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Under review as a conference paper at ICLR 2027

Population-Regularized Learning of Individualized Brain Effective Connectivity

Abstract

Brain effective connectivity (EC) characterizes directed interactions among brain regions, but individualized EC estimation remains challenging with limited and noisy resting-state functional magnetic resonance imaging (rs-fMRI) data. Although population-level connectivity patterns shared among related subjects can provide stable guidance, existing population-informed methods rely largely on global priors that overlook pairwise inter-subject relevance. We propose PR-EC, a population-regularized framework for individualized EC estimation. PR-EC constructs a multimodal similarity graph that encodes pairwise inter-subject relevance, and aggregates the EC estimates of each target’s most relevant neighbors into a subject-specific population reference. This reference provides stable population guidance and is used to refine each target subject’s EC estimate. Because data-quality variations can affect EC edges differently, PR-EC further introduces a quality-control (QC)-aware refinement that adaptively modulates the contribution of the population reference to each edge. Theoretical analysis characterizes the trade-off between leveraging cross-subject information and preserving individual-specific connectivity. Extensive experiments on three datasets show that PR-EC improves EC-based disease classification. Cross-cohort analyses further reveal reproducible autism spectrum disorder (ASD)-related EC alterations as biomarkers, including bidirectionally enhanced thalamo-temporal connectivity.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
Graph Representation Learning, Brain Effective Connectivity, Spatiotemporal Learning, Multivariate Time-Series Analysis

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

This paper introduces PR-EC to estimate each person’s effective brain connectivity from resting-state fMRI. It first uses a self-supervised spatiotemporal attention model to estimate connectivity. It then combines estimates from similar participants to create a reference for each person. Finally, a refinement network uses this reference and data-quality information learned from the training set to adjust individual connections. The authors test disease classification on ABIDE-I, ABIDE-II, and ADHD200 and identify ASD-related connectivity differences that appear in both ABIDE datasets.

Critical strengths

1.The motivation is reasonable: subject-level EC from short, noisy rs-fMRI is unstable, and similarity-weighted borrowing from neighbors is a sensible alternative to a single global prior. The leakage-aware design deserves credit: references are drawn only from training folds, labels are not used for graph construction, and QC is not needed at inference.

  1. The cross-cohort analysis requires FDR-significant effects in the same direction in both ABIDE-I and ABIDE-II. That is a more defensible replication criterion than top-k overlap, and the paper candidly reports that top-k overlap is near zero.
Critical weaknesses
  1. The paper never validates EC against any ground truth, such as directed-network simulations or known pathways. Its only evidence is classification.

  2. The classification gains are marginal. On ABIDE-I, PR-EC’s ACC (60.39) is below FSTA-EC (60.86). In the ablation (Table 2), the full model versus no MPR/QSR changes by +0.9, +0.6 and +0.25 ACC across the three datasets, while fold SDs are about 5. On ABIDE-II, MPR alone (61.96) beats the full model (60.62).

  3. There are no significance tests, and only one seed (42) is used.

  4. Absolute performance (~60% ACC on ABIDE) is below what plain Pearson FC with a linear classifier typically reaches, and a plain FC baseline is absent even though FC is an input to the population graph.

  5. The sensitivity analysis was done on test folds, which the authors acknowledge, and window length and epoch counts differ per dataset without a stated selection procedure.

  6. The population reference uses phenotypic information that may be associated with diagnosis. This makes it unclear how much of the classification gain and the reported ASD differences comes from fMRI connectivity versus the additional phenotypes. Please specify the variables used in each dataset, report the proportion of neighbors sharing each subject’s diagnosis, and include an ablation using only age, sex, and site. Comparing group differences before and after refinement would also help assess whether the procedure amplifies diagnosis-related patterns.

  7. Equations 46–47 use minibatch-averaged attention for feature fusion during training, whereas individualized EC is extracted from subject-specific attention. Individual attention therefore contributes to reconstruction through the batch average, rather than serving as a separate connectivity matrix for each subject. Please explain why this training objective supports the interpretation of individual attention as EC and compare it with subject-specific feature fusion.

  8. Appendix B.3, Equations 74–75, appears to reuse A_tar for both the target EC and the perturbation matrix, making the definitions inconsistent with Equation 8 in the main text. Please correct the notation and clarify which formulation the implementation uses.

Questions for authors
  1. Which phenotypic variables were used on each dataset? What fraction of each subject’s top-K neighbors share its diagnosis, compared with the base rate? Please rerun classification and the ASD replication analysis using only age, sex and site in the phenotypic view.
  2. Please add a plain Pearson-FC baseline, report paired significance tests against FSTA-EC and the no-MPR/QSR variant, and report multiple seeds.
  3. Since training uses the minibatch-averaged W_I, why should the per-subject W read out at inference be subject-specific and directional? 4. Can you validate PR-EC on simulated data with known directed connectivity?
  4. How were window length, stride and epoch counts chosen per dataset? Was any of this done using test folds? Please correct Eqs. 74–75 to match Eq. 8.
6 comments

We sincerely thank the reviewer for their careful evaluation and constructive suggestions. We address each concern below. For clarity, as question number “4” appears twice in the review, we have renumbered the questions sequentially while preserving their original order and content. We appreciate the reviewer’s understanding.

W1 & Q4. Ground Truth Validation of EC

Actually, We have addressed this concern in detail in our response to Reviewer tigW's W1 & Q1, and summarize the key points and findings here. Our original evaluation focused on clinical datasets because individual-level EC ground truth is generally unavailable in real rs-fMRI data, while common simulation datasets lack the phenotypic and QC information required to evaluate the complete MPR/QSR framework. Nevertheless, we agree that the initial EC estimator's directional recovery capability should be independently validated.

