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Under review as a conference paper at ICLR 2027

DeeperBrain: A Neuro-Grounded EEG Foundation Model Towards Universal BCI

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Abstract

Electroencephalography (EEG) foundation models promise general-purpose representations for Brain-Computer Interfaces (BCIs), yet most transfer effectively only under end-to-end fine-tuning and degrade markedly under frozen-probing—a protocol that diagnoses whether task-relevant information is directly accessible in a fixed representation. We attribute this gap to the reliance on generic sequence architectures that overlook the biophysical and dynamical structure of neural activity. We propose DeeperBrain, an EEG foundation model that injects neurophysiological inductive biases at two levels. Architecturally, a volume-conduction-aware channel encoding models spatial mixing from 3D electrode geometry, and a neurodynamics-aware temporal encoding captures slow oscillations and adaptive decay. For pretraining, we combine Masked EEG Reconstruction (MER) with Neurodynamics Statistics Prediction (NSP), an auxiliary self-supervised objective whose targets—spectral power, phase synchronization, cross-frequency coupling, and signal complexity—are computed directly from the signal and aligned with established neurophysiological descriptors. Pretrained on over 17,200 hours of heterogeneous EEG and evaluated on 12 downstream datasets spanning emotion, motor, sleep, seizure, speech, disorder, vigilance, and workload tasks, DeeperBrain achieves state-of-the-art or competitive fine-tuning performance and, notably, consistently superior frozen-probing performance. The results indicate that neurophysiological priors make downstream information more accessible without backbone adaptation, a property we view as a necessary step toward universal BCI. Our code will be publicly available on Github.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG, EEG foundation model, EEG decoding, BCI, Neuro-Grounded

Reviews

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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_DAJwOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper proposes DeeperBrain, an EEG foundation model that injects neurophysiological inductive biases into masked-reconstruction pretraining through a volume-conduction-aware channel positional encoding, an oscillatory temporal encoding, and a dual objective combining Masked EEG Reconstruction (MER) with Neurodynamics Statistics Prediction (NSP), an auxiliary regression of nineteen signal-computed statistics. Using about 17,000 hours of public EEG and 5.8M parameters, the model is evaluated under end-to-end fine-tuning and frozen probing on twelve downstream datasets across eight BCI task categories, where it is competitive under fine-tuning and ranks best on all twelve under frozen probing.

Critical strengths

The frozen probing result is substantial. DeeperBrain wins all twelve datasets in Table 4, often by wide margins, for example 50.96 versus 37.76 on FACED and 63.36 versus 53.00 on MODMA. This addresses a documented failure mode of current EEG foundation models and is practically valuable when downstream labels are scarce.

Critical weaknesses

The fine-tuning state of the art claims are under-supported. Tables 3 and 4 report no significance tests, several margins are within about one standard deviation, the win count in Section 3.3 does not match the table, and the emotion benchmarks SEED-V and SEED-VII use within-subject trial splits, which weakens the generalization narrative.

Questions for authors
  1. Can you add a control pretraining run with an auxiliary target of matched dimensionality that is not neurophysiologically canonical, for example time-domain moments or random linear projections of the spectrum, to isolate whether the gain comes from neurophysiological alignment specifically?
  2. How does a frozen linear probe on classical handcrafted features such as the exact NSP statistics compare on these twelve tasks? Does the DeeperBrain representation exceed the information injected by NSP?
  3. For the probe head family in Section 2.8, was the pooling choice selected per dataset and shared across all models, or tuned per model? What learning rate budget was given to each baseline frozen probe, given that several baselines collapse to exactly chance, for example CSBrain at 20.00 on SEED-V?
4 comments
AuthorsOpenReview ↗

Response to Reviewer DAJw [1/n]

We thank the reviewer for the precise reading — including catching the presentation error, which we correct below — and for the constructive control-experiment suggestions, all of which we have run.

W1 (Critical Weakness)

"The fine-tuning state of the art claims are under-supported. Tables 3 and 4 report no significance tests, several margins are within about one standard deviation, the win count in Section 3.3 does not match the table, and the emotion benchmarks SEED-V and SEED-VII use within-subject trial splits, which weakens the generalization narrative."

Response. We address the four points in turn.

