acceptodds
Under review as a conference paper at ICLR 2027

No Single Recipe for EEG: Phase, Task Regime, and Data Budget Interact

Abstract

For designers of electroencephalography (EEG) foundation models, input choice depends on the target task and available labeled-data budget. We compare raw patches, Morlet log power, and complex coefficients on P300 and N170 event- related potential tasks and one-second sleep-segment classification across five labeled-subject counts and three seeds. We hold the transformer body, subject splits, epochs, and optimization schedule fixed; only the front end varies. Token counts and compute costs differ. On the ERP composite, raw patches outperform fixed Morlet log power throughout the tested range, with a 0.09–0.12 balanced-accuracy advantage after matching normalization scope. Matching token count and per-example compute in both directions retains the log-power advantage at 20 and 40 subjects; the advantage diminishes at larger counts. Complex coefficients from the same filterbank reduce the evoked deficit. In the ERP composite, the largest decomposition contrast is per-trial, per-frequency phase rotation: removing it improves balanced accuracy by 0.12–0.20. Frame averaging changes ERP-composite accuracy by at most about 0.006 at the same output rate. The rotation preserves pre-normalization magnitudes but changes eventalignment and cross-frequency relationships. A tested convolutional spectral embedding does not remove the evoked deficit. With native-target masked pretraining, raw gains more over scratch than complex inputs, although the arms predict different targets.Under a shared target, the six-seed experiment establishes neither a directional advantage nor equivalence between their gains.

Primary area:
learning on time series and dynamical systems
Keywords:
Electroencephalography, Signal Representation, Time–frequency Representation, Biosignals, Event-Related Potentials, Data Scaling

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_b2VsOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper compares three EEG front ends, raw patches, Morlet log power and complex Morlet coefficients, feeding the same small transformer trained from scratch. It covers P300 and N170 ERP tasks and one-second sleep segments at five training subject counts from 20 to 240. Raw beats log power on ERPs by 0.09 to 0.12 balanced accuracy, complex coefficients recover much of that gap, and log power helps on sleep only at small subject counts.

Critical strengths
  1. The study is carefully controlled and unusually honest. The transformer body, splits and schedule are fixed, and the authors add the controls a skeptical reader would ask for, including normalization scope in both directions, token and compute matching for sleep, a six-channel ERP control and a capacity-matched convolution. Failed hypotheses, a falsified mechanism and corrected analyses are all reported rather than hidden, which I appreciate.
  2. The results give practical guidance. On both ERP tasks raw patches beat fixed log power at every subject count, and keeping complex coefficients recovers a median of 72 percent of that gap. Rotating phase per trial and frequency costs 0.12 to 0.20 balanced accuracy. Together with the sleep result, this supports the main message that the best input depends on task and data budget.
Critical weaknesses
  1. The scope is too narrow for a framing aimed at foundation model designers. Everything uses a 0.8M-parameter, four-layer transformer trained from scratch, with a two-point learning rate grid and three seeds. The pretraining experiments end without a conclusion, and sleep uses one-second windows rather than standard 30-second staging. It is unclear whether any of the rankings would hold for large pretrained models or standard benchmarks.
  2. The main mechanistic result is hard to interpret. The per-trial phase rotation changes event alignment and cross-frequency relationships at once, and its angle is a hash of the epoch content, with label independence checked on only three people. That breaking phase locking hurts ERP decoding is also expected from ERP physiology. Separate interventions that change only alignment, such as a time shift, or only cross-frequency structure would make this result far more informative.
  3. The paper is very hard to read. The main text leans on claim codes, registered readings and appendix pointers, and many key numbers sit only in the 37-page appendix. The preregistration is internal, several readings were amended after results or after an earlier review, and the code and evidence archive are private, so reviewers cannot check the provenance the paper relies on. A shorter main text built around three or four findings would help greatly.
Questions for authors

see weaknesses.

