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Under review as a conference paper at ICLR 2027

AxisBrain: Cross-Axis Consistency for Token-Wise Residual Modulation in EEG Foundation Models

Abstract

Electroencephalography (EEG) foundation models aim to learn transferable representations across tasks, subjects, and recording configurations. Recent approaches often pursue improvements through model scaling, complex pretraining pipelines, or anatomical priors. These strategies can introduce additional computational costs, training dependencies, or structural metadata requirements. We introduce AxisBrain, which uses cross-axis consistency to guide token-wise residual refinement while limiting these additional costs and requirements. At each layer, learned-query pooling across channels and temporal mean pooling within each channel produce complementary context descriptors. The sigmoid-transformed cosine similarity between their projected descriptors yields a bounded consistency score that modulates the recombined spatial and temporal attention response at each channel–time token. The 7.46M-parameter encoder is trained end to end using masked raw EEG patch reconstruction, without separately pretrained components or explicit anatomical metadata. Across ten datasets spanning seven task families, AxisBrain achieves a mean balanced accuracy of 75.67%, compared with literature-reported means of 73.25% for CBraMod and 75.42% for PATCHCODE-Large. Controlled ablations further indicate that both the learned modulation scores and their token-wise assignments contribute to performance. These results support cross-axis consistency as an effective basis for token-wise residual refinement in EEG foundation models.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG foundation models, Masked EEG modeling, Cross-axis consistency, Token-wise residual modulation

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_oiPjOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper builds on CBraMod by recombining spatial and temporal attention responses and modulating each channel–time token’s residual update with a cross-axis consistency score. Experiments cover ten downstream datasets with five seeds and systematic ablations. The method is well engineering and competitive, yet the gains are not shown to be significant and the core novelty require stronger evidence.

Critical strengths
  1. The proposed method avoids relying on the predefined brain-region annotations or electrode-coordinate priors, which is a practical advantage for heterogeneous EEG datasets. This design choice keeps the framework compact and broadly applicable across recording conditions.
  2. The paper provides the detailed descriptions of the experimental setup, including evaluation protocols and hyperparameters. These results improve reproducibility and make the empirical results easier to interpret.
Critical weaknesses
  1. The paper should more explicitly clarify its contributions beyond token-wise scores, since the framework appear largely incremental relative to CBraMod. Please clarify which components are genuinely novel would strengthen the claimed contribution.
  2. The comparison lacks parameter-matched baselines, such as a deeper or wider CBraMod at roughly the 7M scale. It is also better that consider another SOTA method REVE. Please provide more discussion about the comparison and performance gains.
Questions for authors
  1. Can the reported gains be attributed to the cross-axis mechanism rather than to increased capacity or random variation?
  2. What evidence shows that a higher cross-axis consistency score actually identifies channel–time tokens that are more important for downstream classification, rather than merely applying an input-dependent but functionally arbitrary scaling?
6 comments
AuthorsOpenReview ↗

Response to Reviewer oiPj [1/4]

We thank the reviewer for recognizing the practical advantages of avoiding electrode-coordinate and predefined brain-region priors, as well as the detailed experimental reporting. We particularly appreciate the requests to clarify the methodological contributions and provide capacity-controlled comparisons. These comments motivated additional experiments and helped us refine the rationale and scope of our claims. Below, we address each concern and present the additional comparisons.

Weakness 1: The paper should more explicitly clarify its contributions beyond token-wise scores, since the framework appear largely incremental relative to CBraMod. Please clarify which components are genuinely novel would strengthen the claimed contribution.

Thank you for asking us to clarify the contributions beyond token-wise scoring. We acknowledge that the manuscript did not sufficiently explain what the proposed modifications contribute or distinguish them clearly from the components inherited from CBraMod. We will revise the contribution statements and methodological rationale accordingly.

Our goal is to improve EEG transfer while preserving a simple, single-stage masked-reconstruction pipeline. We deliberately chose CBraMod as a relatively simple Transformer backbone with factorized spatial and temporal attention. We retain its patch encoder, ACPE, and reconstruction objective. Our methodological contribution concerns two cooperating components that determine how the attention-derived responses are recombined and incorporated into the residual update.

1. Additive response recombination for effective use of expressive capacity. The proposed recombination retains the original response as a direct term and learns an additive spatial–temporal mixing correction:

R=Xcc+WxXcc+bx.R=X^{cc}+W_xX^{cc}+b_x.

Although this has the same affine expressive power as a projection-only alternative, identical function classes do not ensure identical learned solutions. Our design preserves the original attention response through a direct path and allows additional mixing to be learned as a correction to that response. This provides a simple, optimization-oriented structure designed to make more effective use of the available expressive capacity.

Table 3 demonstrates the practical importance of this choice: mean BA increases from 71.83% for our reproduced CBraMod to 73.44% with additive recombination, whereas replacing the response with the projection alone gives 69.42%. Thus, the contribution is not an enlarged affine function class, but an effective parameterization for learning and applying the spatial–temporal correction.

2. Cross-axis agreement for allocating residual refinement strength. Residual scaling itself is established. Our main contribution is a structured rule that determines token-wise gain from the relationship between complementary channel–time contexts.

The score is computed from the current encoder layer’s learned XccX^{cc} representations, not raw EEG. Although an individual token already contains attention-aggregated spatial and temporal information, its representation does not explicitly expose the relationship between the two axis-level summaries. We therefore construct a time-indexed cross-channel descriptor using learned-query pooling and a channel-indexed temporal descriptor by averaging that channel’s representations over the segment. The descriptors are projected into a jointly learned comparison space, where their normalized agreement determines the score.

The design motivation is that agreement with one axis alone can be misleading. Persistent channel-specific contamination can agree with that channel’s temporal context, while contamination affecting several channels at one interval can agree with the corresponding cross-channel context. Comparing the complementary summaries provides a cross-check: it asks whether the pattern summarized across channels is compatible with the temporal context of the channel at their intersection.

This motivates assigning less additional gain when the contexts conflict and more when they agree. The bounded multiplier (1+Sct)(1+S_{ct}) preserves the response RctR_{ct} at every position while varying its additional amplification. The proposed configuration achieves 75.96% mean BA, compared with 73.44% for additive recombination without modulation, supporting the practical contribution of this context-dependent refinement.

This cross-check may mitigate misleadingly high gain caused by an axis-specific distortion provided that the complementary summary is not dominated by that distortion. If both summaries are dominated by the same contamination, their agreement may remain high. We therefore interpret the score as learned contextual compatibility, with this potential limitation, rather than as an independently established measure of physiological importance.

AuthorsOpenReview ↗

Response to Reviewer oiPj [2/4]

Weakness 2: The comparison lacks parameter-matched baselines, such as a deeper or wider CBraMod at roughly the 7M scale. It is also better that consider another SOTA method REVE. Please provide more discussion about the comparison and performance gains.

CBraMod controls at comparable capacity. We evaluated two expanded CBraMod baselines: (i) a deeper model with 19 encoder layers, and (ii) a wider-FFN model that retains 12 encoder layers while increasing the FFN intermediate dimension from 800 to 1340. Both expanded baselines were evaluated across the ten datasets using five fine-tuning seeds.