  1. No significance tests. Added for every Table 3/4 comparison via one-sided Welch t-tests on the reported 5-seed mean±std. Bottom line: frozen-probing gains are significant on 7/12 datasets, mean-best on 12/12, with no significant loss anywhere; fine-tuning is significantly better on 2/12 (FACED +2.80, p=2.0e-06; MODMA +3.46, p=0.034), statistically tied on 8, and significantly worse on 2 (SEED-V −1.29 vs. CSBrain; BCIC-IV-2a −3.27 vs. REVE). Full per-comparison test tables and per-comparison significance markers are now included in the revised Tables 3/4 and appendix (Tables 3–4 with markers, p. 6; full table and discussion: Appendix F, p. 22, Table 9, p. 23). This directly supports the reviewer's reading that several fine-tuning margins are within noise.
  2. Win count (Section 3.3). The reviewer is right: Table 3 bolds 7 datasets, and Section 3.3's "8 of 12" is an error. Corrected to 7 of 12 in the revision (Sec. 3.3, p. 6).
  3. Fine-tuning claims. We agree the "state-of-the-art" phrasing over-reaches given the 2 significant losses (SEED-V, BCIC-IV-2a). The revision states: competitive or superior under fine-tuning (best or second-best on 11/12), and best on all 12 under frozen-probing with statistical support — shifting the weight of the claim to where the evidence is strong. This softened phrasing now appears in the Abstract (p. 1), the contributions in Sec. 1 (p. 2), and the Conclusion (p. 10), and Sec. 3.3 (p. 6) correspondingly reads "best result on 7 of 12 datasets and is competitive on the remainder, never falling below third."
  4. Within-subject trial splits (SEED-V/SEED-VII). These splits follow LaBraM/CBraMod exactly for comparability (both baselines use the same within-subject protocol, so the comparison is internally fair); the remaining 10 datasets use subject-level splits. To address the generalization concern directly we added a within-subject cross-session analysis on SEED-V: frozen representations show only moderate cross-session drift (linear CKA 0.33–0.36) and cross-session decoding remains clearly above chance (Appendix H, p. 26; Fig. 9, p. 26), and we have stated the split limitation explicitly in the revision (Sec. 3.2, p. 5).
AuthorsOpenReview ↗

Response to Reviewer DAJw [2/n]

Q1 (Question)

"1. Can you add a control pretraining run with an auxiliary target of matched dimensionality that is not neurophysiologically canonical, for example time-domain moments or random linear projections of the spectrum, to isolate whether the gain comes from neurophysiological alignment specifically?"

Response. Yes — we ran exactly these controls. We retrained from scratch under the identical protocol (same backbone, MER, mask ratio, optimizer, 2 epochs, batch 64) with three 19-D non-canonical targets, plus the four NSP leave-one-out ablations for completeness, and evaluated all variants under one unified frozen-probing protocol (5 seeds; a single per-dataset learning rate fixed and shared across all variants). Deltas are reported relative to the paper's full-NSP average (Table 4, 12 datasets):

Pretraining target (19-D unless noted)Neurophysiologically canonical?Frozen-probing avg (12 datasets)Δ vs. full NSP
Full NSP (paper)✓54.28—
− spectral power (14-D)partially51.62−2.66
− PLV (9-D)partially51.49−2.79
− CFC (16-D)partially53.32−0.96
− SampEn (18-D)partially50.76−3.52
moments (time-domain moments)✗51.39−2.89
shuffle (NSP targets of mismatched samples)✗48.56−5.72
random_proj (random linear projection of the spectrum)✗46.33−7.95

No variant matches the full NSP target, and the drop scales with how much of the target's neurophysiological structure is destroyed. The two reviewer-suggested controls are covered: random_proj — dimensionality-matched but structure-free — causes the largest degradation (−7.95), ruling out auxiliary-target regularization or dimensionality as the source of the gain; shuffle preserves the exact NSP target marginals while destroying the sample–target correspondence and still loses 5.72 points: even matching dimensionality and target statistics is not enough — the pairing between each sample and its own neurodynamics is what matters. moments keeps only coarse, first-order sample information (−2.89). Among the leave-one-out ablations, every NSP component contributes positively (−0.96 to −3.52), with the largest single-component contribution from SampEn. Overall, the full target's advantage is carried by its sample-specific neurophysiological structure: the more of that structure is removed or destroyed, the larger the degradation. This experiment is now included in the revision (Appendix G, pp. 23–24; Table 10, p. 23).

AuthorsOpenReview ↗

Response to Reviewer DAJw [3/n]

Q2 (Question)

"2. How does a frozen linear probe on classical handcrafted features such as the exact NSP statistics compare on these twelve tasks? Does the DeeperBrain representation exceed the information injected by NSP?"

