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Under review as a conference paper at ICLR 2027

Flattening the Connectome Spectrum: A Spectral Filter for FC Induces a Pretraining Target for fMRI Encoders

Abstract

Self-supervised pretraining reshaped prediction in language and vision, and brain foundation models (BFMs) inherited its promise. Representations learned from large unlabelled corpora should capture individual functional dynamics and generalise across cohorts. However, kernel ridge regression (KRR) fitted on functional connectivity (FC) matrices still predicts individual phenotypes more accurately than any BFM we tested. In this paper, we show that KRR is weighted by the eigenvalues of the FC which are miscalibrated for phenotype prediction. We apply an efficient spectral filter to recalibrate the eigenvalues of each subject's FC matrix, enabling the model to exploit more inter-individual variance. Across the datasets, parcellations and prediction targets we tested, we match or exceed the KRR baseline. Based on this finding, we then pretrain a small encoder model on about hours of fMRI from open datasets, whereby we align the pairwise similarities between the embeddings of recording snippets with those between the recalibrated connectomes. Our model performs on par with the best of the published BFMs we tested while having an order of magnitude fewer parameters. Our encoder performs better than FC on short scans and in smaller cohorts, especially in fingerprinting. We release the pretrained model weights, the code and the pretraining data, preprocessed and parcellated.

Primary area:
applications to neuroscience & cognitive science
Keywords:
fMRI, functional connectivity, brain foundation models, self-supervised learning, representation learning, centered kernel alignment

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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.
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Paper summary

The authors recognize that brain foundation models are lacking relative to much simpler baselines such as kernel ridge regression (KRR) on functional connectivity (FC). A diagnosis is presented showing that the FC eigenvalues are inappropriate for trait prediction, with global components being overweighted by KRR, while some potentially interesting structure that is specific to individuals is captured by intermediate ranks instead, which the paper suggests to calibrate towards. These adapted FCs are in turn used to train an encoder model on a varied dataset with strong downstream results, especially given the limited complexity of the approach.

Critical strengths
  1. The authors present a simple finding that is relevant to ML for neuroscience, which I genuinely can imagine to be adopted in the field. This finding is clearly diagnosed, is given a plausible explanation, and is shown to be likely useful for pretraining encoder models. As such, the paper is valuable as it manages to provide something novel and valuable to the community, without introducing much extra complexity.
Critical weaknesses
  1. The evaluations are currently somewhat lacking, which prevents clearly drawing some of the conclusions the paper attempts to make:

a) I believe pretraining always uses the FC^a* teacher. As such, its unclear to what extend other parts of the pipeline are responsible for the downstream gains, or whether its a* specifically. Ideally, the pretraining pipeline is repeated by only setting a=1 (and perhaps an intermediate value or two, depending on cost).

b) two of the models (BrainLM and BrainJEPA) appear to score very poorly. I'm concerned they were not appropriately reproduced, in which case the BFM comparison is thin.

Questions for authors

Primary questions that would upgrade my score when addressed:

  1. Would it be possible to use a non-a* teacher so its role for pretraining an encoder can be discerned?

  2. For BrainLM/BrainJEPA, are the authors confident the models were evaluated correctly? (small note: those models do not z-score individual parcels and in my experience in order to function they require mean-level offsets between parcels to survive preprocessing - is this the case for your datasets?)

Clarifications:

  1. Could the authors provide a case for the significance of improved fingerprinting (given that its presented as a major eval in the paper)?

  2. Could the authors speculate on why FC wins over the encoder model with larger sample sizes?

3 comments

We thank the reviewer for the positive assessment and for the questions, which we address with new experiments.

Q1. A pretraining run with a non-α∗\alpha^\ast teacher. As suggested, we pretrained fMRI-BERT using the FC-distill objective with the raw FC teacher and everything else unchanged. The student does learn from a raw-FC teacher, but the FC$^{\alpha^\ast}$ teacher is significantly better at both model sizes, on cognition and on fingerprinting, and the raw-FC encoders fall below raw FC at 2.4 minutes. The full tables and paired tests are in the general response. We will add this control to Section 5.4 and Appendix J and reword the contribution statement.

