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Under review as a conference paper at ICLR 2027

Are Foundation Models Enough for Data-Scarce Functional Connectivity Diagnosis? Revisiting Task-Specific Learning with BrainLRR

Abstract

Functional connectivity (FC) derived from Resting-state fMRI captures disruptions in brain-network organization, making FC-based classification a promising non-invasive approach to disease diagnosis. However, FC classification is constrained by small, heterogeneous, and noisy datasets. Whether foundation models (FMs) can transfer effectively under such label scarcity remains unclear. We benchmark general-purpose LLMs, vision backbones, and neuroimaging FMs under zero-shot, few-shot, and target-dataset fine-tuning protocols. Learned alignment improves LLM-based classification from a mean AUROC of 53.3 to 70.8, but encoder-only models using the same learned FC representation achieve comparable performance, suggesting pretrained language representations do not provide a consistent advantage. We therefore introduce Brain Low-Rank Regularization (BrainLRR), a compact task-specific model combining region-of-interest (ROI)-profile masking with low-rank regularization of subject representations. Across four classification tasks spanning Autism spectrum disorder (ASD), Parkinson’s disease (PD), and Alzheimer’s disease (AD), BrainLRR demonstrates favorable sample efficiency and outperforms the evaluated FM baselines across the examined data-scarcity settings. The design components of BrainLRR also generalize to other architectures, improving BrainNetCNN across all four tasks. These results show that, in data-scarce FC classification, FM utility depends on modality alignment and pretraining domain, while carefully designed task-specific models can provide an effective alternative.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Functional connectivity, resting-state fMRI, data-scarce learning, foundation models, low-rank regularization, ROI-profile masking, brain-disorder classification, trustworthy medical AI.

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_3VtdOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This work proposed BrainLRR to combine ROI-profile masking with low-rank regularization of subject representations. It is well-motivated, as reported and substantiated across four clinical tasks.

Critical strengths

The motivation is clear, and the method is evaluated on four clinical tasks, together with a BrainNetCNN generalization study.

Critical weaknesses
  • BrainLRR performs worse than several competing methods on the PPMI PD-versus-HC task, but the paper does not adequately analyze this result.
  • The paper does not sufficiently explain the Bernoulli masking choice or the use of the nuclear norm as a surrogate for rank.
Questions for authors

1- The colored boxes in Figure 2 appear to represent entities with different physical meanings. For example, the pink box seems to denote both the MLP classifier and the LRR loss. Please clarify the meaning of each color and box in the figure or caption.

2- In Eq. (1), please explain why the binary mask mm is sampled from a Bernoulli distribution. The authors should clarify how the Bernoulli parameter is determined and whether alternative masking strategies were considered.

3- In Eq. (6), the authors should provide a clearer mathematical justification for using the nuclear norm. Directly minimizing rank⁡(X)\operatorname{rank}(X) is an NP-hard and non-convex problem. Under suitable conditions, the nuclear norm, defined as the sum of singular values, serves as the convex envelope of the rank function over the unit spectral-norm ball, analogous to the role of the L1L_1 norm as a convex relaxation of the L0L_0 norm. This relaxation makes low-rank recovery computationally tractable. Please explain this rationale and clarify the conditions under which the nuclear norm is used as a surrogate for rank.

4- Under the “PPMI: PD versus HC” setting in Table 1, BrainLRR performs substantially worse than several SOTA methods. The authors should provide additional analysis and discussion of this result, including possible explanations related to dataset characteristics, preprocessing, hyperparameters, or statistical significance.

5- The tables appear incomplete, and their formatting is inconsistent. For example, in Table 1 under “ADNI: NC versus AD,” the best AUROC result is not highlighted in bold. Please carefully check all tables and ensure that the reported metrics, best results, and formatting conventions are complete and consistent.

6- In Table 2, 11 baseline methods are compared on ABIDE, whereas only the “BNT-style” method is included for the other three datasets. This limited comparison is insufficient to robustly demonstrate the effectiveness and generality of BrainLRR. Please include a broader and more consistent set of baseline methods across all datasets, or provide a clear justification for the current selection.

Reviewer_Y7gVOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
2
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2
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Paper summary

BrainLRR combines ROI-profile masking and classwise nuclear-norm regularization with a BNT backbone for data-scarce functional-connectivity diagnosis. The paper compares this approach with foundation-model adaptations across four diagnostic tasks.

