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EpiTAR-Bench: Benchmarking Transferability, Adaptation, and Reliability of Epilepsy Models

Abstract

Automated seizure analysis increasingly relies on deep learning and EEG foundation models, yet their transferability, adaptation, and reliability under heterogeneous recording conditions remain poorly characterized. In this paper, we introduce EpiTAR-Bench, a unified benchmark for the Transferability, Adaptation, and Reliability of epilepsy models across seizure detection and prediction. EpiTAR-Bench spans five datasets, seven transfer directions covering cross-dataset, cross-modality, and cross-time shifts, sixteen models from four families, two window lengths, and five levels of target supervision. We further present RIVER, a transfer-specific model designed for partially observed and heterogeneous electrode configurations. Across zero-shot cross-dataset transfer, EEG foundation models form the strongest baseline family, while longer window lengths provide no consistent advantage. Adaptation gains are concentrated at lower target supervision levels for both cross-dataset tasks and cross-modality detection (p ≤ 0.0004 after Holm correction), whereas cross-modality prediction shows a positive but nonsignificant contrast (p = 0.1605) and cross-time transfer shows no comparable pattern. For seizure detection, scalp EEG transfer followed by target iEEG supervision narrows the gap to direct iEEG training, while prediction retains a larger residual gap. Finally, discrimination, calibration, and seizure onset zone (SOZ) evidence are not consistently aligned. These results establish EpiTAR-Bench as a systematic framework for evaluating how epilepsy models transfer, adapt, and remain reliable across heterogeneous EEG settings.

Primary area:
applications to neuroscience & cognitive science
Keywords:
epilepsy AI, EEG benchmarking, seizure detection, seizure prediction, transfer learning, cross-modality transfer, model reliability, domain adaptation

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
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Paper summary

This paper introduces EpiTAR-Bench, a benchmark for evaluating the transferability, adaptation, and reliability of epilepsy models across heterogeneous EEG and intracranial EEG (iEEG) settings. The benchmark covers five datasets, seven transfer directions involving cross-dataset, cross-modality, and cross-time shifts, 16 models from different families, two input window lengths, and five levels of target-domain supervision. The evaluation includes both seizure detection and seizure prediction.

The authors additionally propose RIVER, a model designed to handle heterogeneous electrode configurations through Observability-Aware Partial Transport (OAPT), which uses state-conditioned unbalanced optimal transport to construct shared latent representations.

Experimental results examine the generalization of EEG foundation models, the performance recovery achieved through target-domain adaptation, the influence of input window length, and the relationships among discrimination, calibration, and SOZ evidence. The findings highlight the dependence of transfer performance on specific tasks, transfer settings, and supervision levels.

Critical strengths

S1. An important and clinically relevant research problem.

EEG is a major modality for clinical epilepsy monitoring, while differences in recording conditions, patient populations, and electrode configurations present substantial challenges for model generalization. The paper discusses these practical issues through a unified benchmark spanning scalp EEG and iEEG, including both seizure detection and prediction. The study is relevant to understanding how existing models perform under heterogeneous clinical recording conditions.

S2. Comprehensive experimental settings and systematic evaluation.

The benchmark evaluates a relatively broad collection of models across multiple transfer settings, window lengths, and target supervision levels. The authors also provide extensive experimental results and employ paired statistical tests with multiple-comparison corrections. These efforts contribute to a systematic characterization of model performance and adaptation behavior under different evaluation conditions.

S3. Meaningful evaluation of window length sensitivity and clinically relevant evidence.

Beyond conventional classification metrics, the paper examines the influence of longer input windows, probability calibration, and spatial evidence associated with the seizure onset zone. In particular, the SOZ analysis provides an additional perspective on the relationship between classification performance and clinically relevant spatial information. These evaluation dimensions are valuable for understanding the behavior and limitations of epilepsy monitoring models.

S4. A reasonable and potentially useful design for heterogeneous electrode modeling.

RIVER introduces a state-conditioned unbalanced optimal transport mechanism to accommodate variable electrode configurations and partially observed signals. The use of transported mass to regulate the contribution of observed representations is a reasonable design choice. The authors also provide parameter-matched ablation studies and electrode scarcity experiments, offering useful empirical support for the proposed architecture.

Critical weaknesses

W1. Limited generalizable insights and mechanistic explanations

Many conclusions remain specific to particular dataset–task combinations, with limited investigation into the underlying mechanisms. Although the benchmark provides extensive empirical results, it offers relatively few new generalizable insights into why models exhibit different transfer and adaptation behaviors.

W2. Insufficient discussion of related benchmarks and heterogeneous electrode modeling

Earlier epilepsy benchmarks, including SzCORE and Quantifying the Generalization Gap in Seizure Detection, receive insufficient attention. Moreover, the methodological connections and differences between RIVER and existing heterogeneous electrode modeling approaches, such as LUNA, MVPFormer, and NeuroCLUS, are not adequately discussed. The relevance of cross-physiological-signal transfer methods such as Brant-X also deserves clarification.

W3. Missing important baselines and limited dataset coverage

The evaluation omits representative models such as REVE, as well as iEEG/ECoG-specific foundation models such as NeuroCLUS, which are particularly relevant to the paper's focus. The limited number of datasets and independent transfer configurations, especially for cross-modality and cross-time transfer, also constrains the generalizability of the findings.

W4. Inconsistent performance advantages of RIVER

RIVER does not consistently outperform competing models across tasks and metrics. Some comparisons in Figure 3 emphasize model-family averages rather than the strongest individual baselines, while Figure 4 shows inferior performance in certain cross-time settings. Table 1 also suggests that RIVER does not exhibit a consistent advantage in adaptation gains under limited target supervision.

W5. Insufficient evidence for task-dependent cross-modal transfer conclusions

The scalp EEG-to-iEEG experiments involve few transfer configurations. Detection and prediction also use different source and target datasets, simultaneously changing task type, data distribution, electrode configurations, and patient populations. These confounding factors make it difficult to attribute the observed differences to task characteristics and limit the generalizability of the conclusions.

