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Paper summary
PyraNet addresses compact neural-signal classification across BCI paradigms. It combines learned spatial mixing with parallel grouped dilated temporal convolutions and selects a pooling grid using penalized validation loss. The selected grid remains fixed during subsequent training and inference. Experiments separately train models on eleven EEG, MEG and ECoG datasets spanning five paradigms. Results support a favorable accuracy/size trade-off and task-dependent effects of aggregation granularity.
Critical strengths
S1. Broad reported utility at small model size. Table 2 reports higher mean balanced accuracy than EEGNet across eleven datasets, with nine wins and two ties at printed precision. Table 14 shows gains over Deformer for all four ECoG participants. Together with the small parameter counts in Table 3, these results support PyraNet’s broad applicability as a compact decoder.
S2. Useful evidence that aggregation matters. Figure 5b and Table 4 show task-dependent grid effects and great SSVEP improvements when the aggregation/training procedure is added to IFNet. This is informative beyond a comparison of complete models.
Critical weaknesses
W1. The distinct methodological contribution and added value of the encoder–selector design are insufficiently established. Li et al. [1] already apply parallel grouped dilated temporal convolutions to spatial features and concatenate the outputs, providing a close precedent for the combined temporal-module principle. Figure 5a supports dilation’s reported parameter efficiency relative to ordinary replacements, but does not establish whether grouping features or combining multiple temporal scales improves the accuracy–parameter trade-off. Table 4 supports the complete encoder’s effectiveness relative to IFNet under the reported aggregation procedure, but does not isolate the benefits of components of the encoder. A focused ablation of grouping or receptive-field diversity would clarify their empirical benefit, although it would not establish architectural novelty relative to prior work.
Given this limited architectural novelty, the selector’s added value becomes particularly important. The described selector performs automated hyperparameter selection through shared warm-up and penalized validation loss. Figure 5b and Table 4 demonstrate that aggregation granularity matters. However, these experiments do not establish whether the proposed procedure improves accuracy or retained model size over independently training the candidate grids and selecting among them using validation data. A focused comparison on one existing MI dataset and one existing SSVEP dataset would help establish the selector’s added value.
W2. Material discrepancies between the described method and supplied implementation limit verification of the results. The supplied speech implementation selects a grid using signal-statistic heuristics and training-trial selection counts, rather than the penalized validation-loss procedure in §2.3. During warm-up, it computes classification loss from the head selected for each trial rather than equally weighting all candidate-head losses. If the restored best-validation checkpoint predates grid selection, testing reverts to trial-dependent grid selection rather than fixed-grid inference. The supplied speech training code also fits one alignment transform on pooled fitting trials and applies it to validation and test trials, unlike the session-wise alignment described in §3.3. Separately, the REVE training path uses AdamW rather than the StableAdamW specified in Appendix C.4.3. These discrepancies leave unclear which implementation generated the reported results and whether those results evaluate the stated method and baseline configurations. Their effect on reported performance remains unknown and requires clarification.
References
[1] Haoyu Li et al. “Manifold-based multi-branch transfer learning for MI-EEG decoding.” Chaos, Solitons & Fractals, 196, 116326, 2025.
Questions for authors
Q1. What specific architectural differences distinguish PyraNet’s encoder from the grouped multiscale dilated design of Li et al. (2025), and which constitute a methodological advance? What emperical evidence distinguishes the proposed encoder's benefit from close grouped/multiscale designs?
Q2. How does grid selector compare with validation selection among independently trained grids 8, 32 and 128 on MI and SSVEP dataset already studied? Please compare balanced accuracy, retained parameters and total training work with comparable stopping protection.
Q3. Which code version and configurations generated the reported speech and REVE results? Please reconcile the discrepancies identified in W2 concerning speech grid selection, warm-up loss, checkpoint restoration, alignment and the REVE optimizer.
Q4. The supplied code assigns BNCI2014_002’s generic channels to LaBraM position indices 1–15 and to a hard-coded montage for REVE. What physical electrode correspondence supports these assignments? Please reconcile them with the dataset’s documented electrode layout and clarify whether these mappings were used for the reported results.
Q5. How were the penalties 1/2/8 chosen, and what do selected-grid frequencies or validation-loss trajectories show for the IFNet speech declines (Table 4)?