Response. We probed the exact 19-D NSP statistics (computed with the same estimators used to build the NSP targets during pretraining — band-power ratios, PLV, CFC, and sample entropy — applied to the raw downstream signals), aggregated to a fixed 38-D sample feature (per-statistic global mean + inter-channel std; PLV is channel-broadcast by construction), with both a linear probe (LogReg, balanced) and a small MLP, selecting on validation — a strictly fair information test of "does the representation merely reproduce the injected statistics?" (12/12 tasks complete):

Dataset (chance)Handcrafted NSP statsDeeperBrain frozen probe (paper Table 4)Gap
FACED (11.11)14.8850.96±0.37+36.08
SEED-V (20.00)20.0435.08±0.26+15.04
SEED-VII (14.29)14.2923.26±0.22+8.97
PhysioNet-MI (25.00)24.5056.57±0.73+32.07
BCIC-IV-2a (25.00)30.4751.01±2.23+20.54
SHU-MI (50.00)50.6960.81±1.80+10.12
ISRUC (20.00)26.2974.10±0.58+47.81
MODMA (50.00)55.9263.36±2.40+7.44
CHB-MIT (50.00)50.0164.95±2.55+14.94
BCIC2020-3 (20.00)23.3343.33±0.64+20.00
SEED-VIG (Pearson r×100, chance 0.00)38.2259.85±1.24+21.63*
MentalArithmetic (50.00)64.2468.05±0.40+3.81

*SEED-VIG is a regression task: both the handcrafted probe (Ridge) and the model are evaluated with Pearson r, and the row is reported as r×100 to match the paper's presentation of this dataset. Handcrafted probes are single validation-selected probes (logistic regression or the small MLP); the logistic-regression ones are deterministic, hence no std is reported for that column.

The probes on the raw NSP statistics are at chance on 5/12 tasks, and even on the tasks where handcrafted statistics carry signal they remain 3.81–47.81 points below the model's frozen probe (average model advantage +19.87 points over the 12 tasks). The answer to the reviewer's question is therefore yes, decisively: the pretrained representation contains substantially more task-relevant information than the NSP statistics injected during pretraining — NSP acts as an alignment signal that shapes the representation, not as a ceiling on it. (FACED has 9 classes (chance 11.11); its handcrafted probe is above chance yet still 36.08 points below the model's frozen probe.) This analysis is now included in the revision (Appendix G, p. 24; full 12-row table with footnotes: Table 11, p. 24).

AuthorsOpenReview ↗

Response to Reviewer DAJw [4/n]

Q3 (Question)

"3. For the probe head family in Section 2.8, was the pooling choice selected per dataset and shared across all models, or tuned per model? What learning rate budget was given to each baseline frozen probe, given that several baselines collapse to exactly chance, for example CSBrain at 20.00 on SEED-V?"

Response.

  • Head family / pooling: task-dependent heads (as stated in Appendix), with the pooling and output structure selected per dataset (by validation) and then fixed and shared across all models for that dataset — never tuned per model.
  • Learning-rate budget: every frozen probe — DeeperBrain and all baselines — used the identical budget: AdamW (wd 5e-2), cosine annealing, lr ∈ {1, 3, 5}×10⁻⁴ selected on validation, batch 32/64 by dataset scale, 50 epochs, 5 seeds (Appendix "Evaluation protocol").
  • Why some baselines collapse to near chance (e.g., CSBrain 20.00±0.00 on SEED-V): we fully share the reviewer's concern that such a low number could stem from insufficient tuning of the baseline on our side, and we therefore treated this as a priority during the discussion period and re-ran CSBrain's frozen probe on SEED-V with a deliberately expanded search — the full head family (all four classifiers), AdamW, lr ∈ {1, 3, 5}×10⁻⁴ selected on validation, 50 epochs, 5 seeds, i.e., the identical budget as every other model. Even under this best-effort protocol the best configuration only reaches BA 22.62±0.28, κ×100 = 3.49±0.36, F1 22.69±0.45. This addresses the concern in three ways: (i) the reproduction is above the paper-reported 20.00 and shows healthy seed variance, so the expanded protocol was in fact slightly more favorable to the baseline; (ii) the value still sits in the chance neighborhood of the 5-class task (20.00), with κ×100 = 3.49 ≈ 0 confirming that no discriminative signal is extractable from CSBrain's frozen features on SEED-V — the near-chance result is a property of the frozen representation, not of the evaluation or of an under-tuned reproduction; (iii) by exhaustion, since every head variant and every learning rate in the grid converges to the same chance-level band, further tuning is unlikely to change the picture. This best-effort re-evaluation has been incorporated in the revised manuscript (Appendix D, "Note on near-chance baseline results", p. 21). For reference, the same budget yields REVE 27.8 and DeeperBrain 35.08 on the same task, and DeeperBrain retains a +12.46-point margin over the reproduced CSBrain. Our unified re-evaluation of all control models applies this same protocol, and the paper-reported numbers of the original weights serve as the reference row so that all control comparisons are within-protocol.
Reviewer_ZWrBOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes DeeperBrain, a neurophysiology-grounded EEG foundation model designed to improve cross-task transferability, particularly under frozen-probing settings. DeeperBrain incorporates neurophysiological inductive biases into both model architecture and pretraining. The model is pretrained on approximately 17,243 hours of EEG recordings and evaluated on 12 downstream datasets spanning eight BCI task categories. Experimental results demonstrate competitive or superior fine-tuning performance and the best frozen-probing performance across all evaluated datasets. The authors conclude that incorporating neurophysiological priors improves the transferability and accessibility of task-relevant information in fixed EEG representations.

