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Withdrawn from ICLR 2027

EEGAtlas: Adaptive Topology Learning for Generalizable EEG Representation Learning

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Electroencephalography (EEG) supports applications from brain–computer interfaces to sleep monitoring. Generalizable representations are needed to transfer across subjects and paradigms, but informative channel relations vary with neural state. Existing encoders infer these relations from content alone or impose input-invariant spatial priors. EEGAtlas introduces a Dynamic Channel Relation Atlas that derives geometric bases from encoder-slot coordinates and selects a content-conditioned top-2 mixture for each sample and temporal patch, together with a shared relation. The resulting biases augment content attention. A Spatial–Temporal–Feature Alternating Block integrates this mechanism with temporal aggregation and token-wise feature transformation. Across five subject-independent frozen-probe tasks spanning event-related potentials, motor imagery, and sleep staging, EEGAtlas outperforms pretrained REVE, LaBraM, EEGPT, and CBraMod on Balanced Accuracy, Cohen's Kappa, and task-specific F1 or AUROC. Its Balanced Accuracy gains average 2.53 percentage points over the strongest task-wise baselines and reach 3.43 points on BCIC-2A. Dynamic relations also outperform static geometric relations in all three evaluated ablations, supporting content-conditioned spatial modeling. Code is available at https://anonymous.4open.science/r/EEGAtlas-ICLR2027.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG, EEG Representation Learning, EEG Foundation Model, PMoE, EEG Classification

Reviews

Among:
Shape:
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_5S1qOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes EEGAtlas, a pretrained EEG encoder centered on a Dynamic Channel Relation Atlas. The atlas constructs pairwise relation bases from electrode coordinates and selects a content-conditioned top-2 mixture for each sample and temporal patch. The resulting biases augment spatial attention. The encoder combines this mechanism with same-channel temporal attention and Progressive MoE, and is pretrained using latent prediction and waveform reconstruction. Evaluation covers five subject-independent tasks with frozen encoders. The paper reports an average Balanced Accuracy improvement of 2.53 percentage points over the strongest task-wise baselines. Dynamic, static, and content-only ablations examine the contribution of adaptive relation modeling.

Critical strengths
  1. The central mechanism addresses a concrete modeling question. The paper distinguishes a stable geometric scaffold from sample-dependent communication between channels. Routing over coordinate-derived relation bases is a specific and understandable way to implement this distinction while retaining ordinary content attention. This gives the method a clearer contribution than simply adding channel coordinates or additional feature experts to an EEG encoder.

  2. The main ablation directly tests adaptive relation selection. Table 3 compares Dynamic Relation with an input-invariant mixture of the same bases and with Content-only attention. Dynamic Relation improves Balanced Accuracy over Static Relation by 0.92, 1.51, and 0.82 percentage points on PhysioP300, BCIC-2A, and SleepEDF, respectively. The consistent ordering across three paradigms supports the proposed mechanism. The broader five-task evaluation also reports consistent gains over several established pretrained EEG models.

Critical weaknesses
  1. The reported Kappa values cannot be reconciled with the stated motor-imagery evaluation protocol. Appendix A.2 states that BCIC-2B uses 400 trials per participant from the first three sessions. The official dataset description specifies equal left- and right-hand trial counts in these sessions. For the same predictions on these balanced binary test sets, Cohen’s Kappa must satisfy �0��0�. This relationship also holds when both metrics are averaged over the same balanced subject folds and seeds. Several Table 2 entries violate this relationship. These differences exceed rounding error. Trial exclusion, different prediction sets, or different aggregation procedures could explain them, but none is documented. The manuscript also does not define the reported “±” statistic. These issues prevent verification that the compared metrics come from a common evaluation procedure.
  2. The claimed matching of the frozen-probe comparisons is insufficiently specified. Section 3.3 states that the baselines use documented checkpoints and matched probe capacity, but the exact checkpoint variants and baseline-specific feature readouts are not identified. Table B5 provides a single projection and head configuration, including a four-layer decoder for SleepEDF, without explaining how each baseline’s differently structured outputs are mapped into this setup. Trainable adapter and head sizes, and the downstream checkpoint-selection rule, are also unspecified. These choices matter because frozen-encoder performance depends on the readout and adaptation procedure. The reported gains are promising, but the available description does not establish that each pretrained model received a comparable evaluation.
Questions for authors
  1. Clarification of the reported metrics.