W6. Potential pretraining–evaluation data overlap

Some evaluated foundation models were pretrained on datasets such as TUEG and CHB-MIT, which may overlap with downstream evaluation data, particularly since TUSZ is derived from TUEG. The authors should verify the pretrained checkpoints, dataset versions, and patient- or recording-level splits to assess potential data contamination and its impact on zero-shot transfer evaluation.

W7. Dataset imbalance and inconsistent label construction

Certain tasks exhibit substantial class imbalance, such as the low positive-window proportion in CHB-MIT Detection. Moreover, seizure prediction datasets use inconsistent temporal exclusion intervals for interictal negative samples. Although partly attributable to dataset constraints, these differences may affect F1, AUPRC, calibration, and cross-dataset comparisons, warranting further examination.

Questions for authors

Q1. The benchmark reveals different adaptation patterns across transfer settings, particularly the diminishing gains beyond 25% target supervision. What factors do the authors believe primarily explain these differences? Can the existing results provide further evidence for these explanations?

Q2. How does the transported mass in RIVER relate to the actual availability of electrophysiological information? Do the authors have additional evidence or analyses showing how this quantity responds to changes in electrode coverage, beyond the reported classification performance?

2 comments
AuthorsOpenReview ↗

Response to Reviewer pREW

We sincerely thank the reviewer for the careful assessment! We respond in the order of all weaknesses and questions.

Weaknesses

W1. Generalizable insights and mechanisms

We connect representation transfer and reliability in Section 5, Table 1 and Appendix E.7. We distinguish contact ordering from concentration in Section 4.4 and window effects from rank stability in Section 4.6. We provide 12 active controls and one alignment reference in Appendix D.4. Selected AUROC means from Tables D.5/D.6 are:

ConfigurationDatasetTimeModality
Full RIVER0.8110.7890.849
Attention with fusion0.7920.5950.847
Static transport0.7320.6570.848

These link correspondence and fusion to transfer setting. In cross-modality transfer, attention with fusion leads AUPRC at 0.882 versus Full RIVER's 0.831. Static transport leads balanced accuracy at 0.746 versus 0.734.

W2. Related benchmarks and electrode modeling

We expand Section 2.3, Adaptation and epilepsy benchmarks, with SzCORE and Quantifying the Generalization Gap (Dan et al., 2025, 2026). In Section 2.2, Transfer across heterogeneous EEG settings, we discuss LUNA, MVPFormer, NeuroCLUS, and Brant-X (Doner et al., 2025; Carzaniga et al., 2025; Zheng et al., 2026; Zhang et al., 2024). We distinguish their queries, parallel attention, clustering, and cross-signal transfer from RIVER's assignment/support separation in Appendices C.2/C.5.1.

W3. Missing models and cohort coverage

We add six models in Section 3.3, with details in Appendix B:

FamilyAdded models
EEG foundationREVE, LUNA
iEEG foundationMVPFormer
EEG-specificDCRNN, GraphS4mer, VQ-MTM

We use pre-trained REVE, LUNA, and MVPFormer (El Ouahidi et al., 2025; Doner et al., 2025; Carzaniga et al., 2025). We add extra iEEG dataset HUP in Section 3.2 and Table A.1, SOZ in Section 4.4, Figures 6 and H.4, and four further EEG tasks in Appendix D.5, Tables D.10/D.11. We also discuss NeuroCLUS in Section 2.2.

W4. Variable RIVER advantages

We separate initial scores, gains, and endpoints in Sections 4.1 to 4.6 and Section 5, Discussion. Figure 3 compares group means: RIVER's AUROC is 0.690 versus 0.653 for EEG foundation models. We provide individual results in Appendix F and controls favoring simpler alternatives in Tables D.5 to D.9. We read Table 1 with absolute trajectories, since a stronger start can leave less room for gain.

W5. Task-dependent modality conclusions

We added TUSZ to HUP alongside TUSZ to Epilepsy-iEEG (Figure F.4). Section 4.4 tests spatial correspondence. Simultaneous scalp/SEEG evidence supplies physiological context (Casale et al., 2022). Sections 3.1, 4.3, and 5 interpret these measured cohort/task combinations alongside population, sensing, and label differences.

W6. Pretraining overlap

We provide dataset-level overlap analysis and weight sources in Table B.3. We list benchmark datasets named in the reported corpora and mark parent-archive relationships separately. Zero-shot denotes no benchmark target adaptation.

W7. Imbalance and label construction

We specify 1:2 detection and 1:1 prediction sampling in Appendix A.2, retaining test prevalence in Tables A.6/A.7. We define positive-class Clip-F1 with balanced accuracy/AUPRC in Appendix E.1. We place the common 30min preictal interval and 5min horizon alongside dataset-specific negatives and prior protocols (Xiang et al., 2025).

Questions for Authors

Q1. Why do later gains diminish?

We discuss early target adjustment and later patient heterogeneity in Sections 4.3/4.5, Section 5, and Appendix E.7. Both detection contrasts have Holm p<0.00001. Target exposure adjusts representations and selection together, while calibration and discrimination recover differently. We provide complementary patient-fold results in Appendix H.5, Figure H.6.

Q2. Transported mass and information availability

A meaningful question! We now provide a matched contact-removal analysis in Appendix C.5.2, Figure C.1, using five-fold 12s TUSZ-to-HUP detection. We remove equal numbers of SOZ or non-SOZ contacts with checkpoint weights fixed. Repetitions and ictal clips are averaged within patients. The patient-paired summaries are:

MetricSOZ removalNon-SOZ removalPaired mean differenceHolm p
Mean absolute raw slot-mass change0.0012580.000757+0.0005010.0083
Log-loss increase0.0295190.010097+0.0194220.0587

We find greater mass changes after SOZ removal at matched contact counts. This supports selective responses to clinically relevant contact information, beyond classification scores. Log loss increases more after SOZ removal. We define this support in Appendix C.5.1.