Q6. Can you provide paired participant-level performance summaries and actual stopping-epoch summaries for PyraNet and the principal compact EEG baselines? Seed-level SDs do not characterize participant variation, and PyraNet’s warm-up protection creates different opportunities for early stopping.
5 comments
Q3. Speech implementation and REVE optimizer
Thank you for carefully comparing the manuscript with the supplied code. We apologize for these inconsistencies and address each point below.
Speech grid selection. The supplied speech code contains an older version of our grid selection method that was not updated in the supplementary package. With the large number of experiments, we overlooked this update. We apologize for this error and will promptly correct the supplementary material.
Speech alignment. The implementation fits one alignment transform on pooled fitting trials and applies it to validation and test trials. The session-wise description in Section 3.3 was not updated to reflect this procedure. We will revise the manuscript accordingly.
REVE optimizer. We initially tried StableAdamW following the REVE paper, but AdamW performed better in our experiments, so we used AdamW for the reported results. We did not update Appendix C.4.3 in time to reflect this change. We will correct the optimizer description and explain this implementation choice.
We appreciate your careful review, which helped us identify these discrepancies and improve the reproducibility of our work.
Q4. Electrode positions
BNCI2014-002 labels its channels EEG1 through EEG15. “The electrodes placement was designed for obtaining three Laplacian derivations. Center electrodes at positions C3, Cz, and C4 and four additional electrodes around each center electrode with a distance of 2.5cm, 15 electrodes total.” Original dataset description
LaBraM assigns indices 1 through 15 in input order. REVE assigns Fz, FC3, FC1, FCz, FC2, FC4, C5, C3, C1, Cz, C2, C4, C6, CP3 and CP4 in that order. We retained these assignments because scores were comparable to other models. This does not verify their physical correspondence. We will document both assumptions in Appendices C.4.1 and C.4.3.
Q5. Penalties and speech results
We chose the penalty coefficients (1, 2, 8) empirically in preliminary experiments for grids of 8, 32 and 128 bins. Thank you for asking about the decline on the speech task. IFNet combines features from different frequency bands and averages them over time. One plausible explanation is that its original pooling better tolerates variation in the timing of consonant–vowel transitions across utterances. The pooling configuration selected by GS may make predictions more sensitive to this variation, reducing generalization to held-out sessions.
Q6. Paired participant scores and stopping epochs
BA averages 3 runs per person, then 141 people across 9 EEG datasets. Gaps and wins/ties/losses compare PyraNet with each baseline. Stop epochs average the last epoch trained (423 runs/model). On BNCI2014-008, seeds varied by model and EEGNet used two kernel settings.
| Model | BA (%) | Median gap (pp) | W/T/L | Mean stop epoch |
|---|---|---|---|---|
| PyraNet | 79.35 | — | — | 33.1 |
| EEGNet | 75.81 | +1.85 | 97/3/41 | 43.0 |
| Conformer | 73.26 | +3.33 | 119/1/21 | 24.9 |
| Deformer | 74.13 | +1.18 | 102/5/34 | 20.8 |
| IFNet | 71.47 | +4.44 | 90/4/47 | 41.8 |
| DBConformer | 59.79 | +2.22 | 100/2/39 | 35.2 |
| FBCNet | 55.07 | +13.75 | 114/1/26 | 45.3 |
Thank you once more for your careful review. We hope the additional explanations and results help clarify our contribution. If your concerns have been resolved, we kindly ask you to consider an upward revision of your score.
Thank you for the careful response and additional experiments. The independent-grid comparison addresses my request and provides useful evidence of reduced training cost with competitive accuracy. The participant-level performance and stopping-epoch summaries also strengthen the empirical evidence. However, my principal concerns remain.
Contribution and distinction from prior work (W1, Q1, Q2). The architectural differences from Li et al. are clearer, but the response does not sufficiently establish the methodological advance beyond the shared grouped multiscale dilated-convolution principle. The specific benefits of grouping and receptive-field diversity also remain insufficiently isolated.
The rebuttal places greater emphasis on the finding that aggregation granularity can substantially affect decoding accuracy, describing this issue as having received little attention in prior work. This framing requires further qualification. FBCNet already evaluated how temporal variance-aggregation window length affects decoding accuracy and discussed the associated model-complexity and training-time implications [1], while Borra et al. included temporal pooling size in hyperparameter optimization across MI, P300 and SSVEP datasets [2]. These precedents show that aggregation granularity had previously been investigated and limit the contribution of the general observation. I acknowledge the new evidence for the selector’s practical efficiency.
