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- Informativeness
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- Presentation
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Paper summary
This paper tackles regional brain age estimation using a weakly supervised framework that integrates an innovative atlas-guided region mixing strategy to supervise regional heads during learning. It demonstrates that the resulting global-regional framework improves global brain age prediction and improves more localized metrics such as regional age ranking accuracy. It also shows qualitative regional BAG results on AD and PD datasets.
Critical strengths
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Relevant and challenging problem. The paper addresses regional brain-age estimation, an important problem given evidence that brain aging involves multiple spatially heterogeneous patterns rather than a single uniform process (Smith et al., 2020).
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Interesting weak-supervision strategy. The authors propose atlas-guided regional replacement to transform subject-level chronological-age labels into localized supervision for the corresponding regional prediction head. Restricting mixed-image gradients to the regional pathway is a reasonable design choice to limit the influence of synthetic-image artifacts on global age prediction. The approach also explicitly addresses the challenge of assigning anatomically meaningful outputs when regional age labels are unavailable.
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Multiple complementary evaluation strategies. Beyond evaluating agreement with the synthetic weak targets, the authors examine anatomical specificity on unspliced MRI using ROI occlusion and input-gradient analyses. These experiments provide useful evidence that the regional heads respond preferentially to their corresponding anatomical parcels rather than relying exclusively on the artificial replacement procedure.
Critical weaknesses
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The problem of regional brain age estimation has been tackled in the neuroimaging literature but always suffer from the same issue: there is no proper ground-truth and the concept of regional biological age is ill-defined. While the authors propose a synthetic way to mix brain regions across subjects in order to artificially introduce brain regional age diversity, it is impossible to assume that brain regions chronological age equal regional biological age. As such, the evaluation metrics are always biased and do not measure whether the model is actually learning this "biological regional brain age". There are only weak proxy of such measures (i.e. the proposed regional age ranking accuracy).
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The method is strongly dependent of the anatomical atlas for the mixing strategy and more experiments should be conducted to assess the sensitivity of the representation to the choice of the atlas. Since atlas-guided replacement is central to the proposed contribution, this sensitivity should be evaluated. The current restriction to 48 cortical regions also limits the scope of the proposed regional analysis, particularly given the importance of subcortical structures in neurodegenerative disorders.
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The optimization procedure and evaluation uncertainty require further justification. The Stage 2 optimization uses separate real-image and mixed-image passes, with explicit gradient routing to prevent mixed-image losses from updating the backbone directly. While this design is understandable, the paper does not establish that separate optimization steps are necessary or superior to an implementation that combines the objectives while preserving the intended gradient restrictions. An ablation comparing these alternatives, including training stability and computational cost, would help justify the additional complexity.
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The training dataset is modest relative to the available pretraining resources, and external generalization is not established: the pretraining dataset is rather small (<4k samples) while much larger-scale datasets are now available (i.e. OpenMind dataset with >100k samples). More importantly, the participant-level split does not establish generalization to an entirely unseen cohort. A leave-one-cohort-out evaluation or independent external validation would help determine whether the learned representations generalize across acquisition protocols and data distributions.
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The clinical utility of the proposed regional representations is not sufficiently evaluated. The authors motivate the method partly through its potential contribution to downstream disease classification. However, the AD-versus-HC and PD-versus-HC experiments primarily report descriptive, region-wise differences in regional brain-age gaps. I would like to see quantitative classification results, including AUC and confidence intervals, for AD versus HC and PD versus HC. In particular, the authors should compare regional BAG features with a global BAG baseline, ideally also assessing whether regional features provide incremental predictive value beyond age, sex, and other relevant covariates. This would better support the paper's stated objective of demonstrating the practical utility of regional brain-age representations. Existing work on brain-structure ages for multi-disease classification (Nguyen et al., 2024) provides a relevant point of comparison.
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Missing baselines in Table 1: direct method such as Peng et al. 2021 or ViT-based methods (e.g. Triamese-ViT, Zhang and Jiang 2024) are missing.
