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Under review as a conference paper at ICLR 2027

PyraNet: A Lightweight Neural Decoder for Diverse BCI Paradigms

Abstract

Neural signal decoding relies on learning effective representations of brain activity. Existing models have largely followed two paths: compact decoders and large pretrained foundation models. The former perform well on certain target paradigms but struggle on others. The latter seek broad generalizability through increased capacity and cross-dataset pretraining but often fail to deliver performance commensurate with their size. This raises a fundamental question: Must general-purpose neural decoding rely on scaling up model size, or can broad applicability be achieved with a lightweight architecture informed by domain knowledge? To address this question, we propose PyraNet, a lightweight, neurophysiology-informed architecture. Specifically, we devise an encoder in which learned spatial filters capture discriminative cross-channel patterns, while grouped and dilated convolutions integrate these patterns over multiple temporal receptive fields to model coupled spatiotemporal dependencies within a small parameter budget. We further introduce a dataset-level adaptive grid selector that automatically configures feature aggregation using the same penalty factors across datasets, without requiring manual granularity selection. After a shared warm-up, it selects the grid with the lowest penalized validation loss and retains it for subsequent training and inference. We evaluated PyraNet against six compact models and three advanced foundation models across eleven electroencephalography (EEG), magnetoencephalography (MEG), and electrocorticography (ECoG) datasets spanning five decoding paradigms: motor imagery (MI), P300 detection, steady-state visual evoked potential (SSVEP) decoding, mental arithmetic (MA) state classification, and speech decoding. PyraNet demonstrated consistently strong performance across all eleven datasets, with the best average rank of 1.8 and a mean balanced accuracy (BAcc) of 66.93%, exceeding the runner-up by 3.1 percentage points. On the nine EEG datasets shared with the foundation models, PyraNet achieved a mean BAcc of 77.55%, outperforming the strongest foundation model by 3.1 percentage points, with approximately one-thousandth as many parameters.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Neural decoding, Brain-Computer Interface, Motor Imagery, EEG

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.75 over 4 reviews, above 25% of the others.
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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

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)(1,2,8), while unpenalized GS uses (1,1,1)(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.

DatasetMethodBA (%)GPU hoursGrid counts 8/32/128Retained parametersMean stop epoch
BNCI2014-002Penalized GS79.240.33114/0/04,22632.21
Unpenalized GS77.990.2220/5/99,71221.00
Independent tuning79.780.8591/13/05,65228.93
BNCI2014-004Penalized GS74.400.5529/0/03,45830.89
Unpenalized GS74.230.4890/9/04,99427.00
Independent tuning73.951.3291/8/04,82329.67
BNCI2015-001Penalized GS74.980.87812/0/04,09838.17
Unpenalized GS74.760.9360/5/79,21841.00
Independent tuning73.832.7490/11/16,14647.58
Nakanishi2015Penalized GS96.980.0750/0/952,42816.89
Unpenalized GS96.980.0730/0/952,42816.89
Independent tuning97.720.4450/0/952,42817.56

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.

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.

ModelBA (%)Median gap (pp)W/T/LMean stop epoch
PyraNet79.35——33.1
EEGNet75.81+1.8597/3/4143.0
Conformer73.26+3.33119/1/2124.9
Deformer74.13+1.18102/5/3420.8
IFNet71.47+4.4490/4/4741.8
DBConformer59.79+2.22100/2/3935.2
FBCNet55.07+13.75114/1/2645.3

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).

Reviewer_N6qqOpenReview ↗
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Paper summary

This paper presents PyraNet, a compact supervised neural decoder for brain–computer interface tasks. The architecture combines learned cross-channel spatial filtering, parallel grouped temporal convolutions with different dilation rates, and a selector over three temporal pooling grids. During a shared warm-up stage, all pooling heads are trained jointly; one is then selected using a penalized validation loss and retained for subsequent training and inference.

The model is evaluated on eleven datasets spanning five BCI paradigms and three acquisition modalities. The breadth of the evaluation and the model’s computational efficiency are appealing. However, the methodological novelty is limited, and several experimental choices weaken the paper’s central claims. In particular, the experiments demonstrate that a compact architecture can be retrained successfully across diverse datasets, rather than showing that a single learned representation generalizes across tasks. The evidence supporting the proposed grid-selection method and the individual encoder components is also incomplete.

Critical strengths
  • PyraNet is compact and computationally efficient.

  • The study covers eleven datasets, five paradigms, and three acquisition modalities. The paper also provides substantial implementation and preprocessing details.

  • The model may be useful in settings where computational or memory constraints make large pretrained models impractical.

Critical weaknesses
  1. The study is a BCI application, not general-purpose representation learning

PyraNet is trained, validated, early-stopped, and grid-selected independently for every dataset. No parameters or representations are shared between datasets. The results therefore show that the same architectural design can be retrained across several paradigms, not that PyraNet learns a general-purpose neural representation. The work is more suitable for BCI specific venue.

