6% at 0–12 months) and reach nominal only at 60–120 months. BrainGenFlow's spread grows with horizon, keeping coverage near nominal (Table M1).

W2. Deterministic Transformer and calibration

The Det-Transformer is our ablation: it keeps DKGP supervision and the residual target and replaces only the flow head with regression. Its point accuracy is comparable: slightly better under five-fold (0.2015 vs. 0.2073; paired over subjects, +0.0058 [+0.0053, +0.0064]) and tied under LOSO (0.1918 vs. 0.1934). With the gap to RNN-AD and Deep Regression, this indicates that accuracy comes from the framework (DKGP supervision, residual target) and the flow head adds the predictive distribution.

To evaluate it, we add each ROI's empirical scan-to-scan noise (~0.20 SD, from visit pairs ≤6 months apart in other folds) to every model's predictive distribution except the DKGP's, whose posterior predictive distribution already includes a learned noise term. BrainGenFlow uses persistent sampling (an inference-time choice; no retraining): each sample keeps its source-noise draw across months, representing a consistently faster or slower progressor.

Table M1. Coverage (%) of nominal 95% intervals, scan noise included.

Model5-fold, all5-fold, 60–120 moLOSO, allLOSO, 60–120 mo
No-change87.071.688.174.1
GAM (145 models)91.484.8––
Det-Transformer (MC dropout)90.882.991.481.6
DKGP (145 models)*97.895.8––
BrainGenFlow (persistent)96.097.396.097.1

*Posterior predictive distribution, which includes its learned noise term; no scan noise added. –: five-fold only; LOSO will be added in the revision.

BrainGenFlow covers 95.0–97.3% in every horizon bin (94.5–97.1% in held-out studies). MC dropout adds little beyond scan noise, so the deterministic head under-covers at long horizons.

W3. Baselines and novelty

  • Tuning. All models select checkpoints on the same inner validation split as BrainGenFlow. RNN-AD and Deep Regression (our own baseline, Appendix G.1) use their published or specified settings, and TFM uses its official code with the learning rate selected on validation. The deterministic heads share BrainGenFlow's encoder, conditioning, optimizer and training schedule: the MLP head matches the velocity network's capacity (0.2047) and the Transformer head has roughly 3× its parameters (0.2015).
  • Why they fall below no-change. Scan noise accounts for ~90% of no-change squared error in years 1–3, where most visits fall. RNN-AD and Deep Regression predict absolute volumes rather than change from the observed baseline, so their first-year error (0.25, 0.30) exceeds no-change (0.17). With DKGP supervision both improve (0.2964→0.2591, 0.3152→0.3091) but remain below no-change. TFM's direct next-state prediction compounds over the 120-step rollout (0.608 at best).
  • Headline gains. We will withdraw the 26.8%/69.9% comparisons and narrow the state-of-the-art claim to published multivariate methods (general comment).
  • Novelty. We agree that predicting change is common, and do not claim it as novel. Our contribution is the combination isolated here: (1) dense DKGP supervision, which improves every architecture trained on it; (2) residual dynamics from the observed baseline, which let a model beat no-change at every horizon; and (3) flow matching, which turns this into a single calibrated forecaster for all 145 ROIs.

Questions. 1: W1. 2: W3. 3: Yes; near-nominal coverage at every horizon, including unseen studies, which MC dropout does not provide (W2).

Ethics. We will add an ethics and data-use statement. This retrospective secondary analysis recruited no new participants; each cohort was collected under its own IRB approval with informed consent, and we used de-identified data under each study's data use agreement, with the required acknowledgments (e.g., ADNI, AIBL, OASIS). We will add the PENN citation in the revised manuscript.

Reviewer_DeHUOpenReview ↗
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Paper summary

The paper introduces BrainGenFlow, a two-stage framework for forecasting monthly trajectories of 145 brain regions from a single baseline scan and clinical covariates. It uses ROI-specific deep-kernel Gaussian processes to impute dense monthly training trajectories from sparse, irregular observations, then trains a residual flow-matching model to predict changes dk=xk+1−xkd_k = x_{k+1} - x_k. The authors evaluate the method on nine studies with 3,969 participants using subject-level cross-validation, leave-one-study-out evaluation, and ablation studies. They report a mean MAE of 0.2167 and show that predicted rates of change differ across clinical progression groups.

