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Under review as a conference paper at ICLR 2027

GACE: Guidance, Assessment, and Correction for EEG Foundation Models

Abstract

EEG foundation models (EFMs) learn rich internal knowledge from large-scale EEG pretraining, encoding transferable spatiotemporal representations and task-relevant priors. We observe that such knowledge is expressed not only in the final Decision Result of an EFM, but also through Decision Evidence, Decision Trajectory, and training-time Decision Dynamics. These internal observations reveal whether an EFM prediction is reliable and whether a misclassified sample still preserves latent support for the correct class. This work aims to turn the internal decision structures of EFMs into actionable signals for self-guidance, self-assessment, and self-correction. We propose GACE, a plug-and-play framework that uses EFM Decision Dynamics to guide fine-tuning, performs reliability modeling around the Decision Result and Decision Evidence, and further incorporates Decision Trajectory to correct high-risk predictions, improving decision reliability without modifying the EFM backbone.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG Foundation Model

Reviews

Among:
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1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_GzHAOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces GACE, a framework for improving downstream EEG foundation models through self-guided fine-tuning, prediction-risk assessment, and selective correction. It combines training-time sample weighting based on true-class margins and confidence stability with two internal signals: channel-level attribution and aggregated intermediate-versus-final logit alignment. After fine-tuning, supervised risk and correction heads are trained on labeled calibration data to identify high-risk predictions and choose between retaining or modifying their labels. Evaluation across three backbones and six main datasets reports average improvements of 4.05 percentage points in balanced accuracy and 3.86 points in weighted F1, supported by component and feature ablations, stage-wise comparisons, and calibration and correction diagnostics.

Critical strengths
  1. This paper is well written and easy to follow. The authors conducted comprehensive experiments to showcase the good performance of the proposed framework.
  2. The evaluation covers multiple backbones and tasks, with positive mean balanced-accuracy gains in all comparisons.
  3. GACE is a plug-and-play framework, which preserves the backbone architecture and separates training adaptation, risk selection, and correction into identifiable modules.
Critical weaknesses
  1. The authors uses internal K-fold validation and out-of-fold risk scoring, but does not clearly consolidate the calibration split’s exact relationship to backbone training and validation, the value of K, or whether folds are grouped by subject or recording.
  2. The main results use a fixed highest-risk selection budget of 12%. Table 19 vary the selection rate, but only evaluates risk-selection precision on Cho2017-MI. The authors should conduct more comparison across tasks to to assess whether the approach remains beneficial when the budget or tasks differ from the main paper setting.
  3. I'm curious about that if the proposed trajectory statistic outperform concatenated or pooled layer-wise outputs when evaluated with the same correction-head capacity.
  4. And I want to know how sensitive are the Evidence gains to a fixed-predicted-class attribution target, the integration baseline, and fewer integration steps.
Questions for authors

Please refer to the weakness.

4 comments

Response to Reviewer 3 (GzHA)

Thank you for recognizing the clarity, experimental coverage, and modular design of our work, and for your specific suggestions on the calibration protocol, risk budget, trajectory design, and attribution sensitivity. We address each point below.

Overview

To facilitate comparison with the review, each response follows this structure:

Summary: A concise restatement of the reviewer's main concern, divided into subquestions A, B, etc., where needed.

Response: Direct answers, explanations, and supporting evidence for each point.

Modification: The corresponding changes to the main text or appendices.


Response for Weakness 1

Review Comments

The authors uses internal K-fold validation and out-of-fold risk scoring, but does not clearly consolidate the calibration split's exact relationship to backbone training and validation, the value of K, or whether folds are grouped by subject or recording.

Summary

How is the calibration set defined, what is the value of K, and how is out-of-fold scoring performed?

Response

(1) The calibration set reuses the original validation set without adding labeled data; this set serves different purposes in backbone model selection and post-hoc training.

Backbone parameters are updated on the training set, and the validation set is used to select the backbone checkpoint. The backbone is then frozen, and the same validation set is used as the calibration set to fit the risk and correction heads. Thus, "calibration" describes the role of existing data in the post-hoc stage, rather than an additional set of labeled data. The validation-set reuse is documented in Appendix O.1.

(2) Internal risk scoring uses 2 or 5 folds, with subject-wise splits for all datasets except ISRUC-S3, which has only one calibration subject.

Within the calibration set, each risk head is fitted on the remaining folds and scores the held-out fold. The resulting out-of-fold scores are pooled to select high-risk calibration samples. The backbone remains fixed throughout this process, so the procedure isolates risk-head fitting rather than providing an out-of-fold evaluation of the entire training pipeline. At test time, the risk head is fitted on all calibration data and directly scores test samples; test samples are not used to fit the parameters of either the risk head or the correction head.

