acceptodds
Under review as a conference paper at ICLR 2027

BOLDFlow: Network-Level Recovery of fMRI Connectivity from EEG via Conditional Flow Matching

Abstract

Functional connectivity (FC) analyses operate on correlations between regional blood-oxygen-level-dependent (BOLD) signals, but estimating them requires functional magnetic resonance imaging (fMRI). Inferring fMRI-like connectivity from scalp electroencephalography (EEG) could broaden access, yet per-region regressors and joint mean-squared-error decoders collapse toward the conditional mean, discarding the residual cross-region covariance. We present BOLDFlow, which models the conditional distribution of parcellated BOLD activity using conditional flow matching with a learned EEG-conditioned source. Sampled trajectories retain the model's residual cross-region covariance, while repeated draws provide input-conditional ensemble spread without a separate uncertainty head. In subject-disjoint evaluations on two simultaneous in-scanner EEG–fMRI datasets spanning rest and sleep, BOLDFlow improves measured-FC recovery (NeuroBOLT: to ; OpenNeuroSleep: to ) and temporal correlation ( to and to , respectively), and scales to output parcellations with 512 components. The recovered connectomes retain individual-specific and community structure, while ensemble spread attains nominal coverage after single-parameter recalibration.

Primary area:
applications to neuroscience & cognitive science
Keywords:
conditional flow matching, EEG-to-fMRI translation, functional connectivity, cross-modal generation, uncertainty quantification

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_nmv6OpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This work proposes BOLDFlow, a novel conditional flow-matching framework that generates ROI-level BOLD time series from EEG and computes functional connectivity from the generated signals. The proposed method combines a pretrained REVE encoder with multiscale spectral features and a learned EEG-conditioned Gaussian source. They also asked the. model to preserve cross-region. covariance that may be lost in previous regression-based supervision. Experiments across two concurrent EEG–fMRI datasets show significant improvements in both temporal correlation and FC recovery, with comprehensive analyses covering different aspects, such as the community structure of the recovered FC, scalability to finer brain parcellations, and uncertainty estimation.

Critical strengths
  1. The paper presents extensive experiments covering EEG context lengths under both seq2one and seq2seq settings, electrode configurations, and architectural and training variants. Subject-disjoint cross-validation with multiple random seeds strengthens confidence in the reported results.
  2. The proposed method consistently outperforms the evaluated baselines on both datasets, with particularly substantial improvements in FC recovery, while also improving the temporal correlation between pred and g.t..
  3. The results and discussion of the trade-off between temporal reconstruction accuracy and FC recovery is insightful.
Critical weaknesses
  1. The writing and presentation could be improved. A clearer explanation of the prediction and aggregation pipeline, particularly the distinction between averaging overlapping block predictions and averaging independently sampled trajectories, would make the method easier to follow. The figures would also benefit from improved legibility and clearer illustration of the complete pipeline. The work provided extensive experimental evaluation, which is great, but the presentation sometimes feels fragmented. Better organization and a clearer synthesis/summary of the key findings may help understand how the individual experiments support the paper’s main claims.

  2. Although the method is evaluated on two datasets, training and testing are performed separately within each dataset. These experiments support the effectiveness of the method across datasets when retrained, but do not establish the transferability of a trained model across datasets or acquisition conditions, which is important for this task and broader application of the method.

  3. The methodological novelty appears a little bit limited. The framework largely combines existing EEG encoders, conditional flow matching, and β-NLL. Although the empirical results are strong, the contribution appears primarily empirical rather than a substantial methodological advance.

Questions for authors
  1. Table 5 results is intereting. If I understand correctly, this is the comparison between seq2one and seq2seq with T=4 averaging. Have you compared, using the same trained seq2seq model, how do temporal correlation and FC correlation change when each TR is reconstructed using a single prediction from a fixed position within the output block (i.e., seq2seq but T=1, maybe just choosing the last prediction point), rather than by averaging overlapping predictions?

  2. How was the Tout = 4 been selected, or have you compared with other numbers e.g., Tout = 2, 6 etc?

  3. FC recovery is the primary evaluation target, yet the training objective supervises BOLD sequence generation without an explicit FC-based loss. Have you considered or evaluated adding an auxiliary FC loss if it's feasible?