Questions for authors
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What exactly is the ground truth for regional biological brain age? The method uses the donor's chronological age as a weak target for a transplanted brain region. Why should this intervention make the donor's chronological age a valid target for the region's biological age? How do the authors distinguish age-related information from inter-individual anatomical variability and other subject-specific characteristics?
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Does the model capture genuine regional aging, or simply respond to the synthetic intervention? Can the authors demonstrate that the regional predictions reflect age-related variation in unmodified MRI independently of the region-mixing procedure? For example, do the predictions replicate in longitudinal data, track within-subject changes over time, or correlate with independent regional markers of neurodegeneration?
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Do the regional representations provide clinically meaningful information beyond global brain age? For AD-versus-HC and PD-versus-HC, what are the AUCs and confidence intervals when using regional BAG features versus global BAG? Does adding regional features significantly improve discrimination after accounting for age and sex?
7 comments
Responses to Weakness 2
W2
Response.
To directly address your concern regarding the atlas-dependence of our atlas-guided replacement strategy and its sensitivity, we evaluated MT-ReBA using two brain atlases: Harvard–Oxford (HO48) and Automated Anatomical Labeling 3 (AAL3).
We agree that limiting the analysis to cortical regions (like the 48 regions in HO48) restricts the scope of regional analysis, especially given the critical importance of subcortical structures in neurodegenerative diseases. To resolve this, we specifically introduced AAL3, which extends to 166 regions and explicitly covers key subcortical structures such as the thalamus, substantia nigra, and locus coeruleus.
We added several experiments:
- If our model were overfitted to a specific atlas, its performance would degrade substantially when transferred. However, MT-ReBA maintained high regional age-ranking accuracy on both atlases (RankAcc: 68.30%–70.17%), consistently outperforming the best baseline methods by a large margin of 10.41–16.11 percentage points across three random seeds. Specifically, RankAcc remained robust at 69.63% on HO48 and 69.11% on AAL3.
These results strongly confirm that our model's regional ranking capability is driven by generalizable biological aging patterns rather than atlas-specific artificial features, demonstrating high robustness across different anatomical resolutions and cortical/subcortical boundaries.(p. 6, Section 4.2.2)
Table 2. Regional brain-age ranking accuracy (RankAcc, %). Results are mean ± SD across three training seeds.
HO48
\hline \text{Method} & \text{Seed 1} & \text{Seed 2} & \text{Seed 3} & \text{Mean ± SD} \\\\ \hline \text{Voxel-level (Gianchandani et al., 2024)} & 55.94 & 60.79 & 60.94 & 59.22 \pm 2.84 \\\\ \text{Global CNN} & 56.47 & 55.76 & 54.76 & 55.67 \pm 0.86 \\\\ \text{SFCN (Peng et al., 2021)} & 56.07 & 55.61 & 56.19 & 55.95 \pm 0.31 \\\\ \text{MT-ReBA with Donor} & 68.34 & \mathbf{69.97} & \mathbf{72.19} & \mathbf{70.17 \pm 1.93} \\\\ \text{MT-ReBA without Donor} & \mathbf{69.69} & 69.69 & 69.50 & 69.63 \pm 0.11 \\\\ \hline \end{array}$$ **AAL3** $$\begin{array}{lrrrr} \hline \text{Method} & \text{Seed 1} & \text{Seed 2} & \text{Seed 3} & \text{Mean ± SD} \\\\ \hline \text{Voxel-level (Gianchandani et al., 2024)} & 50.96 & 51.67 & 51.00 & 51.21 \pm 0.40 \\\\ \text{Global CNN} & 53.36 & 52.44 & 53.20 & 53.00 \pm 0.49 \\\\ \text{SFCN (Peng et al., 2021)} & 52.19 & 52.35 & 52.31 & 52.28 \pm 0.08 \\\\ \text{MT-ReBA with Donor} & 70.12 & 67.36 & 67.41 & 68.30 \pm 1.58 \\\\ \text{MT-ReBA without Donor} & \mathbf{70.74} & \mathbf{68.19} & \mathbf{68.40} & \mathbf{69.11 \pm 1.42} \\\\ \hline \end{array}$$ 2. To further rule out reliance on a single atlas, we analyzed regional age associations in 277 fully independent, held-out HCs using both HO48 and AAL3. After strict FDR correction and controlling for covariates, all 48 HO48 regions and all 166 AAL3 regions showed significant age associations. Crucially, despite their different anatomical coverages (cortical-only vs. whole-brain), both atlases revealed a highly