  1. The architectural contributions are not sufficiently isolated

The PyraNet architecture combines mostly established components, while the current experiments do not isolate the value of the proposed selection rule or individual encoder choices. The foundation-model comparison and aggregate ranking also overstate the strength and generality of the evidence.

  1. The incremental benefit of the grid selector is not isolated

The selector chooses among three predefined pooling grids using penalized validation loss after a shared multi-head warm-up. Figure 5b demonstrates that grid choice matters, and Table 4 shows that adding the selector can substantially affect IFNet. These experiments do not establish that the proposed procedure is better than conventional validation-based tuning.

Questions for authors
  • Were the pooling-grid candidates and penalty coefficients selected before examining the eleven benchmark datasets? What data or principle determined these choices?

  • How does the proposed selector compare with unpenalized shared-warm-up selection and independently trained fixed-grid candidates in terms of accuracy, retained model size, and total training cost?

3 comments
AuthorsOpenReview ↗

Response to Critical Weaknesses

Thank you for reading our manuscript carefully. We appreciate your thoughtful feedback.

W1. BCI Application vs. General-Purpose Representation Learning

We agree that PyraNet is trained independently on each dataset. No learned parameters are shared across datasets, and our experiments do not test whether a representation learned on one dataset transfers to another. We will revise the manuscript to make the scope of our claim explicit.

Our study asks whether the same compact decoder architecture can accommodate different BCI paradigms when trained separately on each dataset. We evaluate this question across eleven datasets spanning five paradigms and three acquisition modalities. This focus on supervised representation learning for neural signals aligns with ICLR’s stated scope.

W2. Architectural Contributions Are Not Sufficiently Isolated

Table 4 provides a comparison at the level of the complete encoder. On the EEG datasets, PyraNet and IFNet+GS use the same grid selection procedure with their respective encoders. Their comparison therefore shows how decoding performance changes when we switch encoders while keeping grid selection the same. We chose IFNet because its temporal feature map allowed us to add GS with minimal changes to the original architecture. This comparison leaves the contributions of individual encoder components open. We address the selection rule separately in Q2, where we compare penalized GS, unpenalized GS, and independent grid tuning.

We also agree that our wording overstated the foundation-model comparison and aggregate ranking. Our results show that, under the evaluated leave-one-subject-out (LOSO) protocol, PyraNet achieved better decoding performance than the evaluated foundation-model baselines on some datasets. We will revise the manuscript to limit this claim to the datasets, paradigms, and baselines tested, and describe the aggregate ranking as a summary of performance on these benchmarks.

W3. The Incremental Benefit of the Grid Selector

Thank you for raising this point. Reviewer pbmk raised a similar question in Q2. We agree that the selection step in GS is similar to conventional validation-based tuning. However, there is an important distinction. We first observed that changing the temporal granularity of feature aggregation could substantially affect decoding accuracy. How well a decoder’s aggregation granularity carries over from one BCI paradigm to another has received relatively little attention. This observation motivated us to design GS and incorporate it into PyraNet.

Our experiments with IFNet, a network designed for motor imagery, illustrate this point. As shown in Table 4, adding GS changed balanced accuracy by less than one percentage point on each of the two motor-imagery datasets. On the two SSVEP datasets, it raised balanced accuracy from 76.11% to 97.10% on Nakanishi2015 (+20.99 percentage points) and from 66.92% to 94.71% on Wang2016 (+27.79 percentage points). We therefore see our main contribution here as identifying how strongly aggregation granularity can affect decoding accuracy across BCI paradigms, rather than simply applying conventional validation-based tuning.

AuthorsOpenReview ↗

Response to Questions For Authors

Q1. What Determined the Pooling-Grid Candidates and Penalty Coefficients?

Thank you for the question. Our choice of candidate grids and penalty coefficients was informed by preliminary observations on a small subset of datasets, where we found that aggregation granularity could affect decoding performance. We then used the same candidate grids and coefficients in the EEG selector experiments. In this sense, these two hyperparameters are similar to the learning rate: their values were set empirically during model development.

Q2. Comparison with unpenalized GS and independent tuning

Thank you for suggesting this comparison. It helped us examine both the role of the penalty and an additional finding about early stopping.

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)(1,2,8), while unpenalized GS uses (1,1,1)(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.