ISRUC-S3 has only one calibration subject, so its internal folds are defined at the sample level. We also examine temporal adjacency using a control with five contiguous time blocks, excluding one adjacent epoch on the training side. Internal risk scoring for Speech uses subject-wise splits, whereas its outer training/validation/test split remains a trial-level split within the same subjects. Correction training generally uses calibration samples selected by out-of-fold risk scores. The settings for each task are summarized in Appendix C.1 (Table 5):

DatasetCalibration samplesCalibration subjectsKUnit for risk-scoring folds
ATTENTION1,62055Subject
BCI-IV-2a1,15222Subject
SEED-2C54022Subject
ISRUC-S396015Sample
Mumtaz20161,02095Subject
Speech-BCIC2020-3750155Subject

Conclusion: The calibration set reuses the original validation set. Internal out-of-fold scoring is performed with a fixed backbone, and the fold unit is chosen according to the calibration subjects available for each task.

Modification

We summarize the calibration folds in Appendix C.1 (Table 5) and clarify reuse of the original validation set in Appendix O.1. This distinguishes backbone model selection from risk-head fitting.


Response for Weakness 2

Review Comments

The main results use a fixed highest-risk selection budget of 12%. Table 19 [now Table 30] vary the selection rate, but only evaluates risk-selection precision on Cho2017-MI. The authors should conduct more comparison across tasks to to assess whether the approach remains beneficial when the budget or tasks differ from the main paper setting.

Summary

Does GACE still improve final performance across tasks when the risk budget changes?

Response

GACE retains positive correction gains across multiple risk budgets on all six tasks; 12% is not the only effective budget.

Across six tasks, two backbones, and three seeds, we keep the trained risk head, correction head, and gates fixed, vary only the test-time risk-selection proportion, and directly evaluate final BACC. A larger risk budget is not necessarily better, as it may also introduce harmful changes. We therefore use 12% as a common evaluation setting, without claiming that it is optimal for every task. Cross-task budget results are reported in Appendix J.3 (Table 33 and Figure 6). The table below reports mean BACC gains over Self-Guidance from the same runs:

Dataset3%5%7%9%12%16%20%30%
ATTENTION+0.628%+0.761%+0.720%+0.813%+1.255%+1.029%+1.132%+0.854%
BCI-IV-2a+0.651%+0.868%+1.056%+1.215%+1.910%+2.025%+2.214%+3.009%
SEED-2C+0.741%+0.905%+1.132%+1.008%+0.700%+0.967%+1.049%+0.782%
ISRUC-S3+0.795%+1.028%+1.253%+1.511%+1.709%+0.995%+0.723%+0.428%
Mumtaz2016+4.334%+7.273%+9.745%+11.027%+7.768%+10.014%+9.221%+7.716%
Speech-BCIC2020-3+0.333%+0.267%+0.267%+0.244%+0.267%+0.156%+0.156%+0.156%

Conclusion: All six tasks retain positive correction gains over the reported budget range, indicating that the method's effectiveness is not limited to a 12% budget.

Modification

We added Appendix J.3, "Correction Budgets across Tasks" (Table 33 and Figure 6). It reports final correction gains under different budgets.


Response for Weakness 3

Review Comments

I'm curious about that if the proposed trajectory statistic outperform concatenated or pooled layer-wise outputs when evaluated with the same correction-head capacity.

Summary

With the same correction-head capacity, do trajectory statistics outperform concatenation or averaging of layer-wise outputs?

Response

In the available comparisons, Trajectory yields larger correction gains than averaging or concatenating layer-wise outputs.

Trajectory explicitly describes alignment between intermediate layers and the final decision, whereas Mean and Concat average or concatenate layer-wise logits, respectively. The table below reports each variant's BACC gain over its corresponding Self-Guidance baseline (Appendix I.9.2, Table 27), averaged equally over CBraMod and CSBrain and three seeds:

DatasetTrajectoryMeanConcat
ATTENTION+1.26%−0.14%+0.06%
BCI-IV-2a+1.91%−0.22%−0.72%
SEED-2C+0.70%+0.08%+0.10%
ISRUC-S3+1.71%+0.54%+0.61%
Mumtaz2016+7.77%+7.23%+7.46%
Speech-BCIC2020-3+0.27%−0.36%−0.24%

Conclusion: In the available comparisons across runs, Trajectory yields larger gains than Mean and Concat on all six tasks.

Modification

We added comparisons in Appendix I.9.2, "Alternative Trajectory Encodings" (Table 27). These include averaging and concatenation of layer-wise outputs.


Response for Weakness 4

Review Comments

And I want to know how sensitive are the Evidence gains to a fixed-predicted-class attribution target, the integration baseline, and fewer integration steps.

Summary

How do the attribution target, integration baseline, and number of integration steps affect final performance?

Response

GACE generally retains positive correction gains across attribution settings, indicating that its effectiveness does not depend on a single specific attribution configuration.