Following your suggestion, we conducted additional five-fold out-of-fold experiments on four simulated networks (Sim1–Sim4) from Sanchez-Romero et al. (2019), with pretraining restricted to training subjects and ground truth used solely for evaluation (page 8, lines 385–387 and 423–431; page 9, Table 2).

Table R1. Individual-level directed connectivity recovery on simulated networks.

NetworkDirected AUPRC ↑Sym. AUPRC ↑Direction Acc. ↑F1 ↑SHD ↓
Sim10.82 ± 0.050.74 ± 0.0266.67%0.68 ± 0.084.43 ± 1.36
Sim20.88 ± 0.050.83 ± 0.0475.56%0.73 ± 0.084.45 ± 1.48
Sim30.89 ± 0.040.86 ± 0.0263.89%0.75 ± 0.063.53 ± 1.08
Sim40.78 ± 0.040.74 ± 0.0375.45%0.66 ± 0.0612.45 ± 3.01

The results show that the initial EC estimator achieved directed AUPRC of 0.78–0.89 and direction accuracy of 63.89%–75.56% across four simulated networks, exceeding the 50% chance level. Symmetrization consistently reduced AUPRC, further supporting its directional recovery capability. Furthermore, we conducted an FC-guided MPR experiment on NetSim Sim21, the FC-guided MPR reference improved F1 from 0.58 to 0.66, reduced SHD from 5.90 to 5.02, and increased ground truth strength correlation from 0.22 to 0.37. Together, these results provide complementary ground truth evidence for the initial EC estimator and MPR, beyond downstream classification performance.

W2. Magnitude and Stability of Classification Performance Improvements

We thank the reviewer for highlighting the variation in module-level improvements. We emphasize that PR-EC aims to refine individualized EC representations using population and QC information without diagnostic labels, rather than directly optimizing classification. Accordingly, we report ACC, AUC, SEN, and F1 to assess downstream utility from multiple perspectives, rather than treating classification performance as direct evidence of EC estimation accuracy.

Furthermore, following Reviewer KKzu's suggestion, we conducted additional five-fold inductive experiments (see our response to Reviewer KKzu's Q1 and Table R4), with the initial EC estimator pretrained exclusively on training subjects. Full PR-EC improved mean AUC over Initial EC by approximately 2.1, 1.7, and 3.7 percentage points on ABIDE-I, ABIDE-II, and ADHD200, respectively. Although these gains vary across datasets and their 95% confidence intervals include zero, the inductive evaluation, ground truth connectivity recovery experiments, and clinical results provide complementary evidence for the utility of PR-EC in individualized EC representation learning.

W3 & W4 & Q2. Pearson FC Baseline, Statistical Significance, and Multi-Seed Evaluation

Although PR-EC incorporates Pearson FC as one of the information sources for constructing the multimodal population similarity graph, directly using Pearson FC for disease classification also represents an important baseline comparison. Therefore, we added a Pearson FC + Linear SVM baseline, using the same subjects, data preprocessing, and cross-validation protocol as PR-EC.

To address the concerns regarding statistical significance and random seeds, we further conducted repeated ten-fold cross-validation with five random seeds (1, 3, 10, 42, and 123) on ABIDE-II (975 subjects), the largest dataset in our study. For PR-EC, the complete training pipeline was independently executed for each seed. In addition, based on the corresponding seed-level ten-fold mean results, we performed two-sided paired statistical tests comparing Full PR-EC against FSTA-EC and Initial EC.

Table R2. Multi-seed classification performance on ABIDE-II.

MethodACC (%)AUC (%)p (ACC vs. Full)p (AUC vs. Full)
Pearson FC55.82 ± 1.0157.59 ± 1.74\\
FSTA-EC57.27 ± 2.9961.58 ± 3.820.11730.1962
Initial EC58.36 ± 0.8263.16 ± 1.610.0000710.0167
Full PR-EC60.00 ± 0.8164.80 ± 1.31\\

As shown in Table R2, across five random seeds, Full PR-EC achieved the highest mean ACC (60.00%) and AUC (64.80%), outperforming Initial EC by 1.64 percentage points on both metrics, with statistically significant differences (p = 0.000071 and 0.0167, respectively). It also exceeded Pearson FC by 4.18 and 7.21 points, and FSTA-EC by 2.73 and 3.22 points, respectively, although the latter differences were not statistically significant. These results support the effectiveness of the complete PR-EC framework while characterizing its variability across random initializations.

W5 & Q5. Hyperparameter Selection

Due to space limitations, the original paper did not sufficiently explain the rationale behind some of these choices, and we would like to provide further clarification here. First, the window length and stride were primarily determined by differences in rs-fMRI time-series lengths across datasets. Since scan durations vary among subjects in multi-site datasets, we adapted these settings according to the shortest valid time series after preprocessing in each dataset. This allows subjects with shorter sequences to be included in EC estimation while using overlapping windows to make better use of temporal information from longer recordings. Accordingly, slightly different window lengths and strides were adopted across datasets, rather than being optimized based on test-set classification performance.

The number of training epochs was mainly predetermined based on prior training experience and kept fixed throughout the main experiments. In addition, while reviewing our experimental configurations, we identified a typographical error in Appendix C.6 concerning the number of initial EC pretraining epochs for ABIDE-I. The actual setting was 81 epochs rather than 101 epochs, and we will correct this in the revised manuscript. I sincerely apologize if this has caused any confusion.

The sensitivity analysis presented in Figure 7 was conducted post hoc, after the main experimental configuration had been finalized, and was not used for hyperparameter selection in the main experiments. This analysis was intended solely to examine how model performance varies under different parameter settings, rather than to select the final configuration based on test-fold results.