Critical strengths
  1. Encoder-only and pretrained-versus-scratch controls help separate adaptation quality from pretraining benefits.
  2. Matched backbone ablations, label-scarcity sweeps, and transfer to BrainNetCNN broaden the empirical assessment.
Critical weaknesses
  1. The methodological distinction is unclear. Eq. (6) closely follows the classwise-minus-global nuclear-norm objective of OLÉ (Lezama et al., CVPR 2018), without its norm floor. This closest regularizer is neither discussed nor compared; combining it with a BNT backbone and row masking needs stronger justification.
  2. Reported results contain substantive inconsistencies. In Table 2, FBNETGNN accuracy (68.0) exceeds both sensitivity (64.7) and specificity (62.4), impossible on the stated fixed binary test partition. Table 10 also reverses the PD and NC-AD backbone-effect estimates relative to Appendix C.5.
  3. The foundation-model comparison remains adaptation-dependent. BrainSegFounder receives depth-repeated FC images (Fig. 8), while BrainLM search trials use only five epochs without convergence evidence or a clear final training budget (Appendix B). The reported gaps do not establish performance under well-converged, modality-appropriate adaptation.
Questions for authors
  1. What improvement remains over OLÉ with the same backbone and masking?
  2. Can corrected tables and per-seed predictions reconcile the metric and paired-effect inconsistencies?
  3. Do the foundation-model gaps persist with validated convergence and modality-appropriate inputs?
2 comments

Q1: We thank the reviewer for pointing to this closely related work. Our regularizer adopts the OLÉ objective (Lezama et al., CVPR 2018), including its per-class norm floor (Δ = 1); we have revised the manuscript to state this explicitly Sec 3.6 and related Work to state this explicitly and to credit OLÉ for the formulation. Our contribution is not a new objective but a training pipeline for data-scarce FC diagnosis that combines input-level ROI-profile masking with this geometry-aware loss, guiding the model to separate diagnostic classes from limited data. Individual FC patterns vary substantially across subjects and acquisition sites, so models trained on limited clinical samples can overfit these non-diagnostic variations. LRR counters this with a low-rank inductive bias: subjects sharing a diagnosis are encouraged to occupy compact embedding subspaces, while within-class heterogeneity is retained. ROI-profile masking is complementary, regularizing the ROI dimension at the input level, whereas LRR regularizes the subject dimension in embedding space. Ablations confirm both contributions: on ABIDE, removing ROI masking lowers AUROC from 79.1 to 75.9, and removing LRR lowers it to 77.9 (Table 3). Both components are not specific to BNT, adding to BrainNetCNN improves AUROC on four tasks(Table11).

Q2: Metric and paired-effect inconsistencies. We thank the reviewer for identifying these issues. The FBNETGNN results in Table 2 were cited from Kan et al. (NeurIPS 2022, Table 1). We acknowledge the inconsistency among the originally reported accuracy, sensitivity, and specificity. To address this, we re-ran FBNETGNN with the authors' official implementation on the same ABIDE data and test split (5 runs; all metrics from the final epoch, as for our other models): AUROC 74.4 ± 1.7, Acc 69.0 ± 2.6, Sens 68.9 ± 6.8, Spec 69.1 ± 3.0. Table 2 is updated accordingly.

Paired-effect inconsistencies. Thank you for highlighting this issue. Table 2 reports the main evaluation, whereas Table 10 presents a separate matched evaluation on split 101. Its bootstrap intervals quantify test-subject sampling uncertainty conditional on that split and the fitted models. For NC–AD, the main evaluation favors BNT over BrainLRR (93.5 ± 1.6 vs. 91.6 ± 1.9 AUROC), corresponding to a BrainLRR–BNT difference of −1.90 points. The additional split-101 evaluation instead yields +3.32 points (95% BCa CI: [0.87, 6.91]; 65 test subjects). This interval supports a positive difference within that evaluation, but does not establish a consistent advantage across splits and runs. Both PD and NC–AD have small test sets (37 and 65 subjects, respectively). Limited sample sizes, together with potential heterogeneity across the four pooled PD cohorts, may contribute to variability. We have clarified the dataset’s performance in Section 4.2, paragraph 4 and Supplementary C5.

Q3.Foundation-model convergence and modality alignment. We thank the reviewer for raising this concern. The original 10-epoch fine-tuning budget was chosen for computational feasibility and is specified in Appendix B. To assess whether longer training would close the performance gap we extended BrainLM fine-tuning to 50 epochs with validation-based checkpoint selection. AUROC increased by 4.2 points on NC–AD FC and 1.4 points on PD time series, but decreased by 2.9, 0.6, and 3.3 points on ABIDE time series, ABIDE FC, and NC–MCI FC, respectively. All configurations remained far below BrainLRR on their corresponding tasks. Thus, longer training benefited some configurations but did not close the observed performance gaps under the evaluated settings.