The current Evidence computation uses a zero baseline and 16 integration steps, taking gradients of the maximum logit along the path and allowing the maximizing class to change along the path. We separately replace this setup with a target that holds the class predicted for the original input fixed along the integration path, a training-set mean baseline, and 4/8 integration steps. On three tasks and two backbones, we keep the backbone fixed, recompute attributions, and retrain and select the risk and correction heads for each setting, using the same 12% selection budget. The table below reports each setting's BACC gain over Self-Guidance from the same run (Appendix I.8, Table 25):

DatasetModelFixed predicted classTraining-set mean baseline4 integration steps8 integration steps
BCI-IV-2aCBraMod+1.215%+2.604%+3.299%+2.517%
BCI-IV-2aCSBrain+1.563%+0.781%+0.174%+1.736%
SEED-2CCBraMod+0.247%+0.617%0.000%+0.370%
SEED-2CCSBrain+0.988%+0.247%+0.494%+2.222%
Mumtaz2016CBraMod+13.859%+13.302%+10.999%+13.659%
Mumtaz2016CSBrain+5.903%+6.098%+5.108%+6.364%

Conclusion: GACE generally retains positive correction gains when the attribution target, integration baseline, or number of integration steps is changed.

Modification

We added Appendix I.8, "Attribution-Setting Sensitivity" (Table 25). It clarifies the attribution definition and compares attribution targets, integration baselines, and step counts.


I sincerely thank the authors for additional experiments and clarification. My concerns are well addressed and I will keep my positive rating.

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

GACE is proposed in this work to augment the performance of existing EEG foundation models on downstream tasks by examining internal information across model layers. Specifically, the authors introduce Decision Evidence to characterize spatial attribution and Decision Trajectory to capture cross-layer logit alignment. This is one of the first works that tries to investigate self-guidance in this field. Based on Decision Trajectory and Decision Evidence, GACE enables self-assessment and self-correction. In experiments across diverse downstream classification tasks, the method demonstrated improved decoding performance.

Critical strengths
  1. The intuition of investigating self-guidance, self-assessment, and self-correction through a foundation model's internal representations is very interesting and novel, with clear implications that can potentially help us better understand EEG foundation models, especially when the field has mixed opinions on foundation models.
  2. GACE improves prediction reliability through learned assessment and correction, theoretically applicable to all EEG foundation models.
Critical weaknesses

Despite the interesting research question and results presented in the paper, the work could be substantially strengthened by more comprehensive experimental investigations and deeper analyses of the proposed methods. Some of them are quite necessary, in my opinion.

1. Insufficient investigation of the proposed internal decision signals.

As argued in the abstract, EEG FMs are believed to capture spatiotemporal representations, yet GACE only investigates spatial attribution. Since Integrated Gradients already provides channel-by-time attribution, investigating joint spatiotemporal evidence would be a natural and informative extension. This can also add an extra dimension to the analysis.

2. Potential limitations of Self-Guidance under substantial inter-subject variability.

Self-Guidance assigns higher weights to samples with stronger true-class margins and more stable confidence. However, in EEG decoding, prediction confidence and stability may be strongly influenced by inter-subject variability. GACE may systematically emphasize subjects whose representations are easier for the model to decode while reducing the contributions of subjects with atypical but still valid neural characteristics. The paper does not sufficiently investigate this potential bias.

3. Insufficient experimental evaluation of generalizability and practical usage.

Although the authors evaluate multiple datasets and foundation models, the experiments rely on fixed subject-disjoint train/validation/test partitions. This evaluation does not fully characterize inter-subject variability or establish whether the reported improvements are consistent across unseen subjects (the bias issue of 2 may play a role here). A leave-one-subject-out or subject-wise cross-validation protocol would enable paired subject-level performance comparisons and more meaningful statistical analyses. Furthermore, how GACE would perform in a subject-dependent case is unknown, which is a more realistic usage case, where each subject develops his/her own decoder.

Questions for authors

Below are some additional minor questions complementary to the above-mentioned weaknesses.

Regarding Critical Weaknesses (CW) 1:

  1. The spatial attribution patterns do not always align with established neurophysiological expectations. For instance, correct right-hand motor imagery predictions show strong attribution around T7 and C4 (Fig.1 a) rather than the expected contralateral sensorimotor regions around C3/C1. How do the authors explain this discrepancy neurophysiologically? The pattern also seems to be model-specific as well (Figure 7). Since EEG features spatiotemporal patterns that are also frequency-band-dependent (ERD/ERS in the mu and beta bands for motor imagery), would GACE fail to capture this due to temporal integration?
  2. Applying a single classification head trained on final-layer representations to intermediate representations seems a bit strange to me. Since the authors acknowledge that different layers may capture different representations, why not use individual trajectories and a layer-specific head?