Can the authors reconcile the BCIC-2B Balanced Accuracy and Kappa values using the same held-out prediction files? Please specify retained class counts, any trial rejection, whether the metrics use the same checkpoints and decision rules, the aggregation order, and the meaning of “±”.

  1. Clarification of baseline evaluation.

Which exact pretrained checkpoints were used? Please provide each model’s feature readout, input adapter, trainable head size, and validation/checkpoint-selection rule. Were these choices fixed or selected using training-subject validation data?

  1. Clarification of the main controls.

In Table 3, are the Static Relation mixture coefficients learned or fixed? Does it retain the shared relation and learned scale? Is the sigmoid attention-output gate in Equation (5) identical across Content-only, Static Relation, and Dynamic Relation? These details determine whether the comparison isolates adaptive geometric routing.

  1. Positioning relative to NeurIPT.

NeurIPT already introduced an EEG Progressive MoE with sparse token routing, a shared expert, and an expert count that increases with depth, alongside temporal and spatial attention. How does the auxiliary architecture here differ from that predecessor, and which components should be attributed to it? The distinction is relevant to assessing the contribution of the complete architecture alongside the proposed relation atlas.

Reviewer_5ZpYOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper introduces EEGAtlas, a foundation model for generalizable EEG representation learning across heterogeneous montages. Within an Alternating Block, EEGAtlas combines a shared static geometric relation bias from pairwise 3D 10–20 slot coordinates ϕij∈R5\phi_{ij} \in \mathbb{R}^5 with a Dynamic Channel Relation Atlas routing top-2 mixtures of four relation kernels per patch via router weights gbng_{bn} (Section 2.1.1, Eq. 2–5). Pretrained with I-JEPA-style latent prediction and MAE waveform reconstruction on five corpora totaling 385 subjects standardized to 58 canonical slots—SEED, M3CV, THU, PhysioNet-MI, and an in-house Cue-Reactivity cohort (Table 1)—the model is evaluated with frozen probes across five benchmarks: PhysioP300, KaggleERN, BCIC-2A, BCIC-2B, and SleepEDF (Table 1; Table 2).