Critical strengths
  • The problem setting is practical, and the method is tailored to the data regime. BrainGenFlow predicts monthly trajectories for 145 ROIs using only a baseline MRI and clinical covariates. It addresses sparse, irregular visits through DKGP imputation and models small month-to-month changes as residuals, aligning the approach with the characteristics of the data.

  • The experiments provide evidence for the contributions of the main components. The authors evaluate the method using cross-validation and external-cohort testing across 3,969 participants from nine studies. Their ablation results show that residual prediction performs better than next-state prediction with the same architecture, and they report a lower overall mean MAE than the comparison methods.

Critical weaknesses
  • The contributions of DKGP-imputed supervision and residual flow matching are not fully disentangled. The endpoint-pair flow and deterministic heads in Table 1 provide partial controls, but the headline improvements—26.8% over RNN-AD and 69.9% over TFM—come from comparisons that change several factors at once. RNN-AD (0.2961) and Deep Regression (0.3003) also perform worse than the no-change baseline (0.2684). Table 4 shows that training the same flow model on linearly interpolated or RBF-GP targets also yields worse performance than this baseline (0.590 and 1.030, respectively), suggesting that a substantial part of the gains may depend on DKGP imputation. However, the main baselines were not trained on the same DKGP-imputed trajectories. It therefore remains unclear how much of the improvement comes from residual flow matching itself.

  • The reliability of the reported gains and long-horizon performance is difficult to assess. The MAE difference from the deterministic Transformer is small (0.2167 vs. 0.2240), and the confidence intervals overlap. This baseline is also omitted from the fold-level results in Table 3. Paired comparisons at the fold level or results from repeated runs would help establish whether the difference is robust. Horizon-specific errors are reported only for BrainGenFlow, and some estimates for longer horizons are based on only a few folds. It is therefore unclear whether the method’s advantage persists at long horizons.

Questions for authors

I have the following questions and suggestions for the authors.

  • Results for the main baselines, such as RNN-AD and Deep Regression, trained on the same DKGP-imputed monthly trajectories used for BrainGenFlow and evaluated under the same protocol, are needed to separate the effect of the imputed supervision from that of the model.

  • Paired fold-level differences between BrainGenFlow and the deterministic Transformer, with an appropriate uncertainty estimate, are needed to assess whether the small MAE gap is meaningful. Results over multiple random seeds would further help establish its robustness.

  • Horizon-stratified MAE for the main baselines, such as the no-change baseline, GAM, the endpoint-pair flow, and the deterministic Transformer, is needed alongside that of BrainGenFlow, together with the number of subjects and observations in each horizon bin.

  • Because this paper uses clinical data, including diagnostic and genetic information, the ethical considerations should be stated explicitly. However, I could not find an ethics or data-use statement in the manuscript. Could the authors clarify the ethics approvals and consent procedures for the nine cohorts, particularly the PENN cohort, for which no citation is provided?

2 comments
AuthorsOpenReview ↗

Response to review

We would like to thank the reviewer for the careful review, and for their comments on the work's practicality and significance.

All neural results use the corrected evaluation (general comment). In short: DKGP supervision helps every model, the residual target is what beats no-change, and the flow head adds calibrated uncertainty at comparable accuracy.

W1. DKGP supervision vs. residual flow matching

Table D1. Five-fold MAE by supervision and target. Original architectures, same validation split and held-out entries, three seeds unless noted.

ModelTargetObserved visitsDKGP trajectories
Deep Regressionabsolute0.3152 [0.3090, 0.3213]0.3091 [0.3045, 0.3136]
RNN-ADabsolute0.2964 [0.2918, 0.3010]0.2591 [0.2551, 0.2631]
Ours (flow)residual0.2112* [0.2060, 0.2163]0.2073 [0.2003, 0.2144]
Det-Transformerresidual–0.2015 [0.1972, 0.2058]

*Endpoint-pair flow (Δ-LFM supervision applied to our network; one seed). No-change: 0.2349 [0.2297, 0.2401].