AuthorsOpenReview ↗

Further Questions Welcome

Thank you again for your thoughtful questions. We realize the discussion period is nearly over, but if time permits, we’d appreciate hearing whether our response addresses your concerns. If any points remain unclear, we’d be happy to clarify.

Reviewer_6NYAOpenReview ↗
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Paper summary

This paper presents EpiTAR-Bench, a comprehensive EEG benchmark for testing the generalizability of the EEG foundation models across dataset, time, and modality (EEG and iEEG). In addition, the paper also presents RIVER, a transfer-specific models that transfer across modality without the needs of electrode correspondences. The paper conducts several generalizability experiment, including varying dataset, times, modality, and supervision levels, and also shows that RIVER achieves best average ranks among benchmarks.

Critical strengths
  1. Comprehensive Benchmark Scope: The paper tries to address an important problem: how well epilepsy models generalize across difference settings. The benchmark settings covers cross-dataset, modality, and time transfer, with 16 models with multiple target supervision levels and two window lengths. The scope coverage is good.

  2. Careful design of the experimental protocols: The paper provide a detailed illustration of the preprocessing, patient splits, target-supervision settings, training configs and model-specific adaptations. The paper has specifically careful design of the target supervision, including checkpoint and threshold selection methods, keeping target test labels isolated, and nested patient-splits.

  3. Evaluation Coverage: The paper not only report the AUROC of each model, but also provide comprehensive statistical testing, calibration analysis, and SOZ evidence analysis for better interpretation. I also appreciate that the paper report nonsignificant findings rather than only presenting positive results.

  4. Strong proposed model: The proposed model, RIVER, shows promising transferability and generalizability across benchmarks.

Critical weaknesses
  1. One central claim, or at least a question, that the paper is trying to make is that "Scalp EEG can support adaptation when iEEG labels are scarce." The paper provide transferred model training on EEG then followed with 0%, 25%, 50%, 75%, and 100% iEEG supervision. To show that scalp EEG truly helps, one would also need a separate curve of directly training on iEEG with >0% to 100% of the data. Without it, we cannot determine if scalp EEG is helpful during the proposed "label scarce" setting (what I want to call it "label-efficient transfer").

One small point is that, during the adaptation, the paper also use a small portion of the source EEG data as rehearsal, so we cannot determine whether the performance gains from the EEG initialization training, or is it from rehearsal which might bring some sort of regularization effects. But that's just a small concern.

Another concern I want to point out is that, the direct iEEG training experiment are still init FM with EEG-pretrained checkpoint, which I found the setting to be a bit confusing as the "direct reference" setting is not truly only iEEG.

  1. Some findings are concluded with questionable settings. In figure 7, the paper is comparing different levels of supervision, and specifically compare the gain from 0% to 25% and point out that this initial level changes results in the most performance gain. However, from 0% to 25% the paper not only changes the number of target data, but also changes the way of selecting checkpoint and F1 threshold. Thus it is not simply comparing supervision levels but also different evaluation regimes. We cannot make the conclusion that the first quarter of the labels are more effective in this case.

In addition, I found that in some data, for example CHB-MIT, there is a significant label imbalance. This is very important to metrics like F1. In imbalanced case, a biased model could also have high metric scores, a macro-averged F1 is needed.

I also have concerns regarding the Calibration recovery settings, currently we cannot know if a model with lower ECE has truly better representation or that it simply needs a temperature scaling.

The paper also make conclusion that increase window length does not always leads to better performance. However, as we are changing the window length, the number of samples used to train and the batch size also changes. It is not a controlled comparision.

I also found that the number of patients in certain validation and test set is as small as 3. This can be concerning as patients-level variance can therefore become significant.

  1. The naming of "EPILEPSY MODELS" is a bit over-claiming. The paper wants to evaluate generalizability of epilepsy models, but it is only using EEG models and completely ignores iEEG foundation models(epilepsy models are not just for scalp EEG!) Recently there are many foundational iEEG models such as Brainbert[1], PopT[2] and Brant[3]. Also, the main task, seizure detection and prediction, are the two basic window classification tasks in epilepsy. There are many clinical tasks that requires finer representation capability or truly anatomical location understanding. For example, in a recent iEEG benchmark, Omni-iEEG [4], it additionally defining epilepsy tasks such as HFO classification, SOZ channel localization, Surgical outcome prediction, anatomical location classification, and more. I therefore suggest the author to narrow down the scope claiming or consider adding more models and tasks.

I also want to raise the concern regarding prediction label definitions. Different dataset used in the paper has different Interictal segment definition: CHB-MIT uses periods from 4h after the previous seizure offset where Siena is only in minute-level. This not fully harmonized setting might affect the transferability results.

[1] Christopher Wang, Vighnesh Subramaniam, Adam Uri Yaari, Gabriel Kreiman, Boris Katz, Ignacio Cases, & Andrei Barbu. (2023). BrainBERT: Self-supervised representation learning for intracranial recordings.

[2] Geeling Chau, Christopher Wang, Sabera Talukder, Vighnesh Subramaniam, Saraswati Soedarmadji, Yisong Yue, Boris Katz, & Andrei Barbu. (2025). Population Transformer: Learning Population-level Representations of Neural Activity.

[3] Daoze Zhang, Zhizhang Yuan, Yang Yang, Junru Chen, Jingjing Wang, & Yafeng Li (2023). Brant: Foundation Model for Intracranial Neural Signal. In Thirty-seventh Conference on Neural Information Processing Systems.

[4] Chenda Duan, Yipeng Zhang, Sotaro Kanai, Yuanyi Ding, Atsuro Daida, Pengyue Yu, Tiancheng Zheng, Naoto Kuroda, Shaun A. Hussain, Eishi Asano, Hiroki Nariai, & Vwani Roychowdhury. (2026). Omni-iEEG: A Large-Scale, Comprehensive iEEG Dataset and Benchmark for Epilepsy Research.

Questions for authors
  1. Can author provide more detail on the training configs for different models? For example, which baseline is using the official config, which is using author-defined bridge?