Q2. Were BrainLM and Brain-JEPA evaluated correctly?

Each model runs from its released checkpoint and released feature-extraction code, at its own parcellation and window length. The reviewer is right that our parcel timeseries are band-passed and z-scored per region, so between-parcel mean levels are absent from our inputs. Both models' own training pipelines, however, rescale every parcel before the encoder: Brain-JEPA applies robust scaling per ROI (Dong et al., 2024, Sec. 4.1) and so does BrainLM's UK Biobank preparation (Ortega Caro et al., 2024, Sec. 2.1 and model card). Rescaling each parcel removes the mean offsets between parcels, so the trained models never saw them either.

An empirical check. We encoded the same HCP-YA segments three ways, with the model's own robust scaling, with a per-parcel z-score and as stored, and probed each frozen embedding with the KRR of Table 3. BrainLM-111M and Brain-JEPA stay at chance in all three cases (∣r∣<0.04|r|<0.04).

In addition, our linear probing results align with those reported by the authors. They, too, scored well below on linear probing compared to fine-tuned models. As we mention in Section 7, fine-tuning could reorder Table 3.

Q3. Why does better fingerprinting matter?

Test–retest identification measures how much subject-specific information a representation keeps. Reliable prediction of individual traits such as cognitive ability requires that sessions of the same subject be more similar to each other than to sessions of other subjects.

The BFMs do not separate subjects better than sessions: their embeddings are stable across sessions, yet they identify the right subject on retest only 1–2% of the time, mapping every subject onto nearly the same point and discarding the individual information that cognition prediction relies on. Identification thus measures how much individual, rather than group-level, variance a representation keeps. We will add this point to Section 5.3.

Q4. Why does Ridge fitted on FC outperform the fMRI-BERT with more subjects and longer scans? Table 4 shows the gain of the encoder over FC is largest with short scans and few subjects and reverses at 38 minutes and ≥500\geq500 subjects. We see three contributing reasons and will add them to Section 5.4. (i) Capacity. KRR on the 101,025 connectome edges can fit more as the number of training subjects grows. A frozen 128- or 384-dimensional embedding cannot. With few subjects the compression helps as a regulariser; as the number of train subjects increases, it becomes a bottleneck. (ii) What the teacher denoises. The student is trained to encode the whole-recording connectome from an 80-volume window, so it helps most when the FC estimate is short and noisy. At 57.6 minutes the FC estimate is already precise. (iii) Teacher mismatch. The student matches similarities between subjects within batches drawn from 162 datasets that do not include HCP. It therefore reproduces the specific structure of HCP-YA only approximately, while KRR fitted on HCP connectomes uses it directly once there are enough subjects.

Thanks to the authors for the additional analyses.

The answers to Q1 and Q4 are especially appreciated.

I'm not quite as convinced about the response to Q2 however. The comparison models' robust scaling use statistics computed across subjects instead of per recording. While it shifts subject-specific amplitude differences, they are very much still present, so from the response I can't tell if the authors still provided OOD inputs. Regarding the empirical check; was this done on z-scored data? If so, there is no way to recover the between-subject offset information and this would not tell us anything.

Q2. We thank the reviewer for this remark. Our check used inputs that were already z-scored per recording, so it could not test the reviewer's point. For the camera-ready version, we will update all results accordingly: Table 3, the other cohorts in the appendix and every corresponding table.

We re-evaluated both models exactly as their released code prepares the data: regional BOLD level kept, robust scaling across subjects, and each model's own region order (Brain-JEPA: Tian-S3 then Schaefer-400 in 17-network order; BrainLM: A424 sorted by yy coordinate).