  • DKGP helps every architecture, including ours (0.2112→0.2073; equal or better in every horizon bin of Table D2; paired over subjects, −0.0038 [−0.0044, −0.0032]).
  • The residual target beats no-change. With the same DKGP supervision, BrainGenFlow is more accurate than RNN-AD (paired over subjects, −0.0517 [−0.0534, −0.0500]; 86% of subjects). RNN-AD and Deep Regression predict absolute volumes instead of residuals, and their first-year error (0.25, 0.30) far exceeds no-change (0.17).
  • Why baselines fall below no-change. Scan-to-scan noise (~0.20 SD, estimated from visit pairs at most six months apart in the other folds) accounts for ~90% of no-change squared error in the first three years, where most visits fall. A model not anchored on the observed baseline adds error the small true change cannot offset.

W2. Gap to the Det-Transformer

We would like to clarify that the Det-Transformer is our own ablation, not a prior method: it replaces only the flow head with regression (roughly 3× the velocity network's parameters). Fold-paired differences (BrainGenFlow − Det, three seeds), folds 0–4: +0.0103, +0.0081, +0.0008, +0.0063, +0.0039; mean +0.0059 [+0.0013, +0.0104]. Under leave-one-study-out they are tied (0.1934 vs. 0.1918; paired over subjects, +0.0004 [−0.0000, +0.0009]). We revise the claim: the heads are comparable in point accuracy. The flow head adds a calibrated predictive distribution: its 95% intervals cover 95.0–97.3% at every horizon (94.5–97.1% in unseen studies; Table M1 in the response to Reviewer Mswv), whereas MC dropout on the deterministic head falls to 82.9% at 60–120 months.

W3. Long horizons

Table D2. Horizon-stratified five-fold MAE, identical held-out entries. All bins include all five folds; counts summed over folds. Det: Det-Transformer.

MonthsSubj.VisitsNo-changeGAM (145 models)DetEndpoint-pair flowOurs
0–121,6362,394.169 [.162, .175].174 [.168, .181].166 [.159, .172].166 [.159, .173].166 [.159, .172]
12–241,7811,942.187 [.179, .196].178 [.168, .188].175 [.166, .185].178 [.168, .188].176 [.166, .186]
24–361,5581,587.204 [.196, .211].181 [.173, .189].180 [.172, .189].187 [.178, .196].183 [.175, .191]
36–602,0642,382.246 [.240, .252].203 [.200, .207].211 [.206, .215].226 [.221, .231].219 [.208, .230]
60–1201,2312,076.368 [.355, .380].259 [.252, .265].273 [.267, .280].296 [.287, .305].291 [.276, .306]
All10,381.235 [.230, .240].200 [.196, .203].202 [.197, .206].211 [.206, .216].207 [.200, .214]

No model is best at every horizon. GAM is univariate, so covering 145 ROIs takes 145 separately fitted models with no shared cross-region structure, while BrainGenFlow is a single joint, multivariate model. GAM pulls forecasts toward the population mean: it is the least accurate in year one but the most accurate beyond three years. BrainGenFlow follows each subject's trajectory, improves on no-change in every bin (1.7% in year one to 20.9% at 60–120 months), beats GAM in year one, and is equal to or better than the endpoint-pair flow in every bin. At 60–120 months its intervals cover 97.3%, vs. 84.8% (GAM) and 82.9% (Det). We will claim 120-month generation, validated only within observed follow-up.

Answers to Questions

1–3. Tables D1–D2, Section W2 above, and Table M1 in the response to Reviewer Mswv (calibration). 4. We will add an ethics and data-use statement. This is a retrospective secondary analysis of existing studies; no new participants were recruited. Each cohort was collected under its own IRB approval with informed consent from participants, and we used de-identified data under each study's data use agreement, with the required acknowledgments (e.g., ADNI, AIBL, OASIS). We will add the citation for the PENN cohort in the revised manuscript.

thank you for the additional experiments and explanations. however, as the authors noted the evaluation protocol had an error and many results must change. i think this needs a major revision beyond the scope of a rebuttal so i will keep my score.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response

General comment to all reviewers: correction to our evaluation

We thank all reviewers for their detailed reviews. Reviewers found the problem clinically meaningful and practical (DeHU, Mswv, wyn3), the two-stage design well suited to sparse, irregular visits (DeHU, zJda, wyn3), the multi-cohort and leave-one-study-out (LOSO) evaluation a strong test of generalization (DeHU, Mswv, wyn3), and the paper clear and concise (DeHU, Mswv, zJda).