For consistency, we count trainable parameters used in the encoder-side forward pass, including the patch encoder and excluding reconstruction and downstream classification heads. Under this convention, the default public CBraMod implementation contains approximately 4.88M parameters, which differs from the approximately 4M reported in the original paper. The expanded models contain 7.70M (+2.82M) and 7.48M (+2.60M) parameters, respectively.

ModelActive backbone parametersTen-dataset mean BA
Reproduced CBraMod4.88M71.83%
Deeper CBraMod, 19 layers7.70M72.23%
Wider-FFN CBraMod, FFN dimension 13407.48M71.05%
AxisBrain7.46M75.96%

Increasing depth provides a modest gain over the reproduced baseline, while widening the FFN does not improve it; neither reaches AxisBrain’s performance. Thus, increasing backbone capacity alone does not reproduce the proposed method’s improvement under the evaluated settings. We will incorporate these controls and their dataset-level results into the revised manuscript.

Selection of additional foundation-model baselines. Our baseline selection aimed to reduce confounding from pretraining resources, downstream adaptation protocols, and additional data augmentation, making the comparisons more informative about methodological contributions.

REVE is highly relevant, but it was pretrained on more than 60,000 hours from 92 datasets, exceeding AxisBrain’s approximately 9,000 pretraining hours by more than sixfold. Its reported downstream adaptation also includes Mixup augmentation. Consequently, directly comparing the published results would combine differences in algorithms with differences in training resources and adaptation procedures.

A comparison that also controls for pretraining resources would require pretraining these models on a common corpus under comparable training budgets, followed by evaluation under a common downstream protocol. We regret that we could not complete this broader evaluation within the available computational resources and time.

AuthorsOpenReview ↗

Response to Reviewer oiPj [3/4]

Question 1: Can the reported gains be attributed to the cross-axis mechanism rather than to increased capacity or random variation?

We respectfully refer the reviewer to our response to Weakness 2, where we present the capacity-controlled CBraMod comparisons and discuss their implications for attributing the observed performance gains.

Reviewer_7k9AOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

AxisBrain modifies the CBraMod criss-cross transformer in two ways. It adds a learned linear correction to the combined spatial and temporal attention output, and it scales each channel-time update by a bounded score taken from the cosine agreement between a pooled cross-channel descriptor and a per-channel temporal mean. The 7.46M-parameter encoder is pretrained on TUEG with masked patch reconstruction and evaluated on ten datasets, with many ablations of the score design.

Critical strengths
  1. The idea is simple and easy to adopt. It is a drop-in change to a public backbone, needs no electrode coordinates, region definitions or extra pretraining stages, and adds a measured 30 percent in FLOPs. The controls are well designed. Randomly permuting the scores, which keeps their distribution but breaks the token assignment, drops mean balanced accuracy from 0.757 to 0.697, which supports the claim that placement matters.

  2. The reporting is unusually transparent. All five fine-tuning seeds are listed per dataset, the authors report their own CBraMod reproduction even though it falls short of the published numbers, and they flag the overlap between TUEG pretraining and TUAB. Results are strong on several datasets, with the best balanced accuracy on Mental Arithmetic, Siena, CHB-MIT and FACED.

Critical weaknesses
  1. The headline relies on balanced accuracy, and the largest gains do not hold up on threshold-free metrics. On Mental Arithmetic, balanced accuracy jumps to 0.801, yet AUROC is 0.824, below CSBrain, PATCHCODE and CodeBrain. On Siena, AUC-PR is 0.348 against 0.410 to 0.502 for three baselines. Also, Appendix B holds out every Siena subject above PN12, while CSBrain tests only on PN16 and PN17, so the test sets may differ.

  2. The ablations may not separate signal from noise. Every variant is pretrained once with seed 42, and only fine-tuning seeds vary. Near-identical variants differ sharply, for example 0.757 with the default score scale against 0.723 with half the scale. Without repeated pretraining, the 2-point gain over a fixed multiplier of 1.5 is hard to trust. It is also unclear whether the Table 10 learning rates were tuned on validation data and reused for every variant.

  3. Part of the gain may come from added capacity rather than the consistency idea. AxisBrain has 7.46M parameters against 4.03M for CBraMod and costs 30 percent more FLOPs, and Table 3 shows that adding just the linear recombination already gives 1.8 points over the reproduced CBraMod. A CBraMod baseline enlarged to the same size would make the comparison fair. The frozen-encoder results are also weak, with Mental Arithmetic at 0.517, close to chance.

Questions for authors

see weaknesses.

6 comments
AuthorsOpenReview ↗

Response to Reviewer 7k9A [1/4]

We thank the reviewer for the careful assessment and for recognizing the simplicity and ease of adoption of our design, the useful score controls, and the transparent reporting. We particularly appreciate the identification of the SIENA split discrepancy and the recommendation for capacity-controlled CBraMod comparisons, which prompted re-evaluation and additional experiments. Below, we address each concern and describe the additional results and planned manuscript revisions.

Weakness 1: The headline relies on balanced accuracy, and the largest gains do not hold up on threshold-free metrics. On Mental Arithmetic, balanced accuracy jumps to 0.801, yet AUROC is 0.824, below CSBrain, PATCHCODE and CodeBrain. On Siena, AUC-PR is 0.348 against 0.410 to 0.502 for three baselines. Also, Appendix B holds out every Siena subject above PN12, while CSBrain tests only on PN16 and PN17, so the test sets may differ.

Thank you for highlighting that balanced accuracy alone does not sufficiently characterize decoding performance. We particularly appreciate your identification of the SIENA split discrepancy, which prompted us to correct the evaluation and repeat the experiment.

Metric trade-offs and complementary analysis. We acknowledge that the BA improvement on MentalArithmetic is accompanied by an AUROC of 0.824, below the reported CSBrain and CodeBrain results. Higher BA at the evaluated operating point does not necessarily imply better ranking performance across thresholds.

To examine whether the favorable results extend beyond average BA, we additionally calculated metric-specific means and mean ranks. Models are ranked separately within each dataset for each metric, with rank 1 indicating the highest reported mean; these ranks are then averaged with equal dataset weights. Metric means also use equal dataset weights and serve as supplementary descriptive measures. AUC-PR and AUROC are summarized only across binary datasets, while Cohen’s kappa and weighted F1 are summarized only across multi-class datasets. Different metrics are never pooled into a single average.

The summaries below incorporate the paper-aligned SIENA results described below. Each entry reports metric mean (mean rank). Higher means and lower ranks are better; bold identifies the best mean and best rank separately, including ties.

Comparison across the ten-dataset evaluation suite. All four models have results on all ten datasets. CodeBrain is omitted because results on four datasets are unavailable.