Both models are now well above chance, but F-BERT remains significantly better. HCP-YA cognition composite, same subjects, folds and probe as Table 3; mean ±\pm std over the 200 folds:

EncoderScanCognition rr
BrainLM-111M2.4 min0.324±0.0950.324 \pm 0.095
BrainLM-650M2.4 min0.384±0.0930.384 \pm 0.093
Brain-JEPA5.8 min0.308±0.0900.308 \pm 0.090
F-BERT-1M (ours)2.4 min0.408±0.1000.408 \pm 0.100
F-BERT-8M (ours)2.4 min0.404±0.1000.404 \pm 0.100
F-BERT-1M (ours)57.6 min0.491±0.0900.491 \pm 0.090
F-BERT-8M (ours)57.6 min0.520±0.0830.520 \pm 0.083

On full scans, F-BERT-1M exceeds BrainLM-650M by 0.1080.108 (p=0.001p = 0.001), BrainLM-111M by 0.1670.167 (p≤0.001p \le 0.001) and Brain-JEPA by 0.1840.184 (p≤0.001p \le 0.001). At 2.4 minutes F-BERT-1M is level with BrainLM-650M, which has almost 800 times more parameters, and above the other two (p≤0.03p \le 0.03). Tests are the corrected resampled tt-test on the 200 paired folds.

We will correct every affected row.

Reviewer_uizTOpenReview ↗
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Paper summary

The paper observes that each subject's functional connectivity matrix has a very uneven eigenvalue spectrum, which concentrates correlation-kernel ridge regression on a few percent of the eigenvectors. Its proposal is to raise each subject's eigenvalues to a single global power, chosen once on one dataset, parcellation and target from outer-fold scores and reused everywhere. The recalibrated connectome then serves as a pretraining target, aligning pairwise embedding similarities with pairwise connectome similarities for 1M and 8M encoders trained on open data. The two claims are that the transform matches or improves phenotype prediction across the evaluated settings, and that the encoder matches or passes the brain foundation models at an order of magnitude fewer parameters.

Critical strengths

A one-parameter spectral transform produces large paired gains over raw FC on identical folds, and it holds at every dataset and parcellation tested. The paper also tests the mechanism by scoring the same top-k eigenvectors with raw and with recalibrated eigenvalues, so the weighting is isolated from the eigenvectors it is applied to. The evaluation addresses the biases that usually inflate results in this literature, with family-aware HCP-YA folds, site-grouped folds on the clinical cohorts, prediction components fit on training folds only, and corrected paired tests. Section 7 discloses that the exponent was chosen on outer-fold scores rather than inside the nested loop, instead of leaving a reader to notice, and the code, the encoders and the pretraining corpus are released.

Critical weaknesses

The short-window transform rows are a prominent sub-claim, and I could not find a statement of how zero or numerically negative eigenvalues are handled there. Section 3.2 assumes every eigenvalue strictly positive, whereas the 2.4-minute rows give 200 timepoints across 450 parcels and a rank-deficient correlation matrix. The transform still computes, since a positive power leaves zero eigenvalues at zero, but the readings that motivate it do not all survive: the log and geodesic limits of the same family are unavailable on a singular matrix, and the conditioning ratio offered as motivation is computed across full-scan subjects. None of this touches the encoder's short-scan advantage, whose teacher comes from the full recording.

The second contribution's attribution is also untested. The title has the spectral filter inducing the pretraining target, and the contribution is described as derived from the transformation, but I could not find a run with the teacher's exponent at one, so nothing separates a recalibrated teacher from a whole-recording teacher seen by a windowed student. The mechanism the paper itself offers for the short-scan result is the second of those, and a raw-FC teacher would supply it. On fingerprinting the encoder does reach 0.841 where raw FC is at 0.762, which is at least consistent with the recalibration mattering, though a distilled student is not barred from exceeding its teacher on a downstream score, so I would not read it as attribution. On the full-scan cognitive composite, where the comparison against published models lives, the encoder sits below raw FC. A single pretraining run with a raw-FC teacher would directly test this attribution

Questions for authors

Q1. Is there a pretraining run with a raw-FC teacher? Without one I cannot separate the recalibration from the fact that the teacher sees the whole recording while the student sees a window.

Q2. If the implementation clips or floors eigenvalues before raising them to the power, what is the threshold, and does the 2.4-minute advantage over raw FC survive setting everything below it exactly to zero?