  4. Beyond the NeuroBOLT-encoder hybrid in Table 1, have you compared REVE with other EEG foundation-model backbones under otherwise matched settings?

4 comments
AuthorsOpenReview ↗

Comment 1/2: Weaknesses

Thank you for your thorough review and for recognizing our novel conditional flow-matching framework, rigorous multi-seed subject-disjoint evaluation, consistent gains in FC and temporal correlation, and insight into the accuracy–FC trade-off.

Revisions in the PDF are highlighted in blue. Below we address your concerns (Part 1/2: Weaknesses; Part 2/2: Questions):

[W1] Clarification on the pipeline, figures, and organization. We describe the pipeline and both types of averaging in the Method section (with pseudocode in Algorithm 1, App. B), and we made this comparison more direct in the revision. Both seq2one and seq2seq take the same 32 s EEG window as input; the only difference is that seq2one outputs one BOLD vector (1 TR), while seq2seq (our default) outputs a matrix of 4 TRs. In seq2seq, averaging overlapping blocks takes the mean of overlapping 4-TR predictions obtained by shifting the EEG window by 1 TR to form a single trajectory (M=1M=1, Eq. 8; used for all Table 1 results), whereas averaging independent trajectories runs this generation MM times with fresh noise draws and averages the MM trajectories (used only for the ensemble ablation in Table 14 and UQ at M=50M=50).

Regarding figure legibility, we redrew all figures with larger fonts and restructured Figure 2 into a clear end-to-end pipeline diagram.

Finally, we appreciate your note on the breadth of our experiments. To make the Experiments section easier to follow, we added a short opening paragraph linking its three parts (connectivity recovery, decoder/readout analysis, and uncertainty estimation) directly to our main contributions and findings.

[W2] Analysis on the transferability across datasets and acquisition conditions. We do not claim cross-dataset generalization of a trained model (noted as a limitation in App. I). Instead, as you note, we test the transferability of the method: freezing all architecture and hyperparameters on NeuroBOLT and training unchanged on OpenNeuroSleep, where BOLDFlow still outperforms all baselines (0.340→0.5280.340 \to 0.528 FC Corr, Table 1). Clean zero-shot evaluation on public paired data is difficult because NeuroBOLT (N=22N=22) and OpenNeuroSleep (N=33N=33) differ simultaneously in scanner, EPI sequence, montage, brain state (rest vs. sleep), and age.

Following your suggestion, we trained BOLDFlow on OpenNeuroSleep alone (22 shared channels) and tested it zero-shot on NeuroBOLT with no fine-tuning: it reaches 0.528±0.1080.528 \pm 0.108 FC Corr, beating in-domain NeuroBOLT (0.4280.428) and UnEBOLT (0.4180.418), whereas T. Corr drops to 0.1300.130. These preliminary results suggest that BOLDFlow can generalize across datasets, with a clear takeaway: connectivity structure transfers zero-shot across scanners and brain states, whereas pointwise timing shifts without light target-domain adaptation (App. F).

[W3] Clarification on methodological novelty and combining existing components. We are glad you found our empirical results strong, and while individual building blocks (REVE, CFM, β\beta-NLL) exist, simply combining off-the-shelf parts does not recover FC. To our knowledge, no prior EEG-to-fMRI work has diagnosed why point predictors fail on FC or formulated connectivity recovery as conditional distribution matching; our core contribution is identifying this fundamental limitation and redesigning the generative pipeline around three critical bottlenecks:

  1. Distributional vs. MSE decoding: MSE predictors converge to the conditional mean and lose the residual covariance that FC depends on (Prop. 1). With the encoder fixed, switching from an MLP regressor to our generative decoder lifts FC from 0.4200.420 to 0.5840.584 with REVE (Table 6), and from 0.4280.428 to 0.5500.550 with NeuroBOLT's encoder (Table 1).
  2. Learned β\beta-NLL source vs. plain CFM: Standard N(0,I)\mathcal{N}(0,I) CFM reaches only 0.4610.461 FC and lowers T. Corr (0.2810.281 vs. 0.3150.315), while with a fixed-variance source ODE integration contracts the spread to 7%7\% of its initial value (Table 10) and FC reaches only 0.4420.442 (Table 6, fixed σ\sigma with AdaLN-Zero). Conditioning the Gaussian source on EEG via β\beta-NLL preserves spread and pushes FC to 0.5840.584 (0.3260.326 T. Corr).
  3. Single-trajectory readout (M=1M=1): Even on the same weights, averaging MM draws washes out residual covariance and drops FC from 0.5840.584 to 0.4710.471 (Cor. 1, Table 14), giving the accuracy/FC trade-off you noted.
AuthorsOpenReview ↗