W6 & Q1. Phenotypic Information and Its Impact on Classification and ASD Connectivity Analyses

We would like to clarify that PR-EC does not use diagnostic labels, symptom scores, or disease-specific questionnaires to construct the population similarity graph. The phenotypic inputs include Sex, FIQ, and PIQ for ABIDE-I/II, and Gender, Age, Full4 IQ, and Handedness for ADHD200. Our existing modality ablation (Figure 6) shows that combining PH and FC improves F1 to 61.10%, compared with PH-only (58.32%) and FC-only (60.92%) on ABIDE-I.

To further address this concern, we analyzed same-diagnosis neighbor proportions against training-set diagnostic base rates (Table R3). Higher diagnostic agreement among neighbors does not imply label usage, but may reflect disease-related similarities captured by non-diagnostic features. We also conducted an additional Age/Sex/Site phenotypic ablation across all three datasets, keeping other configurations unchanged, to assess the influence of phenotypic feature selection. Following the reviewer's suggestion, we have added the Age/Sex/Site phenotypic ablation and neighbor diagnostic consistency analysis to Appendix C.7 of the revised manuscript.

Table R3. Neighbor diagnosis consistency and classification performance under different phenotypic configurations.

DatasetPH settingSame-diagnosis neighbors (%)Base rate (%)ACC (%)AUC (%)
ABIDE-IOriginal52.2950.2860.39 ± 5.1266.85 ± 4.32
Age/Sex/Site52.1450.2859.60 ± 4.7064.60 ± 3.83
ABIDE-IIOriginal53.9650.1360.62 ± 5.1466.83 ± 3.92
Age/Sex/Site53.9050.1360.00 ± 4.6666.33 ± 3.83
ADHD200Original56.1754.1658.62 ± 6.3661.21 ± 5.85
Age/Sex/Site57.2154.1658.24 ± 6.2260.21 ± 6.93

As shown in Table R3, same-diagnosis neighbor proportions exceed the training-set base rates by 2.01–3.83 percentage points under the original setting. Replacing the original phenotypic features with Age/Sex/Site changes these proportions by only −0.15 to +1.04 points, suggesting that the observed diagnosis-related clustering among neighbors does not strongly depend on additional phenotypic features, such as IQ, in the original configuration. Meanwhile, the simplified setting reduces AUC by 2.25, 0.50, and 1.00 points across the three datasets, indicating that the original phenotypic features provide some downstream predictive benefits despite their limited influence on neighbor diagnostic consistency.

Furthermore, in response to the reviewer's comments, we examined the dependence of ASD-related connectivity findings on phenotypic configurations by comparing Initial EC, Original PH, and Age/Sex/Site in terms of between-group differences in connectivity and cross-cohort replication on ABIDE-I and ABIDE-II.

Table R4. ASD-related group differences and cross-cohort replication before and after refinement.

EC representationABIDE-I mean |g|ABIDE-II mean |g|Replicated edgesASD-enhancedASD-reduced
Initial EC0.091580.09927202101101
Full PR-EC (Original PH)0.091590.10221213111102
Full PR-EC (Age/Sex/Site)0.091580.10212210109101

The results show that Initial EC, Original PH, and Age/Sex/Site identified 202, 213, and 210 cross-cohort replicated connections, respectively. Importantly, Age/Sex/Site retained 210 of the 213 connections (98.59%) identified under Original PH, all with consistent effect directions. The remaining three connections also showed no direction reversal but narrowly missed the FDR significance threshold in ABIDE-II. Moreover, mean absolute effect sizes remained nearly identical across the two refined configurations. These results support the robustness of ASD-related connectivity findings to phenotypic feature selection.

Reviewer_KKzuOpenReview ↗
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Paper summary

The paper proposes PR-EC to improve individualized brain effective connectivity estimation from limited and noisy rs-fMRI data. It combines multimodal population reference construction (MPR) with QC-aware self-supervised refinement (QSR). Experiments on three datasets show improved disease classification, while ablations indicate dataset-dependent gains. Cross-cohort analyses identify replicated ASD-related connectivity alterations.

Critical strengths
  1. The paper addresses an interesting and important problem: improving individualized effective connectivity estimation from limited and noisy rs-fMRI data.

  2. The proposed components are clearly presented and well motivated, with distinct roles for population reference construction and QC-aware refinement.

Critical weaknesses
  1. The necessity of the manually specified QC-guided targets and perturbation procedures is not fully established. A comparison with an end-to-end baseline that learns to aggregate neighboring subjects’ information directly for downstream prediction would help clarify the value of these intermediate design choices.

  2. The paper would benefit from an analysis of when neighboring subjects help or hurt performance. Identifying the characteristics of neighbors that cause negative transfer would clarify when population regularization is beneficial and when it may distort individual-specific connectivity patterns.

Questions for authors

The paper states that the initial EC estimator is pretrained on all subjects without diagnostic labels, which appears to include the held-out test subjects. Could the authors provide the detailed pretraining protocol and clarify whether the reported evaluation should therefore be considered transductive? Please also report results under a strictly inductive protocol, with the estimator pretrained only on the training subjects within each cross-validation fold.

3 comments

Thank you very much for your detailed and thoughtful response and for highlighting these two key issues. To address these concerns, we conducted the following additional control experiments and analyses.

W1. The Role of QC-Guided Targets and Perturbation-Based Training

We would like to clarify that the edge-specific QC-associated patterns in QSR are learned rather than manually specified. Specifically, they are estimated through edge-wise ridge regression using QC measures and initial EC, and subsequently used to construct self-supervised targets and structured perturbations (Section 4.3, pages 6–7).