ModelBA (10 datasets)AUC-PR (6 datasets)AUROC (6 datasets)Kappa (4 datasets)Weighted F1 (4 datasets)
AxisBrain0.7596 (1.60)0.7252 (1.83)0.8707 (2.00)0.6262 (1.75)0.7026 (1.50)
CSBrain0.7404 (2.00)0.7150 (1.83)0.8764 (1.83)0.6125 (2.25)0.6900 (2.25)
CBraMod0.7325 (2.60)0.6731 (2.33)0.8662 (2.33)0.6098 (2.50)0.6863 (2.50)
LaBraM0.7114 (3.80)0.6322 (4.00)0.8437 (3.83)0.5914 (3.50)0.6682 (3.75)

Comparison across the six datasets shared with CodeBrain. These are MentalArithmetic, SHU-MI, ISRUC, CHB-MIT, FACED, and TUAB. AUC-PR and AUROC use the four binary datasets, while kappa and weighted F1 use ISRUC and FACED.

ModelBA (6 datasets)AUC-PR (4 datasets)AUROC (4 datasets)Kappa (2 datasets)Weighted F1 (2 datasets)
AxisBrain0.7395 (1.67)0.7415 (2.25)0.8343 (2.75)0.6537 (1.00)0.7115 (1.00)
CodeBrain0.7215 (2.33)0.6955 (2.25)0.8456 (1.75)0.6441 (2.00)0.6986 (2.00)
CSBrain0.7181 (2.83)0.7024 (2.50)0.8387 (2.75)0.6305 (3.50)0.6893 (3.50)
CBraMod0.7115 (3.17)0.6588 (3.00)0.8253 (3.00)0.6241 (3.50)0.6815 (3.50)
LaBraM0.6866 (5.00)0.6253 (5.00)0.8006 (4.75)0.5964 (5.00)0.6549 (5.00)
AuthorsOpenReview ↗

Response to Reviewer 7k9A [2/4]

Continued from reply [1/4]

AxisBrain achieves the highest means for BA, AUC-PR, kappa, and weighted F1 in both comparison sets. It also obtains the lowest mean ranks for BA, kappa, and weighted F1, and ties for the lowest AUC-PR mean rank. For BA, it ranks first on six of the ten datasets and four of the six shared datasets. These findings show that its favorable performance extends beyond average BA.

The advantage remains metric-dependent: CSBrain leads on both AUROC summaries in the four-model comparison, while CodeBrain leads in the five-model comparison. Mean ranks complement the dataset-level findings but neither quantify improvement magnitudes nor establish statistical significance. We therefore interpret these results as improvements in several complementary measures, with unresolved trade-offs on particular tasks and metrics.

Task dependence also occurs in existing EEG foundation models. CSBrain reports lower CHB-MIT BA than CBraMod (0.7262 versus 0.7398; Table 10), despite improving other metrics. CodeBrain likewise reports lower BA on CHB-MIT (0.7273 versus 0.7398) and ISRUC-S1 (0.7835 versus 0.7865), with only a small TUAB difference (0.8294 versus 0.8289). These examples provide context for the broader challenge; they do not diminish our responsibility to explain and address our own limitations.

SIENA split correction and remaining metric trade-offs. Our original preprocessing followed the public CSBrain code, which held out available subjects above PN12, whereas the CSBrain paper specifies PN16 and PN17 as the test subjects. This discrepancy between the split implemented in CSBrain’s publicly released preprocessing code and the split specified in the CSBrain paper led to the mismatch you identified.

SIENA evaluationBalanced accuracyAUC-PRAUROC
Original split0.8023 ± 0.00650.3478 ± 0.00990.9007 ± 0.0023
Paper-aligned split0.8316 ± 0.01010.3888 ± 0.01080.8911 ± 0.0034

The corrected evaluation yields higher BA and AUC-PR by 2.93 and 4.10 percentage points, respectively. These changes reflect evaluation under the corrected split, rather than an architectural improvement on an unchanged test set. Relative to the reported CBraMod results, the corrected BA advantage is 9.99 percentage points, and the AUC-PR deficit narrows from 6.29 to 2.19 percentage points. Nevertheless, AUC-PR remains lower, and AUROC is 1.27 percentage points below CBraMod. Further analysis is needed to understand why the substantial BA advantage is not accompanied by corresponding improvements in ranking metrics.

We will revise Section 3.2 and the affected tables to incorporate the corrected SIENA results, these multi-metric summaries, and a clearer discussion of task-specific improvements and limitations.

AuthorsOpenReview ↗

Response to Reviewer 7k9A [3/4]

Weakness 2: The ablations may not separate signal from noise. Every variant is pretrained once with seed 42, and only fine-tuning seeds vary. Near-identical variants differ sharply, for example 0.757 with the default score scale against 0.723 with half the scale. Without repeated pretraining, the 2-point gain over a fixed multiplier of 1.5 is hard to trust. It is also unclear whether the Table 10 learning rates were tuned on validation data and reused for every variant.

Our five fine-tuning seeds assess variability conditional on a fixed pretrained checkpoint. We understand why the substantial difference between the score-scale variants raises this concern. A systematic assessment would involve multiple independent pretraining seeds, analogous to our five fine-tuning seeds, followed by repeated downstream evaluation of each pretrained checkpoint. The resulting summaries would account for variability at both stages.

Conducting this systematic evaluation for both the proposed method and the ablation variants would require multiple pretraining runs per configuration, followed by downstream fine-tuning of every checkpoint. The substantial additional training time makes it difficult to complete this evaluation within the current revision period.

Our experiments followed the evaluation practice adopted in representative EEG foundation-model studies, using a pretrained checkpoint and repeated downstream fine-tuning runs. Our pretraining seed of 42 also matches the default in the public pretraining implementations of CBraMod, CSBrain, and CodeBrain. We hope this clarifies the methodological context of our experimental setup, while recognizing that following prior practice does not replace an assessment across independent pretraining seeds.

We determined the learning rates based on experimental results on the validation data. Although AxisBrain and its ablation variants differ relatively little architecturally, modest variant-specific learning-rate adjustments yielded better observed results than applying one learning rate throughout. The selected rates were generally identical or close to the corresponding values in Table 10.

Reviewer_3cBSOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

AxisBrain extends the CBraMod backbone with an affine recombination of spatial and temporal attention responses and an input-dependent multiplier on the attention residual path. At each layer, learned-query pooling across channels and mean pooling across time produce complementary descriptors. Their projected cosine similarity, passed through a sigmoid, determines a scalar multiplier for each channel–time token. The encoder is pretrained through masked raw-EEG reconstruction. The paper evaluates ten datasets, reports five fine-tuning seeds, and provides extensive score, pooling, and assignment ablations, alongside frozen-encoder, scaling, and computational-cost analyses. It reports a mean balanced accuracy of 75.67% with a 7.46M-parameter encoder.

Critical strengths

1. Broad evaluation and detailed reporting.

The paper evaluates ten datasets spanning seven task families, reports multiple task-appropriate metrics, and discloses individual results for five fine-tuning seeds. The appendices additionally cover frozen-encoder transfer, mask-ratio sensitivity, model/data scaling, and computational cost. This provides a substantial empirical basis for assessing the method, including its unfavorable results.