Critical strengths
  1. Meaningful integration of neurophysiological priors into EEG foundation modeling. The paper presents a coherent framework that incorporates neurophysiological knowledge into both model architecture and self-supervised pretraining. The proposed spatial and temporal positional encodings, together with the NSP objective, provide a physiologically motivated approach to improving EEG representation learning. This integration offers a meaningful direction beyond purely data-driven EEG foundation models.
  2. Comprehensive evaluation and strong frozen-probing performance. The experiments cover 12 downstream datasets across eight BCI task categories, including both end-to-end fine-tuning and frozen-probing protocols. DeeperBrain achieves the best frozen-probing performance on all evaluated datasets. The ablation studies further demonstrate the effectiveness of the proposed positional encodings and the complementary contributions of MER and NSP, providing substantial empirical support for the method.
Critical weaknesses
  1. Insufficient physiological validation of the proposed spatial and temporal encodings. Although the ablation experiments demonstrate that the proposed spatial and temporal encodings improve downstream performance, their physiological interpretations remain insufficiently validated. For spatial encoding, Figure 4 mainly visualizes the predefined distance-decay prior rather than demonstrating its correspondence to actual EEG volume conduction. For temporal encoding, Figure 5 illustrates the designed oscillatory and adaptive decay functions without directly validating their relationship to neural dynamics. Moreover, the paper lacks dedicated within-subject cross-session or longitudinal evaluations to examine whether the temporal encoding improves representation stability across recording times. Consequently, it remains unclear whether the improvements arise from meaningful neurophysiological modeling or more general architectural inductive biases.
  2. Insufficient evidence that NSP learns broadly generalizable neurophysiological representations. Although NSP incorporates established physiological statistics, the contributions of individual statistics to downstream improvements remain unclear. Figure 6 shows strong prediction consistency for spectral power and sample entropy but near-zero correlations for cross-frequency coupling. Furthermore, the evaluated downstream tasks may already benefit from the handcrafted statistics used as NSP supervision. Without component-wise ablations or evaluations on tasks less aligned with these predefined descriptors, it is difficult to determine whether NSP learns generalizable neurophysiological representations or primarily improves performance through task-relevant statistical supervision. This limits the strength of the paper's central claim regarding neurophysiologically grounded transferability.
Questions for authors
  1. Physiological validity of the spatial encoding. Although the spatial encoding ablation demonstrates performance improvements, Figure 4 primarily visualizes the predefined distance-decay prior. Can the authors provide more direct evidence that the learned spatial representations correspond to actual EEG volume-conduction properties? Additionally, how does the proposed encoding perform under controlled changes in electrode density or montage configuration?
  2. Temporal encoding and within-subject generalization. The proposed temporal encoding is motivated by slow neural oscillations and adaptive decay. However, the current evaluation does not directly establish whether these mechanisms improve temporal generalization. Can the authors provide within-subject cross-session or longitudinal evaluations to assess representation stability across recording times? Is there evidence that the learned representations reflect actual neural adaptation dynamics rather than simply benefiting from alternative temporal basis functions?
  3. Contribution and generalizability of individual NSP statistics. Figure 6 shows substantial differences in prediction consistency across NSP statistics, particularly the near-zero correlations for cross-frequency coupling. Can the authors provide component-wise ablations to clarify which statistics contribute most to downstream performance? Furthermore, does NSP remain beneficial for downstream tasks whose discriminative information is not well captured by the predefined physiological descriptors?
8 comments
AuthorsOpenReview ↗

Response to Reviewer ZWrB [1/n]

We thank the reviewer for the detailed reading and for identifying exactly the two places — encodings and NSP — where physiological grounding needed harder evidence. All new experiments below use the paper's unchanged protocol.

W1 (Critical Weakness)

"1. Insufficient physiological validation of the proposed spatial and temporal encodings. Although the ablation experiments demonstrate that the proposed spatial and temporal encodings improve downstream performance, their physiological interpretations remain insufficiently validated. For spatial encoding, Figure 4 mainly visualizes the predefined distance-decay prior rather than demonstrating its correspondence to actual EEG volume conduction. For temporal encoding, Figure 5 illustrates the designed oscillatory and adaptive decay functions without directly validating their relationship to neural dynamics. Moreover, the paper lacks dedicated within-subject cross-session or longitudinal evaluations to examine whether the temporal encoding improves representation stability across recording times. Consequently, it remains unclear whether the improvements arise from meaningful neurophysiological modeling or more general architectural inductive biases."