Comment 2/2: Questions

[Q1] Single-position readout (seq2seq without overlap averaging). Your understanding of Table 5 is exact. To investigate your point, we took the same trained seq2seq model and reconstructed each TR from a single fixed position of the output block (either the last or the first prediction point) instead of averaging:

ReadoutT. CorrFC Corr
Seq2one, 32 s0.3170.564
Seq2seq, single position: last TR0.3130.575
Seq2seq, single position: first TR0.3150.569
Seq2seq, overlap average (reported)0.3260.584

Without overlap averaging, single-position seq2seq performs on par with seq2one, while averaging overlapping blocks yields a consistent + ⁣0.01+\!0.01 gain in both T. Corr and FC Corr. This is in line with the 26–32 s context plateau in Table 5 (seq2one T. Corr: 0.3110.311–0.3200.320), since both output positions still see ≥ ⁣25.7 s\ge\!25.7\text{ s} of preceding EEG.

[Q2] Selection of Tout=4T_{\text{out}} = 4. We fixed Tout=4T_{\text{out}} = 4 without a grid search over other block lengths, since seq2one (Tout=1T_{\text{out}}=1) already achieves 0.5640.564 FC Corr and tuning ToutT_{\text{out}} is orthogonal to our core generative contribution. Practically, ToutT_{\text{out}} is coupled to the input window length (App. C): larger blocks leave less preceding EEG for the earliest TR unless the input window is also extended, and Tout=4T_{\text{out}}=4 provides overlap averaging while keeping all outputs within the ≥ ⁣25 s\ge\!25\text{ s} hemodynamic regime at Δctx=32 s\Delta_{\text{ctx}}=32\text{ s} (Table 5).

[Q3] Adding an auxiliary FC loss. We considered adding an explicit FC loss early on, but decided against it because it does not fit cleanly into per-window flow-matching training. Each training step only predicts the velocity of one 4-TR block at a random flow time τ\tau, without integrating the ODE to generate BOLD outputs. Since FC is a correlation over a full scan (Eq. 1), adding an FC loss would require batching long consecutive segments from the same scan and unrolling ODE integration inside the training loop. Moreover, learning the conditional distribution already targets the second moments that determine FC (Corollary 1), lifting FC Corr from 0.4200.420 to 0.5840.584 without an explicit FC term (Table 6).

[Q4] Comparing REVE with other EEG foundation-model backbones. Our framework is encoder-agnostic, and Table 1 already isolates the backbone effect by pairing our generative decoder with two distinct EEG foundation models, LaBraM (via NeuroBOLT's encoder) and REVE: the decoder alone drives the bulk of the FC gain (0.428→0.5500.428 \to 0.550 on NeuroBOLT; 0.340→0.4890.340 \to 0.489 on OpenNeuroSleep), while upgrading the backbone to REVE adds a consistent +0.034+0.034 / +0.039+0.039. We selected REVE as our default rather than sweeping additional backbones because it reports state-of-the-art results on ten downstream EEG tasks, with an average balanced-accuracy gain of 2.5%2.5\% over the previous best foundation model, CBraMod (El Ouahidi et al., 2025), and its 4D coordinate encoding natively handles arbitrary montages (26, 30, 19, and 6 channels; App. C) without architectural changes.

Thank you again for your time and constructive feedback. We hope our clarifications and new experiments address all of your questions, and we would be grateful if you considered raising your score.

Thank you again for your constructive feedback. We have clarified the prediction and averaging pipeline and added the single-position readout and cross-dataset experiments discussed in our response. We hope these additions help, and we would welcome any further questions or remaining concerns.

Thank you for the detailed response and revisions. Most of my concerns have been addressed, so I am happy to raise my score.

Reviewer_UmMSOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

This paper presents a framework for reconstructing fMRI FC from simultaneously acquired EEG using conditional flow matching. The framework models the conditional distribution of regional BOLD activity that can better preserve cross-region covariance. Experiments on two EEG–fMRI datasets demonstrate improved temporal BOLD prediction and FC reconstruction compared with existing baselines.