For modality-appropriate inputs concern, We considered each model’s input requirements and evaluated closer alignment where feasible. In our Table1, we evaluated BrainLM with ROI time series to better match its pretraining input. AAL-424 was unavailable for ABIDE, so CC200 was used. On PD, BrainLM using its original AAL-424 atlas achieved 56.2 ± 3.0 AUROC, versus BrainLRR's 68.0 ± 2.3 using CC200. Additionally, the LLaMA adapter and matched FC encoder-only classifier achieved the same rounded four-task mean AUROC (70.8), Thus, the aggregate improvement is matched by the learned FC encoder alone, with no additional aggregate advantage from LLaMA in this configuration.

Overall, foundation-model gaps still persist under validated convergence and modality-appropriate inputs.

Thank you for the detailed response and additional experiments. However, the rebuttal does not explicitly reconcile the conflicting PD and NC–AD paired-effect estimates between Table 10 and Appendix C.5 or provide the requested per-seed predictions. Furthermore, extending BrainLM training to 50 epochs does not by itself establish convergence, and the concern about BrainSegFounder’s depth-repeated FC inputs remains unaddressed. Thus, the broader claim that foundation-model performance gaps persist under validated convergence and modality-appropriate adaptation remains insufficiently supported. These unresolved issues affect the reliability and scope of the conclusions, so I will maintain my original score.

Reviewer_X6e9OpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
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Paper summary

This paper tests whether foundation models (LLMs, vision models and neuroimaging models) transfer to FC-based disease classification with little labeled data, and finds that they mostly do not. A matched encoder-only model does as well as Llama with an FC adapter (both 70.8 mean AUROC). The authors then propose BrainLRR, a BNT-style model with ROI masking as data augmentation, clustering from learned centers, and a low-rank regularizer. It reaches 81.1 mean AUROC across ABIDE, PD and two ADNI tasks.

Critical strengths
  • Very sensible results, and the controlled Llama comparison is a clean experiment.
  • The data-efficiency plot (Figure 3) is very good. With 25% of ABIDE, BrainLRR already beats every foundation model trained on all of it.
  • Simple and cheap method, and the components also help BrainNetCNN (Table 12).
Critical weaknesses
  • How the FC was generated is not described. The paper says Pearson correlation, but Appendix A only says "standard rs-fMRI preprocessing".
  • The analysis varies the number of subjects but not the amount of temporal data per subject. With less data the FC is a worse estimate (Birn et al., NeuroImage 2013).
  • Static FC does not account for the temporal profile of the data, so the conclusions about foundation models should be limited to static-FC inputs.
  • It is unclear whether the FC-as-text approach can work, since a short text summary of a 200×200 matrix loses most of the structure. It would be better framed as a lower bound.
  • Limited method novelty. The backbone and readout come from BNT (Kan et al., NeurIPS 2022), and the low-rank loss (Eq. 6) is essentially the OLÉ loss (Lezama et al., CVPR 2018), which is not cited.
  • Results come from a single fixed split.
Questions for authors
  • How was the FC generated? Please report preprocessing, TR and number of time points per dataset.
  • Can you truncate the time series before computing FC and show how performance changes?
  • How does your loss differ from OLE?
1 comment

Q1.FC generation (preprocessing, TR, time points). Thank you for highlighting this omission. Across the three datasets, rs-fMRI preprocessing includes motion correction, spatial registration, nuisance regression, and temporal filtering (0.01–0.1 Hz), with dataset-specific implementations. We extract ROI-level BOLD time series using the CC200 atlas and compute pairwise Pearson correlations to construct 200 × 200 FC matrices. We have expanded Appendix A with dataset-specific preprocessing details, acquisition TRs, and time-point counts to ensure reproducibility.

Q2: Temporal truncation experiments. We thank the reviewer for this valuable suggestion. While BrainLRR focuses on subject-level classification using static FC rather than longitudinal disease progression or temporal dynamics, investigating the effect of recording duration is valuable.

Following the reviewer's suggestion, we conducted additional experiments on ABIDE by truncating each subject's ROI time series to the first T∈{25,50,75,100}T \in \{25,50,75,100\} time points, recomputing Pearson FC matrices, and retraining BrainLRR and the matched BNT baseline using identical training settings (five seeds per configuration). As expected, shorter recordings produced less consistent FC estimates, with correlation to full-scan FC decreasing from 0.89 (T=100T=100) to 0.56 (T=25T=25). Despite this reduction in FC reliability, BrainLRR consistently outperformed BNT at every evaluated scan length, including the shortest recording, and achieved 78.6 versus 75.5 AUROC on full-length scans. These results demonstrate that BrainLRR maintains its advantage over the matched backbone under reduced temporal sampling. We have included this analysis in the supplementary C10.