Response (summary; detailed evidence in our replies to Q1 and Q2 below). The reviewer's concern splits into a spatial part and a temporal part, and we added one new experiment for each. (a) Spatial: we computed the empirical channel-to-channel correlation as a function of inter-electrode distance over 171,000 channel-pair observations from the pretraining corpus; the empirical decay constant (τ_emp = 7.73 cm) quantitatively matches the designed prior (τ = 8 cm), so the injected prior corresponds to the observed volume-conduction scale of real EEG rather than to a convenient parameterization (full reply in Q1 below, new experiment). (b) Temporal: on SEED-V — which records every subject in three sessions up to two weeks apart — the frozen representations show only moderate cross-session drift (linear CKA 0.33–0.36) and cross-session probes remain clearly above chance; moreover, the paper's positional-encoding ablation shows that replacing our oscillatory/adaptive temporal basis with a generic sinusoidal PE degrades probing by 3.20 points on average, indicating the benefit is not from any temporal basis (full reply in Q2 below, new experiment). Each experiment comes with a dedicated interpretability visualization (matrix-level spatial correspondence; basis-wise temporal-utilization profiles). Together these two results address the reviewer's final sentence directly: the improvements arise from physiologically calibrated structure, not from generic inductive biases. Both new analyses and their visualizations are now in the revised manuscript (Appendix H, pp. 24–27; Figs. 7–10, pp. 25–27).

W2 (Critical Weakness)

"2. Insufficient evidence that NSP learns broadly generalizable neurophysiological representations. Although NSP incorporates established physiological statistics, the contributions of individual statistics to downstream improvements remain unclear. Figure 6 shows strong prediction consistency for spectral power and sample entropy but near-zero correlations for cross-frequency coupling. Furthermore, the evaluated downstream tasks may already benefit from the handcrafted statistics used as NSP supervision. Without component-wise ablations or evaluations on tasks less aligned with these predefined descriptors, it is difficult to determine whether NSP learns generalizable neurophysiological representations or primarily improves performance through task-relevant statistical supervision. This limits the strength of the paper's central claim regarding neurophysiologically grounded transferability."

Response (summary; detailed evidence in our reply to Q3 below). We ran exactly the two missing experiments the reviewer asks for: (a) component-wise leave-one-out pretraining — four retraining runs, each with one NSP component removed; every component contributes positively (0.96–3.52 points on the 12-dataset average), and the ordering tracks the predictability hierarchy of Fig. 6: the two statistics with strong prediction consistency — spectral power and PLV — are among the larger contributors, CFC with its near-zero prediction consistency contributes the least (0.96 points), and SampEn contributes the most (3.52 points), reflecting nonlinear signal irregularity that the spectral measures do not capture; (b) probes on the raw NSP statistics themselves — on 5/12 tasks these sit at chance, and on every task they stay below the model's frozen probe (average gap +19.87 points), so the evaluated tasks do not simply benefit from the injected handcrafted statistics. Full tables and the tasks-poorly-aligned-with-descriptors analysis are in Q3 below; both are incorporated in the revision (Appendix G, pp. 23–24; Tables 10–11, pp. 23–24).

AuthorsOpenReview ↗

Response to Reviewer ZWrB [2/n]

Q1 (Question)

"1. Physiological validity of the spatial encoding. Although the spatial encoding ablation demonstrates performance improvements, Figure 4 primarily visualizes the predefined distance-decay prior. Can the authors provide more direct evidence that the learned spatial representations correspond to actual EEG volume-conduction properties? Additionally, how does the proposed encoding perform under controlled changes in electrode density or montage configuration?"

Response.

(a) Direct evidence that the prior matches volume conduction. Beyond visualizing the designed prior (Fig. 4), we computed the empirical signed correlation of channel signals as a function of inter-electrode distance using 1,000 pretraining-corpus subjects (10-20 derivations with known 3D coordinates; 171,000 channel-pair observations). The empirical decay is well fit by the same exponential form with τ_emp = 7.73 cm, closely matching the designed prior τ = 8 cm — i.e., the injected prior quantitatively corresponds to the observed volume-conduction scale of real EEG, not merely to a convenient parameterization. The correspondence also holds at the matrix level: across the 171 channel pairs of the 10-20 montage, the prior-kernel value and the empirical inter-channel correlation agree with a Pearson correlation of 0.90 (Spearman ρ = 0.90; per-pair linear fit R² = 0.81), i.e., the prior reproduces the distance-ordered component of the pairwise structure. The remaining variance reflects region-specific neural synchrony (e.g., coherent frontal and occipital clusters) that a pure distance kernel is not designed to capture — this residual structure is precisely what the learned component refines on top of the fixed prior (see (b)). (figures: empirical decay vs. prior; matrix-level correspondence with a per-channel-pair scatter — discussion and figure now in Appendix H, pp. 24–25, Fig. 7, p. 25)