Critical strengths
  1. The paper addresses a meaningful limitation of conventional EEG-to-fMRI mapping approaches failing to preserve cross-region covariance and consequently producing suboptmial FC reconstruction.

  2. BOLDFlow substantially improves FC reconstruction over existing baselines on two EEG–fMRI datasets, while also achieving modest improvements in BOLD time-series prediction.

  3. The constant-input, subject-pairing, and temporal-alignment controls help establish that the reconstructed connectivity depends on EEG information, not solely on learned population-level patterns.

  4. They provided experiments on dynamic-FC and multi-parcellation; although not very comprehensive, I still consider them as a strength, again, because there is a lack of prior works on such analyses.

Critical weaknesses
  1. Despite improvements over existing methods, the correlations between predicted and measured BOLD time series remain relatively low (0.326 and 0.212).

  2. (not as critical) There are only very few baselines being compared; it might represent that this is an understudied problem, but the question is do I need a complex flow matching to produce FC measures.

Questions for authors
  1. Given the small number of subjects, I wonder whether cross-dataset generalization experiments, i.e, train on one dataset and test on another.

  2. Given that the method is not very good at recovering subject-level FC precisely beyond population-level FC (r=0.146), it would be helpful to compare population-residual FC reconstruction across all competing methods? I don't think I see those results here.

  3. Could the authors also report the absolute dynamic FC reconstruction accuracy and compare it against the baseline methods?

5 comments
AuthorsOpenReview ↗

Comment 1/2: Weaknesses

Thank you for your positive review and for recognizing that BOLDFlow addresses a key limitation of prior EEG-to-fMRI methods, the substantial FC gains on two datasets, our EEG-specificity controls, and our dynamic-FC and multi-parcellation analyses.

Revisions in the PDF are highlighted in blue. Below we address your concerns and questions (Part 1/2: Weaknesses; Part 2/2: Questions):

[W1] Explanation on relatively low temporal correlations. Whole-brain temporal correlations stay around 0.3260.326 and 0.2120.212 because T. Corr averages across all 64 DiFuMo components, including deep subcortical and non-neural compartments that scalp EEG cannot physically resolve. As shown in Table 13 (App. F), both BOLDFlow and per-ROI NeuroBOLT drop sharply in the ventricles (0.030.03–0.070.07) and in deep gray matter and cerebellum (0.140.14–0.320.32), whereas in visual and sensorimotor cortex BOLDFlow reaches 0.410.41–0.430.43. Averaging over all 64 components pulls down every method's mean, while 0.3260.326 and 0.2120.212 remain the highest T. Corr among all compared methods, and we now highlight this cortical vs. deep/non-neural breakdown directly in the Experiments section (with full regional details in App. F).

[W2] Expanded baseline comparisons and justification for conditional flow matching. As you note, this is still an understudied problem, which helped motivate our work. Alongside NeuroBOLT (per-ROI and joint), REVE regressors, and our hybrid, we added the recent UnEBOLT model to Table 1 across both datasets, trained on our exact 5-fold splits ×\times 3 seeds with the authors' code:

MethodNeuroBOLT MSE ↓NeuroBOLT T. Corr ↑NeuroBOLT FC Corr ↑OpenNeuroSleep MSE ↓OpenNeuroSleep T. Corr ↑OpenNeuroSleep FC Corr ↑
BOLDFlow0.239 ± 0.0020.326 ± 0.0080.584 ± 0.0170.255 ± 0.0010.212 ± 0.0010.528 ± 0.017
UnEBOLT0.238 ± 0.0010.308 ± 0.0090.418 ± 0.0180.261 ± 0.0030.193 ± 0.0110.274 ± 0.027

UnEBOLT is competitive on pointwise MSE, yet as a deterministic regressor it hits the same FC ceiling (0.4180.418 vs. 0.5840.584 on NeuroBOLT, and 0.2740.274 vs. 0.5280.528 on OpenNeuroSleep; ARI 0.2440.244 vs. 0.4300.430 at 10%10\% edge density).