Importantly, PR-EC aims to refine individualized EC representations without diagnostic labels, rather than directly optimize disease classification. MPR and QSR separately construct population references and perform QC-guided refinement. Given the lack of individual-level EC ground truth in clinical datasets, we follow prior studies (Jun et al., 2020; Abraham et al., 2017) in using classification to assess downstream utility. Furthermore, as detailed in our response to Reviewer tigW's W1 & Q1, additional simulations on four networks (Sanchez-Romero et al., 2019) achieved a directed AUPRC of 0.78–0.89 for the initial EC estimator, providing direct evidence of directional recovery.

  1. Comparison with End-to-End Neighbor Aggregation: Following the reviewer’s suggestion, we added an End-to-End Neighbor Attention (E2ENA) baseline, which jointly optimizes neighbor attention and classification using diagnostic labels, without QSR, under the same training configuration as PR-EC.

    Table R1. Comparison with End-to-End Neighbor Aggregation (10-fold mean ± std, %).

    DatasetMethodACCSENAUCPREF1
    ABIDE-IFull PR-EC60.39 ± 5.1270.50 ± 13.8366.85 ± 4.3255.83 ± 4.8761.73 ± 6.89
    E2ENA61.20 ± 4.2655.87 ± 17.7567.35 ± 4.9360.19 ± 7.5055.49 ± 10.77
    ABIDE-IIFull PR-EC60.62 ± 5.1469.69 ± 7.8866.83 ± 3.9257.52 ± 5.3362.61 ± 3.91
    E2ENA60.71 ± 4.2558.89 ± 12.4965.66 ± 3.0958.61 ± 4.3558.07 ± 7.28
    ADHD200Full PR-EC58.62 ± 6.3657.50 ± 20.1761.21 ± 5.8545.83 ± 6.9847.78 ± 11.11
    E2ENA59.26 ± 5.7054.29 ± 10.8161.11 ± 6.6544.74 ± 5.6248.37 ± 5.89

    The results indicate that directly supervised neighbor aggregation is a viable alternative strategy, with mean AUC values broadly comparable to those of Full PR-EC. E2ENA performs slightly better on ABIDE-I, whereas PR-EC achieves marginally higher AUC on ABIDE-II and ADHD200. Meanwhile, PR-EC attains higher mean SEN across all three datasets and higher F1 scores on both ABIDE-I and ABIDE-II. This comparison suggests that, despite their different optimization objectives, PR-EC can achieve competitive downstream classification performance without using diagnostic labels to train its EC refinement module.

  1. Ablations of QC-Guided Target Correction and Perturbation Restoration: To further examine the contributions of these two intermediate designs, we conducted two additional ablation experiments.

    • w/o QC Target Correction: We set the target correction coefficient to zero, reducing the self-supervised target to the initial EC while retaining QC-association estimation and structured perturbation restoration training.
    • w/o Perturbation Restoration: We retained the QC-guided target and removed the structured perturbation restoration training branch.

    Both ablations kept MPR, the QSR network architecture, and all other training configurations unchanged.

    Table R2. Ablation of QC-guided target correction and perturbation restoration (10-fold mean ± std, %).

    DatasetMethodACCSENAUCPREF1
    ABIDE-IFull PR-EC60.39 ± 5.1270.50 ± 13.8366.85 ± 4.3255.83 ± 4.8761.73 ± 6.89
    w/o Restoration61.43 ± 5.7363.75 ± 16.7167.30 ± 4.5557.95 ± 5.6059.38 ± 9.99
    w/o QC Target Correction60.97 ± 4.2067.31 ± 15.0565.26 ± 4.2457.09 ± 4.6460.72 ± 7.36
    ABIDE-IIFull PR-EC60.62 ± 5.1469.69 ± 7.8866.83 ± 3.9257.52 ± 5.3362.61 ± 3.91
    w/o Restoration59.39 ± 3.0563.02 ± 12.8765.11 ± 4.1957.31 ± 4.1658.97 ± 5.04
    w/o QC Target Correction60.51 ± 4.7968.60 ± 7.9166.56 ± 4.4457.50 ± 5.1162.16 ± 3.79
    ADHD200Full PR-EC58.62 ± 6.3657.50 ± 20.1761.21 ± 5.8545.83 ± 6.9847.78 ± 11.11
    w/o Restoration58.88 ± 7.1254.64 ± 22.4260.73 ± 6.2644.98 ± 5.8046.22 ± 12.38
    w/o QC Target Correction60.28 ± 4.2550.71 ± 22.5260.99 ± 6.1245.09 ± 5.7045.13 ± 12.14

    As shown in Table R2, removing QC target correction reduces AUC by 1.59, 0.27, and 0.22 percentage points on ABIDE-I, ABIDE-II, and ADHD200, respectively, with lower SEN and F1 across all three datasets. Removing perturbation restoration reduces SEN by 6.75, 6.67, and 2.86 points and F1 by 2.35, 3.64, and 1.56 points, respectively. These results support the contributions of both QSR components, particularly to SEN and F1. We appreciate the reviewer's valuable suggestion and have included these additional QSR ablations in Appendix C.6 of the revised manuscript.

W2. Effectiveness of Population Neighbors and Potential Negative Transfer

We thank the reviewer for this important observation. We agree that population references may be less beneficial when neighboring subjects have dissimilar connectivity patterns or poor data quality, consistent with our analysis in Proposition 4.1.

To investigate this concern, we conducted an additional neighborhood-based subgroup analysis using the original ten-fold cross-validation. With Top-K = 20 fixed, we stratified subjects by weighted neighbor FC similarity and mean FD, using training-fold medians as thresholds and selecting neighbors exclusively from training subjects. We then compared the AUC gains of MPR-only over Initial EC and Full PR-EC over MPR-only within matched test subgroups.