consistent spatial pattern of age effects, with the strongest associations in limbic, insular, and frontotemporal regions. This cross-atlas consistency strongly confirms that our model captures genuine biological aging trajectories. **(p. 7, Section 4.2.3; p. 22, Appendix O)** 3. To evaluate atlas adaptability, we performed cross-atlas downstream validation in two independent cohorts (ADNI-AD and NYU-PD) using both HO48 and AAL3. The incremental benefit of regional brain-age features for AD classification was highly consistent across atlases. In ADNI, adding regional features increased AUC from 0.615 to 0.743 with HO48 ($\Delta$AUC = +0.128, 95% CI [0.065, 0.190], $p < 0.0005$), and from 0.642 to 0.762 with AAL3 ($\Delta$AUC = +0.120, 95% CI [0.061, 0.186], $p < 0.0005$). Conversely, PD classification showed disease-specific atlas sensitivity. These findings indicate that while the model captures robust aging patterns across atlases, as demonstrated in AD, the downstream discriminative utility in PD is influenced by anatomical granularity. Overall, MT-ReBA learns generalizable, whole-brain regional representations that capture anatomical heterogeneity and support the study of regional aging across different neurodegenerative diseases.**(p. 8, Section 4.2.4)**Responses to Weakness 3 and Weakness 4
W3
Reviewer comment. The optimization procedure and evaluation uncertainty require further justification. The Stage 2 optimization uses separate real-image and mixed-image passes, with explicit gradient routing to prevent mixed-image losses from updating the backbone directly. While this design is understandable, the paper does not establish that separate optimization steps are necessary or superior to an implementation that combines the objectives while preserving the intended gradient restrictions. An ablation comparing these alternatives, including training stability and computational cost, would help justify the additional complexity.
Response.
The main purpose of separate optimization is to control how real and synthetic images affect gradients in different network modules, rather than to add independent training stages. Losses on real MRI update the backbone and regional branches. Losses on mixed MRI update only the regional branches, with BatchNorm statistics frozen during the mixed-image forward pass. This prevents splicing artifacts from interfering with the pretrained global age representation. We further tested the need for joint optimization through an ablation of the global and regional objectives. With only the global objective, Splice-Error was 18.95 years and SW5 was 6.0%. With only the regional objective, global MAE worsened to 24.78 years. Joint optimization achieved a global MAE of 3.10 years, a Splice-Error of 8.13 years, and an SW5 of 62.0%. This demonstrates that the two types of supervision are complementary. (p. 19, Table 9)
W4
Reviewer comment. The training dataset is modest relative to the available pretraining resources, and external generalization is not established: the pretraining dataset is rather small (<4k samples) while much larger-scale datasets are now available (i.e. OpenMind dataset with >100k samples). More importantly, the participant-level split does not establish generalization to an entirely unseen cohort. A leave-one-cohort-out evaluation or independent external validation would help determine whether the learned representations generalize across acquisition protocols and data distributions.
Response.
We added an external generalization experiment using all 561 IXI participants as a single external cohort. They were excluded from training, validation, and parameter selection and used only for the final external evaluation. This tests generalization to an unseen data source. MT-ReBA achieved an MAE of 6.681 ± 0.231 years (95% CI [6.23, 7.14]) and an RMSE of 8.666 years. These were 15.84% and 15.45% lower, respectively, than those of the next-best method, SFCN. It also achieved the highest R² (0.723) and Pearson correlation (ρ = 0.854). These results show that MT-ReBA maintains high prediction accuracy and correlation on a single external cohort, demonstrating good cross-cohort generalization. (p. 18, Appendix F)
Table 8. Generalization to a single external cohort (IXI). MAE uncertainty is based on 10,000 participant-level bootstrap resamples. MAE and RMSE are in years; RMSE, , and are point estimates. Best results for each metric are shown in bold.