DatasetMethodBA (%)GPU hoursGrid counts 8/32/128Retained parametersMean stop epoch
BNCI2014-002Penalized GS79.240.33114/0/04,22632.21
Unpenalized GS77.990.2220/5/99,71221.00
Independent tuning79.780.8591/13/05,65228.93
BNCI2014-004Penalized GS74.400.5529/0/03,45830.89
Unpenalized GS74.230.4890/9/04,99427.00
Independent tuning73.951.3291/8/04,82329.67
BNCI2015-001Penalized GS74.980.87812/0/04,09838.17
Unpenalized GS74.760.9360/5/79,21841.00
Independent tuning73.832.7490/11/16,14647.58
Nakanishi2015Penalized GS96.980.0750/0/952,42816.89
Unpenalized GS96.980.0730/0/952,42816.89
Independent tuning97.720.4450/0/952,42817.56

Removing the penalty reduced BA by 1.25, 0.16 and 0.22 percentage points on the three BNCI datasets and left Nakanishi2015 unchanged. It changed every BNCI fold from grid 8 to grid 32 or 128, increasing retained parameters to 2.30, 1.44 and 2.25 times their original values. Thus, these results suggest that the penalty mainly controls the balance between validation fit and model size. A larger head must reduce validation loss enough to offset its larger multiplier.

A larger head does not necessarily take longer to train to early stopping. On BNCI2014-004, unpenalized GS stopped at epoch 27.00 on average, compared with 30.89 for penalized GS, and used less total time despite retaining more parameters.

Independent tuning required 2.4 to 5.9 times the training time of penalized GS. Its selected models were larger on the BNCI datasets and identical in size on Nakanishi2015.

We appreciate this question and will include these results in the revision.

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.

AuthorsOpenReview ↗

Additional Ablation Results

In addition, we evaluated the spatial module, the multiscale temporal module, and GS through ablation experiments. Removing GS fixes the aggregation grid at 8 bins.

DatasetFull modelw/o Spatialw/o SpatioTemporalw/o GS (grid 8)
BNCI2014-00153.5751.5825.9653.89
Nakanishi201597.1095.5195.2350.33
EEGMAT71.2064.9450.9370.62
BNCI2014-00871.7671.4067.7171.44

All values are balanced accuracy (%).

The spatial filter has a smaller overall effect, but still provides meaningful gains. It also maps datasets with different input channel counts to a fixed number of feature channels, which simplifies processing in later modules. Removing the spatiotemporal module causes large drops on BNCI2014-001 and EEGMAT. Surprisingly, its effect on the SSVEP dataset is much smaller. In contrast, removing GS sharply reduces SSVEP performance, while its effect on the other datasets is small. Together, these results suggest that the modules play complementary roles. Together, these modules support strong performance when the model is trained separately on each paradigm.

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Paper summary

PyraNet combines spatial filtering, multiscale temporal convolutions, and dataset-level pooling-grid selection for neural decoding. Across eleven datasets, it reports the highest overall mean balanced accuracy and outperforms the evaluated foundation models on eight of nine EEG datasets. The results demonstrate competitive supervised decoding, although improvements over the strongest dataset-specific baselines are uneven and parameter advantages depend on the selected grid and comparator.

Critical strengths

S1. Broad empirical coverage. The evaluation spans multiple decoding paradigms, recording modalities, compact baselines, and foundation models. The competitive aggregate results, together with the ablations and interpretability analyses, constitute a useful empirical study.

Critical weaknesses

W1. Limited scientific contribution beyond empirical recombination. The paper primarily recombines established EEG modeling components and demonstrates dataset-dependent improvements, without establishing a sufficiently substantive new insight into neural decoding. The limited and protocol-dependent advantages of EEG foundation models have already been documented in [1, 2], both cited by the authors. Reproducing this observation with another supervised decoder does not explain the limitations of existing representations or address acquisition heterogeneity, an important obstacle to transferable EEG models. Separate training on each dataset does not resolve that issue. The authors should identify and substantiate what is scientifically learned beyond existing benchmark findings and incremental architectural tuning.

W2. Grid selection (GS) is a configuration-selection procedure, not a new architectural operation. GS evaluates three pooling resolutions using penalized validation loss and retains one fixed configuration. This is conventional validation-based hyperparameter selection. Figure 5(b) confirms that pooling resolution affects performance, while Figure 4 illustrates one case favoring finer resolution. These observations motivate tuning the pooling hyperparameter; they do not establish that performing this tuning constitutes an architectural innovation. The authors should distinguish the selection procedure from the resulting architecture and clarify its claimed methodological novelty. The efficiency framing also requires qualification: in Table 3, grid 128 has 20,548 parameters, including 16,388 in the head, exceeding EEGNet, IFNet, and FBCNet. Being much smaller than foundation models does not establish a consistent parameter advantage over compact decoders.

[1] Yang et al. “Are EEG Foundation Models Worth It? Comparative Evaluation with Traditional Decoders in Diverse BCI Tasks.” ICLR, 2026.

[2] Liu et al. “EEG-FM-Compass: Progress, Benchmarking and Future Directions for EEG Foundation Models.” National Science Review, 2026.