Critical strengths
  1. Multi-Paradigm Pretraining Suite and Empirical Gains Across Five Benchmarks (Section 3.1, Table 1; Section 3.4, Table 2): Standardized to 58 slots across 385 subjects, EEGAtlas achieves the highest Balanced Accuracy across five frozen-probe benchmarks (+2.53 pp mean gain over strongest baselines), led by 22-channel BCIC-2A at 0.5208±0.0031 vs. REVE 0.4865±0.0058 Balanced Accuracy (+3.43 pp; three fixed seeds, non-overlapping ± ranges) and 0.5066±0.0063 vs. REVE 0.4692±0.0017 weighted F1 (+3.74 pp).
  2. Modular Alternating Block Architecture (Section 2.1, Figure 1): Decoupling spatial relation routing (RelationAttn, Eq. 2–5) from temporal modeling (GroupAttention, Section 2.1.2) and token-level mixture of experts (PMoE, Section 2.1.3) maintains clean tractability over variable visible channel subsets during masked pretraining.
Critical weaknesses
  1. Interpretability of Scalp Geometry on 2-Channel SleepEDF and Unclear Link Between Dynamic Relation Modulation and Ablation Gains (Section 2.1.1 Eq. 3–5 Section 3.3, Section 3.5 Table 3, Section 3.6 Figure 4a, Appendix A.2 Table B2):
  • 2-Channel Virtual Geometry on SleepEDF: The SleepEDF setup retains only two bipolar EEG derivations (Fpz–Cz and Pz–Oz). Appendix A.2 states that the adaptive filter "performs learned channel alignment rather than anatomical channel reconstruction" and that the 13 slots produced by the 2 -> 13 filter are "learned mixtures of the two recorded derivations". Because the geometric relation bases are built from the standard 10–20 coordinates attached to these 13 slots (Eq. 2), and a 1×11 \times 1 filter yields at most rank-2 linear mixtures, the geometric prior is hard to interpret on SleepEDF. It is therefore unclear how the SleepEDF row supports the conclusion in Section 3.5 that "This consistent ordering supports both the geometric prior and its content-conditioned selection,".
  • Link Between Dynamic Relation Modulation and the Ablation Gain: In Table 3, Dynamic Relation adds +0.92, +1.51, and +0.82 pp over Static Relation on PhysioP300, BCIC-2A, and SleepEDF (0.6841 vs 0.6749, 0.5208 vs 0.5057, 0.6706 vs 0.6624; Static exceeds Content-only by +0.81, +1.21, +0.63 pp). The analysis offered for the dynamic term, Figure 4(a) (Section 3.6), shows Layer 4 relation-logit biases on BCIC-2A that are averaged over heads, temporal patches, and held-out subjects and centered by the class-pooled bias; the resulting deviations are displayed on a color scale of about ±0.0002\pm 0.0002. A logit change of that size would rescale an unnormalized attention weight by exp⁡(±0.0002)≈1±0.0002\exp(\pm 0.0002) \approx 1 \pm 0.0002, i.e., about 0.02% (relative). However, because Figure 4(a) is an averaged and centered summary, it does not bound the per-sample or per-patch magnitude of Δij=ρ∑k=14gbnkBijhk\Delta_{ij} = \rho \sum_{k=1}^4 g_{bnk} B_{ijh}^k, and Figure 4(b) reports only a relative class-separation measure. The reported summary statistics therefore do not show how the dynamic term could account for the +1.51 pp gain; since the Table 3 variants appear to be separately pretrained ("All other pretraining and evaluation settings are matched"), the gain could also reflect effects of routing during pretraining rather than inference-time modulation. Raw uncentered distributions of the dynamic term and a g=0g = 0 (routed term removed) inference ablation would clarify this.
  • Positioning Against Related Work & Incremental Novelty: The components are closely related to existing lines of work. Electrode-coordinate-aware positional encoding is already used by REVE (cited in Section 1); attention-logit biases computed from pairwise structural features are central to Graphormer (Ying et al., NeurIPS 2021), which is not discussed; learnable electrode-relation graphs (DGCNN, RGNN) are cited and contrasted in Section 1, but EEG graph models such as LGGNet are not discussed, nor is cross-montage EEG tokenization such as BIOT (Yang et al., NeurIPS 2023). A more explicit comparison against these approaches would clarify what is new beyond their combination.
  1. Incomplete Ablation Coverage (Section 3.5, Tables 3 & 4), plus Minor Points that do not drive my rating (Section 3.3, Appendix A.1, Appendix B.2 Table B5, Ethics Statement):
  • Omission of KaggleERN and BCIC-2B from Ablations: Tables 3 and 4 report ablations only on PhysioP300, BCIC-2A, and SleepEDF. On BCIC-2B, Table 2 shows that the margins over the strongest baselines in Cohen's Kappa (0.4623±0.0015 vs. LaBraM 0.4606±0.0065; 0.0017) and AUROC (0.8137±0.0047 vs. EEGPT 0.8122±0.0057; 0.0015) lie within the baselines' reported ± ranges over three seeds (the paper does not state whether ± denotes SD or SE) and are small, as the authors note ("The margins in Kappa and AUROC on BCIC-2B are small, but all three metrics remain highest."), making full 5-benchmark ablations essential.
  • Minor: Cross-Task Probe Capacity Asymmetry on SleepEDF: While baselines share matched probes within tasks (Section 3.3), Appendix B.2 Table B5 reveals cross-task asymmetry: PhysioP300, KaggleERN, BCIC-2A, and BCIC-2B use linear heads (Flatten-> 2 or Flatten-> 4), whereas 2-channel SleepEDF employs a non-linear 4-layer decoder (20 epochs, batch size 12; 20 / 12), raising the question of whether the MLP compensates for 13-slot virtual projection distortion (2 -> 13).
  • Minor: Sample-Level Pretraining Validation Split & Boundary Conditions: Pretraining validation sets for SEED, M3CV, THU, and PhysioNet-MI use a random sample-level 0.9/0.1 split (Appendix A.1: "prepared samples were assigned independently to the training or validation partition with probabilities 0.9 and 0.1") rather than subject-wise partitioning, so samples from the same subjects and recordings can fall in both partitions; this risks making the validation loss in Figure B1 optimistic as an indicator of generalization to unseen subjects. Moreover, 120 of 385 pretraining subjects come from an unreleased Cue-Reactivity cohort (Ethics Statement: "The recordings were used only for self-supervised pretraining and are not released with this paper.") without a public-only ablation, and the paper omits a dedicated Limitations section on sparse-montage failure modes and compute overhead (Section 4).