  2. I am a bit confused on table D4 vs D3, why the Keep 1.00 column in table D.4 not matching the number in table D.3?

  3. For the baseline foundation model, is there any overlapping between their pre-trained corpus and the dataset used in this benchmark?

1 comment
AuthorsOpenReview ↗

Response to Reviewer 6NYA

We sincerely thank the reviewer for the careful assessment! We respond in the order of all weaknesses and questions.

Weaknesses

W1. Target-only comparisons

Thank you for the advice of this essential control. We provide matched comparisons in Appendix F.4.1, Figure F.7. At 25%:

SettingMean AUROC orderingMatched models
Detection 12sTransfer > Direct16
Detection 60sTransfer > Direct14
Prediction 12sTransfer > Direct16
Prediction 60sTransfer > Direct13

We provide AUPRC and std in Figure F.7. At 100%, direct AUROC leads except for 12s detection.

W1.1. Rehearsal contribution

We retain 25% source data for rehearsal (Rolnick et al., 2019) to reduce catastrophic forgetting. We further explain this in Appendix B.2. Figure F.7 evaluates initialization and rehearsal together.

W1.2. Direct-reference initialization

We clarify direct training in Appendix F.4. Both arms share external initialization, following pre-trained seizure evaluation in BIOT and MVPFormer (Yang et al., 2023; Carzaniga et al., 2025).

W2. Checkpoint and threshold changes

We specify the validation domain in Appendix E.1, following explicit selection protocols under shift (Gulrajani and Lopez-Paz, 2021). The F1 threshold objective stays fixed. Source dev at 0% changes to target dev at positive levels. We interpret adaptation and selection jointly in Appendices E.1/E.2 and Sections 4.3/4.5.

W2.1. Imbalance and macro-F1

We report positive-class Clip-F1 in Section 3.1 and Appendix E.1, alongside balanced accuracy/AUPRC. We retain test prevalence and use 1:2 detection and 1:1 prediction training sampling in Appendix A.2. Dynamic negative subsampling is used by Hogan et al. (2025), and 1:1 interictal/preictal undersampling by Chung et al. (2020). Macro-F1 in Table D.11 concerns separate multiclass tasks.

W2.2. ECE versus temperature scaling

We agree that lower ECE measures calibration, not representation quality. Positive temperature scaling preserves binary score ordering (Guo et al., 2017). We distinguish ECE from AUROC/AUPRC in Appendix E.5 and Table 1. RIVER's ECE decreases are:

Transfer0% to 25%25% to 50%50% to 75%75% to 100%
Cross-dataset-0.0051+0.0073+0.0220-0.0009
Cross-modality+0.1483+0.0236+0.0340-0.0133
Cross-time+0.0411+0.0151-0.0061+0.0229

Cross-modality ECE decreases most at 0% to 25%. Cross-dataset ECE falls from 25% to 75%, then rises slightly. All three tracks end below their zero-shot ECE. These trajectories describe calibration recovery. We use the accompanying AUROC/AUPRC results to assess discrimination and make no attribution to a specific calibration mechanism.

W2.3. Window-length controls

We provide the 128/64 batch sizes and 12s/60s clip counts in Appendix B.2 and Tables A.6/A.7. Appendix E.4 interprets the joint sampling/training setting, not duration alone. Prior work also uses these lengths (Tang et al., 2022).

W2.4. Small patient cohorts

Thank you for highlighting patient variability. We provide five-fold 12s TUSZ-to-HUP results in Appendix H.5, Figure H.6, with across-fold std bands for both outcomes. RIVER retains early detection recovery and leads neural-family SOZ means across supervision levels.

W3. iEEG models and clinical task coverage

We added pre-trained MVPFormer (Carzaniga et al., 2025) in Section 3.3.2 and SOZ in Section 4.4, Figures 6 and H.4, extending evaluation beyond window classification as in Omni-iEEG (Duan et al., 2026). We also compare RIVER with four baselines on extra diagnosis, sleep, EEG event, and emotion tasks in Appendix D.5, Table D.11.

W3.1. Prediction negative labels

We provide shared positive intervals and dataset-specific negatives in Appendix A.2. Xiang et al. (2025) also use different CHB-MIT/Siena exclusions.

Questions for Authors

Q1. Configurations and bridges

We provide initialization and upstream component settings in Tables B.1/B.2 and channel bridges in Tables B.6/B.7. Appendix B.1 separates official components from benchmark labels, partitions, and selection.

Q2. Table D.3 versus Table D.4

We align the full-electrode reference. Table D.4 now reports absolute AUROC, with the same Keep 1.00 means and std as Table D.3:

VariantTables D.3/D.4 Keep 1.00
Full RIVER0.849
balanced OT0.776
set projector0.772
Softmax pooling0.778

We specify training-run variability at full coverage and subsampling variability at lower coverage in Table D.4 and Figure D.2.

Q3. Pretraining overlap

We provide dataset-level pretraining overlap analysis in Table B.3, listing benchmark datasets named in the reported corpora and marking parent-archive relationships separately. Zero-shot denotes no benchmark target adaptation.

Reviewer_4dggOpenReview ↗
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Paper summary

This paper introduces a benchmark EpiTAR-Bench to test the transferability, adaptation, and reliability of epilepsy models across seizure detection and prediction. And the paper designs RIVER, a transfer-specific model designed for partially observed and heterogeneous electrode configurations.

Critical strengths

Interesting methodological design. RIVER offers an interesting approach to handling heterogeneous electrode configurations by combining non-balanced optimal transport with an explicit measure of observation support.

Critical weaknesses
  1. Missing classic baselines for seizure analysis. The benchmark omits several classic seizure analysis models, including DCRNN[1], VQ-MTM[2], and GraphS4mer[3]. Including these models is important for assessing whether the reported advantages of foundation models and RIVER hold against strong alternatives. Their inclusion could change model rankings in individual settings and affect the broader conclusions about the relative performance of different model families.