Regarding CW2:

Given the current cross-subject evaluation framework, I think the authors should consider including some classic decoding methods for fair comparisons, such as simple EEGNet and commonly used Euclidean Alignment methods. These comparisons would help position the reported improvements relative to conventional EEG decoding approaches. Furthermore, since GACE does not require modifications to the backbone architecture, the same framework could also be applied to lightweight architectures such as EEGNet. Evaluating GACE on these models would help establish whether its benefits are specific to pretrained foundation models or generalize to conventional EEG decoders.

Regarding CW3:

  1. In the Self-Assessment stage, the method selects the highest-risk 12% of samples within the test set for subsequent correction. This step requires access to the distribution of the entire (or a subset) test set and makes individual correction decisions dependent on other test samples. In other words, this makes the framework inherently batch-dependent. A sample may fall in the top 12% in one batch, but not in the other batch. How GACE would be adjusted to an online setting is unknown: the decoder will only receive data from a single subject, most likely in a sliding-window manner, with only current and past data available.
  2. The authors mention GACE as a plug-and-play framework, yet it still requires model fine-tuning. How would GACE perform when only doing linear probing? Also, this framework seems to work only for classification tasks; generalization to regression and generative tasks is not trivial.

As a reviewer, I think it is essential to evaluate the proposed framework under more rigorous and practically relevant decoding settings. The authors could strengthen the work in either of two directions: (1) investigating subject-dependent decoding, including how GACE could benefit practical applications with subject-specific calibration, or (2) establishing a more comprehensive subject-independent benchmark with rigorous subject-wise data splits, statistical analyses, and comparisons against established EEG decoding and transfer methods.

For (2), I would suggest comparisons with conventional neural decoders, like EEGNet, and widely used cross-subject adaptation techniques such as Euclidean Alignment. Although I acknowledge that the novelty of this work lies in leveraging the internal decision information of EEG foundation models, demonstrating improvements over fine-tuned foundation-model baselines alone does not establish its competitiveness against established EEG decoding approaches. If the proposed framework cannot achieve competitive performance against simpler models or established transfer methods, its practical significance remains unclear. Finally, evaluating GACE on lightweight architectures such as EEGNet, where technically feasible, would help clarify whether its benefits arise from the pretrained knowledge of foundation models.

23 comments

Response to Reviewer 2 (kxXm)

Thank you for your careful review and specific comments on internal decision signals, inter-subject variability, generalizability, and practical usage. We address your concerns point by point below.

Overview

To facilitate comparison with the review, each response follows this structure:

Summary: A concise restatement of the reviewer's main concern, divided into subquestions A, B, etc., where needed.

Response: Direct answers, explanations, and supporting evidence for each point.

Modification: The corresponding changes to the main text or appendices.


Response for Weakness 1

Review Comments

Insufficient investigation of the proposed internal decision signals. As argued in the abstract, EEG FMs are believed to capture spatiotemporal representations, yet GACE only investigates spatial attribution. Since Integrated Gradients already provides channel-by-time attribution, investigating joint spatiotemporal evidence would be a natural and informative extension. This can also add an extra dimension to the analysis.

Summary

Why focus only on spatial attribution, and can joint spatiotemporal evidence provide additional information?

Response

Joint spatiotemporal evidence does not provide consistent additional gains, while spatial channels offer more suitable shared attribution anchors across trials and models.

The discriminative time periods in motor imagery vary across brain regions and subjects [8], and backbones also differ in their temporal encoding and aggregation mechanisms [9,10]. Joint spatiotemporal evidence is therefore more susceptible to these differences and may not remain stable across trials and models. We aggregate attribution over the entire trial at the channel level, retaining overall channel contributions while reducing dependence on precise temporal localization. Across six datasets, two backbones, and three seeds, we fix the backbones and high-risk samples and compare spatial Evidence with channel-by-time-segment Evidence using correction heads with similar parameter counts. The corresponding experiment is presented in Appendix I.7 (Table 24). The table reports mean BACC gains over Self-Guidance from the same run and their differences, with Δ = spatiotemporal − spatial:

BackboneMetricATTENTIONBCI-IV-2aSEED-2CISRUC-S3Mumtaz2016Speech-BCIC2020-3
CBraModSpatial Evidence gain+1.337%+2.575%+0.782%+0.219%+8.517%+0.178%
CBraModSpatiotemporal Evidence gain-0.926%+0.608%+0.041%-0.025%+7.883%-0.222%
CBraModΔ-2.263%-1.968%-0.741%-0.244%-0.633%-0.400%
CSBrainSpatial Evidence gain+1.173%+1.244%+0.617%+3.198%+7.018%+0.356%
CSBrainSpatiotemporal Evidence gain+0.432%+0.463%+0.576%+1.071%+7.089%-0.400%
CSBrainΔ-0.741%-0.781%-0.041%-2.127%+0.071%-0.756%

Conclusion: Joint spatiotemporal evidence does not provide consistent additional gains; spatial Evidence yields better overall correction performance.