Questions for authors

Q1. Scientific contribution beyond existing findings. What substantive scientific insight does PyraNet establish beyond recombining established components and obtaining dataset-dependent improvements? Given the existing findings in [1, 2], please identify the new explanation or generalizable finding and its supporting evidence. In particular, does the study provide insight into acquisition heterogeneity and transferable representations, or establish only competitive performance after separate training on each dataset?

Q2. Contribution of grid selection. Since GS selects a pooling hyperparameter through penalized validation loss and then fixes the configuration, what methodological novelty is claimed beyond conventional hyperparameter selection? Please distinguish the architecture from its configuration-selection process and explain why the latter warrants a separate scientific contribution. If no additional methodological novelty is intended, please revise the contribution claims accordingly.

5 comments

We wish to thank the reviewer for your time and careful reading of our manuscript. We also appreciate your recognition of the scope of our experiments and the work that went into them. We’d like to clarify the two points you raised and answer the two corresponding questions.

Q1. Scientific contribution beyond existing findings.

Our model design and experiments focused mainly on comparing decoding performance across paradigms. We trained the models separately on each dataset. Our study therefore offers no firm conclusions on acquisition heterogeneity or the transferability of learned representations. Still, we gained some insights that may be useful for transfer learning. To answer your question, we’d like to start by briefly explaining what motivated this work.

EEG foundation models use a range of architectures, and the reasons for particular design choices are not always clear. This led us to ask whether a single architecture could extract useful neural signal features across different paradigms.

Our results suggest two ideas. First, we trained a separate model on each dataset and found that the same encoder design worked well across several paradigms. This makes it a promising candidate backbone for future transfer studies. Second, the appropriate feature aggregation granularity can differ across tasks. A coarse grid worked well on the tested motor-imagery and P300 datasets. On the SSVEP dataset, a finer grid gave much better results. For foundation models that use the same aggregation scheme across paradigms, it may be worth allowing this choice to vary by task.

Q2. Contribution of grid selection.

We agree that the selection step seems 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. If this were simply a routine validation-based tuning, it would be hard to explain why the original IFNet used a fixed aggregation grid instead of tuning it. 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.

Regarding your point about efficiency, we agree that the 128-bin model has more parameters than EEGNet, IFNet, and FBCNet. Across all three grid sizes, PyraNet still has the lowest inference FLOPs in Table 3.

Thank you again for raising these questions. If these clarifications address your concerns, we’d be grateful if you would consider revisiting your score.

Thank you for clarifying the distinction between parameter count and FLOPs.

I particularly appreciate the abstract’s motivation of general-purpose neural decoding with lightweight models. This question should not be replaced by the narrower claim that separately configured and trained models perform well on individual datasets.

I agree that temporal pooling resolution is an important factor affecting accuracy, and the gains from adding GS support this finding. However, GS still selects a resolution separately for each dataset using labeled validation data. For a general-purpose decoder, which configuration should be used when the input’s dataset identity is unknown or ambiguous? This dependence matters for cross-dataset generalization and scaling toward a foundation model. I consider addressing it necessary to support the abstract’s framing, rather than simply a topic for future work.

One possible solution is a shared, input-driven selector over the candidate resolutions, such as an MoE-style router, without dataset identifiers or separate validation-based grid selection. Three stages of evidence would be useful.

  1. Show that the router works when trained and evaluated separately on each dataset.
  2. Train one shared model jointly across datasets and show that it performs well on each.
  3. Train on several datasets and demonstrate generalization to a held-out dataset without dataset-specific grid selection.

The third stage would provide the strongest evidence toward the abstract’s motivation. Positive results from even the first two stages would strengthen the paper, and I would consider raising my score based on such evidence.

AuthorsOpenReview ↗

Response to Stage2 Evaluation

We sincerely thank you for your thoughtful feedback and valuable suggestions. Following your advice, we tested your second proposed stage by jointly training one shared model across four EEG paradigms. We added an input-driven router to PyraNet so that it can select a pooling resolution for each trial without being given its dataset identity.

We used BNCI2014_001 for motor imagery (MI), Nakanishi2015 for SSVEP, BNCI2014_008 for P300, and EEGMAT for mental arithmetic (MA). The shared model predicts directly among their combined 20 classes. No dataset-specific class mask is used at test time.

PyraNet has one shared encoder and three heads with pooling grids of 8, 32, and 128. We train a small MLP router to learns to minimize the expected classification error of the selected head. No target labels are used to train or select it.

We used four-fold cross-validation by subject. Within each dataset, we randomly divided subjects into four groups using seed 42. Each fold held out one group from every dataset for testing. Trials from the remaining subjects were split 80/20 for training and validation. Every subject was tested exactly once, and test subjects were excluded from both training and validation.

We compared PyraNet with EEGNet, IFNet, and EEG-Deformer. Signal amplitudes in all datasets were converted to μV before preprocessing. All models used the same splits, 200 Hz signals, Euclidean alignment (EA), batch size 256, and optimizer settings. Best checkpoints were selected from epoch 1, with early stopping after five epochs without validation improvement. EA was computed separately from each subject's unlabeled trials, including the test subjects. At test time, trials from all four datasets were randomly mixed and evaluated individually with the model and router frozen.