Reviewer_6MgPOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

The paper investigates which input representation an EEG transformer should use for a given task and labeled-data budget (i.e., the number of labeled subjects available for training), framing its findings as guidance for EEG foundation models. The authors compare raw EEG patches, Morlet log-power, and complex coefficients on P300, N170, and one-second sleep-segment classification across five labeled-subject budgets. Using a fixed transformer architecture (~0.8M parameters) and training protocol, they additionally investigate normalization, computation, phase manipulation, and spectral embedding.

The results report that raw inputs outperform log-power on the ERP tasks, while retaining complex coefficients minimizes that gap. Moreover, they report that log-power provides an advantage for sleep-segment classification at smaller subject counts.

Critical strengths
  1. The paper addresses an interesting question concerning EEG input representations and their dependence on downstream tasks and labeled-data availability.

  2. The authors keep the transformer architecture, subject splits, training schedule, and model-selection procedure consistent, with parameter counts differing by less than 0.7% across the main input variants. (However, it is not clear whether they convergence, which would affect results and the soundness of the approach)

Critical weaknesses
  1. Presentation and clarity

The paper is extremely dense and difficult to follow. For example, it introduces numerous representation names (R, M, M-phi, M-sub, M-phi-scram, etc.), “claim identifiers” (C1–C19), “experiment identifiers” (E01–E16), and decision labels (e.g., E4- NULL, SURVIVES). The representation names are introduced in Section 3, but the claim and experiment identifiers are defined only in the “claim ledger” (S1) and “evidence index” (S7) in the appendix.” For example, the pretraining results in §4.4 are presented through multiple internal identifiers and decision labels (C4-E3, E12, C4-E4, E16, E4-NULL), although the central conclusion seems to be that raw inputs gain more from pretraining than complex coefficients when each model reconstructs its own input. Given the stated goal of providing guidance to EEG foundation-model researchers, the paper would benefit from a substantially clear presentation of its principal comparisons, findings, and limitations.

  1. Limited evidence supporting the claimed relevance to EEG foundation models

The paper presents its findings as guidance for EEG foundation models, but its main representation comparisons use a single 0.8M-parameter transformer trained from scratch with at most 204 training subjects. The supplementary pretraining experiments use 230 subjects and 111,566 one-second epochs (approximately 31 hours of summed segment duration). In contrast, established EEG foundation models are larger in parameter size and have been pretrained on substantially larger datasets (e.g., approximately 2,500 hours for LaBraM (Jiang et al., 2024), over 9,000 hours for CBraMod (Wang et al., 2025), and more than 60,000 hours for REVE (El Ouahidi et al., 2025)). While a small backbone is appropriate for controlled experiments, there is no evaluation across backbone sizes or larger pretraining scales Consequently, the relationship between the controlled results and the foundation-model setting motivating the paper remains insufficiently established.

  1. Limited insight relative to prior EEG research

The paper's main observation, that EEG representation performance depends on the task and available labeled data, has already been explored in prior work. For example, XSleepNet (Phan et al., 2022) investigated how raw and time-frequency representations perform under different dataset sizes and architectures, while Haghayegh et al. (2023) directly compared raw and spectral inputs for sleep staging. Although the controlled transformer comparisons across subject counts could be a useful methodological contribution, it remains unclear what new insight they establish beyond these earlier findings. The study provides additional evidence within a very particular experimental setup which is not motivated adequately.

References

  1. Phan, H., et al. (2022). XSleepNet: Multi-View Sequential Model for Automatic Sleep Staging. IEEE Transactions on Pattern Analysis and Machine Intelligence, 44(9), 5903–5915.
  2. Haghayegh, S., et al. (2023). Automated Sleep Stages Classification Using Convolutional Neural Network From Raw and Time-Frequency Electroencephalogram Signals: Systematic Evaluation Study. Journal of Medical Internet Research, 25, e40211.
  3. Jiang, W., Zhao, L., & Lu, B. (2024). Large Brain Model for Learning Generic Representations with Tremendous EEG Data in BCI. ICLR 2024.
  4. Wang, J., et al. (2025). CBraMod: A Criss-Cross Brain Foundation Model for EEG Decoding. ICLR 2025.
  5. El Ouahidi, Y., et al. (2025). REVE: A Foundation Model for EEG—Adapting to Any Setup with Large-Scale Pretraining on 25,000 Subjects. NeurIPS 2025.
Questions for authors
  1. Have all input representations converged under the fixed setup? How sensitive are the results to longer training, given that larger subject budgets also receive more optimization steps?