Selected bin-averaged empirical correlations (full curve: revised Fig. 7, p. 25):

Distance bin center (cm)5.57.59.511.513.515.517.519.5
Empirical corr (mean ± s.e.m.)0.736 ± 0.0020.583 ± 0.0040.502 ± 0.0030.514 ± 0.0030.273 ± 0.0030.238 ± 0.0040.116 ± 0.0040.010 ± 0.004
Designed prior, exp(−d / 8 cm)0.5030.3920.3050.2380.1850.1440.1120.087

(b) What the model learns on top of the prior. Inspecting the trained encoder, the learned distance-scale parameter moves from its initialization (effective τ = 8 cm) to a much sharper local scale (τ ≈ 0.77 cm): the model retains the physically-calibrated global prior through the fixed additive prior branch while learning an additional sharp local component — consistent with the design intent that the prior supplies volume-conduction structure and the learned parameters refine short-range interactions. This observation is now reported in the revision (Appendix H, pp. 24–25).

AuthorsOpenReview ↗

Response to Reviewer ZWrB [3/n]

(c) Robustness to density/montage changes — stress-tested by the protocol, and now by a direct halved-montage experiment. Two properties of our pipeline already directly address this question: (i) during pretraining, channel reorganization randomly permutes the channel order and randomly truncates the montage to a random subset of channels at every batch — the model never sees a fixed montage or fixed density; (ii) downstream evaluation spans montages from 6 to 128 channels (and 160–500 Hz sampling), all handled by the same encoding without architecture modification.

(iii) Direct test: retraining and testing on a halved montage. We additionally ran a controlled electrode-density experiment on all 12 datasets: randomly remove 50% of each dataset's channels, recompute the 3-D coordinates of the retained electrodes, retrain the frozen probe on the reduced montage, and test on it — under the paper's probing protocol, and with the paper's Std. Spatial ablation (a standard fixed channel-index spatial embedding, trained under the identical protocol) evaluated on the same halved montages as the key control.

Our encoding consumes arbitrary electrode coordinates, so the halved montage is handled without any architectural change — it simply receives the retained electrodes' positions and recomputes the distance structure directly. A fixed channel-index encoding instead assigns embeddings by slot in the channel array: when half the electrodes are removed, slot i no longer corresponds to the same electrode (nor to the same spatial neighborhood), so the pretrained embeddings become systematically mismatched with what they now represent.

The result isolates the benefit to the coordinate-conditioned design rather than to any spatial encoding per se. Our encoding degrades gracefully: the 12-dataset average moves from 54.28 (full montage, Table 4) to 51.71 under the halved montage (−2.6 points; the per-dataset drop is ≤3.4 points on 11/12 datasets, and only 1.22 points on PhysioNet-MI). The fixed channel-index encoding degrades by 8.8 points on average under the identical halving (51.48 → 42.65), and is worse than our halved-montage result on every one of the 12 datasets. Consequently, the advantage of the coordinate-conditioned encoding widens from 2.8 points (full montage) to 9.1 points (halved montage); our halved-montage probe even outperforms the fixed-index encoding with its full montage (51.7 vs. 51.5), and still outperforms every baseline operating on its full montage (12-dataset average 51.7 vs. 46.2 for the strongest baseline, REVE). The spatial physiology is thus carried by the distance-ordered, coordinate-conditioned prior validated in (a), so the representation — and its frozen probe — transfers across electrode-density changes instead of breaking with them.

Frozen probe (12-dataset average)Full montage50% channels removedΔ
DeeperBrain (coordinate-conditioned)54.2851.71−2.57
Std. Spatial (fixed channel-index)51.4842.65−8.83
Encoding gap (DeeperBrain − Std. Spatial)2.809.06+6.26

Reference point: the strongest baseline (REVE) reaches 46.18 on its full montage — our halved-montage probe (51.71) still exceeds it. Full visualization: revised Fig. 10 (p. 27). This analysis is now included in the revision (Appendix H, "Electrode-density stress test (halved montage)", p. 26; Fig. 10, p. 27).

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

The paper is introducing a neuro-grounded EEG foundation model toward universal BCI under frozen-probing. They integrate neurophysiological inductive biases into both architecture and learning. The main component of their method is: 1- neurophysiologically grounded positional encodings by combining channel positional encoding combined with a temporal positional encoding. 2- Training based on neurodynamic by combining Neurodynamics Statistics Prediction with Masked EEG Reconstruction as training objective

Critical strengths

The proposed model is has been training using 14 public dataset and evaluated on 12 datasets representing 8 downstream BCI tasks. The result showed that, the proposed model (under frozen-Propoing) outperformed the SOTA method which indicate the model ability to encapsulates core neurodynamical properties. This improvement will reduce the training time and efficiency.