  2. Unclear connection between the benchmark and RIVER. The paper does not sufficiently explain how the benchmark motivates the introduction of RIVER or how its findings inform the model’s specific design choices. If RIVER is intended as a seizure-specific method, the authors should clarify which aspects of its architecture address the particular characteristics of seizure detection and prediction, beyond general EEG modeling challenges. Alternatively, if RIVER is intended as a general approach to handling heterogeneous electrode configurations, evaluation exclusively on seizure-related tasks is insufficient to establish its broader applicability. Experiments on other EEG tasks, such as emotion recognition and sleep staging, would help substantiate this positioning. The paper should clarify RIVER’s intended scope and align its motivation, evaluation, and claims accordingly.

[1] Self-supervised graph neural networks for improved electroencephalographic seizure analysis, in: International Conference on Learning Representations 2023.

[2] Vector quantization pretraining for eeg time series with random projection and phase alignment, in: International Conference on Machine Learning 2024.

[3] Modeling multivariate biosignals with graph neural networks and structured state space models, in: Conference on health, inference, and learning 2024

Questions for authors

1.Clarification of “cross-modality” transfer. Could the authors clarify their definition of “modality” in this benchmark? Since scalp EEG and iEEG both measure electrical brain activity, what motivates describing their difference as a modality shift rather than a shift in recording configuration or sensing domain?

2.Justification for the optimal transport formulation. RIVER separates content encoding from the construction of aggregation weights. Could the authors clarify what the unbalanced optimal transport formulation contributes beyond conventional attention-based aggregation? In particular, what justifies interpreting transported mass as a measure of observability, rather than simply as an input to a learned gating mechanism? Targeted comparisons with attention-based aggregation using a comparable gate, and with UOT without mass-based gating, would help establish the role of the transport formulation.

  1. Missing target-only baselines under matched supervision budgets. The direct iEEG reference in Appendix F.4 uses the full target training set. However, demonstrating that scalp EEG training benefits adaptation with limited iEEG labels requires comparison against target-only training at the same supervision budgets, such as 25% and 50%. For foundation models, the target-only baseline should retain the same original pretrained initialization while omitting the scalp EEG training stage. Without these controls, improvements following target adaptation cannot be clearly attributed to knowledge transferred from scalp EEG, rather than to the additional target supervision itself.

  2. Inconsistent interictal definitions across prediction datasets. Appendix A.2 uses different temporal criteria to construct interictal samples. For example, CHB-MIT includes intervals from four hours after the preceding seizure to one hour before the next seizure, whereas Siena uses intervals from five minutes after the preceding seizure to 35 minutes before the next seizure. Consequently, cross-dataset prediction results may reflect differences in negative-class construction in addition to changes in the underlying recordings.

4 comments
AuthorsOpenReview ↗

Response to Reviewer 4dgg

We sincerely thank the reviewer for the careful assessment! We respond in the order of all weaknesses and questions.

Weaknesses

W1. Missing seizure baselines

Following your kind suggestion, we added DCRNN, VQ-MTM, and GraphS4mer (Tang et al., 2022, 2023; Gui et al., 2024), together with REVE, LUNA, and MVPFormer. Section 3.3 and Appendix B now describe 22 models. The additions are organized as follows:

Model familyAdded architectures
EEG foundationREVE, LUNA
iEEG foundationMVPFormer
EEG-specificDCRNN, VQ-MTM, GraphS4mer

We updated Figures 3 to 8 and Appendix F with these results. We provide architecture, initialization, and benchmark interfaces in Tables B.1/B.2/B.7.

W2. Benchmark motivation and broader EEG scope

To address the broader-scope question, we connect native electrode encoding, latent correspondence, and support fusion to heterogeneous transfer in Section 5 and Appendix C.2. Tables D.5 to D.9 test these choices across three 12s detection tracks. To examine applicability beyond seizure analysis, we added four extra EEG tasks in Appendix D.5. Selected means from Table D.11 are:

Dataset / metricRIVERBest baseline
ds004504 / AUROC0.7710.764
HMC / macro-F10.7150.712
TUEV / kappa0.4280.408
FACED / macro-F10.5230.628

RIVER ranks first on four of eight reported metrics and second on four. These tasks broaden the empirical scope of the native electrode interface.

Questions for Authors

Q1. Meaning of cross-modality

We clarify in Section 3.1 that this denotes a sensing-domain change within electrophysiology. Scalp EEG and iEEG share an electrical origin but differ in electrode proximity, tissue filtering, coverage, and seizure visibility. This usage follows CST (Wang et al., 2025), while simultaneous scalp/SEEG measurements document visibility differences (Casale et al., 2022). We specify each source and target in Appendix A.3.

Q2. Transport versus attention and the meaning of mass

We appreciate the request for a closer attention comparison. We separate normalized assignments from raw transport support in Appendix C.5.1. Marginal relaxation allows unequal transported mass (Chizat et al., 2018). The assignments aggregate content, while support controls interpolation between observed content and a learned latent prior. We interpret mass as model-relative support conditional on costs, priors, and masks, with its scale determined by the learned transport problem.

We compare attention and transport with and without the same fusion interface in Table D.5. Selected mean AUROC values are:

AggregationDatasetTimeModality
Full RIVER0.8110.7890.849
Attention with fusion0.7920.5950.847
UOT without fusion0.7540.6660.849

Mapping and fusion interact with transfer setting. Attention with fusion leads cross-modality AUPRC at 0.882 versus 0.831 for Full RIVER. We examine state context, priors, and temporal components in Tables D.6 to D.9, and provide matched SOZ/non-SOZ removal results in Appendix C.5.2, Figure C.1.

Q3. Direct iEEG training at matched supervision levels

We added Figure F.7 and Appendix F.4.1, comparing transfer and direct training at 25%, 50%, 75%, and 100% for 12s/60s detection and prediction. Each positive-level pair uses identical available models with equal model weights and std across model means. Transfer has higher mean AUROC at 25% in all four settings. At 100%, direct training leads for 60s detection and both prediction configurations, whereas 12s detection favors transfer.