2. Useful controls beyond simply removing the proposed module.

Tables 4–5 include fixed and random multipliers, alternative score mappings, disrupted score assignments, and alternative descriptor constructions. The proposed method exceeds the fixed-midpoint control by 1.96 percentage points in mean balanced accuracy, supporting the usefulness of learned, position-dependent modulation within the evaluated architecture. The authors also appropriately acknowledge that the affine recombination does not increase affine expressivity and that the multiplier amplifies rather than suppresses the recombined response.

Critical weaknesses

1. The methodological advance is narrow, and the experiments do not sufficiently isolate the distinctive value of cross-axis consistency.

AxisBrain retains CBraMod’s patch encoder, ACPE, criss-cross attention, and masked raw-reconstruction objective (§2.1). The response recombination is an affine reparameterization, as acknowledged in §2.2. The main new hypothesis is therefore that agreement between two pooled axis contexts provides a particularly useful residual multiplier.

However, Figure 1 demonstrates variability in channel energy, which motivates input dependence in general but does not establish why agreement between these descriptors should determine refinement strength. Self-attention already produces input-dependent responses, and agreement could reflect shared background activity as well as task-relevant information.

The paper cites relevant precedents, including direction-wise pooled descriptors in Coordinate Attention and learned gating in CodeBrain, but does not compare against an adapted coordinate-attention module or a learned token-wise gate using the same descriptors and multiplier range. The fixed/random controls establish a narrower result: they do not determine whether the specific cosine-agreement construction is preferable to generic learned modulation. Retraining with permuted scores also changes the optimization problem and does not directly validate the interpretation of agreement.

This distinction matters because the contribution rests largely on this particular relational construction. Moreover, AxisBrain increases the reported encoder parameters from 4.03M to 7.46M, approximately 85%, while Appendix G reports 30.42% additional encoder-side FLOPs. A capacity- or compute-matched CBraMod and a strong learned-gating alternative would help distinguish the proposed inductive bias from additional capacity or different optimization behavior.

2. Protocol differences limit the headline comparison, while aggregate reporting obscures important qualifications to the improvement.

The most consequential issue is adaptation-protocol comparability. The published PATCHCODE paper specifies frozen encoders with linear heads in §3.1.4 and Appendix F, whereas AxisBrain’s main results use full fine-tuning and task-specific nonlinear heads (§B.4). Unless a different source version or separately matched result is being used, the comparison of 75.67% versus 75.42% combines different adaptation settings. Labeling these numbers as literature-reported is transparent, but does not make this a controlled accuracy–size comparison.

The local CBraMod reproduction is useful, but its mean balanced accuracy is 71.34%, versus the literature reference of 73.25%. Tables 10 and 16 list different selected fine-tuning settings, while comparable search budgets and the tuning policy across ablations remain unclear. Tables 3–5 report only aggregate ablation results, and their standard deviations average dataset-level standard deviations rather than quantify uncertainty in the aggregate effect. Table 8 specifies one pretraining seed; five fine-tuning seeds therefore do not establish robustness to pretraining randomness.

Finally, gains in balanced accuracy are not uniformly supported by other metrics. On SIENA, AxisBrain improves balanced accuracy over the reported CBraMod result from 0.7317 to 0.8023, while AUC-PR decreases from 0.4107 to 0.3478 and AUROC changes from 0.9038 to 0.9007 (Table 12). On TUAB, balanced accuracy is essentially unchanged while both ranking metrics decrease. These are legitimate metric trade-offs, but they weaken a broad interpretation of improved decoding performance and warrant matched evaluation and clearer threshold reporting.

Questions for authors
  1. Under comparable capacity and tuning budgets, how does the proposed score compare with a learned token-wise MLP gate using the same descriptors, or an adapted coordinate-attention gate, with the same multiplier range? A capacity-matched CBraMod would also help establish whether the improvement specifically requires the proposed relational construction.

  2. Figure 9 averages scores over classes and therefore cannot establish sample-level temporal selectivity. Can the authors quantify within-sample variation across both axes and compare against scores averaged over time within each channel or over channels within each time step? These controls would distinguish joint channel–time modulation from simpler channel-only or time-only weighting.

  3. SIENA metric trade-off. Were identical test examples, positive-class definitions, AUC-PR implementations, and decision-threshold rules used for the compared results? Please clarify threshold selection and report sensitivity/specificity, to distinguish an operating-point improvement from a broader improvement in discrimination.

8 comments
AuthorsOpenReview ↗

Response to Reviewer 3cBS [1/8]

We thank the reviewer for the careful examination of our methodology and evaluation protocols, and for recognizing the breadth of the experiments, detailed reporting, and value of the score controls. We particularly appreciate the recommendations for learned-gating and capacity-controlled comparisons, as well as the identification of adaptation-protocol differences. These comments motivated additional experiments and helped us clarify the scope of our evidence and the revisions needed in the manuscript. Below, we address each concern and present the additional results.

Weakness 1: The methodological advance is narrow, and the experiments do not sufficiently isolate the distinctive value of cross-axis consistency. AxisBrain retains CBraMod’s patch encoder, ACPE, criss-cross attention, and masked raw-reconstruction objective (§2.1). The response recombination is an affine reparameterization, as acknowledged in §2.2. The main new hypothesis is therefore that agreement between two pooled axis contexts provides a particularly useful residual multiplier. However, Figure 1 demonstrates variability in channel energy, which motivates input dependence in general but does not establish why agreement between these descriptors should determine refinement strength. Self-attention already produces input-dependent responses, and agreement could reflect shared background activity as well as task-relevant information. The paper cites relevant precedents, including direction-wise pooled descriptors in Coordinate Attention and learned gating in CodeBrain, but does not compare against an adapted coordinate-attention module or a learned token-wise gate using the same descriptors and multiplier range. The fixed/random controls establish a narrower result: they do not determine whether the specific cosine-agreement construction is preferable to generic learned modulation. Retraining with permuted scores also changes the optimization problem and does not directly validate the interpretation of agreement. This distinction matters because the contribution rests largely on this particular relational construction. Moreover, AxisBrain increases the reported encoder parameters from 4.03M to 7.46M, approximately 85%, while Appendix G reports 30.42% additional encoder-side FLOPs. A capacity- or compute-matched CBraMod and a strong learned-gating alternative would help distinguish the proposed inductive bias from additional capacity or different optimization behavior.

We acknowledge that the manuscript did not sufficiently explain the rationale and contribution of the proposed modifications, which could make the method appear to be only an incremental extension of CBraMod. We particularly thank the reviewer for suggesting learned-gating and capacity-controlled comparisons: these suggestions helped us test whether the proposed axis-descriptor agreement provides value beyond generic modulation and additional model capacity. We clarify these points below and will incorporate them into the manuscript.

Scope of the methodological contribution. Our goal is to improve EEG transfer while preserving a simple, single-stage masked-reconstruction pipeline. We deliberately chose CBraMod as a relatively simple Transformer backbone with factorized spatial and temporal attention. We retain its patch encoder, ACPE, and reconstruction objective, and investigate how its attention-derived responses should contribute to the residual update.