Critical weaknesses

the gap between the result of the proposed model under frozen-Probing and under End-to-end-Fine-tuning setting

Questions for authors

1- Can the authors provide statistical validation confirming that the performance gains of the proposed method are significant compared to competing approaches?

2- To what extent does the adoption of a dual-objective design, MER and NSP impact the overall complexity and training overhead of the model?

3 comments
AuthorsOpenReview ↗

Response to Reviewer mFfU [1/n]

We thank the reviewer for recognizing the breadth of the evaluation and the practical value of strong frozen-probing performance. We address the one critical weakness and both questions in turn.

W1 (Critical Weakness)

"The gap between the result of the proposed model under frozen-Probing and under End-to-end-Fine-tuning setting"

Response. We agree this gap deserves attention, and we would first like to point out that it is a field-wide phenomenon rather than specific to our model: as stated in Sec. 1 (p. 1), current EEG foundation models typically transfer effectively only under end-to-end fine-tuning and degrade markedly when the backbone is frozen — e.g., the FT→probing drop on FACED is −20.9 for CSBrain and −9.4 for DeeperBrain, and on MODMA −20.5 vs. −13.0. Narrowing exactly this gap is one of the core motivations of our paper: DeeperBrain's FT→probing drop is the smallest or second-smallest among all compared models on every dataset, i.e., DeeperBrain substantially shrinks the frozen↔fine-tuning gap relative to existing methods while simultaneously attaining the best frozen-probing accuracy on all 12 datasets. In other words, the remaining gap measures how much extra fine-tuning buys, and keeping it minimal means the representation is already usable without touching the backbone — precisely the practically valuable property. The new statistical validation (Q1 below) strengthens this reading — the frozen-probing advantage is significant on 7/12 datasets and mean-best on 12/12 — and the control-pretraining and handcrafted-probe experiments (full data in DAJw's Q1–Q2 below) show it is not an artifact of the probe protocol (identical budget for all models) nor of the injected statistics alone (handcrafted probes below the model's probe on every task). We have added a dedicated discussion of the FT→probing gap to the revised manuscript (Appendix F, p. 22, blue-highlighted).

AuthorsOpenReview ↗

Response to Reviewer mFfU [2/n]

Q1 (Question)

"Can the authors provide statistical validation confirming that the performance gains of the proposed method are significant compared to competing approaches?"

Response. We computed one-sided Welch t-tests from the reported 5-seed mean±std of every Table 3/4 comparison (DeeperBrain vs. the strongest baseline per dataset), with Cohen's d for effect size.

Frozen-probing (Table 4, the paper's central claim). DeeperBrain's mean is best on 12/12 datasets; the gain over the second-best method is significant at p < 0.05 on 7/12 datasets, and DeeperBrain never significantly loses on any dataset (win/tie/loss = 7/5/0):

DatasetBest baselineΔCohen's dp (one-sided)Sig.
FACEDREVE 37.76±0.54+13.2028.52.9e-10✓✓
SEED-VLaBraM 32.63±0.53+2.455.95.3e-05✓✓
SEED-VIICBraMod 17.32±0.27+5.9424.12.4e-10✓✓
PhysioNet-MICBraMod 53.73±0.39+2.844.91.2e-04✓✓
BCIC-IV-2aREVE 42.73±1.12+8.284.71.7e-04✓✓
MODMAREVE 53.00±3.48+10.363.54.4e-04✓✓
SEED-VIGLaBraM 56.92±1.56+2.932.15.9e-03✓
SHU-MI / ISRUC / CHB-MIT / BCIC2020-3 / MentalArith—+0.55…+4.290.14–1.040.07–0.42tie (mean best, n.s.)

The five non-significant datasets all remain mean-best; their wide baseline std (e.g., REVE 39.04±9.59 on BCIC2020-3) with n=5 seeds limits test power rather than indicating a loss. We have added per-comparison significance markers to Tables 3/4 and the full test table to the revised appendix (Tables 3–4 with **/* markers on significantly-better comparisons, p. 6; full test table including all loss comparisons and discussion: Appendix F, p. 22, Table 9, p. 23).

Fine-tuning (Table 3). We agree that the fine-tuning gains are not uniformly significant: vs. the strongest baseline, DeeperBrain is significantly better on FACED (+2.80, p=2.0e-06) and MODMA (+3.46, p=0.034), statistically tied on 8 datasets, and significantly worse on 2 (SEED-V −1.29 vs. CSBrain; BCIC-IV-2a −3.27 vs. REVE). We have accordingly softened the fine-tuning claim from "state-of-the-art" to "competitive or superior" in the revision (Abstract p. 1; Sec. 1, p. 2; Conclusion, p. 10) and corrected the Section 3.3 win count to 7 of 12, where Sec. 3.3 (p. 6) now reads "best result on 7 of 12 datasets and is competitive on the remainder" (Sec. 3.3, p. 6), while emphasizing that the paper's central and now statistically supported claim is the frozen-probing advantage.