Modification

We added Appendix I.7, "Spatial and Spatiotemporal Evidence" (Table 24). It compares correction gains from the two representations and explains how temporal attribution is aggregated.


Response for Weakness 2

Review Comments

Potential limitations of Self-Guidance under substantial inter-subject variability. Self-Guidance assigns higher weights to samples with stronger true-class margins and more stable confidence. However, in EEG decoding, prediction confidence and stability may be strongly influenced by inter-subject variability. GACE may systematically emphasize subjects whose representations are easier for the model to decode while reducing the contributions of subjects with atypical but still valid neural characteristics. The paper does not sufficiently investigate this potential bias.

Summary

Does Self-Guidance favor subjects who are easier to decode, reducing the contribution of atypical subjects?

Response

Self-Guidance first uses stable samples to establish a foundation for adaptation, then progressively learns harder patterns; all samples participate in training throughout.

Early in training, more stable samples play a greater guiding role, helping the model establish a reliable discriminative foundation and reducing the disturbance to pretrained representations caused by highly variable samples. As adaptation proceeds, sample weights are dynamically updated according to the current learning state, and training continues on harder samples. Lower initial weights thus reflect a temporary learning emphasis rather than the exclusion of those samples or subjects.

(1) Epoch-wise weight analysis shows no concentration of training weights on individual subjects.

Across six datasets, two models, and three seeds, we compute each subject's share of the total training weight in every epoch and measure the normalized entropy. A value of 1 indicates equal weight shares across subjects, while values closer to 0 indicate concentration on a few subjects. The minimum across all non-warmup epochs remains above 0.976. Thus, even in the least balanced epoch, the overall weights remain broadly distributed, with no dominance by a small number of subjects, as shown by the statistics and epoch-wise weight curves in Appendix K.7 (Table 45; Figures 62 and 63):

DatasetNumber of training subjectsMinimum normalized entropyMaximum single-subject weight share
ATTENTION160.99737.65%
BCI-IV-2a50.977327.21%
SEED-2C100.997111.50%
ISRUC-S380.986419.02%
Mumtaz2016430.97684.51%
Speech-BCIC2020-3150.987410.41%

Conclusion: Training weights remain broadly distributed in every task, with no dominance by a small number of subjects.

(2) All subjects, including those with lower weights, maintain high final training performance.

We summarize the range of final performance across all training subjects and three seeds. We use class recall for Mumtaz2016 and BACC for the other tasks, with detailed results in Appendix K.7 (Table 46; Figures 64–99):

DatasetCBraModCSBrain
ATTENTION100%100%
BCI-IV-2a100%100%
SEED-2C82.96%–97.41%90.00%–99.63%
ISRUC-S3100%100%
Mumtaz2016100%100%
Speech-BCIC2020-3100%96.00%–100.00%

Conclusion: All subjects, including those with lower weights, maintain high final training performance.

Modification

We added Appendix K.7, "Training-Subject Weights and Learning Progress" (Tables 45 and 46; Figures 62–99). It presents epoch-wise weight distributions and the final training performance of each subject.


Response for Weakness 3

Review Comments

Insufficient experimental evaluation of generalizability and practical usage. Although the authors evaluate multiple datasets and foundation models, the experiments rely on fixed subject-disjoint train/validation/test partitions. This evaluation does not fully characterize inter-subject variability or establish whether the reported improvements are consistent across unseen subjects (the bias issue of 2 may play a role here). A leave-one-subject-out or subject-wise cross-validation protocol would enable paired subject-level performance comparisons and more meaningful statistical analyses.

Furthermore, how GACE would perform in a subject-dependent case is unknown, which is a more realistic usage case, where each subject develops his/her own decoder.

Summary

  • A: Can subject-wise cross-validation and paired statistics establish consistent gains on unseen subjects?

  • B: Is GACE also effective for subject-dependent decoding?

Response

  • A

    (1) The main experiments follow existing benchmark splits, and GACE retains positive mean gains under additional subject-disjoint three-fold evaluation.

    We follow CBraMod and CSBrain benchmark splits for comparability [9,10]. Given the cost of repeated adaptation for large EEG foundation models under full LOSO, we add subject-disjoint three-fold evaluation across three datasets and four models (36 within-fold configurations; Appendix H.2, Table 12). BACC gains over standard fine-tuning are averaged equally across the three outer folds:

    DatasetCBraModCSBrainEEGNetEEGNet+EA
    BCI-IV-2a+4.15%+3.61%+4.78%+4.54%
    Mumtaz2016+5.47%+2.70%+6.76%+4.03%
    SEED-2C+6.22%+4.37%+4.17%+7.16%

    Conclusion: GACE achieves positive three-fold mean gains across all three datasets and four model configurations.

    (2) In paired subject-level comparisons, GACE achieves positive mean gains over both standard fine-tuning and Self-Guidance.