  2. What specific new insights do the controlled experiments establish beyond earlier raw-versus-spectral EEG comparisons and existing foundation-model benchmarks?

  3. What motivates the choice of a single small transformer and relatively limited pretraining size? What evidence supports generalizing these findings as guidance for larger, extensively pretrained EEG foundation models?

  4. Could the authors provide a table of absolute balanced accuracies for each input representation and task, particularly sleep? The paper primarily reports differences between representations, while absolute ERP performance is shown only in an appendix figure. This makes it difficult to assess the competitiveness of the models relative to established task-specific architectures.

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

This paper conducts a controlled comparison of raw waveform patches, Morlet log power, and complex Morlet coefficients for two ERP tasks (P300 and N170) and one-second sleep-segment classification. Across labeled-data budgets of 20–240 subjects, the study fixes the Transformer body, subject splits, training schedule, and model-selection protocol, and supplements the primary grid with controls for token count, per-example computation, normalization scope, spectral embedding, phase rotation, and pretraining target. Raw patches outperform log power by approximately 0.09–0.12 balanced accuracy on the ERP composite, whereas log power has a small advantage for sleep at low subject counts that diminishes with more data. Complex coefficients recover much of the ERP deficit, and a per-trial, per-frequency rotation produces the largest change in the paper’s partial decomposition, although the authors appropriately note that this intervention changes both event alignment and cross-frequency relationships.

Critical strengths
  1. The experimental reasoning is unusually careful and transparent. The paper distinguishes matched training schedules from matched computation, defines the interpretation licensed by each contrast, reports failed predictions, and explicitly limits null findings that do not establish equivalence. The correction for dependence among evaluation participants and the separation of conditional subject uncertainty from seed variability further strengthen the presentation.

  2. The study includes a thoughtful set of targeted controls. Bidirectional normalization-scope controls, token/compute matching in both directions, convolutional embedding variants, frequency permutation, learned envelope filters, phase perturbation, and native-versus-common pretraining targets address many obvious alternative explanations. The resulting conclusions are substantially more nuanced than a simple raw-versus-spectral ranking.

  3. The findings are practically informative. The persistence of the ERP gap, the task-dependent sleep behavior, and the partial recovery obtained from complex coefficients provide useful evidence that representation choice should depend on task regime and labeled-data budget. The paper’s willingness to withdraw a broader architectural prescription after the relevant test failed is scientifically commendable.

Critical weaknesses
  1. The external validity is narrow relative to the paper’s framing. The evidence comes from two closely related ERP paradigms and a nonstandard one-second sleep task, using a small approximately 0.8M-parameter Transformer and primarily supervised training from scratch. It remains unclear whether the same ranking holds for motor imagery, pathology detection, longer sleep context, larger backbones, or modern large-scale EEG pretraining. The implications for EEG foundation-model design should therefore be stated as hypotheses supported by these specific regimes rather than as general guidance.

  2. Several central contrasts remain only partially identified. The primary grid gives the spectral arms substantially more computation, while the compute-matched sleep controls necessarily change spectral averaging resolution or raw patch length. The normalization controls match scope but not the statistics themselves. Most importantly, the phase-rotation intervention changes event alignment, cross-frequency relations, and subsequent coordinate-wise normalization together; the large effect demonstrates sensitivity to that intervention but does not isolate “phase” as a single causal factor.

  3. The uncertainty analysis does not cover the full variation relevant to several claims. Most primary experiments use only three fitted seeds, and the reported person-level intervals condition on the selected training draws and fitted models. They therefore omit optimization randomness and variation from resampling the training cohort; this is especially consequential because several complex-input fits collapse and some sleep gaps are smaller than the observed seed spread. The intervals are also pointwise, with no multiplicity control across the many arms, budgets, and outcomes.

Questions for authors

See Weaknesses.

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