AuthorsOpenReview ↗

Response to Reviewer mFfU [3/n]

Q2 (Question)

"To what extent does the adoption of a dual-objective design, MER and NSP impact the overall complexity and training overhead of the model?"

Response. The dual objective adds negligible overhead, measured on the paper's pretraining setup:

ComponentOverhead
NSP prediction head parameters3,819 params = 0.065% of the 5.85M backbone
Per-step wall-clock (NSP target computation + head, batch 16, online)<1% vs. MER-only (measured, 200-step average)
Extra memoryNone beyond the existing batch: the 19-D targets are computed from the input batch itself; the head operates on already-computed patch representations
Total pretraining~7 h on a single RTX A5000 (unchanged)
InferenceZero: the NSP head is discarded after pretraining; fine-tuning and probing architectures are identical to MER-only

The dual design therefore trades a negligible training cost for the representation gains quantified in the control-pretraining experiments (DAJw Q1 below). This overhead note is now included in the revised manuscript (Appendix K, p. 29).

Comments on the paper

1 comment
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Global Rebuttal

We thank all reviewers for their careful reading and constructive feedback, and we are encouraged by their positive assessments:

  • Reviewer mFfU highlights that the model is trained on 14 public datasets and evaluated on 12 datasets across 8 downstream BCI tasks, and that under frozen-probing it outperforms SOTA methods, indicating — in the reviewer's reading — the model's ability to encapsulate core neurodynamical properties, while reducing training time and improving efficiency.
  • Reviewer ZWrB considers the integration of neurophysiological priors "a meaningful direction beyond purely data-driven EEG foundation models", and acknowledges the comprehensive evaluation, the best frozen-probing performance on all evaluated datasets, and ablations that demonstrate the effectiveness of the positional encodings and the complementary contributions of MER and NSP.
  • Reviewer DAJw judges the frozen-probing result "substantial" — winning all twelve datasets, often by wide margins — addressing "a documented failure mode of current EEG foundation models" that is "practically valuable when downstream labels are scarce"; their precise reading also helped us catch two presentation errors, and their concrete control-experiment suggestions have all been run.

What we did during the discussion period. Guided by the reviews, we conducted seven new sets of experiments under the paper's exact protocol: (1) statistical validation of every Table 3/4 comparison; (2) seven control/ablation pretraining runs from scratch; (3) frozen probes on the exact NSP statistics; (4) physiological validation of the spatial encoding (171k channel-pair observations); (5) a within-subject cross-session analysis and a learned-utilization analysis of the temporal encoding; (6) training-overhead profiling; (7) a halved-montage stress test on all 12 datasets. Their motivation, full data tables, and detailed point-by-point discussions are given in the individual responses below; here we summarize only the resulting manuscript changes.

Changes to the revised manuscript (all highlighted in blue per the ICLR revision policy):

  1. Two corrections: Section 3.3 win count 8→7 of 12 (p. 6); fine-tuning claims softened from "state-of-the-art" to weaker statements (Abstract p. 1; Sec. 1 p. 2; Conclusion p. 10: "competitive or superior"; Sec. 3.3 p. 6: "best result on 7 of 12 datasets and is competitive on the remainder").
  2. Split-limitation statement added in Sec. 3.2 (p. 5).
  3. Significance analysis: per-comparison markers in Tables 3–4 (p. 6); full Welch-test table and FT→probing-gap discussion in Appendix F (pp. 22–23; Table 9, p. 23).
  4. NSP attribution: control-pretraining, component-decomposition and handcrafted-probe analyses in Appendix G (pp. 23–24; Tables 10–11).
  5. Encoding analyses: spatial empirical validation, temporal utilization, cross-session and halved-montage analyses with visualizations in Appendix H (pp. 24–27; Figs. 7–10, pp. 25–27).
  6. Protocol notes: training-overhead note (Appendix K, p. 29); CSBrain best-effort reproduction (Appendix D, p. 21).

The headline outcomes: the central frozen-probing advantage is significant on 7/12 datasets (mean best 12/12, no significant loss); non-neurophysiological NSP controls lose 2.89–7.95 points; raw NSP statistics probe on average +19.87 points below the learned representation; the empirical spatial decay (τ = 7.73 cm) matches the designed prior (8 cm); and the coordinate-conditioned spatial encoding degrades by only 2.6 points under 50% channel removal (vs. 8.8 for the fixed-index encoding).

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