Score rationale

Presentation (2). Figures (Figure 1) and text (Section 3.1) are clear. Presentation is rated 2 because: (1) Figure 4(a) reports only head-, patch-, and subject-averaged, class-centered Layer 4 bias deviations (color scale about ±0.0002\pm 0.0002), without raw magnitudes that would connect the routing analysis to the Table 3 gains; (2) Appendix A.2 states that the SleepEDF slots are learned channel alignment rather than anatomical reconstruction, while Section 3.5 reads the ablation ordering, including SleepEDF, as support for the geometric prior; and (3) a Limitations section is omitted (Section 4).

Informativeness (2). Standardizing EEG corpora into a 58-slot encoder with consistent frozen-probe gains across five benchmarks (Table 2; +3.43 pp on BCIC-2A over REVE) is practically useful. However, informativeness is rated 2 (Fair) because the core components read as an incremental synthesis of related work: coordinate-aware positional encoding (REVE, cited), attention-logit biases from pairwise structural features (Graphormer, Ying et al., NeurIPS 2021, not discussed), and learnable or dynamic electrode-relation graphs (DGCNN and RGNN, cited; LGGNet, not discussed), with cross-montage EEG tokenization such as BIOT (Yang et al., NeurIPS 2023) also not discussed. Furthermore, the reported analyses (averaged, class-centered Layer 4 deviations of about ±0.0002\pm 0.0002 in Figure 4a) do not show how large the dynamic routing term is in practice.

Soundness (2). Soundness is rated 2 due to: (1) attaching standard 10–20 scalp coordinates to learned (at most rank-2) mixtures of two derivations on SleepEDF, which makes the geometric prior hard to interpret there (Appendix A.2); (2) the dynamic-relation analysis (averaged, class-centered Layer 4 deviations of about ±0.0002\pm 0.0002 in Figure 4(a)) does not show how the dynamic term accounts for the +1.51 pp Table 3 gain; and (3) omission of KaggleERN/BCIC-2B from the ablations (Tables 3–4).

Rating (2). Weak rejection is recommended because: (1) on SleepEDF, the 13 encoder slots are learned mixtures of two derivations (Appendix A.2), so the 10–20 coordinates attached to them make the geometric prior hard to interpret, yet the SleepEDF ablation is used to support that prior (Section 3.5); (2) the reported dynamic-relation analysis (averaged, class-centered deviations of about ±0.0002\pm 0.0002 in Figure 4(a)) does not show that the dynamic term drives the +1.51 pp BCIC-2A gain in Table 3; (3) the relation and component ablations omit KaggleERN and BCIC-2B (Tables 3–4); and (4) positioning against closely related work (Graphormer-style attention biases, LGGNet, BIOT) is incomplete. The minor points (the SleepEDF decoder head, the sample-level pretraining validation split, and the private pretraining cohort) do not drive this rating. A linear-probe SleepEDF result, complete five-task ablations, and raw uncentered dynamic-bias distributions with a g=0g = 0 ablation would warrant reconsideration.