While running the requested experiments, we found an error in our evaluation pipeline.

Our training and test files listed the 145 regional volumes in different orders, so at evaluation BrainGenFlow, every ablation (the deterministic heads and the Table 2 variants), the endpoint-pair flow (Δ-LFM supervision applied to our network) and TFM received regions in a different order from training. Because residual models add a predicted change to their own input, the error misassigned predicted changes across regions rather than the volumes themselves, which is why its effect on MAE is moderate. No-change, the statistical baselines and the DKGP do not use this mapping and were not affected. Separately, in the submission the no-change and statistical baselines were computed from a separately processed copy of the data that included follow-up visits beyond 120 months; all models are now evaluated on identical held-out entries (no-change 0.2684 → 0.2349; GAM, refit on these entries, 0.2384 → 0.1995). We re-evaluated every affected model with regions remapped to the training order. All neural results in our responses use the corrected evaluation. BrainGenFlow's MAE is 0.2073 (manuscript: 0.2167).

Table G1. Corrected five-fold results on identical held-out entries (standardized units). Coverage of nominal 95% intervals, with scan-to-scan noise added for all models except the DKGP.

ModelMAECoverage at 60–120 mo (%)
No-change0.234971.6
GAM (145 per-ROI models)0.199584.8
DKGP (145 per-ROI models), used directly0.197195.8*
Det-Transformer (our ablation)0.201582.9
BrainGenFlow (one model)0.207397.3†

Three seeds per neural model. *From the DKGP's posterior predictive distribution. †Intervals from persistent sampling (each sampled trajectory keeps its source-noise draw across months); point forecasts use the standard sampler.

What the corrected results show. All differences are BrainGenFlow minus the comparison model; negative values favour BrainGenFlow.

  • BrainGenFlow improves on no-change at every horizon (11.7% overall, from 1.7% in year one to 20.9% at 60–120 months), and in unseen studies for 79% of subjects. RNN-AD and Deep Regression, which predict absolute volumes rather than change from the observed baseline, remain worse than no-change even when trained on DKGP trajectories (0.2591 and 0.3091), consistent with our residual vs. next-state ablation.

  • The deterministic variant is comparable in point accuracy: the Det-Transformer is slightly more accurate under five-fold cross-validation (paired over subjects, +0.0058 [+0.0053, +0.0064]) and tied under LOSO (+0.0004 [−0.0000, +0.0009]).

  • BrainGenFlow's intervals stay near nominal at every horizon, including in unseen studies: 95.0–97.3% (five-fold) and 94.5–97.1% (LOSO). The Det-Transformer and the GAM fall to 82–85% at long horizons. The DKGP's constant-width intervals over-cover at short horizons (98.6%).

  • The GAM and DKGP are more accurate overall, but they address a different, univariate problem. Each fits a separate model per region (145 in total), and exact DKGP prediction also requires the training cohort's data at inference. We therefore report them as per-region reference points rather than like-for-like competitors: BrainGenFlow is a single multivariate model that forecasts all 145 regions jointly and needs neither (0.055 s per subject for a 120-month trajectory). In the first year, BrainGenFlow is more accurate than both.

In the revision, we:

  • withdraw the 26.8%/69.9% comparisons and narrow the state-of-the-art claim: among published methods that forecast all 145 ROIs jointly from a single baseline scan (TFM, RNN-AD, endpoint-pair flow), BrainGenFlow is the most accurate; it improves on no-change at every horizon, is comparable to its deterministic ablation in point accuracy, and its per-region intervals widen with horizon and stay near nominal, including in unseen cohorts;
  • rerun every neural result under the corrected evaluation, including the ablations (Tables 2, 4, 15), the rate-of-change analysis (Section 5.2, Figure 2) and the per-region analyses (Appendix H);
  • add the DKGP as a baseline, report the GAM refit on the identical held-out entries, and add horizon-stratified results for all main models;
  • add the calibration analysis, which the manuscript listed as future work;
  • add an ethics and data-use statement.

We apologize for the error and thank the reviewers whose requests led us to find it.

AuthorsOpenReview ↗

Note for revisions

We would like to thank all reviewers for their feedback. We have uploaded a revised manuscript in which all changes are marked in red, and we would be grateful if Reviewers DeHU, Mswv and wyn3 could let us know whether our responses have addressed their concerns.

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

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