Q 3: Our low-rank regularizer adopts the OLÉ objective, originally introduced to regularize CNN image features. In small-sample functional-connectivity (FC) diagnosis, high-dimensional inputs and limited labeled subjects make learned representations vulnerable to fitting subject-specific variation unrelated to diagnosis. We therefore apply OLÉ to graph-level subject embeddings, introducing a soft prior that encourages low-dimensional structure within diagnostic groups and separation across groups. This complements ROI-profile masking: masking promotes robustness to regional input perturbations, while the low-rank term regularizes embedding geometry across subjects. Together, they provide complementary constraints on regional dependence and cross-subject structure when diagnostic supervision is limited.

The ablation in Table 3 supports the incremental benefit of each component. We have revised the manuscript in Section 3.6 to cite OLÉ explicitly and clarify that our contribution lies in its adaptation to FC graph embeddings and its integration with ROI-profile masking within the diagnosis framework.

Comments on the paper

1 comment

Q1. Figure 2 clarity. Thank you for pointing out the ambiguity. The similar colors were intended for visual grouping rather than indicating identical functions. We have revised Figure 2 to use distinct colors for the MLP classifier and LRR loss, and clarified the meaning of the components and connections in the caption.

Q2. Bernoulli masking. We use Bernoulli sampling to independently mask complete ROI connectivity profiles during training, reducing over-reliance on individual regions while preserving the remaining network information. The masking probability (p) controls the perturbation strength and was examined through a sensitivity analysis (Fig. 4), with (p=0.4) giving the best ABIDE performance. We also evaluated symmetric versus row-only masking (Table 10). On ABIDE, row-only masking achieved higher AUROC (78.58 vs. 75.94), suggesting that preserving connectivity information in unmasked profiles is beneficial. We have clarified this motivation and the masking alternatives in Section 3.3 and Section 4.4.

Q3. We thank the reviewer for this suggestion. Rank counts the nonzero singular values of a matrix, whereas the nuclear norm sums them. Replacing rank with the nuclear norm therefore parallels using ℓ₁ as a surrogate for ℓ₀ sparsity. More precisely, the nuclear norm is the tightest convex lower approximation to rank on matrices whose largest singular value is at most one, and on matrices whose largest singular value is at most MM the same holds for ∥⋅∥∗/M\|\cdot\|_*/M (Recht et al., 2010, Theorem 2.2 and the subsequent discussion).

We use this established surrogate to regularize graph-level embeddings. The classwise terms penalize each class’s nuclear norm, encouraging compact low-dimensional class subspaces, while the whole-batch term encourages the batch to span a high-dimensional space. By subadditivity, the combined objective is non-negative and reaches zero only when class subspaces are mutually orthogonal. The per-class floor Δ = 1 prevents the classwise penalty from being reduced by trivially shrinking the features.

The complete objective remains nonconvex and nonsmooth, but supports practical SVD-based subgradient updates. Exact rank-recovery guarantees require additional conditions on the measurement process, such as the restricted isometry property; Our setting has no such target: the regularizer only needs to bias the embeddings toward compact, mutually orthogonal class subspaces, and the properties it relies on for this (singular-value shrinkage and nuclear-norm subadditivity) hold without additional assumptions. We have clarified this in section 3.6.

Q4. PD performance and uncertainty. The FC encoder-only control achieves a higher AUROC than BrainLRR (71.0 vs. 68.0), indicating that a lower-capacity encoder remains competitive in this setting. Our PD dataset is the smallest in the study, comprising 183 subjects (110 PD and 73 HC), with only 37 held-out test subjects. Given the limited publicly available data, we pooled four cohorts (Tao Wu, NEUROCON, ds000245, and ds005892), introducing potential heterogeneity in acquisition protocols and subject characteristics. The small sample size and cross-cohort heterogeneity may contribute to performance variability and limit the precision of model comparisons. We have clarified the PD's dataset’s performance in Section 4.2, paragraph 4.

Q5. Table formatting. Thank you for identifying these presentation issues. We have carefully reviewed all tables and correct missing boldface, inconsistent formatting, and metric highlighting, including the ADNI NC–AD results in Table 1.

Q6. We thank the reviewer for this suggestion. In Table 2 we prioritized a matched BNT-style backbone across all four tasks to isolate the effects of ROI-profile masking and LRR to test the generalizability of our proposed components. Therefore We also additionally evaluated Portability to other backbones, and tested on BrainNetCNN across all four tasks (Table 11), observing AUROC improvements of 0.43–4.66 points after incorporating our components, supporting portability beyond transformer backbones. To strengthen baseline coverage under other three tasks, we extended the comparison to GBT and BrainNetCNN using matched FC inputs and data splits, and updated Table 2.

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