\hline \text{Method} & \text{MAE ± SD} & \text{95\\% CI} & \text{RMSE} & R^2 & \rho \\\\ \hline \text{y-Aware InfoNCE (Dufumier et al., 2021)} & 9.675 \pm 0.326 & [9.04, 10.32] & 12.358 & 0.438 & 0.743 \\\\ \text{SFCN (Peng et al., 2021)} & 7.938 \pm 0.272 & [7.41, 8.48] & 10.250 & 0.613 & 0.802 \\\\ \text{InfoNCE (Barbano et al., 2023)} & 10.258 \pm 0.358 & [9.57, 10.97] & 13.271 & 0.351 & 0.713 \\\\ \text{RNC (Zha et al., 2023)} & 10.390 \pm 0.341 & [9.73, 11.06] & 13.148 & 0.363 & 0.753 \\\\ \text{Triamese-ViT (Zhang et al., 2025)} & 18.667 \pm 0.572 & [17.57, 19.79] & 23.028 & -0.953 & 0.131 \\\\ \text{Anatomical} & 9.459 \pm 0.323 & [8.84, 10.10] & 12.107 & 0.460 & 0.791 \\\\ \text{MT-ReBA(Ours)} & \mathbf{6.681 \pm 0.231} & [6.23, 7.14] & \mathbf{8.666} & \mathbf{0.723} & \mathbf{0.854} \\\\ \hline \end{array}$$
Responses to Weakness 1
Thank you very much for taking the time to review and for your support. We try our best to address your questions as follows. Changes are marked in the revised PDF for easy reference.
W1
Reviewer comment. The problem of regional brain age estimation has been tackled in the neuroimaging literature but always suffer from the same issue: there is no proper ground-truth and the concept of regional biological age is ill-defined. While the authors propose a synthetic way to mix brain regions across subjects in order to artificially introduce brain regional age diversity, it is impossible to assume that brain regions chronological age equal regional biological age. As such, the evaluation metrics are always biased and do not measure whether the model is actually learning this "biological regional brain age". There are only weak proxy of such measures (i.e. the proposed regional age ranking accuracy).
Response.
Regional brain-age estimation is an emerging field, and it indeed lacks clear, unified definitions, directly observable biological ground-truth labels, and universally accepted evaluation criteria. Without regional ground-truth, establishing a reliable evaluation framework remains the primary open challenge. Our aim is to develop a systematic framework for regional brain-age learning and evaluation through weak supervision and multidimensional validation.
Crucially, as the reviewer noted, all existing works in this field face this exact limitation. For instance, Popescu et al. (2021, Frontiers in Aging Neuroscience) validated voxel-level predictions indirectly through test-retest reliability and disease-related differences. Gianchandani et al. (2024, MELBA) relied on voxel-level regional age differences between healthy and dementia patients. Fong et al. (2025, IEEE EMBC) assessed representations via hemispheric symmetry and cognitive associations. None of these studies possess direct measures or objective ground-truth to establish absolute validity; instead, they all rely on indirect, weak proxy evidence. Therefore, metrics like our RankAcc are not intended to be perfect ground-truth measures, but rather necessary proxies in the absence of absolute labels.
To address the inherent bias of any single proxy metric, we expanded and strengthened our evaluation into a rigorous multidimensional validation framework. These independent experiments converge to support that MT-ReBA learns anatomically localized, age-related representations:
1.Validity of weak supervision: Mixed-effects models on 74,700 donor comparisons yielded test-set slopes of 0.267–0.334, with zero-dose controls showing no shift (pp. 9–10, Sec 4.2.6).
2.Anatomical specificity: ROI occlusion on unspliced MRI yielded a localization accuracy of 75.0% (chance level: 2.1%, p = 0.0005) (pp. 21–22, App N).
3.Natural aging & cross-atlas robustness: In 277 independent HCs, all HO48 and AAL3 regions passed FDR correction (p. 7, Sec 4.2.3).
4.Disease relevance: Regional features significantly increased AD classification AUC (+0.128 for HO48, +0.120 for AAL3, p < 0.0005)(pp. 7–9, Secs 4.2.4–4.2.5).