Conditional flow matching is essential because any MSE regressor converges to the conditional mean and discards the cross-region residual covariance that drives FC (Prop. 1). Holding the REVE encoder fixed (Table 6, App. C), linear and MLP regressors reach only 0.3970.397–0.4200.420 FC Corr and a standard N(0,I)\mathcal{N}(0,I) flow reaches 0.4610.461, whereas BOLDFlow reaches 0.5840.584. Even a simpler post-hoc baseline, adding calibrated fixed-covariance Gaussian noise to BOLDFlow's mean prediction, cannot replace the learned distribution: because the noise is input-independent, it dilutes EEG-specific signal. On a separate set of checkpoints, this control reaches 0.6090.609 FC Corr versus 0.6550.655 for BOLDFlow, which also retains more subject-specific FC (+0.024+0.024, 95% CI [0.009,0.041][0.009, 0.041]) and time-specific FC (+0.010+0.010, [0.001,0.019][0.001, 0.019]; App. D).

AuthorsOpenReview ↗

Comment 2/2: Questions

[Q1] Cross-dataset generalization (train on one dataset, test on the other). Even though the two cohorts are small (22 and 33 subjects) and differ in scanner, montage, and brain state (rest vs. sleep), we ran this test. Trained on OpenNeuroSleep alone (22 shared EEG channels) and tested directly on NeuroBOLT with no fine-tuning, BOLDFlow reaches 0.528±0.1080.528 \pm 0.108 FC Corr, beating both NeuroBOLT (0.4280.428) and UnEBOLT (0.4180.418) trained in-domain, while T. Corr drops to 0.1300.130. Connectivity transfers across sites, whereas pointwise timing shifts without local adaptation (App. F).

[Q2] Population-residual FC across competing methods. Regarding subject-level FC beyond population-level FC (r=0.146r = 0.146), this residual is naturally small because human connectomes share a strong group pattern. To compare population-residual FC across all competing methods as you suggested, we evaluated every baseline with the exact template, mask, and folds of Appendix D:

MethodResidual FC Corr ↑
BOLDFlow0.146
Linear regression (Table 6)0.051
NeuroBOLT (joint)0.033
NeuroBOLT†0.027
REVE-FT0.015
REVE-NoFT0.009
UnEBOLT−0.013

Regression baselines stay near zero and predict almost only population-level FC, as Prop. 1 predicts. BOLDFlow is the only method capturing a clear subject-specific residual (≈3×\approx 3\times the closest baseline), and correct-subject EEG beats wrong-subject EEG in all folds ([0.070,0.280][0.070, 0.280], App. D).

[Q3] Absolute dynamic FC accuracy vs. baselines. To compare absolute dynamic FC reconstruction accuracy against all baseline methods, we computed window-wise FC correlation (120 s windows, App. D) across every model:

MethodDynamic FC Corr ↑
BOLDFlow0.424
UnEBOLT0.306
Linear regression (Table 6)0.218
REVE-FT0.202
REVE-NoFT0.181
NeuroBOLT (joint)0.178
NeuroBOLT†0.160

BOLDFlow achieves the highest absolute dynamic FC accuracy, 39%39\% above the runner-up (UnEBOLT).

Thank you again for your questions, which led to the cross-dataset test, the UnEBOLT baseline, and the residual and dynamic FC comparisons. If these address your concerns, we would appreciate it if you considered raising your score.

Thank you again for your helpful questions. They motivated the cross-dataset experiment and the additional comparisons of population-residual and dynamic FC. We would appreciate hearing whether these results address your concerns and would be happy to clarify anything further.

Reviewer_753oOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes BOLDFlow, a conditional flow-matching framework for generating atlas-level BOLD time series from EEG, with the goal of improving functional connectivity reconstruction. Although the method demonstrates promising quantitative improvements over the reported baselines, I have several substantial concerns regarding the significance of the proposed task, the justification for flow matching, the completeness and fairness of the experimental comparisons, and the interpretation of the reported results.

Critical strengths

The paper addresses an interesting problem and reports encouraging improvements in functional connectivity correlation.