The table reports balanced accuracy (BA, %). For each subject, BA averages recall over the classes in that dataset. Predicting a class from another paradigm counts as an error. We average subjects within each dataset, then give the four datasets equal weight.

MethodMISSVEPP300MAAverage BA
PyraNet with router42.1194.3259.5363.6164.89
EEGNet22.7413.2161.0451.2037.05
IFNet40.5725.4951.1361.6744.71
EEG-Deformer26.7959.261.6950.6534.60

PyraNet achieved the highest average BA, exceeding IFNet by 20.18 percentage points. It performed best on MI, SSVEP, and MA, while EEGNet performed best on P300.

We also measured paradigm prediction accuracy (%) by mapping each predicted class back to its paradigm. A wrong SSVEP frequency, for example, still counts as a correct paradigm prediction. This uses the same predictions and does not introduce a separate classifier. Averaging follows the same subject-then-dataset procedure.

MethodMISSVEPP300MAAverage
PyraNet with router91.6797.84100.0098.9897.12
EEGNet64.0648.70100.0086.6774.86
IFNet100.00100.00100.00100.00100.00
EEG-Deformer65.1478.023.1482.5957.22

IFNet identified every trial's paradigm correctly, but its lower BA reflects errors within paradigms. EEG-Deformer assigned most P300 trials to other paradigms. These comparisons use a common training recipe, not separately optimized settings for each baseline. PyraNet also has three-head supervision and additional router training, so the performance gap cannot be attributed solely to its encoder.

Taken together, these results support PyraNet's ability to learn across EEG paradigms in a shared model and select its pooling resolution from trial features. We warmly thank you again for proposing this evaluation. Following your advice has helped us test the broader applicability of our approach more directly.

Our Stage 3 evaluation is still in progress. Given the limited time, we are sharing the completed Stage 2 results first to help you assess this additional evidence. These results do not yet establish generalization to an unseen dataset.

Reviewer_w8uTOpenReview ↗
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Paper summary

The paper proposes PyraNet, a small supervised network intended to decode several BCI paradigms without per-paradigm redesign. It has three modules: a learned cross-channel linear filter that maps every recording channel into 64 virtual channels; an encoder of four parallel temporal branches, each a grouped and dilated convolution with kernel length five and dilations chosen so the receptive fields span roughly fs/4 down to fs/32; and a dataset-level adaptive grid selector that pools the encoder output to one of three candidate grids (8, 32 or 128 bins) and keeps a linear head of matching size.

The selector is the second contribution. After a shared ten-epoch warm-up in which the encoder and all three heads are trained jointly, one grid is chosen per dataset by minimising a penalty-weighted validation loss, with fixed coefficients (1, 2, 8) applied to the increasingly fine grids; the unused heads are then removed and training continues with the retained one.

Validation covers eleven datasets over five paradigms (motor imagery, P300, SSVEP, mental arithmetic and speech) and three modalities. The nine EEG datasets use leave-one-subject-out, the two speech datasets use leave-one-session-out within each subject, Euclidean alignment is applied per subject or per session, and every experiment is repeated with three seeds. Six compact models and three pretrained EEG foundation models are compared, the foundation models only on the nine EEG datasets. The reported outcome is a mean balanced accuracy of 66.93% and a mean rank of 1.82 over the eleven datasets against 63.82% for the runner-up (EEGNet), and 77.55% over the nine EEG datasets against the strongest foundation model.

Critical strengths

Two things about this paper seem to me worth recording, and I say at the outset what standing they have: they concern the benchmark and the bookkeeping, not the mechanism the paper is built around.

  1. The breadth of the comparison is real. Eleven datasets, three modalities, five paradigms, and three pretrained foundation models run from their public checkpoints under one protocol and the same folds. Whatever one concludes about the architecture, that table is the part of the paper others are likely to reuse, and assembling it is not a small amount of work. Its standing in this review is at the level of the benchmark: it tells me that a small model can be competitive, not why.

  2. The numbers as printed are internally consistent. I recomputed the seven overall averages, the ten rank entries, the three means of the ablation table, the parameter counts at the three grid sizes and the joint warm-up total, and every one of them reproduces from the paper's own cells. That is unusual, and it is the reason no figure below needs hedging. It also locates the disagreement: nothing in this review is about arithmetic, only about what the arithmetic is evidence for.

Neither point touches the question the paper asks, which should be said plainly rather than left for the reader to work out. The benchmark and the bookkeeping would both survive a complete replacement of the encoder, so neither can be used to argue that the encoder is doing the work, and neither is a reason to accept the paper on its own terms. The evaluation and the accounting are sound; the mechanism is not supported. That combination is awkward to revise, because the parts that are sound are the parts that carry the evidence, and the evidence stops short of the claim.