Questions for authors
  1. [clarification] Raw Dynamic Relation Bias Magnitude vs. Table 3 Gain: Figure 4(a) shows Layer 4 deviations that are averaged over heads, patches, and subjects and centered by the class-pooled bias (color scale about ±0.0002\pm 0.0002); this summary does not indicate how large the dynamic term is for individual samples and patches, or how it could account for the +1.51 pp BCIC-2A gain in Table 3. What is the raw, uncentered per-sample/per-patch distribution of ∣ρ∑k=14gbnkBijhk∣|\rho \sum_{k=1}^4 g_{bnk} B_{ijh}^k| across the relation-enabled Layers 1–6, and what is downstream performance when the routed term is removed at inference (gbnk=0g_{bnk} = 0)?
  2. [clarification] Biophysical Basis for SleepEDF Virtual Geometry: How do authors justify assigning 13 standard 10–20 3D coordinates to rank-2 linear mixtures of two bipolar derivations on SleepEDF (Appendix A.2 Table B2), and how should the SleepEDF ablation ordering be read as support for the geometric prior (Section 3.5), given that Appendix A.2 describes these slots as learned channel alignment rather than anatomical reconstruction?
  3. [clarification] Linear-Probe Control on SleepEDF: Given within-task probe parity (Section 3.3) but cross-task use of a 4-layer decoder on SleepEDF vs. linear heads on the other four tasks (Table B5), what are SleepEDF results under a linear Flatten-> 5 probe, and does the MLP compensate for 13-slot virtual projection distortion?
  4. [clarification] Complete 5-Dataset Ablations: Please report Table 3 and Table 4 ablations on KaggleERN and BCIC-2B.
  5. [future work] Subject-Wise Pretraining Partitioning and Public Pretraining: How do validation curves (Figure B1) and transfer change under subject-wise validation splits (Appendix A.1) and without the unreleased 120-subject Cue-Reactivity cohort?
Reviewer_9GoQOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

EEGAtlas is an EEG representation method that combines standard content attention with spatial relation patterns whose mixture adapts to each input. Its contribution lies in using adaptive spatial structure to learn transferable EEG representations.

Critical strengths
  1. The method clearly defines what changes with the input and what remains shared, adding a content-conditioned mixture of geometric relation bases to content attention as an adaptive spatial bias. Controlled comparisons among dynamic relations, static relations, and content-only attention within the same framework provide meaningful support for this adaptive design. See Section 2.1 and Tables 3–4.

  2. The evaluation spans multiple EEG paradigms, and the class-balanced relation analyses incorporate participant-aware aggregation and resampling. These analyses provide useful descriptive observations of content-dependent routing across participants. See Table 2 and Section 3.6.

Critical weaknesses
  1. The controls do not yet establish what the geometric structure contributes beyond a general conditional attention bias (Table 3). The comparison of dynamic and static relations supports adaptation, and the comparison of static relations and content-only attention supports adding a relation bias. Neither comparison tests a dynamic bias with comparable capacity but without meaningful spatial alignment. A matched dynamic-bias control without meaningful spatial alignment, such as a controlled coordinate permutation, would help identify what is specifically geometric about the benefit. The analyses in Section 3.6 establish that the routing biases vary with class, but do not explain which changes in relative attention contribute to the prediction gains. A router reading discriminative input can produce class-dependent maps without those maps explaining the improvement. A limited analysis connecting altered routing or relative channel weights to predictions would make the explanation more convincing.

  2. The reliability of the transfer gains across participants is also unclear (Tables 2–3 and B5). While participant-aware uncertainty is supplied for relation-map separation, that is a different quantity from accuracy gains. The performance summaries do not clearly explain how uncertainty is aggregated across random seeds, held-out participants, and repeated training folds, or whether paired gains occur across participants rather than a few individuals. Repeating initialization does not establish population-level uncertainty, particularly when training folds reuse the same evaluation population or when a sleep-task result uses a small participant subset; the existing predictions could instead be used to report paired participant-level gains and their uncertainty. Finally, the supplementary code saves checkpoints using evaluation-participant metrics, but the manuscript does not establish whether those checkpoints generated the reported results. If they did, the comparisons need to be reassessed using checkpoint selection independent of the evaluation labels.

Questions for authors
  1. What evidence separates the benefit of meaningful electrode geometry from generic conditional bias capacity, and can a control retain the dynamic mixture and comparable capacity while disrupting meaningful spatial alignment?

  2. How are the content-dependent relation patterns linked to prediction quality beyond class association, for example under a limited routing intervention or an analysis of relative attention weights?

  3. How are the reported performance uncertainties aggregated across random seeds, held-out participants, and training folds sharing an evaluation population, and do paired improvements hold consistently across the held-out participants?

  4. Which checkpoint selection rule generated the main results, was it independent of evaluation labels, and do the conclusions hold under independent selection if evaluation-selected checkpoints were used?

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