We retain the same external pre-trained initialization in both arms where used, with random initialization for scratch models. This follows downstream seizure evaluation using pre-trained BIOT and MVPFormer (Yang et al., 2023; Carzaniga et al., 2025), and evaluates each foundation model with its learned representation. We specify this shared starting point in Appendix F.4 and document corpus exposure in Table B.3. Direct training omits the supervised scalp stage and source rehearsal. The transfer arm includes both, so this tests the complete pipeline. Figure F.7 reports available-model counts.

Q4. Interictal definitions

We agree that these definitions should be read together. We provide the common 30min preictal interval, 5min horizon, and dataset-specific negative exclusions in Appendix A.2. Xiang et al. (2025) use different interictal separation intervals for CHB-MIT and Siena, providing precedent for dataset-dependent construction. Their numerical choices differ from ours. We place our explicit intervals alongside prior definitions in Appendix A.2 and interpret the resulting cohort and label settings in Section 5, Discussion.

Thank you for the additional experiments and the revised manuscript. However, several concerns remain:

  1. RIVER’s motivation and scope. Table D.11 broadens the evaluation, but they show that RIVER’s advantages do not consistently extend across tasks. For example, its improvements over the best baseline are small on ds004504 and HMC, while its macro-F1 on FACED is substantially lower (0.523 versus 0.628). As the paper including the title comes from epilepsy models, it remains unclear which architectural components address the particular characteristics of seizure detection and prediction beyond general EEG modeling challenges, and what is the relationship between seizure-focused benchmark and RIVER's design. And why RIVER is not applicable for other tasks beyond epilepsy

2.Reporting inconsistencies. Figure 6(c–d) reports EEG foundation model SOZ AUPRC values of 0.346/0.302, whereas the accompanying text states 0.340/0.291. Additionally, Tables D.2–D.3 change the uncertainty label from SEM to STD, while the numerical uncertainties remain unchanged. In addition, in Table D.4. balanced OT at Keep 1.00, the original normalized value was 0.583, whereas the revised absolute AUROC is 0.776. Under the original normalization formula, this would require a reference AUROC of 0.776/0.583≈1.330.776/0.583 \approx 1.33, which is impossible.

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Follow-up Response to Reviewer 4dgg

Thank you for your careful follow-up. Your comments helped us clarify how the seizure-focused benchmark motivated RIVER’s design. In the previous rebuttal round, we added several experiments and updated the figures, tables, and text. As we incorporated the new results, some reporting conventions became inconsistent across these updates. We appreciate you pointing out these discrepancies and giving us the opportunity to clarify how the results were reported. Page references below refer to the revised manuscript.

1. RIVER’s motivation and scope

EpiTAR-Bench examines seizure detection, prediction, and spatial localization across changes in cohort, recording period, and sensing domain. RIVER addresses the electrode heterogeneity exposed by these settings, especially in scalp-to-iEEG transfer. Native-to-latent mapping accommodates different electrode sets without requiring fixed scalp-to-intracranial channel correspondence. Partial transport and support-dependent fusion accommodate incomplete spatial coverage. Local and global temporal modeling and evidence aggregation combine brief activity with sustained context for ictal/non-ictal and preictal/interictal decisions. Sec. 3.3.4 (p. 6) now explains how the seizure-focused benchmark motivated this combination of components.

RIVER also applies beyond epilepsy. Table D.11 evaluates diagnosis, sleep staging, event recognition, and emotion recognition. We agree that the gains over the strongest baseline are small on ds004504 and HMC, and that RIVER’s macro-F1 on FACED is lower than CBraMod’s (0.523 vs. 0.628). These results show that RIVER can be used for other EEG tasks and that its relative performance varies by task. We clarify in Sec. D.5 and the discussion of Table D.11 (p. 36) that heterogeneous seizure transfer remains the primary design objective.

2. Reporting consistency

We appreciate your detailed checks of score aggregation, uncertainty labels, and the full-electrode reference.

2.1. Figure 6 and SOZ AUPRC. Figure 6(c–d) averaged seed-level family summaries based on different numbers of available models, while the text used model-level summaries with intermediate rounding. This yielded 0.346/0.302 in the figure and 0.340/0.291 in the text. We now use unrounded model values, weight the two intracranial targets equally for each model, and weight models equally within each family. We truncate only for display. Figure 6 and Sec. 4.4 (p. 8) now report 0.341 at 12 s and 0.291 at 60 s for the EEG foundation model family. Sec. E.6 documents the procedure (pp. 38–39). The target-specific results agree across Sec. H.3 (pp. 49–50) and Figure H.4 (p. 51).

2.2. SEM and STD. During revision, we incorrectly relabeled SEM as STD while retaining the original SEM values. We restored the SEM label in Tables D.2–D.4 (pp. 30–31) and Figures D.1–D.2 (pp. 30 and 32). Tables D.5–D.9 retain mean ± SEM for the inherited cross-modality Full RIVER reference and use sample standard deviation for the new summaries (pp. 33–35). Table F.1 reports across-run STD (p. 46), and Figures H.2–H.3 report patient-level STD after averaging seeds within each patient (pp. 50–51). Sec. E.1 now specifies these definitions.

2.3. Table D.4 and the full-electrode reference. Thank you for checking the normalization. The earlier value of 0.583 came from the normalized electrode-scarcity summary, which had not been reconciled with the full-electrode results in Table D.3. For the revised Table D.4, we rechecked the experimental records and used each model’s full-electrode AUROC from Table D.3 as its Keep 1.00 entry. For balanced OT, that value is 0.776. The entries at Keep 0.75, 0.50, and 0.25 report the recorded absolute AUROCs for those conditions (Sec. D.3, p. 31).

We redrew Figure D.2 with all four Keep points for each model (p. 32). The descriptive slopes come from least-squares fits with an intercept to the four unrounded means. Full RIVER’s displayed AUROCs are 0.849, 0.852, 0.854, and 0.846, with a slope of +0.004. The other slopes are +0.298, +0.220, and +0.290. The caption specifies that SEM is calculated across three training seeds at Keep 1.00 and across three electrode-subsampling repetitions at lower Keep ratios.