Table R3. Changes in AUC under different neighborhood conditions.

DatasetComparisonHigh FC matchLow FC matchLow neighbor FDHigh neighbor FD
ABIDE-IMPR − Initial+0.11−0.25−0.39−0.43
Full − MPR+0.86+1.18+0.91+1.05
ABIDE-IIMPR − Initial+0.39−2.08+0.20−1.50
Full − MPR+0.19+2.75+0.99+1.06
ADHD200MPR − Initial+0.96+0.34+1.44−0.86
Full − MPR+0.20+0.35−0.61+1.18

The results indicate that MPR's benefits depend on neighbor similarity and data quality. For example, on ABIDE-II, MPR-only improves AUC by 0.39 points for high FC match subjects but reduces it by 2.08 points for low FC match subjects; similarly, higher neighbor motion is associated with lower gains across all three datasets. Importantly, QSR partially mitigates these unfavorable effects, improving AUC over MPR-only by 2.75 points in the low FC match subgroup of ABIDE-II and 1.18 points in the high neighbor FD subgroup of ADHD200, suggesting that QSR can, to some extent, improve the utilization of population references under these conditions. Although these gains are not universal, the observed trends are consistent with the structural mismatch–variance trade-off in Proposition 4.1 and highlight the value of selective population reference refinement.

Q1. Initial EC Pretraining Protocol and Inductive Evaluation

We thank the reviewer for raising this important concern. We agree that clearly specifying the data used during pretraining is essential for assessing generalization. As Reviewer tigW raised a similar concern (W2 & Q2(3)), we provide further details in our response to that reviewer and briefly clarify the rationale behind our original experimental design below.

Our original experiments used a staged training strategy. In the first stage, following the self-supervised spatiotemporal reconstruction approach used in FSTA-EC (Xiong et al., 2025), we pretrained a shared initial EC estimator on unlabeled rs-fMRI time series from the entire cohort, without using diagnostic labels. Because pretraining included unlabeled validation and test subjects, this constitutes a transductive setting. Given the limited availability of fMRI data, this design aimed to make full use of the available unlabeled observations to learn stable spatiotemporal representations. In the second stage, MPR population reference construction, QC regression, and the training of QSR and the classifier were restricted to the training subset of each cross-validation fold. Test subjects were excluded from all fitting procedures at this stage. The staged design also facilitated separate optimization and analysis of the components, allowing us to examine the role of population reference information in individualized EC estimation more clearly. We therefore chose this strategy to make effective use of the available data while supporting a focused analysis of the method’s components.

We acknowledge that our original transductive protocol differs from a strictly inductive evaluation. Following your suggestion, we conducted additional five-fold inductive experiments (Table R4), where the initial EC estimator was independently pretrained using only unlabeled time series from training subjects in each fold and then frozen for test inference, with the remaining module and classification settings unchanged.

Table R4. Classification results under 5-fold inductive evaluation (mean ± std, %).

DatasetMethodACCSENAUCPREF1
ABIDE-IInitial EC55.46 ± 3.0758.38 ± 14.2261.28 ± 6.9651.63 ± 2.6954.02 ± 7.02
+MPR57.64 ± 3.6559.59 ± 17.4362.31 ± 6.0654.23 ± 4.5855.30 ± 8.92
Full PR-EC58.21 ± 5.4760.55 ± 3.8263.41 ± 5.2354.95 ± 6.3157.41 ± 3.89
ABIDE-IIInitial EC55.69 ± 2.0769.24 ± 8.6160.56 ± 2.1252.77 ± 2.2959.49 ± 2.65
+MPR56.00 ± 2.1674.23 ± 10.1560.64 ± 3.3552.91 ± 2.5461.28 ± 2.63
Full PR-EC56.51 ± 1.7974.65 ± 13.4162.27 ± 3.1653.20 ± 1.7161.50 ± 3.84
ADHD200Initial EC51.54 ± 9.7765.00 ± 10.6356.49 ± 7.4440.43 ± 6.2449.03 ± 3.95
+MPR51.78 ± 7.4370.36 ± 16.7460.00 ± 3.9340.42 ± 4.0050.41 ± 5.56
Full PR-EC51.66 ± 7.8572.86 ± 9.4860.20 ± 4.0840.62 ± 4.5551.80 ± 4.56

Under this setting, Full PR-EC achieved AUCs of 63.41%, 62.27%, and 60.20% on ABIDE-I, ABIDE-II, and ADHD200, respectively, improving over Initial EC by approximately 2.1, 1.7, and 3.7 percentage points. All three datasets showed progressive mean AUC improvements from Initial EC to MPR-only and Full PR-EC, providing encouraging evidence of generalization to unseen subjects. We will explicitly distinguish the transductive and inductive protocols and clarify the data usage at each stage in the revised manuscript. Thank you very much, sincerely.

Reviewer_tigWOpenReview ↗
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Paper summary

PR-EC reconstructs fMRI windows to derive an individual asymmetric attention matrix, then refines that matrix using a personalized population reference and QC-related patterns. Neighbors are selected from functional and phenotypic similarities. The code fits a QC regression basis and constructs a pseudo-target by subtracting part of the estimated QC component, with a bound on the relative change. A learned refiner uses these pseudo-targets and perturbations. Experiments evaluate ASD/ADHD classification on ABIDE-I, ABIDE-II and ADHD200, and directional ASD-related group differences. The release confirms fold-local reference and QSR fitting, while the initial reconstruction encoder is trained on the full cohort before cross-validation.