Critical weaknesses

Two considerations drive my recommendation. They are of different kinds, and neither is a matter of wording.

  1. The reported gains are not attributable to the proposed encoder, and the paper's own ablation points at the selector instead.

On the two SSVEP datasets the encoder contributes nothing measurable. Table 4 reports that IFNet with the grid selector reaches 97.10 on Nakanishi2015 with κ 0.9684, identical to PyraNet in both the mean and the reported standard deviation, and 94.71 on Wang2016 against PyraNet's 94.06; only the weighted F1 separates the two rows on Nakanishi2015, at 97.03 against 97.04. These are also the two datasets on which the selector adds most to a baseline backbone, moving IFNet from 76.11 to 97.10 and from 66.92 to 94.71, whereas on the other six it moves by more than four points only once, and downward, taking bouchard2019 from 13.63 to 8.12. Where the selector is doing the work, the encoder is not.

Apart from bouchard2019, the encoder's advantage over IFNet with the selector is small. Table 4's own means are 64.47 for PyraNet and 61.34 for IFNet with the selector; on bouchard2019 the two rows read 26.86 and 8.12, while on the other seven the largest gap is 79.46 against 77.17. A mean whose bulk comes from one 54-class dataset where both numbers sit far below thirty percent is not evidence of a broad architectural advantage, and I do not see a reading of this table that makes it one.

The architecture itself is never ablated, although Section 3.6 carries that title. What that section ablates is the grid selector, through IFNet, and the dilation rate; the only encoder component switched off anywhere in the paper or its appendices is dilation, and Figure 5a reports 53.6 against 53.5, 79.5 against 79.4, 71.8 against 71.8 and 97.1 against 97.0 for dilated versus ordinary convolution, alongside an 82.6%–91.7% reduction in kernel parameters. Appendix G varies the warm-up length, which is a training schedule rather than an architectural component. No condition anywhere removes the cross-channel filters, collapses the four branches to one, or disables grouping. The one component that is tested turns out to be accuracy-neutral, and the components that carry the claim are exactly the ones left untested.

The backbone chosen to isolate the encoder is described as "the strongest baseline among those that can be adapted", but Table 2's own overall averages put EEGNet at 63.82, Deformer at 62.57 and Conformer at 61.85 against IFNet's 60.40, so the reference sits fourth among the six compact models. The difference the ablation attributes to the encoder is therefore measured against a weaker reference than the paper's own results supply.

In short: the encoder is replaceable where the selector contributes most, its residual advantage elsewhere rests on a single dataset, the one component that was tested does not affect accuracy, and the reference it is measured against is not the strongest available. Those four facts point the same way. The first contribution is not established by this evidence, and I do not see a run of the current design that would establish it, because the components the claim rests on are precisely the untested ones, while the one component that was tested has already come back neutral.

  1. The headline aggregate mixes quantities that are not commensurable, and a baseline matches or beats the model on six of its eleven datasets.

The headline mean averages balanced accuracies whose chance level ranges from under 2% on a 54-class task to 50% on the six binary tasks. Under equal weighting a gain on a task where chance is 2% and a gain on a task where chance is 50% enter the same sum. Against EEGNet, the runner-up by overall average, the two numbers read 71.76 against 71.59 on BNCI2014_008, are identical at 74.24 on BNCI2014_004 and at 81.52 on BNCI2014_009, and read 26.86 against 19.09 on bouchard2019. The sentence in the abstract that the model is consistently strong across all eleven datasets, and the claim of a 3.1 point margin over the runner-up, both rest on that sum.

The per-dataset picture does not match that summary. PyraNet is strictly below a baseline on four datasets: BNCI2014_004 at 74.24 against IFNet's 74.47, BNCI2015_001 at 75.03 against 75.37, Wang2016 at 94.06 against Deformer's 94.15, and EEGMAT at 71.20 against IFNet's 75.19. It ties on two more, BNCI2014_008 at 71.76 and BNCI2014_009 at 81.52. On six of the eleven datasets a baseline therefore either matches or exceeds it, which is not what "consistently strong performance across all eleven datasets" describes.

On two of those datasets it is also behind on the paper's own secondary metrics. On BNCI2015_001 IFNet is higher on balanced accuracy (75.37 against 75.03), AUC-PR (84.70 against 83.01) and AUROC (85.19 against 82.99); on EEGMAT PyraNet's AUC-PR of 79.99 sits below FBCNet's 88.34. The balanced accuracy in Table 2 is thus not understating an advantage the stricter metrics would reveal; on these two datasets there is none to reveal.

Nothing quantifies whether any of these differences exceed seed noise. I could not find a confidence interval, a paired test or a multiple-comparison correction anywhere in the paper; the only cross-dataset summaries it reports are the overall average and the overall rank at the foot of Table 2, and neither comes with an interval. Since the ranking is the headline, the absence of the standard test for that protocol is what makes it unusable as evidence rather than merely unpolished.