    Using the same three-fold results, we compare GACE with standard fine-tuning (CE) and Self-Guidance (SG) on each subject's held-out outer-fold test samples (Appendix H.3, Table 13; Figure 5). Gains are equally weighted means of paired differences across all test subjects. Parentheses count subjects scoring lower with GACE than the reference; n is the total subject count. For single-class Mumtaz2016 subjects, we use class recall:

    BackboneReferenceBCI-IV-2a (n=9)Mumtaz2016 (n=62)SEED-2C (n=15)
    CBraModCE+4.10% (0)+5.96% (20)+6.22% (2)
    CBraModSG+1.82% (1)+2.71% (27)+2.37% (1)
    CSBrainCE+3.61% (0)+2.48% (11)+4.37% (1)
    CSBrainSG+1.64% (0)+1.29% (12)+2.40% (1)
    EEGNetCE+4.74% (0)+6.44% (13)+4.17% (3)
    EEGNetSG+2.03% (1)+4.89% (14)+2.40% (4)
    EEGNet+EACE+4.53% (0)+4.05% (19)+7.16% (0)
    EEGNet+EASG+0.86% (1)+3.64% (21)+3.65% (1)

    Conclusion: Paired subject-level results further support GACE's overall advantage, with positive mean gains over both standard fine-tuning and Self-Guidance.

  • B

    In subject-dependent decoding comparisons, GACE improves performance in all six task–model combinations.

    Each subject has an independent decoder with disjoint training, calibration, and test subsets. GACE and standard fine-tuning use identical splits and test samples. Results are averaged equally across subjects, with Δ = GACE − CE (Appendix H.4, Table 14):

    DatasetBackboneCESGGACEΔ95% interval
    ATTENTIONCBraMod55.199%60.185%61.574%+6.375%[4.416, 8.405]
    ATTENTIONCSBrain54.701%58.440%61.859%+7.158%[4.024, 10.541]
    BCI-IV-2aCBraMod56.867%59.954%60.417%+3.549%[1.813, 5.710]
    BCI-IV-2aCSBrain45.293%48.765%49.113%+3.819%[1.312, 6.674]
    SEED-2CCBraMod60.148%62.593%64.444%+4.296%[1.852, 6.741]
    SEED-2CCSBrain56.963%61.037%61.630%+4.667%[1.259, 9.778]

    Conclusion: All six subject-dependent decoding settings show improvements, and the 95% intervals for paired gains are all above 0.

Modification

  • A: Added subject-disjoint three-fold and subject-level analyses in Appendix H.2, "Lightweight Decoder Comparisons" (Table 12), and H.3, "Subject-Wise Generalization" (Table 13; Figure 5).

  • B: Added subject-dependent performance and gain intervals in Appendix H.4, "Subject-Dependent Personal Decoding" (Table 14).


Reviewer_DAc4OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes GACE, a post-hoc wrapper for fine-tuned EEG foundation models with three parts. First, a sample-reweighting scheme during fine-tuning (“Self-Guidance”). Second, a supervised risk head trained on a labeled calibration set (“Self-Assessment”). Third, a supervised keep-or-flip head applied to the top 12% riskiest predictions (“Self-Correction”). The design is motivated by two observations: correct and incorrect predictions have different channel attributions, and intermediate-layer readouts sometimes favor the true class more than the final layer does. The authors report an average gain of about 4 pp B-ACC over standard fine-tuning across 3 backbones and 6 datasets.

Critical strengths
  1. The question of whether EFM internals carry useful signal is reasonable.
  2. The evaluation spans several backbones and tasks, and the appendix is unusually thorough and transparent about what each analysis does and does not show.
Critical weaknesses
  1. The motivating observations are weak. Observation I rests on group-mean attribution differences of roughly 1 pp of normalized share. These differences flip sign across seeds (e.g., right-hand C4), and no significance testing is reported. The individual examples were selected for maximal cross-seed consistency. The headline example in Fig. 1a, where correct right-hand MI predictions rely on T7/C4, is also not neurophysiologically compelling. Observation II applies the final classification head to intermediate representations it was never trained on. The errors are then grouped by the layer that maximizes the margin over the final layer. By construction, this guarantees that some earlier layer “looks better” for many errors. Two controls are missing: the same analysis on correctly classified samples, and a chance-level reference.
  2. The proposed signals contribute little. Table 15 shows that removing the evidence features, the trajectory features, or both changes the correction gain by only −0.65, −0.37, and −0.85 pp on average. Most of that change comes from Mumtaz2016. The features that motivate the paper therefore account for a sub-1-pp effect. Most of the remaining gain comes from a supervised head trained on logits and softmax statistics.
  3. Gains are dominated by one dataset, and trivial rules nearly match them. In Table 16, simply flipping high-risk predictions to the runner-up class recovers most of the Mumtaz2016 gain (e.g., +7.9 vs. +9.0 pp for CodeBrain). In a binary task, that amounts to a decision-threshold shift. Outside Mumtaz2016, correction gains are mostly under 1.5 pp and often within one SD across three seeds. Speech-BCIC2020-3 and ISRUC-S3 (CodeBrain) are essentially unchanged.
  4. The baseline comparison is unfair. GACE uses an additional labeled calibration set, while the baseline does not. A fair comparison would give the baseline the same labels, for example through threshold or bias tuning, temperature scaling, or a learned risk/flip head on logits alone. The MSP comparison in Table 2 contrasts a supervised head with an unsupervised score.
Questions for authors
  1. How do the baselines compare with the published numbers for each backbone under the same splits?
  2. Which data forms the calibration set? Does it overlap with the validation set used for baseline checkpoint selection?
  3. How does GACE compare with simple label-using baselines on the same calibration data, such as threshold or prior correction and a logit-only risk/flip head?
  4. Are the gains significant across seeds, excluding Mumtaz2016?
13 comments