Role of the additive recombination. Although the recombination has the same affine expressive power as a linear projection, it retains the original response as a direct term and learns an additive correction:

R=Xcc+WxXcc+bx.R=X^{cc}+W_xX^{cc}+b_x.

Table 3 shows an empirical benefit of this parameterization: mean BA increases from 71.83% for our reproduced CBraMod to 73.44%, whereas replacing the response with the projection alone gives 69.42%. This is an optimization-oriented additive parameterization designed to make more effective use of the available expressive capacity. Retaining the original response as a direct path allows spatial–temporal mixing to be learned as a correction to that response. The results support the practical value of this design despite its unchanged affine function class.

AuthorsOpenReview ↗

Response to Reviewer 3cBS [2/8]

Continued from reply [1/8]

Why compare complementary axis contexts? We agree that Figure 1 motivates input dependence in general, but does not establish a monotone relationship between agreement and physiological relevance. The score is computed from the current layer’s learned XccX^{cc} representations, rather than raw EEG or channel energy. A time-indexed descriptor summarizes channels through learned-query pooling, while a channel-indexed descriptor summarizes that channel’s temporal context. Their agreement is measured after learned projections and therefore represents latent compatibility, rather than raw-signal correlation.

A token and its single-axis reference can agree because both share a distortion—for example, persistent channel-specific contamination or contamination affecting several channels at one time interval. Comparing complementary contextual summaries provides a cross-check that can reduce misleadingly high gain from such shared distortion when the complementary summary is not dominated by it. This motivates the proposed relational construction; it does not guarantee that agreement identifies physiologically important activity. Shared background activity or contamination dominating both descriptors can still produce high agreement. We will clarify this interpretation and distinguish predictive effectiveness from physiological explanation.

Comparison with learned token-wise gates. To test whether simpler learned modulation is sufficient, we will add two ablations to Table 4:

  • [15] Token-input MLP: the gate receives the token representation XctccX^{cc}_{ct} itself, using a 200→64→1 MLP.
  • [16] Descriptor-input MLP: the gate receives the concatenated descriptors [AcC;AtT][A^C_c;A^T_t], using a 400→64→1 MLP.

Both controls use S=sigmoid⁡(tanh⁡(MLP⁡(⋅)))S=\operatorname{sigmoid}(\tanh(\operatorname{MLP}(\cdot))) and the same residual rule (1+S)R(1+S)R. Thus, their scores remain within the same bounds as the proposed sigmoid-transformed cosine agreement.

Their ten-dataset mean BAs are 72.67% and 71.82%, respectively, compared with 75.96% for the proposed method. Both are below additive recombination without modulation, which achieves 73.44% in Table 3. In particular, [16] supplies both contextual descriptors to the gate: its lower performance suggests that access to these summaries alone does not reproduce the benefit of explicitly comparing them through normalized agreement.

For transparency, the dataset-level results are reported below as mean ± sample SD across fine-tuning seeds.

For the six binary datasets—MentalArithmetic, Mumtaz2016, SHU-MI, SIENA, CHB-MIT, and TUAB—the last two columns report AUC-PR and AUROC. For PhysioNet-MI, ISRUC, HMC, and FACED, they report Cohen’s kappa and weighted F1.

[15] MLP gate receiving XctccX^{cc}_{ct}.

DatasetBAAUC-PR / KappaAUROC / Weighted F1
MentalArithmetic0.6340 ± 0.03400.7703 ± 0.00780.8565 ± 0.0048
Mumtaz20160.9128 ± 0.02970.9939 ± 0.00080.9943 ± 0.0007
SHU-MI0.6029 ± 0.01920.6553 ± 0.02370.6547 ± 0.0264
SIENA0.7765 ± 0.06730.4368 ± 0.02100.8980 ± 0.0123
CHB-MIT0.7677 ± 0.03470.5769 ± 0.08990.9278 ± 0.0270
TUAB0.8254 ± 0.00930.9103 ± 0.00320.9060 ± 0.0031
PhysioNet-MI0.6348 ± 0.00380.5130 ± 0.00500.6357 ± 0.0039
ISRUC0.7952 ± 0.00800.7581 ± 0.00900.8122 ± 0.0083
HMC0.7228 ± 0.00380.6722 ± 0.00900.7429 ± 0.0057
FACED0.5948 ± 0.00300.5417 ± 0.00390.6014 ± 0.0044

[16] MLP gate receiving both axis descriptors.

DatasetBAAUC-PR / KappaAUROC / Weighted F1
MentalArithmetic0.7062 ± 0.02610.6116 ± 0.04620.7826 ± 0.0235
Mumtaz20160.9227 ± 0.02270.9938 ± 0.00170.9937 ± 0.0018
SHU-MI0.6204 ± 0.02240.6792 ± 0.01340.6818 ± 0.0113
SIENA0.6562 ± 0.10500.2984 ± 0.02240.8999 ± 0.0089
CHB-MIT0.7194 ± 0.01280.4631 ± 0.08120.8724 ± 0.0349
TUAB0.8139 ± 0.00380.8985 ± 0.00240.8924 ± 0.0034
PhysioNet-MI0.6312 ± 0.00450.5082 ± 0.00600.6317 ± 0.0048
ISRUC0.7954 ± 0.00230.7602 ± 0.00470.8158 ± 0.0042
HMC0.7200 ± 0.00220.6732 ± 0.00360.7426 ± 0.0041
FACED0.5966 ± 0.00730.5439 ± 0.00840.6031 ± 0.0068

These experiments directly test generic learned modulation using either the token itself or the same contextual descriptors.

AuthorsOpenReview ↗

Response to Reviewer 3cBS [3/8]

Continued from reply [2/8]

CBraMod controls at comparable capacity. We agree that the additional parameters and the reported 30.42% encoder-side FLOP overhead require explicit consideration. We therefore evaluated two expanded CBraMod baselines that increase capacity without introducing the proposed recombination or consistency score:

  • Deeper CBraMod: 19 encoder layers, with FFN intermediate dimension 800.
  • Wider-FFN CBraMod: 12 encoder layers, with FFN intermediate dimension increased from 800 to 1340.

For consistency, we count trainable parameters used in the encoder-side forward pass, including the patch encoder and excluding reconstruction and downstream classification heads. Under this convention, the default public CBraMod implementation contains approximately 4.88M parameters, which differs from the approximately 4M reported in the original paper. The deeper and wider-FFN controls contain 7.70M (+2.82M) and 7.48M (+2.60M) parameters, respectively, compared with 7.46M for AxisBrain.

ModelActive backbone parametersTen-dataset mean BA
CBraMod, 19 layers7.70M72.23%
CBraMod, FFN dimension 13407.48M71.05%
AxisBrain7.46M75.96%

Deeper CBraMod: dataset-level results over five fine-tuning seeds.