Q3. One exponent at 0.35 carries across parcellations from 100 to 1000 regions, where both the shape of the spectrum and the number of estimable directions change a great deal. Is there a reading of why a single value transfers that far, or is it an empirical regularity for now?

3 comments

We thank the reviewer for the positive assessment and interest in the paper.

W1, Q2: Zero and numerically negative eigenvalues. This is an omission on our part. We will add it to Section 3.2 and Appendix D. Two pipelines handle the spectrum differently.

  • KRR rows (Tables 1, 2, 5–8). The connectome is estimated with Ledoit–Wolf shrinkage of the z-scored timeseries and eigenvalues are clipped from below at 10−710^{-7}. The shrunk matrix is positive definite, so λα\lambda^\alpha, log⁡Σ\log\Sigma and the geodesic readings of Appendix D are defined, including on AOMIC, where the sample correlation is singular.
  • Short-window rows of Table 3 and the pretraining teacher. These use the plain Pearson correlation of the window, which has rank at most T−1T-1, so most eigenvalues are zero. Before the power, every eigenvalue below 10−810^{-8} is set to 10−810^{-8}; this also covers the slightly negative values produced by round-off. After the power these modes weigh (10−8)0.35=1.6×10−3(10^{-8})^{0.35}=1.6\times10^{-3}, against 0.5–5 for the non-zero modes, so they are almost but not exactly removed. The pretraining teacher is the matrix itself, not its logarithm, so zero eigenvalues cause no problem there.

We agree that the log and geodesic readings do not apply to a singular matrix, and that the condition number quoted in Section 3.2 is for full scans. We will say so where they appear.

Does the 2.4-minute advantage survive setting the zero eigenvalues exactly to zero? Yes, to the third decimal. We re-scored the 2.4-minute rows of Table 3 (955 subjects, 450 regions, same folds and probe) with α=0.35\alpha=0.35 and different treatments of the small eigenvalues:

handling of the spectrumpooled rrfold mean ± stdvs paper (Δ\Delta, pNBp_{NB})
raw FC (α=1\alpha=1)0.3500.346±0.105-0.092, 5×10−65\times10^{-6}
clip at 10−810^{-8} (the paper)0.4600.438±0.101–
eigenvalues <10−6<10^{-6}, <10−4<10^{-4} or <10−2<10^{-2} set to exactly 00.4600.438±0.1010.000, ≥0.31\geq0.31
eigenvalues <10−1<10^{-1} set to 00.4580.436±0.101-0.002, 0.06
only the T−1T-1 largest modes kept0.4600.438±0.1010.000, 0.06
Ledoit–Wolf shrinkage, as in Table 10.4570.435±0.101-0.003, 0.06

Every variant beats raw FC and none differs from the paper. The reason is that the clipped modes together carry only 0.6% of the trace of FC$^{0.35}$. Because the timeseries are band-passed to 0.01–0.08 Hz, a 200-volume window has rank about 55, so 393–398 of the 450 eigenvalues are zero up to round-off. The short-scan gain therefore does not depend on how these eigenvalues are treated.

The second contribution's attribution (Weakness 2, Q1). We agree: without a raw-FC teacher we cannot tell whether the gain comes from the recalibration or from distilling a whole-recording teacher into a windowed student. We ran this control, both encoders pretrained again with raw FC as teacher and everything else unchanged. The student does learn from a raw-FC teacher, but the FC$^{\alpha^\ast}$ teacher is significantly better at both model sizes, on cognition and on fingerprinting, and the raw-FC encoders fall below raw FC at 2.4 minutes. The full tables and paired tests are in the general response. We will add this control to Section 5.4 and Appendix J and reword the contribution statement.

Q3. Why does one exponent transfer across parcellations from 100 to 1000 regions? We acknowledge that we overstated the transfer claim for α=0.35\alpha=0.35 specifically; multiple values can result in good performance across parcellations. First, the range of optimal values is flat: on the fine grid of Figure 3 every exponent in [0.25,0.50] is within 0.01 of the best. Second, the exponent acts on how unequal the eigenvalues are, not on how many there are. On HCP-YA the twenty largest eigenvalues hold 90/83/80/77% of the total at Schaefer-100/200/300/400, and the training-fold criterion of Section 3.3 gives αA\alpha_A = 0.27/0.35/0.39/0.42, with α=0.35\alpha=0.35 within 1.3% of the best value at every resolution. The dominant modes are the same 7 Yeo networks at any resolution, so one exponent has roughly the same effect regardless of the parcellation. We will discuss this in Section 7.