Critical strengths
  1. A relevant individual-versus-population estimation problem

The individual-versus-population tradeoff is a reasonable problem to study. A single cohort-wide template can erase individual differences, while fitting each subject separately can be noisy. Selecting related training participants provides a plausible middle ground. The paper makes its local-smoothness and additive-bias assumptions visible, and the code places an explicit bound on QC correction magnitude. I find these modeling choices more useful than a claim that any population average automatically improves an individual estimate. They could be studied even if the resulting matrices were interpreted as learned connectivity representations.

  1. Multi-cohort evaluation with explicit reference-pool restrictions

The source code confirms that the reference library and subsequent refinement are restricted to the training fold. Functional descriptors are scaled from training data; validation and test participants query training participants for their reference; and the QC basis, pseudo-targets and refiner are fitted from training inputs (workflow.py, lines 20–69 and 113–127). This resolves uncertainty about those stages and is a useful reproducibility detail. Evaluation spans three cohorts, and the replicated ASD group analysis asks a question beyond classification accuracy. The code-supported fold restrictions should be stated clearly alongside the different scope of initial pretraining.

Critical weaknesses
  1. Asymmetric reconstruction attention is not validated as effective connectivity

The release confirms that the initial edges are reconstruction attention weights. The estimator reconstructs the same input window with an attention-based decoder; subject matrices average those weights and transpose them to set the source-target convention (individual_ec/encoder.py, lines 48–54; individual_ec/utils.py, lines 71–84). The loss combines reconstruction error with attention entropy. These operations define an asymmetric representation, but they do not validate recovery of directed neuronal effects. A successful classifier or an anatomically plausible ASD group difference is compatible with an associative feature matrix.

The QSR implementation also clarifies what is corrected: a ridge regression estimates the QC-associated component and builds a pseudo-target by subtracting eta times that component (qsr/qc_target.py, lines 114–137 and 169–179). The refiner's perturbation loss trains it to restore these pseudo-targets. This is a coherent training construction, but the pseudo-target has no independently established neuronal ground truth. A signal correlated with QC could contain biological differences that the regression and shrinkage also remove. The theoretical assumptions do not supply empirical identification of either the initial direction or the nuisance component. I would need a controlled direction-recovery and nuisance-removal evaluation before accepting claims of improved individualized effective connectivity.

  1. The classification evidence does not establish a robust benefit from the proposed population/QC modules

The module ablation gives only small increments over the initial estimator: AUC changes from 66.20 to 66.85, 66.53 to 66.83, and 60.68 to 61.21 in Table 2 (p. 8). MPR alone lowers AUC on both ABIDE cohorts. Those means are not sufficient to establish a consistent benefit across folds; the relevant uncertainty is the paired difference for each proposed module. The larger ABIDE-II gap against FSTA-EC in Table 1 is not the incremental effect of MPR/QSR, and phenotype information also requires comparators with the same available inputs.

The code makes the transductive stage explicit. runner.py loads the full cohort and calls load_pipeline_data before run_cross_validation; generate_subject_ec trains the encoder on all of those time series (runner.py, lines 20–27; ec_estimator.py, lines 9–25). This is unsupervised use of eventual test inputs, so it should be evaluated and described as such. Fold-local MPR/QSR does not make the whole pipeline inductive. I would want an additional fold-specific encoder fit, paired confidence intervals for the increments, and phenotype-only or simple FC-plus-phenotype controls. Together these would show whether the proposed regularizers provide a useful benefit for a new population beyond the underlying representation and extra subject information.

Questions for authors
  1. What experiment establishes that the attention-derived directions correspond to directed neuronal interactions? A controlled benchmark should separately test the initial estimator and the effect of MPR/QSR, including whether QC correction preserves known individual or disease-related differences. Does the complete pipeline improve edge direction recovery as well as classification?

  2. Do the Table 2 increments remain when the initial encoder is fitted inside each training fold? Please report paired uncertainty across the same held-out subjects and provide controls with the same phenotype inputs. It would also help to separate the transductive protocol from this inductive evaluation.

  3. For the 213 replicated ASD-related edges, what covariate-adjusted group model handles age, sex, site and motion? How do the results change when resampling recomputes population references and QC refinement? Shared references make subjects' refined matrices dependent, which should be reflected in the uncertainty of the directional findings.

3 comments

We thank the reviewer for the careful evaluation of our work and the detailed examination of the methodology and code. We take these concerns seriously and address them below, with further clarification of our design choices.

W1 & Q1. Validation of individualized EC estimation

To directly address this concern, we have added simulation experiments to validate the initial EC estimator’s ability to recover edge directions in the revised manuscript (page 8, lines 385–387 and 423–431; page 9, lines 432–442).

  1. Validation of directed connectivity recovery by the initial EC estimator: We evaluated four networks (Sim1–Sim4) from the Sanchez simulated fMRI dataset using five-fold out-of-fold evaluation, with self-supervised pretraining restricted to training subjects and ground truth used solely for testing. As shown in Table R1, the estimator achieved directed AUPRC values of 0.78–0.89, consistently outperforming symmetrized predictions, and direction accuracy of 63.89%–75.56%, exceeding the 50% chance level. These results support its ability to recover directed connectivity structure.

    Table R1. Directed connectivity recovery by the initial EC estimator on the Sanchez simulated fMRI dataset.