In short: the aggregate weights chance levels that differ by more than an order of magnitude, a baseline matches or beats the model on six of the eleven datasets, on two of those it is behind on the secondary metrics as well, and no uncertainty is placed on any comparison. The abstract states that sum accurately, and that is precisely what makes it hard to repair: a version of the sentence that the tables could support would have to say that the model is matched or beaten on six of eleven datasets, and that the headline mean averages tasks whose chance levels differ by more than an order of magnitude. That is not tighter writing; it is a different result, and it would cost the paper the number it is built on.

Neither of the two critical weaknesses is settled by rewriting, and together they are what determines my recommendation. The first is not answered by running more of the current design: the ablation that would separate the pyramid from its parts is not among the experiments, and further training on the present architecture would not supply it. The second is not answered by running anything at all, since a chance-normalised or per-paradigm figure would not sit beside 66.93% and the 3.1 point margin; it would replace them. Taken together, the abstract claim has no reading of the paper's own tables that supports it, and I do not see a rewrite producing one.

Questions for authors
  1. Figure 5b marks the selected grid for five of the eleven datasets, and no table records the selection at all; can the authors state the selected grid for each of the eleven?

  2. Table 1 gives 34 participants and 62 retained channels for Wang2016, while the publication that introduced that dataset describes 35 participants and 64 channels; is one participant excluded by the loader, and if so on what basis?

  3. Attaching the grid selector to IFNet raises its mean from 54.93 to 61.34 but lowers bouchard2019 from 13.63 to 8.12; is that reversal understood, and does it bear on how the selector's benefit should be read?

  4. Would the authors report a chance-normalised or per-paradigm aggregate alongside the eleven-dataset mean, together with a multiple-comparison test over the datasets? (suggestion)

3 comments
AuthorsOpenReview ↗

Response to Questions for Authors

Q1. Which pooling grid was selected on each dataset?

DatasetSelected grid
BNCI2014_0018
BNCI2014_0028
BNCI2014_0048
BNCI2015_0018
BNCI2014_0088
BNCI2014_0098
EEGMAT8
Nakanishi2015128
Wang2016128
text-MEG8
Bouchard20198

Q2. Why does Table 1 report 34 participants and 62 EEG channels for Wang2016?

The original dataset contains 35 participants. The official MOABB loader used in our experiments returned 34. MOABB later documented the issue: “S35.mat was never loaded.” MOABB release notes

MOABB also explains: “The original dataset includes two channels labeled ‘CB1’ and ‘CB2’, which are not part of the standard 10-20 EEG montage.” Our loader version labeled both as misc, so selecting EEG channels retained 62 of the 64 recorded channels. MOABB Wang2016 documentation

Q3. Why does IFNet+GS perform worse on Bouchard2019?

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.

Q4. Does the aggregate advantage persist after accounting for chance level?

Thank you for this great suggestion. For each dataset with KK classes, we computed the chance-adjusted balanced accuracy as BA−1/K1−1/K\frac{\mathrm{BA}-1/K}{1-1/K}, where BA\mathrm{BA} is balanced accuracy on the 0–1 scale. We then averaged the adjusted scores across the eleven datasets, giving each dataset equal weight.

ModelMean BA (%)Chance-adjusted mean BA (%)
PyraNet66.9351.84
EEGNet63.8247.50
Conformer61.8544.54
Deformer62.5744.37
IFNet60.4044.20
DBConformer52.8036.51
FBCNet47.2126.42

A Friedman test across the seven models gave p = 0.000099. For PyraNet versus EEGNet, an exact two-sided paired sign-flip test on the eleven raw BA differences gave Holm-adjusted p = 0.0117 across the six comparisons with PyraNet. After chance correction, PyraNet retains the highest mean, 4.34 percentage points above EEGNet.

AuthorsOpenReview ↗

Response to Critical Weaknesses

We sincerely appreciate your time and great effort in reviewing our work and providing valuable feedback. Below, we provide our clarifications and explanations in response to your concerns, and we sincerely hope they help address your questions and provide a better understanding of our work.

W1. Contribution of the encoder and grid selector.

The grid selector (GS) is itself a component of PyraNet. Its contribution therefore counts when assessing the performance of the complete decoder. We agree with the reviewer that GS accounts for much of the improvement on the two SSVEP datasets. This finding helps identify which part of PyraNet contributes to its performance on these tasks.

Regarding the encoder itself, Figure 5(a) directly ablates dilation by replacing the dilated temporal convolutions with ordinary convolutions. The purpose of this experiment was to test whether the multiscale encoder could preserve decoding accuracy while using fewer kernel parameters. Across the four datasets shown, dilation reduced the number of temporal-kernel parameters by 82.6–91.7%, while balanced accuracy differed by at most 0.1 percentage points. Our claim for dilation is therefore one of parameter efficiency.