Response to Reviewer 1 (DAc4)

Thank you for your careful review and specific comments on the motivating observations, the contribution of internal signals, correction gains, and the fairness of the comparisons. We address your concerns point by point below.

Overview

To facilitate comparison with the review, each response follows this structure:

Summary: A concise restatement of the reviewer's main concern, divided into subquestions A, B, etc., where needed.

Response: Direct answers, explanations, and supporting evidence for each point.

Modification: The corresponding changes to the main text or appendices.


Response for Weakness 1

Review Comments

The motivating observations are weak. Observation I rests on group-mean attribution differences of roughly 1 pp of normalized share. These differences flip sign across seeds (e.g., right-hand C4), and no significance testing is reported. The individual examples were selected for maximal cross-seed consistency. The headline example in Fig. 1a, where correct right-hand MI predictions rely on T7/C4, is also not neurophysiologically compelling.

Observation II applies the final classification head to intermediate representations it was never trained on. The errors are then grouped by the layer that maximizes the margin over the final layer. By construction, this guarantees that some earlier layer "looks better" for many errors. Two controls are missing: the same analysis on correctly classified samples, and a chance-level reference.

Summary

A and B address motivating observations I and II, respectively.

A · Evidence

  • A1: Are the approximately 1% attribution differences stable and significant?

  • A2: Are the selected individual examples representative of the full sample set?

  • A3: Is the T7/C4 attribution for right-hand predictions consistent with physiological expectations?

B · Trajectory

  • B1: Is reusing the final classification head to read intermediate layers justified?

  • B2: Can controls using correct predictions and chance-level references rule out grouping bias in the apparent advantage of earlier layers?

Response

A · Evidence

  • A1

    (1) Attribution share differences of approximately 1% can still correspond to substantial overall attribution differences, which are statistically significant in most settings.

    For CSBrain on Cho2017, the average normalized share across 64 channels is about 1.56%. In right-hand motor imagery, C6's mean normalized share differs by 1.0051 percentage points between groups; its mean raw attribution is 4.3498 for correct and 8.4112 for incorrect predictions, a 93.37% increase. Across six datasets, relative L2 distance is the L2 distance between group-mean raw attribution vectors divided by their average norm (Appendix K.2.1, Table 39):

    BackboneMetricATTENTIONBCI-IV-2aSEED-2CISRUC-S3Mumtaz2016Speech-BCIC2020-3
    CBraModRaw L2 distance15.930115.31515.424561.970910.8886265.2006
    CBraModRelative L2 distance35.93%13.62%34.59%33.80%20.43%54.23%
    CSBrainRaw L2 distance15.21323.24958.138423.271724.8386171.0475
    CSBrainRelative L2 distance33.45%20.30%34.86%27.31%51.77%46.09%

    Conclusion: Across datasets and backbones, the relative L2 distance between the correct and incorrect groups' mean raw attribution vectors ranges from 13.62% to 54.23%, with an equally weighted mean of 33.87%, indicating substantial overall attribution differences.

    We test overall attribution-vector differences by permuting correct/incorrect labels within each subject and true class, preserving group sizes. Each permutation computes L2 distance using the same aggregation across subjects, classes, and seeds. We report p-values from 1,999 permutations, with Holm correction applied separately across the 12 dataset/backbone combinations for raw and normalized attributions (Appendix K.2.1, Table 40).

    BackboneAdjusted p-valueATTENTIONBCI-IV-2aSEED-2CISRUC-S3Mumtaz2016Speech-BCIC2020-3
    CBraModRaw attribution L20.0060.0060.0060.0060.0060.176
    CBraModNormalized attribution L20.0060.0060.0060.0060.0060.019
    CSBrainRaw attribution L20.0060.0060.0060.0060.0060.006
    CSBrainNormalized attribution L20.0060.0060.0060.0130.0060.006

    Conclusion: After Holm correction, the overall between-group difference in normalized attribution is significant for all dataset/backbone combinations (p ≤ 0.019).