    NetworkDirected AUPRC ↑Sym. AUPRC ↑Direction Acc. ↑Precision ↑Recall ↑F1 ↑Accuracy ↑SHD ↓
    Sim10.82 ± 0.050.74 ± 0.0266.67%0.63 ± 0.120.77 ± 0.150.68 ± 0.080.78 ± 0.074.43 ± 1.36
    Sim20.88 ± 0.050.83 ± 0.0475.56%0.65 ± 0.110.85 ± 0.100.73 ± 0.080.78 ± 0.074.45 ± 1.48
    Sim30.89 ± 0.040.86 ± 0.0263.89%0.78 ± 0.130.74 ± 0.100.75 ± 0.060.82 ± 0.053.53 ± 1.08
    Sim40.78 ± 0.040.74 ± 0.0375.45%0.71 ± 0.130.65 ± 0.120.66 ± 0.060.86 ± 0.0312.45 ± 3.01
  2. Additional validation of the MPR population reference: Commonly used EC simulation datasets typically lack the phenotypic and multi-site information required to reproduce the full multimodal MPR setting. Following prior studies evaluating connectivity-based methods on clinical datasets (Parisot et al., 2018; Crimi et al., 2021), we assess MPR’s downstream contribution through clinical ablation experiments (page 9, Table 3 and Figure 6).

    To further validate the population reference against ground truth, we conducted additional five-fold out-of-fold experiments on NetSim Sim21 (Smith et al., 2011), using FC-guided MPR with neighbors selected exclusively from training subjects (Table R2). Compared with the initial EC, the MPR reference improved F1 from 0.58 to 0.66, reduced SHD from 5.90 to 5.02, and increased ground truth strength correlation from 0.22 to 0.37, supporting its effectiveness in connectivity recovery.

    Table R2. Recovery of ground truth by the initial EC and the MPR population reference on Sim21. True Strength r measures the correlation between estimated and true connection strengths.

    MethodDirected AUPRC ↑F1 ↑SHD ↓True Strength r ↑
    Initial EC0.56 ± 0.080.58 ± 0.095.90 ± 1.390.22
    FC-guided MPR Reference0.56 ± 0.060.66 ± 0.015.02 ± 0.140.37
  3. Whether QSR may remove genuine connectivity information: We thank the reviewer for this important question. Existing simulation datasets with known ground truth connectivity typically lack subject-level QC measures (e.g., FD and DVARS), making direct validation of the full QSR module challenging. Following prior work (Takahara et al., 2025), we assess QSR through coarse and fine-grained ablations on clinical datasets (page 9, Table 3 and Figure 6). Further ablations of QSR’s internal architecture are provided in our response to Reviewer KKzu’s W1(2).

    We would also like to further clarify that our study aims to explore how population-level connectivity information from similar individuals can be combined with QC information to improve individualized EC estimation under limited and noisy rs-fMRI conditions. Since directly observable ground truth for individual-level EC in the human brain is generally unavailable, previous studies have also used disease classification to assess the downstream utility of brain connectivity representations (Jun et al., 2020; Abraham et al., 2017). Thus, our intention is not to substitute classification performance for the validation of neural causal relationships, but rather to evaluate the practical value of the estimated connectivity representations in real clinical settings from two perspectives: downstream predictive performance and the cross-cohort consistency of disease-related patterns. We therefore prioritize evaluation on real multi-site datasets, such as ABIDE-I, to preserve individual heterogeneity and the complex relationships between functional and phenotypic information.

W2 & Q2. Clarification of Module Contributions and Experimental Evaluation Protocol

We thank the reviewer for their detailed comments. We provide further details below.

  1. Classification performance and module contributions: We thank the reviewer for highlighting the incremental benefits of the modules and their stability. Although the improvements are relatively modest on some datasets, PR-EC still achieves competitive overall classification performance across all three datasets (Table 1). Regarding the slight performance decreases observed with MPR-only on certain datasets, we believe these may be related to its reliance on population similarity for constructing individualized references. Differences in cohort composition, phenotypic distributions, and acquisition sites across datasets may lead to variations in the effectiveness of the resulting population references. More importantly, MPR and QSR play complementary roles in the complete PR-EC framework: MPR provides a subject-specific population reference, while QSR further incorporates QC information to selectively utilize this reference, reducing the risk of inappropriate population information directly affecting individualized EC estimation. Table 3 also shows that adding QSR improves AUC by 1.07, 1.44, and 0.34 percentage points across the three datasets, respectively, highlighting the potential value of selectively incorporating population reference information.

    To further assess the stability of these module-level gains, we additionally calculated paired AUC differences and their 95% confidence intervals on matched test folds from the original ten-fold cross-validation.

    Table R3. Paired AUC differences across 10-fold cross-validation.

    Dataset(MPR-only) − (Initial EC)(PR-EC) − (MPR-only)(PR-EC) − (Initial EC)
    ABIDE-I−0.41 [−1.49, 0.67]+1.07 [−0.11, 2.24]+0.66 [−0.55, 1.87]
    ABIDE-II−1.14 [−2.64, 0.36]+1.44 [0.06, 2.83]+0.30 [−0.16, 0.77]
    ADHD200+0.19 [−0.68, 1.06]+0.34 [−0.45, 1.13]+0.53 [−0.56, 1.62]

    The results show that full PR-EC achieved positive mean AUC gains over both MPR-only and Initial EC across all three datasets, although most confidence intervals included zero. We thank the reviewer for suggesting this additional analysis, which helps us assess the contributions of the individual modules more objectively and identify opportunities to improve the use of population reference information.

  2. Phenotypic information and control experiments: We respectfully clarify that Table 3 and Figure 6 (page 9, lines 445–466) already provide coarse and fine-grained ablation studies. In Figure 6, combining PH and FC improves AUC to 65.79%, compared with PH-only (65.53%) and FC-only (65.21%), with gains in SEN and F1. Further incorporating QC increases AUC, SEN, and F1 to 66.85%, 70.50%, and 61.73%, respectively, supporting the effectiveness of multimodal similarity modeling and QSR.

  3. The Transductive and Inductive evaluation protocols: We appreciate the reviewer for pointing out the difference in data usage between initial EC estimation and the subsequent cross-validation stage. Actually, the staged training procedure was described in Appendix C.3 of the original paper, but we would like to further explain the rationale for this design.