Overall, the evidence is more convincing as a demonstration of effectiveness through architectural integration than as an advance in the underlying methodology. I value the broad evaluation and the new evidence for the selector’s training efficiency. However, the response leaves insufficiently clear what new methodological principle or sufficiently distinct empirical insight is established beyond the related architectural designs and prior investigations of aggregation granularity. This is my main remaining concern.
Foundation-model comparisons (Q4). Thank you for explicitly acknowledging that the channel-position assignments were not physically verified. Comparable scores do not validate those assignments, and documenting the assumptions alone does not establish a well-controlled comparison of LaBraM and REVE on BNCI2014-002. Please provide justified mappings and reevaluate the affected models. If this is not possible, the affected entries should be excluded from the principal comparative analysis.
Overall. The rebuttal has strengthened the practical evidence, particularly for training efficiency. However, the remaining concerns about the distinct contribution and the affected baseline comparisons lead me to maintain my current rating of 2.
References
[1] Mane et al. FBCNet: A Multi-view Convolutional Neural Network for Brain-Computer Interface (2021).
[2] Borra et al. A protocol for trustworthy EEG decoding with neural networks (2025).
We greatly appreciate the careful proofreading of the manuscript and your close reading of our code.
Q1. Encoder design
Thank you for pointing us to Li et al.’s work. Li et al. use parallel grouped dilated convolutions within three filtered EEG bands and then combine the bands for motor imagery. PyraNet applies four temporal convolutions directly to one learned spatial projection. We evaluated this design across five paradigms and will cite Li et al. to clarify the shared design and the differences.
Q2. Grid selection
We agree that the selection step is similar to conventional validation-based tuning. However, there is an important distinction. We first found that changing the feature aggregation granularity could have a large effect on decoding accuracy. Based on this observation, we designed GS and incorporated it into our model. This issue has received little attention in prior work. Our experiments with IFNet, a network designed specifically for motor imagery, illustrate this point. As shown in Table 4, adding GS to IFNet raised balanced accuracy from 76.11% to 97.10% on Nakanishi2015 and from 66.92% to 94.71% on Wang2016. These are gains of 20.99 and 27.79 percentage points on the two SSVEP datasets. So we see our main contribution as the finding that aggregation granularity can strongly affect decoding accuracy, rather than the use of conventional hyperparameter selection.
Thank you for suggesting this comparison. We conducted additional experiments to examine the selection rule more closely.
We evaluated all LOSO folds with matching validation splits and early stopping settings on RTX 3090 GPUs. Runs with competing compute processes were discarded. Penalized GS multiplies validation losses by (1,2,8), while unpenalized GS uses (1,1,1). In each LOSO fold, independent tuning trains three complete models sequentially, with grids fixed at 8, 32 and 128. Each model has its own encoder and classifier and is trained with early stopping on the same validation split. We then compare the validation cross-entropy of their selected checkpoints and retain the model with the lowest loss. BA, retained parameters and actual stopping epochs are averaged across participants. For independent tuning, these refer to the selected model, while GPU hours include all three candidates. Timing includes training and validation.
Without the penalty, BA decreased by 0 to 1.25 percentage points across these four datasets. Grid choices changed much more strongly. All folds on the three BNCI datasets moved from grid 8 to larger grids, with retained parameter counts increasing by 44% to 130%. Both methods selected grid 128 on every Nakanishi2015 fold. This suggests that the penalty primarily favors compact models unless a larger head provides a sufficient reduction in validation loss.
Training time also depends on when training stops. For BNCI2014-004, choosing grid 32 reduced the mean stopping epoch from 30.89 to 27.00, so total time fell despite the larger head. Model size and total training time therefore need to be reported separately.
Independent tuning took 2.4 to 5.9 times as long as penalized GS. Its final models had more parameters on the BNCI datasets, while Nakanishi2015 retained the same head. Across all three candidates, the parameter totals per fold were 21,894, 19,590, 21,510 and 74,340 in table order. Only the selected candidate is needed for inference.
We are grateful for this suggestion and will add these comparisons to the manuscript. They support a modest performance effect and a clearer effect on model size in these experiments.