Critical weaknesses
  1. Limited practical significance and insufficient validation beyond a predefined functional atlas. The proposed framework predicts atlas-level BOLD time series rather than spatially resolved 4D fMRI. While this is meaningful for functional connectivity analysis, the resulting representation discards fine-grained spatial information and is not directly suitable for applications requiring subject-specific anatomical localization, such as presurgical functional mapping. Moreover, the reported experiments on DiFuMo-64, DiFuMo-256, and DiFuMo-512 only evaluate different resolutions within the same atlas family. They do not establish generalization across fundamentally different brain parcellation schemes. This limitation should be more clearly acknowledged when discussing scalability and potential clinical applications.
  2. Insufficient evidence supporting the necessity of flow matching. The theoretical motivation is based on the observation that deterministic conditional-mean prediction may fail to preserve residual covariance. However, this observation does not imply that a learned flow-matching model necessarily recovers the true conditional covariance, nor does it guarantee improved functional connectivity estimation from finite-length generated time series. Although the proposed method improves FC correlation over deterministic baselines, comparisons with alternative probabilistic generative approaches, particularly conditional diffusion models and covariance-aware probabilistic regression, are insufficient. Consequently, the experiments do not convincingly isolate the contribution of flow matching itself.
  3. Incomplete comparisons with relevant EEG-to-fMRI approaches. The experimental evaluation should include or more thoroughly discuss recent approaches such as UnEBOLT, CATD, and context-aware EEG-to-fMRI synthesis methods. UnEBOLT is particularly relevant because it explicitly addresses BOLD prediction and functional connectivity reconstruction. For volumetric EEG-to-fMRI methods, a comparison under a common ROI extraction and FC evaluation protocol would also help clarify the trade-off between atlas-level prediction and spatially resolved reconstruction. Such comparisons should account for differences in data availability, model capacity, and computational cost.
  4. Several experimental results require further explanation. On OpenNeuroSleep, the reported MSE differs substantially between the original ROI-wise NeuroBOLT baseline (0.406) and its joint-output variant (0.260), whereas BOLDFlow achieves 0.255. This raises questions about the consistency of baseline implementations, preprocessing, and optimization settings. Furthermore, although the model supports 512-dimensional DiFuMo outputs, the reported effective rank of the measured signals is only approximately 7.9. Therefore, the experiment does not establish the accurate recovery of 512 independent functional components. The uncertainty results also reveal substantial miscalibration: the uncalibrated nominal 95% intervals achieve only 38.5% empirical coverage. Although a single-parameter rescaling improves coverage to 94.8%, this result demonstrates successful post-hoc marginal calibration rather than intrinsically reliable uncertainty estimation.
  5. Insufficient qualitative evaluation of the generated signals and connectivity structures. Given that the primary output is a BOLD time series, direct visual comparisons between generated and measured temporal signals are essential for assessing temporal fidelity. Similarly, the evaluation would benefit from side-by-side ground-truth FC matrices, predicted FC matrices, and FC error heatmaps. The reported community similarity and subject identification results provide useful evidence, but they do not fully establish faithful reconstruction of individual-specific functional connectomes. More direct predicted-to-measured subject identification and analyses across multiple graph thresholds would strengthen these claims.
Questions for authors

seee weakness

3 comments
AuthorsOpenReview ↗

Comment 1/2: W1 to W3

Thank you for your detailed review and for recognizing that EEG-to-fMRI connectivity recovery is an interesting problem with encouraging FC improvements.

Revisions in the PDF are highlighted in blue. Below we address your concerns (Part 1/2: W1–W3; Part 2/2: W4–W5):

[W1] Clarification on parcellated BOLD targets and parcellation scope. As you note, atlas-level BOLD time series are meaningful for functional connectivity analysis, which is the exact goal of our paper (network biomarkers, fingerprinting, community structure; Introduction). Voxel-level tasks such as presurgical mapping require fine anatomical localization that 26–30 scalp electrodes cannot resolve, and are outside our scope. For the atlas choice, the public NeuroBOLT dataset provides only preprocessed DiFuMo time series without raw 4D fMRI volumes, so other parcellations (e.g., Schaefer or AAL) cannot be extracted. We therefore used DiFuMo on OpenNeuroSleep as well to keep both benchmarks comparable, showing consistent FC gains across 64, 256, and 512 components (Table 8), and updated Appendices A and I to clearly state both scope boundaries.

[W2] Isolating conditional flow matching vs. theory, covariance-aware regression, and diffusion. We agree that Proposition 1 only explains why conditional-mean regressors hit an FC ceiling, without guaranteeing that flow matching succeeds on finite scans; Corollary 1 states recovery only if conditional first and second moments are matched (App. G). We therefore test finite-scan recovery directly: on the exact same trained weights, a single sampled trajectory (M=1M=1) reaches 0.5840.584 FC Corr versus 0.4710.471 when averaging M=200M=200 draws to isolate the conditional mean (Table 14).