Thanks to the authors for the additional analyses. My main concerns are resolved, and I keep my score.

Please also add the Ledoit-Wolf estimation used for the KRR rows to Section 3.2, which currently defines FC as the sample Pearson matrix.

We thank the reviewer for their time. We will feature the requested estimation in the revised manuscript.

Reviewer_eEm4OpenReview ↗
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Paper summary

The paper studies the problem of phenotype prediction from functional connectivity data. They argue that the kernel ridge regression (KRR) is one of the top models for this prediction problem and show how these models are often miscalibrated (biased towards the top eigenvectors of the FC matrix) and correcting for this bias improves predictions across several datasets. Finally, they also show that while brain foundation models often can't match the KRR baseline, training encoders to produce similarities aligned with the recalibrated connectomes gives superior performance (ie they can match the foundation models despite fewer parameters).

Critical strengths
  • The paper is clear and easy to follow
  • The authors introduce a simple fix (flattening the connectome's eigenspectrum) and show that it substantially improves the prediction of phenotypes. This performance advantage despite the simplicity of the method is interesting
  • The authors perform a rigorous comparison across multiple datasets.
Critical weaknesses
  1. Broader baseline comparisons would strengthen the evaluation. The comparisons with brain foundation models are useful, but other supervised approaches, such as BrainNetCNN or 3D CNNs, are missing. I understand that a central goal is to show that KRR itself can be improved through spectral recalibration. Still, these additional comparisons would help establish how competitive the resulting approach is more broadly. Testing recalibration with another FC-based predictor would also help clarify whether its benefits extend beyond KRR.

  2. A more intuitive scientific discussion of the FC eigenspectrum would be helpful. The paper provides mathematical interpretations of the transformation, but I would appreciate a clearer explanation of what the eigenvectors and eigenvalues represent in terms of coordinated brain activity, and what flattening the spectrum means from this perspective. For example, why might modes that explain less within-subject activity variance carry useful information about differences between individuals? How should we understand the balance between making these modes more influential and amplifying noise? Connecting the spectral transformation to these questions would make the findings easier to interpret scientifically.

  3. For the pretraining experiments, another control is missing. Particularly, the authors should try training the encoders using raw FC rather than recalibrated FC to show that it was really recalibration that improved the performance.

  4. The authors acknowledge that the exponent was selected using the same HCP folds on which its performance is reported. But this should be corrected as it is essentially double-dipping. A separate validation set or nested cross-validation pipeline is needed for unbiased comparisons on HCP.

  5. In Table 2, recalibrating just the top 20 modes improves prediction from 0.544 to 0.610 but adding the remaining 380 modes increases it only to 0.624. Thus, much of the improvement comes from rebalancing the leading modes, with a smaller additional contribution from the tail. This deserves a clearer discussion before interpreting the improvement as recovering information spread across many low-variance modes.

Questions for authors

See weaknesses above

1 comment

We thank the reviewer for their time and thoughtful feedback.

W1. Broader baselines, and does the recalibration help predictors other than KRR?

Why KRR is the reference. On this protocol deep networks on FC have not beaten kernel ridge regression (He et al., 2020); KRR is also the baseline that the brain-foundation-model literature itself fails to beat (Ling et al., OHBM 2026), which is the gap the paper starts from.