    (2) Sign flips in local between-group differences reflect relative fluctuations in attribution magnitude and do not necessarily change the channels on which the model primarily relies.

    A sign flip changes which group has higher attribution; it does not mean the model stops attending to that channel. For C3 in the original CodeBrain/Cho2017 left-hand analysis, we report the between-group share difference and its rank among 64 channels (Appendix K.2.2, Table 41):

    SeedC3 share difference (incorrect − correct)C3 rank in correct groupC3 rank in incorrect group
    0+0.465 pp18th9th
    1−0.186 pp5th3rd
    2+0.633 pp7th1st

    Conclusion: In this example, the between-group difference for C3 flips sign across seeds, but it remains among the top 18 of 64 channels for all three seeds.

  • A2

    The individual examples are illustrative; analysis of all samples without selection also shows similarity in channel rankings across seeds.

    A class/channel combination is directionally consistent if the same group has higher attribution across all three seeds. We report this rate, with consistent/total counts in parentheses. For each sample, we rank channels by attribution, compute cross-seed Spearman correlations, and aggregate across samples. Values closer to 1 indicate more consistent channel-importance rankings (Appendix K.2.3, Table 42):

    BackboneMetricATTENTIONBCI-IV-2aSEED-2CISRUC-S3Mumtaz2016Speech-BCIC2020-3
    CBraModSign consistency rate42.9% (24/56)69.3% (61/88)75.0% (90/120)46.7% (14/30)13.2% (5/38)40.9% (131/320)
    CBraModRanking Spearman correlation0.7070.5860.7750.6160.4670.571
    CSBrainSign consistency rate35.7% (20/56)46.6% (41/88)65.0% (78/120)53.3% (16/30)50.0% (19/38)38.8% (124/320)
    CSBrainRanking Spearman correlation0.3620.6250.8450.6520.5580.698

    Conclusion: The full sample set without selection still exhibits cross-seed ranking similarity, although its degree varies across tasks and models.

  • A3

    (1) The overall left–right difference in Figure 1(a) is partly consistent with the expected contralateral dominance for right-hand motor imagery.

    Right-hand motor imagery typically exhibits more pronounced μ/β rhythm desynchronization in the left sensorimotor region [1,2]. In Figure 1(a), correct predictions show prominent attribution on the left, whereas incorrect predictions lack similarly prominent left-sided attention and shift their main attribution to the right. This overall lateralization trend is physiologically plausible, although it does not imply that every prominent channel precisely corresponds to a motor cortical location.

    (2) The additional spatial attribution maps across datasets and backbones are generally consistent with the physiological expectations for the respective tasks; the local tendency in Figure 1 is not a universal pattern.

    Figure 1(a) presents group-averaged attribution for a specific model, dataset, and class. Additional spatial maps in Appendix K.1.1 (Figures 9 and 13) and K.1.3 (Figure 21) show distributions consistent with the physiological expectations for their respective tasks, such as prominent attribution at contralateral C4 for left-hand motor imagery, and predominantly central attribution for N2 and frontal attribution for N3 in sleep staging. Evidence describes the channel reliance learned by a model under a particular dataset and architecture, without imposing explicit physiological constraints on the attended locations. The local tendency in Figure 1 should therefore also be interpreted in the context of the specific model and data.

B · Trajectory

  • B1

    (1) Reusing the final classification head to read intermediate layers has established precedents and provides a common task-discriminative probe.

    Reusing the final output projection to read intermediate representations has precedents in both computer vision and natural language processing, including class-space analysis of ViTs and cross-layer decoding in language models [3,4]. In GACE, the shared classification head provides the same discriminative criterion across layers, reads class-related components already formed in intermediate representations, and compares how these components change across layers. The rationale for this readout is provided in Appendix E.2.

    (2) Independent layer-specific heads do not consistently provide additional gains in final correction performance.

    We freeze the same backbone and train an independent classification head for each layer. In the correction comparison, we replace the intermediate readouts while retaining the original final-layer output and using the same risk selection and correction-head architecture. The experimental comparison is provided in Appendix I.9.1 (Table 26). The table below reports the mean B-ACC gains of both approaches over the same Self-Guidance baseline after separate searches. Both improve the final predictions, but independent layer-specific heads do not consistently yield additional gains.

    DatasetBackboneIndependent heads ΔB-ACC (pp)Shared head Full ΔB-ACC (pp)
    BCI-IV-2aCBraMod+5.440+5.961
    BCI-IV-2aCSBrain+4.225+4.282
    Mumtaz2016CBraMod+14.497+14.451
    Mumtaz2016CSBrain+11.233+10.860
    SEED-2CCBraMod+2.469+2.387
    SEED-2CCSBrain+2.305+2.346

    Conclusion: Independent layer-specific heads do not consistently provide additional gains, and the shared classification head still provides effective correction signals.

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