Holding the REVE encoder fixed also isolates what each generative component contributes over probabilistic alternatives: MLP regression reaches 0.4200.420 FC Corr, standard N(0,I)\mathcal{N}(0,I) flow matching (which encompasses continuous-time Gaussian diffusion) reaches only 0.4610.461, and BOLDFlow reaches 0.5840.584 (Table 6). Because our β\beta-NLL source is diagonal across regions (Eq. 3), cross-region residual correlations come entirely from the joint velocity field. Conversely, covariance-aware probabilistic regression (adding calibrated full-covariance Gaussian noise to BOLDFlow's conditional mean) injects the exact same static covariance into every window regardless of brain state or subject. On a separate set of checkpoints, this control reaches 0.6090.609 FC Corr versus 0.6550.655 for BOLDFlow, which also retains more subject-specific FC (+0.024+0.024, 95% CI [0.009,0.041][0.009, 0.041]) and time-specific FC (+0.010+0.010, [0.001,0.019][0.001, 0.019]; App. D).

[W3] Expanded comparisons with UnEBOLT and discussion of CATD, volumetric, and context-aware methods. Following your suggestion, we added UnEBOLT (which you highlighted as particularly relevant for BOLD and FC) to Table 1 across both datasets, trained on our exact 5-fold splits ×\times 3 seeds with the authors' official code:

MethodNeuroBOLT MSE ↓NeuroBOLT T. Corr ↑NeuroBOLT FC Corr ↑OpenNeuroSleep MSE ↓OpenNeuroSleep T. Corr ↑OpenNeuroSleep FC Corr ↑
BOLDFlow0.239 ± 0.0020.326 ± 0.0080.584 ± 0.0170.255 ± 0.0010.212 ± 0.0010.528 ± 0.017
UnEBOLT0.238 ± 0.0010.308 ± 0.0090.418 ± 0.0180.261 ± 0.0030.193 ± 0.0110.274 ± 0.027

While UnEBOLT is competitive on pointwise MSE, as a deterministic point predictor it hits the same FC ceiling (0.4180.418 vs. 0.5840.584 on NeuroBOLT, and 0.2740.274 vs. 0.5280.528 on OpenNeuroSleep), and BOLDFlow also leads on NeuroBOLT community recovery (ARI 0.4300.430 vs. 0.2440.244 at 10%10\% edge density), population-residual FC (0.1460.146 vs. −0.013-0.013), and dynamic FC (0.4240.424 vs. 0.3060.306).

For volumetric and cortical-surface methods such as CATD, evaluating under a common ROI-extraction protocol on NeuroBOLT is not possible because NeuroBOLT distributes no raw 3D/4D fMRI volumes (W1). Finally, as suggested, the revision adds UnEBOLT to the Related Work section and discusses UniEFS and the trade-offs of volumetric and surface models in App. H. Volumetric and surface models require voxel- or vertex-level fMRI and predict far higher-dimensional outputs, whereas parcellated generation operates directly in the low-dimensional connectome space; context-aware conditioning is complementary to our distributional decoder.

AuthorsOpenReview ↗

Comment 2/2: W4 and W5

[W4] Clarifying baseline MSE, DiFuMo-512 rank, and uncertainty calibration.

On OpenNeuroSleep, all methods share identical data, preprocessing, and splits. The jump in NeuroBOLT† MSE (0.4060.406) happens because it fits 64 separate single-ROI models per fold, and 9 of them collapsed during training to near-constant outputs (MSE≈1.25\text{MSE}\approx 1.25 each, versus 0.250.25–0.280.28 on the remaining 55), which alone pulls up the 64-ROI mean. Every single-model method on those exact splits lands around 0.2550.255–0.2610.261 (BOLDFlow 0.2550.255, joint NeuroBOLT 0.2600.260, UnEBOLT 0.2610.261), and all our main claims compare against the stronger joint NeuroBOLT baseline (0.340→0.5280.340 \to 0.528 FC Corr).