DatasetBAAUC-PR / KappaAUROC / Weighted F1
MentalArithmetic0.7312 ± 0.02810.7000 ± 0.05920.8558 ± 0.0206
Mumtaz20160.9063 ± 0.01220.9874 ± 0.00810.9857 ± 0.0112
SHU-MI0.6225 ± 0.01010.6746 ± 0.01820.6824 ± 0.0143
SIENA0.6888 ± 0.09360.4330 ± 0.02860.8993 ± 0.0040
CHB-MIT0.7347 ± 0.02990.4865 ± 0.15780.8853 ± 0.0293
TUAB0.8206 ± 0.00510.9039 ± 0.00280.8982 ± 0.0037
PhysioNet-MI0.6316 ± 0.00580.5087 ± 0.00770.6320 ± 0.0062
ISRUC0.7851 ± 0.00610.7447 ± 0.01240.8016 ± 0.0107
HMC0.7137 ± 0.00990.6625 ± 0.01280.7358 ± 0.0111
FACED0.5888 ± 0.00860.5341 ± 0.00910.5926 ± 0.0069

Wider-FFN CBraMod: dataset-level results over five fine-tuning seeds.

DatasetBAAUC-PR / KappaAUROC / Weighted F1
MentalArithmetic0.6812 ± 0.01860.4873 ± 0.02560.7291 ± 0.0096
Mumtaz20160.9420 ± 0.01040.9904 ± 0.00060.9899 ± 0.0006
SHU-MI0.6275 ± 0.01200.6825 ± 0.01750.6855 ± 0.0148
SIENA0.5978 ± 0.08630.4434 ± 0.09250.9023 ± 0.0186
CHB-MIT0.7345 ± 0.02190.6149 ± 0.05670.9355 ± 0.0108
TUAB0.8197 ± 0.01080.9008 ± 0.00720.8978 ± 0.0068
PhysioNet-MI0.6241 ± 0.00800.4988 ± 0.01070.6243 ± 0.0083
ISRUC0.7615 ± 0.01800.7042 ± 0.02720.7657 ± 0.0248
HMC0.7235 ± 0.00220.6675 ± 0.00760.7394 ± 0.0070
FACED0.5933 ± 0.00520.5394 ± 0.00620.5971 ± 0.0061

The ten-dataset mean BAs are 72.23% for deeper CBraMod and 71.05% for wider-FFN CBraMod, compared with 71.83% for our reproduced CBraMod and 75.96% for AxisBrain. Increasing depth provides a modest gain over the reproduced baseline, while widening the FFN does not improve it; neither reaches AxisBrain’s performance. These results indicate that increasing backbone capacity alone does not reproduce the proposed method’s improvement under the evaluated settings.

Together, the learned-gating and expanded-backbone comparisons support the usefulness of the proposed relational scoring rule beyond supplying the descriptors to an MLP or increasing backbone capacity.

Reviewer_MVD1OpenReview ↗
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Paper summary

The authors propose a new EEG FM that control how much each EEG token is updated in the transformer backbone, based on the agreement between its spatial and temporal contexts.

Critical strengths

Interesting architecture design in terms of information routing inside the Transformer backbone.

Critical weaknesses
  1. Limited novelty, the proposed architecture is mostly adapted from CBraMod, with an additional projection and token-wise residual modulation. I acknowledge that the authors introduce a new way to combine spatial and temporal information, but I don't find much novelty in terms of EEG SSL pretraining. For example, Section 2.2 also mentions that the proposed spatial-temporal recombination has the same expressive power as a linear projection. I don't feel convinced about the necessity of these modifications, especially when the authors have not compared with a simpler learned gating mechanism.

  2. I don't feel convinced about the explanation for the improvement. Spatial-temporal context agreement is a reasonable principle for EEG representation learning, but why should higher agreement between two pooled descriptors result in a stronger residual update? I think a stronger physiological justification is still needed. Also, the improvement is somewhat marginal. For example, Tab. 2 shows almost no improvement on TUAB (0.8289 to 0.8290), while the results on SHU-MI and PhysioNet-MI are even worse than CBraMod. Besides, I find the average BA somewhat questionable, since different tasks have very different performance scales. I think the authors should focus more on the improvement for each individual task, rather than using the average BA as the main evidence.

  3. I also have concerns about the experimental evaluation. The quality of frozen representations is only compared against CBraMod, while several other EEG FMs are mentioned in the study. For example, newer EEG FMs such as REVE [1] and ST-EEGFormer [2] are not included. I don't understand why the authors only compare with CBraMod, especially when the main contribution is supposed to improve EEG representation learning. Also, Tab. 2 mainly uses results reported in previous papers, while the authors' own reproduction of CBraMod achieves 0.7134 mean BA, compared with 0.7325 in the original paper. I think the authors should at least provide more comparisons under the same experimental conditions.

References

[1] REVE: A Foundation Model for EEG – Adapting to Any Setup with Large-Scale Pretraining on 25,000 Subjects. NeurIPS 2025.

[2] Are EEG Foundation Models Worth It? Comparative Evaluation with Traditional Decoders in Diverse BCI Tasks. ICLR 2026 (ST-EEGFormer).

Questions for authors

Why should agreement between two pooled contextual descriptors determine the strength of a residual update, rather than simply learning a token-wise gate directly?

5 comments
AuthorsOpenReview ↗

Response to Reviewer MVD1 [1/5]

We thank the reviewer for the careful assessment and for recognizing the interest of our information-routing design within the Transformer backbone. We particularly appreciate the suggestions to compare with simpler learned gates, examine individual-task outcomes more closely, and clarify the experimental comparisons. These comments motivated additional gating experiments and helped us sharpen the explanation of our contributions and their limitations. Below, we address each concern and describe the additional results.

Weakness 1: Limited novelty, the proposed architecture is mostly adapted from CBraMod, with an additional projection and token-wise residual modulation. I acknowledge that the authors introduce a new way to combine spatial and temporal information, but I don't find much novelty in terms of EEG SSL pretraining. For example, Section 2.2 also mentions that the proposed spatial-temporal recombination has the same expressive power as a linear projection. I don't feel convinced about the necessity of these modifications, especially when the authors have not compared with a simpler learned gating mechanism.

We acknowledge that the manuscript did not sufficiently explain the contribution of the proposed modifications. We thank the reviewer for suggesting comparison with simpler learned gates, which helped us examine whether the improvement comes from generic gating or the proposed cross-axis agreement rule.

Our goal is to improve EEG transfer while preserving a simple, single-stage masked-reconstruction pipeline. We deliberately chose CBraMod as a relatively simple Transformer backbone with factorized spatial and temporal attention. We retain its patch encoder, ACPE, and reconstruction objective, and investigate how its attention-derived responses should contribute to the residual update.

Role of the additive recombination. Although the recombination has the same affine expressive power as a linear projection, it retains the original response as a direct term and learns an additive correction: R=Xcc+WxXcc+bxR=X^{cc}+W_xX^{cc}+b_x. Table 3 demonstrates an empirical benefit of this parameterization: mean balanced accuracy increases from 71.83% for our reproduced CBraMod to 73.44%, whereas replacing the response with the projection alone gives 69.42%. The contribution of this component is an additive parameterization designed to facilitate optimization and make more effective use of the model's existing expressive capacity. By retaining the original response as a direct path, it allows spatial–temporal mixing to be learned as a correction to that response. The improvements in Table 3 demonstrate the practical value of this design despite its unchanged affine expressive power.