    • First stage: The initial EC estimator follows the self-supervised spatiotemporal reconstruction approach used in FSTA-EC (Xiong et al., 2025). We train a shared estimator using unlabeled rs-fMRI time series from the entire cohort. Given the limited amount of fMRI data, this design aims to make full use of the available unlabeled observations to learn stable spatiotemporal representations. No diagnostic labels are used at this stage. Because pretraining includes unlabeled validation and test subjects, this constitutes a transductive setting.
    • Second stage: Since MPR and QSR rely on inter-subject similarity information and QC-associated connectivity variations, we strictly restrict population reference construction, QC regression, and QSR to the training subjects within each cross-validation fold. Validation and test subjects obtain their population reference information exclusively from the training set and do not participate in parameter fitting for these modules.

    Thus, initial EC estimation and subsequent population regularization are two relatively independent stages, with different considerations regarding the scope of data usage. We recognize that this differs from a strictly inductive setting. However, transductive pretraining does not inherently imply label leakage, and the experiments under this protocol also yield favorable results. In addition, the staged training design provides greater modularity, facilitating independent optimization and adjustment of individual components.

We acknowledge the distinction between our original transductive protocol and a strictly inductive setting. To address this concern, we conducted additional five-fold inductive experiments, retraining the initial EC estimator exclusively on training subjects in each fold while keeping the remaining configurations unchanged (Table R4).

Table R4. Classification performance and paired AUC differences under 5-fold inductive evaluation.

DatasetMethodACC (%)SEN (%)AUC (%)PRE (%)F1 (%)ΔAUC vs. Initial [95% CI]ΔAUC vs. MPR [95% CI]
ABIDE-IInitial EC55.46 ± 3.0758.38 ± 14.2261.28 ± 6.9651.63 ± 2.6954.02 ± 7.02——
+MPR57.64 ± 3.6559.59 ± 17.4362.31 ± 6.0654.23 ± 4.5855.30 ± 8.92+1.03 [−4.25, 6.31]—
Full PR-EC58.21 ± 5.4760.55 ± 3.8263.41 ± 5.2354.95 ± 6.3157.41 ± 3.89+2.14 [−1.77, 6.04]+1.10 [−2.77, 4.97]
ABIDE-IIInitial EC55.69 ± 2.0769.24 ± 8.6160.56 ± 2.1252.77 ± 2.2959.49 ± 2.65——
+MPR56.00 ± 2.1674.23 ± 10.1560.64 ± 3.3552.91 ± 2.5461.28 ± 2.63+0.08 [−2.01, 2.17]—
Full PR-EC56.51 ± 1.7974.65 ± 13.4162.27 ± 3.1653.20 ± 1.7161.50 ± 3.84+1.71 [−3.66, 7.06]+1.63 [−4.72, 7.97]
ADHD200Initial EC51.54 ± 9.7765.00 ± 10.6356.49 ± 7.4440.43 ± 6.2449.03 ± 3.95——
+MPR51.78 ± 7.4370.36 ± 16.7460.00 ± 3.9340.42 ± 4.0050.41 ± 5.56+3.52 [−4.26, 11.30]—
Full PR-EC51.66 ± 7.8572.86 ± 9.4860.20 ± 4.0840.62 ± 4.5551.80 ± 4.56+3.71 [−4.41, 11.83]+0.19 [−0.29, 0.67]

Under this setting, Full PR-EC achieved AUCs of 63.41%, 62.27%, and 60.20% on ABIDE-I, ABIDE-II, and ADHD200, respectively, improving over Initial EC by 2.14, 1.71, and 3.71 percentage points. Positive mean gains over MPR-only were also observed across all three datasets. Although all paired 95% confidence intervals included zero, these results provide preliminary evidence of PR-EC's generalization to unseen subjects. Given the different evaluation protocols, we focus on within-protocol module improvements rather than direct comparisons of absolute performance. We sincerely thank the reviewer for these valuable suggestions again.

Q3. Statistical Reliability and Robustness of ASD-Related Connectivity Differences

We clarify that QC-aware regression within QSR differs from covariate adjustment in ASD group comparisons. To address this concern, we conducted additional edge-wise regression analyses on ABIDE-I and ABIDE-II, controlling for age, sex, acquisition site, and mean FD. After adjustment, 90 connections remained FDR-significant across both cohorts, with 59 overlapping the original 213 connections. Importantly, 212/213 (99.53%) original connections maintained consistent effect directions across cohorts after adjustment, indicating robust directional patterns despite fewer significant edges.

To assess potential dependence introduced by shared population references, we further conducted five training-reference resampling experiments, holding the initial EC and test folds fixed while reconstructing MPR references, re-estimating QC-associated patterns, and retraining QSR (Table R5).

Table R5. Stability of ASD-related EC findings under reference resampling.

MetricOriginalResampling (5 runs)
Replicated edges9086–103
Overlap with original 213 edges5958–64
Effect-direction consistency99.53%99.06%–99.53%
MTG–thalamus direction consistency100%100%

Across resampling runs, 86–103 connections were replicated, with effect-direction consistency exceeding 99%. All eight MTG–thalamus connections retained their ASD-enhanced directions, supporting the robustness of the findings to population-reference resampling.

Comments on the paper

1 comment

Dear Reviewer,

Thank you for your thoughtful and constructive feedback, which has been invaluable in strengthening our work. With the discussion period ending tomorrow, we would appreciate your thoughts on our responses and additional experiments. We hope these have addressed your concerns and would be grateful if you could reconsider your assessment and score in light of the new evidence. We remain eager to address any issues.

Thank you again for your time and consideration.

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

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