For DiFuMo-512, we do not claim recovery of 512 independent components; in fact, we reported the effective rank of 7.97.9 in Appendix C ourselves to point out that ground-truth fMRI parcels are strongly correlated, which bounds every method equally. What Table 8 tests is whether our joint decoder scales cleanly to finer atlas resolutions (4×512=20484\times 512 = 2048 outputs per block), where BOLDFlow maintains its FC lead across 64, 256, and 512 components (0.584/0.620/0.5500.584 / 0.620 / 0.550 vs. NeuroBOLT's 0.428/0.427/0.4330.428 / 0.427 / 0.433).

Finally, we agree that 94.8%94.8\% coverage comes from post-hoc marginal rescaling rather than raw interval calibration (App. I): ODE integration contracts initial spread, even though our learned source retains 29%29\% of its spread versus 7%7\% for a fixed source (Table 10). Still, rescaling by a single positive constant cannot change how predictions are ranked by uncertainty. Even before rescaling, BOLDFlow's raw spread ranks prediction errors much better than source noise, MC-Dropout, and deep ensembles (Spearman 0.1550.155 vs. 0.0050.005–0.0450.045, Table 2), and filtering out the 50%50\% most uncertain FC edges lowers connectivity error by 6.9%6.9\% ([2.0%,11.5%][2.0\%, 11.5\%], App. E), showing that the relative uncertainty signal is intrinsic to the model.

[W5] Visual comparisons, individual-specific connectomes, and multi-threshold community recovery.

Direct visual overlays of generated and measured BOLD time courses are already provided in Appendix F (Fig. 4, spanning both high- and low-correlation regions on a held-out subject, alongside quantitative trajectory diagnostics in Table 9, App. D), while Figure 1 compares group-level FC network by network.

To test directly whether BOLDFlow captures individual-specific connectomes rather than just the shared group pattern, we evaluated population-residual FC after subtracting the training-fold group template across all methods (App. D): deterministic baselines collapse near zero (≤0.051\le 0.051, with joint NeuroBOLT at 0.0330.033 and UnEBOLT at −0.013-0.013), whereas BOLDFlow reaches 0.1460.146 (≈3×\approx 3\times the closest baseline) and outperforms wrong-subject EEG in all 5 folds ([0.070,0.280][0.070, 0.280]). Finally, sweeping Louvain community recovery across graph edge densities from 5%5\% to 20%20\% confirms that our topological gain does not depend on a single threshold: all baselines remain at or below 0.260.26 ARI across densities, while BOLDFlow leads throughout, reaching 0.3010.301 at 5%5\% and 0.4300.430 at 10%10\%.

Thank you again for your detailed feedback. We hope the new UnEBOLT benchmark across both datasets, the covariance-aware regression control, and the individual-connectome and multi-threshold analyses address your concerns, and we would be grateful if you considered raising your score.

Thank you again for your detailed feedback. Your comments helped us strengthen the paper with the UnEBOLT comparison and additional covariance and connectivity analyses. We hope our responses clarify the points you raised, and we would be happy to discuss any remaining concerns.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal Summary for AC

Dear Area Chair,

We sincerely thank you and the reviewers for the time and effort devoted to our submission. All three reviews noted the improvement in functional connectivity (FC) recovery, and their feedback helped us further strengthen the evidence.

During the discussion phase, we provided point-by-point responses and revised the manuscript. The main points are summarized below:

  • Need for the proposed decoder (753o, nmv6, UmMS). With the same EEG encoder on NeuroBOLT, BOLDFlow reaches 0.584 FC correlation, against at most 0.420 with regression decoders and 0.461 with flow matching from a standard Gaussian source. In FC recovery it also outperforms the added UnEBOLT baseline on both datasets and a simpler model that adds a fixed residual covariance to BOLDFlow's mean prediction.
  • Cross-dataset transfer (nmv6, UmMS). Trained on OpenNeuroSleep and tested on NeuroBOLT without fine-tuning, BOLDFlow reaches 0.528 FC correlation, even above the best baseline trained on NeuroBOLT itself (0.428).
  • Readability (nmv6). The revised PDF describes the prediction and averaging pipeline more directly, with redrawn figures and Figure 2 restructured as an end-to-end pipeline diagram.

We are also encouraged that Reviewer UmMS followed up on our responses and raised their score to clear accept. We believe the additional evidence has further strengthened the paper and hope it will be taken into consideration in your final assessment.

Best regards, The Authors

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.