We chose IFNet for Table 4 because its temporal feature map allowed us to add GS with few changes. To address your question about the choice of backbone, we also added GS to EEGNet, the compact baseline with the highest mean balanced accuracy in Table 2. The table reports balanced accuracy in percent as the mean ±\pm SD across three seeds.

DatasetEEGNetEEGNet + GSPyraNet
BNCI2014-00151.54±1.4451.54 \pm 1.4450.54±0.7950.54 \pm 0.7953.57±0.2653.57 \pm 0.26
BNCI2014-00274.90±0.5374.90 \pm 0.5376.82±0.7276.82 \pm 0.7279.46±0.3879.46 \pm 0.38
BNCI2014-00871.59±0.0771.59 \pm 0.0771.70±0.2971.70 \pm 0.2971.76±0.1271.76 \pm 0.12
BNCI2014-00981.52±0.3981.52 \pm 0.3981.70±0.1281.70 \pm 0.1281.52±0.1481.52 \pm 0.14
Nakanishi201592.88±0.8192.88 \pm 0.8196.46±0.2496.46 \pm 0.2497.10±0.0597.10 \pm 0.05
Wang201690.56±0.1990.56 \pm 0.1994.58±0.0994.58 \pm 0.0994.06±0.0894.06 \pm 0.08
Mean across six datasets77.1778.6379.58

Adding GS to EEGNet improved balanced accuracy by 3.58 percentage points on Nakanishi2015 and 3.20 on Wang2016. On the two P300 datasets the changes were small, and on the two MI datasets the results went in opposite directions. This supports your observation that the pooling grid accounts for much of the SSVEP gain. With GS on both backbones, PyraNet had the higher mean across the six datasets by 0.95 percentage points. Its largest advantage was on BNCI2014-002 (2.64 points), while EEGNet + GS scored higher on Wang2016 (0.52 points) and BNCI2014-009 (0.18 points).

W2. The headline aggregate mixes quantities that are not commensurable, and a baseline matches or beats the model on six of its eleven datasets.

We thank the reviewer for recognizing the scale of our experiments, the range of paradigms covered, and the quality of the reported results. As you know, even state-of-the-art decoders do not outperform all competing models across every task and paradigm. Given your familiarity with the field, we believe you would also agree that the baselines we selected are among the strongest in the field, we did not include weaker models simply to increase the number of comparisons. We took the same approach to dataset selection. As Table 2 shows, PyraNet trails IFNet by 3.99 percentage points on EEGMAT. Although the evaluation would still have been extensive without EEGMAT, we retained it to give an accurate account of where PyraNet performs well and where it falls short. We hope you will appreciate this effort to present a fair comparison.

Although PyraNet does not achieve the highest score on every dataset, the strongest baseline varies across the six datasets you mention. When each compact baseline is compared individually with PyraNet across all eleven datasets, PyraNet achieves a higher mean balanced accuracy in every comparison. We believe this shows that PyraNet remains competitive across diverse paradigms, even as the leading competitor changes.

We also agree that chance levels differ across tasks, which makes the mean balanced accuracy across datasets difficult to interpret. For this reason, Table 2 also reports mean rank. We rank the models within each dataset and then average those ranks across datasets. PyraNet achieves the best mean rank of 1.82. Liu et al. [2] use the same metric to compare decoders across datasets in their benchmark.

[2] Liu et al. “EEG-FM-Compass: Progress, Benchmarking and Future Directions for EEG Foundation Models.” National Science Review, 2026.

We would greatly appreciate it if you could let us know whether our responses have adequately addressed your concerns. If our clarifications have helped resolve your concerns and changed your assessment of the paper, we would be grateful if you would consider adjusting your score accordingly.

AuthorsOpenReview ↗

Additional Ablation Results

In addition, we evaluated the spatial module, the multiscale temporal module, and GS through ablation experiments. Removing GS fixes the aggregation grid at 8 bins.

DatasetFull modelw/o Spatialw/o SpatioTemporalw/o GS (grid 8)
BNCI2014-00153.5751.5825.9653.89
Nakanishi201597.1095.5195.2350.33
EEGMAT71.2064.9450.9370.62
BNCI2014-00871.7671.4067.7171.44

All values are balanced accuracy (%).

The spatial filter has a smaller overall effect, but still provides meaningful gains. It also maps datasets with different input channel counts to a fixed number of feature channels, which simplifies processing in later modules. Removing the spatiotemporal module causes large drops on BNCI2014-001 and EEGMAT. Surprisingly, its effect on the SSVEP dataset is much smaller. In contrast, removing GS sharply reduces SSVEP performance, while its effect on the other datasets is small. Together, these results suggest that the modules play complementary roles. Together, these modules support strong performance when the model is trained separately on each paradigm.

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

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