AuthorsOpenReview ↗

Further Questions Welcome

Thank you again for your thoughtful questions. We realize the discussion period is nearly over, but if time permits, we’d appreciate hearing whether our response addresses your concerns. If any points remain unclear, we’d be happy to clarify.

Reviewer_84tcOpenReview ↗
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Paper summary

This paper introduces EpiTAR-Bench, a comprehensive evaluation framework for studying the transferability, adaptation, and reliability of epilepsy models under heterogeneous EEG and intracranial EEG (iEEG) settings. The benchmark considers seizure detection and prediction across five datasets and seven transfer directions, including cross-dataset, cross-modality, and cross-time transfer. It evaluates 16 models from four methodological families under two window lengths and five target-supervision levels.

In addition to the benchmark, the authors propose RIVER, a transfer-oriented architecture incorporating Observability-Aware Partial Transport (OAPT), which maps heterogeneous electrode configurations into a shared latent space using partial optimal transport.

The experiments investigate zero-shot transfer, adaptation with progressively increasing target supervision, sensitivity to recording window length, probability calibration, and seizure onset zone (SOZ) evidence. The authors find that pretrained EEG foundation models provide relatively strong zero-shot cross-dataset baselines, while adaptation gains are often concentrated at low target-supervision levels. They also observe that classification performance, calibration, and spatial evidence do not necessarily align.

Critical strengths

S1. A useful multidimensional evaluation of epilepsy model generalization.

S2. Meaningful analysis of limited-supervision adaptation and heterogeneous electrode observability.

Critical weaknesses

W1. The benchmark's breadth in experimental configurations is not matched by sufficient diversity of independent datasets and transfer scenarios.

W2. The statistical and reliability analyses do not fully justify the breadth of the conclusions about adaptation and clinical robustness.

Questions for authors

Q1. To what extent do the conclusions about cross-modality transfer generalize beyond the two specific source–target dataset pairs? Can the authors provide additional transfer directions or an analysis distinguishing task effects from dataset-pair effects?

Q2. Can the authors complement the model-level statistical tests with patient-level or cohort-level uncertainty estimates for the principal adaptation claims? In particular, how sensitive is the conclusion about disproportionate initial adaptation gains to the absolute number and identity of target patients selected at the 25% supervision level?

Q3. Can the authors provide event-level seizure detection and prediction metrics, including false alarms per hour and clinically relevant prediction sensitivity or warning-time measures? These would materially strengthen the interpretation of the benchmark's reliability dimension.

2 comments
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Response to Reviewer 84tc

We sincerely thank the reviewer for the careful assessment! We respond in the order of all weaknesses and questions.

Weaknesses

W1. Dataset and transfer diversity

Following your suggestion on coverage, we expanded the benchmark to six datasets, eight classification directions, 22 models, and three epilepsy tasks (Sections 3.1 to 3.3). We added REVE, LUNA, MVPFormer, DCRNN, GraphS4mer, and VQ-MTM. HUP provides a second intracranial detection target with 58 patients. Tables A.2/A.7 report 35/10/13 train/dev/test patients and 193/58/62 recordings at both window lengths.

We now evaluate SOZ localization for CHB-MIT to TUSZ and TUSZ to Epilepsy-iEEG/HUP in Section 4.4 and Figure 6. To examine RIVER beyond seizure analysis, we added four EEG tasks in Appendix D.5. Selected means from Table D.11 are:

Dataset / metricRIVERBest baseline
ds004504 / AUROC0.7710.764
HMC / macro-F10.7150.712
TUEV / kappa0.4280.408
FACED / macro-F10.5230.628

RIVER ranks first on four of eight metrics and second on four. We distinguish this task expansion from additional independent transfer cohorts.

W2. Statistical support and reliability

We now identify the matched unit and correction family in Appendix E. Supervision/window length contrasts use 22 model blocks, with six track/task comparisons in one Holm family. Both detection gain contrasts have Holm p<0.00001. Appendix F tests each positive level against zero, matching direction, window, model, and seed, with four Holm-corrected contrasts per AUROC panel or ECE family. Figure 3 pairs eight direction/window settings for rank comparisons and corrects across five comparator groups.

We add component controls in Tables D.5 to D.9 and connect their effects to representation transfer and electrode heterogeneity in Section 5, Discussion. We interpret calibration, contact retrieval, and detection false-alarm rates as complementary reliability outcomes. We provide the latter in Appendix H.4 and Figure H.5, following the interest in alarm-based evaluation emphasized by SzCORE (Dan et al., 2025).

Questions for Authors

Q1. Additional directions and task effects

We added TUSZ to HUP alongside TUSZ to Epilepsy-iEEG in Figure F.4, holding source and detection task fixed while changing the intracranial cohort. Both windows are reported, and Figure 6 tests contact correspondence. Tables D.5 to D.9 retain 12s detection across three transfer tracks for component comparisons.

This additional target lets us examine whether the detection pattern recurs. Sections 4.3 and 5 interpret detection/prediction differences as task/cohort patterns, with their respective label protocols.

Q2. Patient uncertainty and supervision levels

Thank you for highlighting patient composition. We now provide five-fold 12s TUSZ-to-HUP detection and SOZ results in Appendix H.5, Figure H.6. We vary the target patient partition, average models equally within families in each fold, and report the mean and sample std across five folds. Selected family and RIVER mean AUPRC values are:

Outcome0%25%100%
RIVER detection0.5960.6360.634
RIVER SOZ0.2910.2990.300
EEG FM SOZ0.2740.2690.265

At 25% and 100%, RIVER's std is 0.014 for detection and 0.013 for SOZ. Most of its mean detection recovery occurs at 25%, with smaller changes thereafter. Its SOZ AUPRC improves early and remains above the EEG foundation family mean at all supervision levels, preserving the localization hierarchy across patient partitions. We include eight detection models and seven neural localization models. We specify the original quotas in Appendix A.4 and Table A.5, and present fold sensitivity separately from the model-block tests in Appendix E.2.