Contribution beyond generic residual scaling. Residual scaling itself is established; our main contribution is a rule for determining token-wise refinement strength using EEG's channel–time structure. At each layer, complementary cross-channel and temporal descriptors are constructed from the learned XccX^{cc} representations. Their projected cosine agreement determines a bounded additional gain for the response at their intersection.

AuthorsOpenReview ↗

Response to Reviewer MVD1 [2/5]

Continued from reply [1/5]

To test whether a simpler learned gate is sufficient, we will add two ablations to Table 4: [15] an MLP gate receiving the token representation XctccX^{cc}_{ct} itself, and [16] an MLP gate receiving both axis descriptors. Their ten-dataset mean balanced accuracies are 72.67% and 71.82%, respectively, compared with 75.96% for the proposed method. Both are below the unmodulated recombination reference reported in Table 3 (73.44%).

In particular, variant [16] supplies both contextual descriptors to the gate, so its lower performance suggests that access to these summaries alone is insufficient to reproduce the benefit of the proposed scoring rule. Together, these results support explicitly comparing complementary contexts through normalized agreement in the evaluated setting.

Dataset-level results for the additional learned gates. Entries report mean ± sample standard deviation. For binary tasks (MentalArithmetic, Mumtaz2016, SHU-MI, SIENA, CHB-MIT, and TUAB), the last two columns report AUC-PR and AUROC. For the remaining multi-class tasks, they report Cohen's kappa and weighted F1. Mean BA is the unweighted average of the ten dataset means.

[15] Token-representation MLP gate

DatasetBalanced accuracyAUC-PR / Cohen's kappaAUROC / Weighted F1
MentalArithmetic0.6340 ± 0.03400.7703 ± 0.00780.8565 ± 0.0048
Mumtaz20160.9128 ± 0.02970.9939 ± 0.00080.9943 ± 0.0007
SHU-MI0.6029 ± 0.01920.6553 ± 0.02370.6547 ± 0.0264
PhysioNet-MI0.6348 ± 0.00380.5130 ± 0.00500.6357 ± 0.0039
ISRUC0.7952 ± 0.00800.7581 ± 0.00900.8122 ± 0.0083
HMC0.7228 ± 0.00380.6722 ± 0.00900.7429 ± 0.0057
SIENA0.7765 ± 0.06730.4368 ± 0.02100.8980 ± 0.0123
CHB-MIT0.7677 ± 0.03470.5769 ± 0.08990.9278 ± 0.0270
FACED0.5948 ± 0.00300.5417 ± 0.00390.6014 ± 0.0044
TUAB0.8254 ± 0.00930.9103 ± 0.00320.9060 ± 0.0031
Mean BA0.7267——

[16] Two-descriptor MLP gate

DatasetBalanced accuracyAUC-PR / Cohen's kappaAUROC / Weighted F1
MentalArithmetic0.7062 ± 0.02610.6116 ± 0.04620.7826 ± 0.0235
Mumtaz20160.9227 ± 0.02270.9938 ± 0.00170.9937 ± 0.0018
SHU-MI0.6204 ± 0.02240.6792 ± 0.01340.6818 ± 0.0113
PhysioNet-MI0.6312 ± 0.00450.5082 ± 0.00600.6317 ± 0.0048
ISRUC0.7954 ± 0.00230.7602 ± 0.00470.8158 ± 0.0042
HMC0.7200 ± 0.00220.6732 ± 0.00360.7426 ± 0.0041
SIENA0.6562 ± 0.10500.2984 ± 0.02240.8999 ± 0.0089
CHB-MIT0.7194 ± 0.01280.4631 ± 0.08120.8724 ± 0.0349
FACED0.5966 ± 0.00730.5439 ± 0.00840.6031 ± 0.0068
TUAB0.8139 ± 0.00380.8985 ± 0.00240.8924 ± 0.0034
Mean BA0.7182——

The learned gates also exhibit substantial seed-to-seed variability on some tasks. On SIENA, their balanced-accuracy standard deviations are 0.0673 and 0.1050, compared with 0.0101 for the proposed method. On MentalArithmetic, the corresponding values are 0.0340 and 0.0261, compared with 0.0067. These observations support the proposed rule in terms of both average transfer performance and stability on these tasks

We will incorporate these comparisons and clarify the respective contributions of additive recombination and cross-axis agreement-based modulation in Sections 2.2–2.3 and 3.3.

AuthorsOpenReview ↗

Response to Reviewer MVD1 [3/5]

Weakness 2: I don't feel convinced about the explanation for the improvement. Spatial-temporal context agreement is a reasonable principle for EEG representation learning, but why should higher agreement between two pooled descriptors result in a stronger residual update? I think a stronger physiological justification is still needed. Also, the improvement is somewhat marginal. For example, Tab. 2 shows almost no improvement on TUAB (0.8289 to 0.8290), while the results on SHU-MI and PhysioNet-MI are even worse than CBraMod. Besides, I find the average BA somewhat questionable, since different tasks have very different performance scales. I think the authors should focus more on the improvement for each individual task, rather than using the average BA as the main evidence

Thank you for identifying the missing justification linking contextual agreement to residual-update strength, and for highlighting that the TUAB and motor-imagery results require a more task-specific assessment than average BA alone.

Rationale for agreement-based residual modulation. Why higher agreement should lead to a stronger residual update is an important concern shared by several reviewers. We address this question in the global response, including the rationale for comparing complementary contexts and the supporting ablations. We respectfully refer the reviewer to that discussion.

Individual-task improvements and limitations. We agree that the TUAB difference (0.8289 to 0.8290; +0.01 percentage points) should be described as essentially unchanged performance.

As discussed in the submitted manuscript, SHU-MI and PhysioNet-MI are the two datasets on which AxisBrain obtains lower BA than CBraMod. We considered the spatial localization of motor-imagery-related EEG activity as one possible explanation and investigated this possibility in Appendix D by replacing dense softmax channel pooling with sparse entmax pooling under the same fine-tuning protocol and five matched seeds. This modification did not resolve the gaps: BA decreased by 0.64 and 0.42 percentage points relative to the original pooling on SHU-MI and PhysioNet-MI, respectively. Thus, the tested sparse-pooling modification was insufficient, and spatial localization remains a hypothesis rather than an established explanation.

We agree that individual-task outcomes deserve greater emphasis. We will make these limitations clearer in the main text and pursue more consistent improvements across heterogeneous EEG tasks. Since both datasets with lower BA involve motor imagery, our future work will extend evaluation to a broader range of motor-imagery tasks, investigate the factors underlying these gaps, and develop improvements informed by that analysis.