New experiment: BrainNetCNN and an MLP. We trained BrainNetCNN (Kawahara et al., 2017) and a two-hidden-layer MLP, each on FC and on FC$^{\alpha^\ast}$, for the HCP-YA cognitive composite on 50 of the 200 folds of Table 1 (its first 5 repetitions).

predictor, HCP-YA Schaefer-400FC (α=1\alpha=1)FC$^{\alpha^\ast}$\Delta\pNBp_{NB}
KRR (same folds)0.541±0.0830.622±0.080+0.0815×10−85\times10^{-8}
BrainNetCNN0.437±0.1400.480±0.106+0.0430.41
MLP0.389±0.1780.554±0.116+0.1650.016

The recalibration helps both non-kernel predictors, significantly so for the MLP and in direction for BrainNetCNN, and KRR on FC$^{\alpha^\ast}$ remains the best predictor on these folds, which is consistent with our results and with He et al. (2020). We will add this table to Appendix F.

W2. An interpretation of the eigenspectrum rebalancing. We agree this reading was missing; we will add it to Section 3.2 and the new analyses to the appendix.

Our interpretation is that the transform attenuates most of the group mean component and lets the intermediate eigenmodes, which carry the subject-specific weights, enter the kernel. This explains the gain in fingerprinting. In raw FC the first eigenmode dominates the regression: λ1/λ20=48.9\lambda_1/\lambda_{20}=48.9. This mode loads most on the sensory networks and is nearly the same for every subject: in effect the group-mean connectivity. The exponent lowers it relative to the other modes. The individual structure sits in the network-level modes that follow, roughly the second to the twentieth, whose relative weights differ between subjects.

Two new experiments support this. First, the recalibration acts like a group demeaning. Over HCP-YA subjects, each parcel's dependence on the first eigenmode is 49.7% on average with raw FC and 8.5% with FC$^{\alpha^\ast};subtractingthegroup−meanFCgives8.8; subtracting the group-mean FC gives 8.8%, and the two changes agree across parcels (r=0.92$). Similar to other transformations that score below FC$^{\alpha}$ (Appendix E). Second, the networks whose share of the matrix grows most are the default and frontoparietal control networks (+2.4 and +2.6 points), the networks shown to carry most individual-specific information (Kong et al., 2019).

A deeper explanation would extend beyond the scope of this work.

W3. A raw-FC teacher for the pretraining. We ran this control, both encoders pretrained again with raw FC as teacher and everything else unchanged. The student does learn from a raw-FC teacher, but the FC$^{\alpha^\ast}$ teacher is significantly better at both model sizes, on cognition and on fingerprinting, and the raw-FC encoders fall below raw FC at 2.4 minutes. The full tables and paired tests are in the general response. We will add this control to Section 5.4 and Appendix J and reword the contribution statement.

W4. Selecting α\alpha on the reported HCP folds. We agree this is double dipping for the HCP Schaefer-400 cell and have removed it. We re-ran HCP-YA and AOMIC with α selected inside each training fold, together with the ridge penalty, on the same 200 folds:

cohortnested α\alphafixed α=0.35\alpha=0.35raw FC (α=1\alpha=1)nested vs fixednested vs raw FC
HCP-YA (n=955n=955)0.625±0.0790.627±0.0800.543±0.083-0.001, pNB=0.26p_{NB}=0.26+0.083, pNB=1×10−9p_{NB}=1\times10^{-9}
AOMIC-ID1000 (n=877n=877)0.427±0.0820.432±0.0810.348±0.085-0.005, pNB=0.15p_{NB}=0.15+0.079, pNB=2×10−4p_{NB}=2\times10^{-4}

Nested selection reproduces the fixed exponent to within 0.005. The selected exponent was 0.35 in 118 of the 200 HCP folds and 0.40 in 74, and never outside [0.30,0.45]. The exponent was never tuned on AOMIC, CoRR, ABIDE-I or ADHD-200, which act as held-out cohorts for the fixed value. We will report the nested rows in Table 1 and Appendix B and drop the caveat in Section 7.

W5. Table 2: most of the gain comes from the leading modes. Agreed, and the introduction overstates the tail. More than 80% of the total gain in performance comes from re-balancing the weights within the leading twenty modes, and the rest from the remaining 380. We will (i) replace the sentence in Section 1 ("the variance that distinguishes individuals is spread over a larger space") by this statement, (ii) make the same point when Table 2 is introduced, and (iii) keep the small tail contribution as what it is: small, and only recoverable once the leading modes no longer dominate.

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