This task dependence also appears in the reported evaluations of existing EEG foundation models. For example, CSBrain reports lower CHB-MIT BA than CBraMod (0.7262 versus 0.7398; Table 10), despite improving other metrics. CodeBrain likewise reports lower BA on CHB-MIT (0.7273 versus 0.7398) and ISRUC-S1 (0.7835 versus 0.7865), with only a small TUAB difference (0.8294 versus 0.8289). These examples provide context for the challenge; they do not remove our responsibility to explain and address our own limitations.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Global Response [2/3]: SIENA Split Discrepancy, Metric Trade-offs, and Updated Ten-Dataset Averages

We thank the reviewers for highlighting the SIENA metric trade-off and the potential mismatch in dataset splits. These comments helped us identify a split discrepancy and repeat the experiment using the protocol described in the CSBrain paper. We clarify this issue and report the updated results below.

Clarification of the SIENA split.

Our original preprocessing followed the publicly released CSBrain code. On re-examination, we found a difference between the subject-selection rule in the code we used and the split described in the CSBrain paper, which we had not recognized when preparing the original comparison.

ProtocolTraining and validationTest
Released code used in our original experimentAvailable subjects with IDs up to PN12; 8:2 split within each subject and classPN13, PN14, PN16, PN17
CSBrain paper; adopted in our repeated experimentAll 12 subjects other than PN16 and PN17; 8:2 split within each subject and classPN16, PN17

Thus, PN13 and PN14 were included in our original test set but belong to the training/validation pool under the paper-described protocol. We have now prepared the data according to that protocol and repeated the SIENA experiment using the same five seeds.

Updated SIENA results.

Evaluation splitBalanced accuracyAUC-PRAUROC
Original, following the released code0.8023 ± 0.00650.3478 ± 0.00990.9007 ± 0.0023
Aligned with the CSBrain paper0.8316 ± 0.01010.3888 ± 0.01080.8911 ± 0.0034
Change in mean (percentage points)+2.93+4.10−0.96

The repeated evaluation yields higher balanced accuracy and AUC-PR, while AUROC decreases. These changes reflect the revised training and test partitions and should therefore be interpreted as updated results under the aligned protocol.

Compared with the reported CBraMod result, balanced accuracy is higher by 9.99 percentage points (0.8316 versus 0.7317). AUC-PR remains lower, although the gap narrows from 6.29 to 2.19 percentage points (0.3888 versus 0.4107). AUROC is also lower (0.8911 versus 0.9038).

The split correction therefore does not eliminate the metric trade-off. Balanced accuracy evaluates predictions at a particular decision threshold, whereas AUC-PR and AUROC summarize performance across thresholds. The updated results support stronger performance at the evaluated operating point, but do not establish uniformly improved discrimination. Understanding why the gains are particularly pronounced in balanced accuracy merits further analysis of prediction-score distributions and threshold-dependent behavior.

Effect on the aggregate results.

BA is averaged across all datasets, while AUC-PR and AUROC are averaged across binary-classification datasets. Each dataset receives equal weight within its corresponding group.

EvaluationBAAUC-PRAUROC
Original0.75670.71830.8723
Updated with SIENA re-evaluation0.75960.72520.8707

The SIENA re-evaluation increases mean BA by approximately 0.29 percentage points. For binary classification, mean AUC-PR increases by approximately 0.68 percentage points, while mean AUROC decreases by 0.16 percentage points.

We will update Tables 2, 3, 4, 5, 12, 13, 15, and 17 to reflect the SIENA re-evaluation and the corresponding aggregate statistics, and revise the associated descriptions and discussion accordingly.

AuthorsOpenReview ↗

Global Response [1/3]: Rationale for Cross-Axis Agreement in Residual Refinement

We thank the reviewers for their careful assessment and constructive suggestions. We appreciate their recognition of the breadth of the evaluation, the extensive score ablations, the transparent reporting, and the practical advantages of a design that requires neither electrode coordinates nor predefined brain-region annotations. Their comments also helped us identify where the contribution, the rationale for residual modulation, and the comparability of the experimental protocols needed clearer explanation.

Our objective is to improve EEG transfer while retaining a single-stage masked raw-EEG reconstruction pipeline with one pretraining objective. We deliberately build on CBraMod because its relatively simple factorized Transformer provides a useful setting for studying how attention-derived responses should contribute to residual updates. We will sharpen the contribution statements and clarify the evidence and limitations supporting the proposed design.

We organize this global response into three parts covering concerns shared by multiple reviewers or issues requiring substantial revisions throughout the manuscript:

Rationale for using agreement between axis descriptors to determine residual refinement strength.

We acknowledge that the manuscript did not sufficiently explain the rationale for using agreement between axis descriptors to determine residual refinement strength. We thank the reviewers for highlighting this issue and suggesting comparisons with simple gating mechanisms, which helped us clarify and evaluate the proposed design. Below, we compare three ways of assigning token-wise residual gain. All compute scores from the current layer's learned XccX^{cc} representations rather than raw EEG, but differ in the information and structure supplied to the scoring function.

1. Predicting gain from the token representation alone.
A token-wise MLP predicts the score from a single vector, XctccX^{cc}_{ct}. Although this vector contains attention-aggregated spatial and temporal information, the gate is not explicitly supplied with the relationship between the two axis-level contextual summaries.

An XccX^{cc}-based MLP gate and an MLP gate taking both axis descriptors as input will be added to Table 4 as variants [15] and [16], respectively. Both variants perform worse than additive cross-axis recombination without modulation (73.44% mean BA; Table 3). Thus, neither predicting gain from a token representation alone nor supplying both contextual summaries to a generic MLP improves upon the unmodulated baseline in our experiments. Together with the proposed method's higher performance, these results support explicitly comparing descriptor agreement as an effective structure for gain allocation among the tested alternatives.

2. Comparing a token with a single-axis context.
A score can instead measure whether the token agrees with its cross-channel or temporal context. However, the token and its reference context may share the same distortion. Persistent channel-specific contamination can produce high token–temporal-context similarity. Conversely, contamination affecting multiple channels at one time interval can produce high token–cross-channel-context similarity. The Query–Token and Token–Mean variants in Table 5 achieve 71.10% and 72.92% mean BA, respectively, both below the unmodulated baseline. These results suggest limitations of the tested scoring rules.

3. Comparing complementary contexts at the same channel–time intersection.
Our method compares the time-indexed cross-channel descriptor with the channel-indexed temporal descriptor after learned projections. The former uses learned-query pooling across channels, while the latter averages the channel's representations over the segment. Their comparison checks whether a pattern summarized along one axis is compatible with the complementary context, addressing the possibility that a token and its single-axis reference context agree merely because both share an axis-specific distortion.

This provides a rationale for assigning less additional gain when the contexts conflict and more when they agree. The bounded multiplier (1+Sct)(1+S_{ct}) retains the response RctR_{ct} at every position while varying its additional amplification. The proposed configuration achieves 75.96% mean BA, exceeding both the unmodulated baseline and the token–context alternatives.

The proposed cross-check may mitigate misleadingly high gain caused by contamination shared within one axis provided that the complementary summary is not dominated by that contamination. If both descriptors are dominated by the same distortion, their agreement may remain high, which is a potential limitation of the proposed approach.

We will add the above explanation to the Methods section of the revised manuscript.

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

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