Q3. Detection false-alarm rates

Thank you for suggesting clinically interpretable measures. We provide detection false alarms per hour and per 24h in Appendix H.4, Figure H.5, across 22 models, five detection directions, both window lengths, and all supervision levels. Zero/full-supervision means for all five families and RIVER are:

GroupFA/h, 0%FA/h, 100%FA/24h, 0%FA/24h, 100%
EEG FMs3.0193.03872.46872.934
iEEG FM3.6392.60887.33762.615
EEG-specific4.1814.171100.367100.127
Transfer-specific3.3602.81480.64967.556
Traditional ML2.4302.34158.33356.195
RIVER2.4252.22558.21353.403

We average directions/windows within tracks, then tracks equally, with equal model weights within families. Figure H.5 shows means and across-run std bands. Per-24h values equal 24 times per-hour values before truncation. RIVER, the iEEG foundation model, and transfer-specific comparators show lower endpoint rates. Traditional ML reaches its minimum at 50%, while EEG foundation models remain comparatively stable.

AuthorsOpenReview ↗

Further Questions Welcome

Thank you again for your thoughtful questions. We realize the discussion period is nearly over, but if time permits, we’d appreciate hearing whether our response addresses your concerns. If any points remain unclear, we’d be happy to clarify.

Comments on the paper

5 comments
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Follow-up Response to Reviewer 6NYA

Thank you for your continued careful reading and constructive questions. We appreciate the opportunity to clarify each point below.

1. Detailed SOZ comparison

We appreciate your request for individual comparisons. The mean SOZ AUPRC for each model family in Finding 4 summarizes family-level performance, but does not show how RIVER compares with individual models. We therefore provide corresponding results for all 19 localization-capable models below. E/H denote Epilepsy-iEEG/HUP; Avg is the equally weighted mean across the two targets at each window length. Scores are truncated to three decimals. Bold and underline mark first and second, respectively, based on the full-precision values.

ModelE12sE60sH12sH60sAvg12sAvg60s
RIVER0.541‾\underline{0.541}0.5050.3150.2950.4280.400‾\underline{0.400}
BENDR0.3040.2300.1310.1280.2180.179
BIOT0.4520.5140.3570.341‾\underline{0.341}0.4050.427
CBraMod0.4910.4430.349‾\underline{0.349}0.3470.420‾\underline{0.420}0.395
EEGPT0.5460.2840.1880.1810.3670.232
LaBraM0.4990.3800.3370.3220.4180.351
ST-EEGFormer0.4940.2690.3460.3220.4200.296
REVE0.2950.2710.1100.1030.2020.187
LUNA0.3110.2910.2390.2280.2750.260
MVPFormer0.3110.2340.1740.1700.2430.202
EEGNet0.4560.4530.3490.3350.4030.394
EvoBrain0.3840.1910.3490.3280.3670.260
ScatterFormer0.5370.1920.0930.0920.3150.142
BF-EML0.5060.3840.2060.1930.3560.289
DCRNN0.3550.2670.1720.1660.2630.216
GraphS4mer0.2760.2600.1750.1710.2250.216
VQ-MTM0.3360.2580.1920.1800.2640.219
CST0.2800.2660.2040.2020.2420.234
TSMNet0.5240.508‾\underline{0.508}0.1080.1030.3160.306

Across the 19 models, RIVER has the highest equal-target mean at 12 s (0.428) and the second-highest at 60 s (0.400), behind BIOT (0.427). The per-target results show that rankings vary across targets and time windows, so the family-level summary and model-by-model comparisons provide complementary views of performance.

2. Alignment-weight-zero reference in D.7

We appreciate your question. Your same-checkpoint expectation is correct: alignment operates only during target adaptation, so changing its coefficient alone cannot affect zero-shot predictions from fixed source weights.

D.7 labels this entry as a reference, and Appendix D.4 identifies alignment as inactive at zero supervision. Full retains the original benchmark reference.

3. D.4 reports absolute AUROC at all coverage levels

We appreciate the opportunity to clarify this reporting change. D.4 now gives absolute AUROC at every ratio, including Keep 0.75, 0.50, and 0.25. Keep 1.00 matches the model-specific D.3 results; lower-coverage entries use the recorded absolute AUROC observations.

VariantKeep1.00Keep0.75Keep0.50Keep0.25
Full RIVER0.8490.8520.8540.846
Balanced OT0.7760.5700.5350.538
Set projector0.7720.5540.5220.599
Softmax pooling0.7780.5560.5440.540

Full remains within 0.846 to 0.854 across coverage levels. Slopes use absolute AUROC per unit removed-electrode fraction: +0.004 for Full, versus +0.298, +0.220, and +0.290. Similar lower-coverage patterns can remain after changing the scale.

4. Interpreting the cross-modality ablations

We appreciate your question about the design choices. D.3 reports AUROC 0.849 for Full, versus 0.776 for balanced OT, 0.772 for the set projector, and 0.778 for Softmax pooling. D.5 to D.9 test finer controls retaining more of the architecture.

In the reported cross-modality results, single-scale state, no relation context, content-only state, and uniform electrode support give 0.831, 0.832, 0.838, and 0.836, respectively. Mapping/fusion controls have similar AUROC, while attention with fusion has higher AUPRC, 0.882 versus 0.831. These observations support a task- and metric-specific interpretation. D.3 and the SOZ comparison separately characterize formulation-level performance and spatial retrieval.

AuthorsOpenReview ↗

Further Questions Welcome

Thank you again for your thoughtful questions. We realize the discussion period is nearly over, but if time permits, we’d appreciate hearing whether our response addresses your concerns. If any points remain unclear, we’d be happy to clarify.

Thank the author for the additional experiment and the detailed response. I have two last concerns:

  1. Regarding the new detailed SOZ comparison, it seems like RIVER is not leading the majority ot he settings. This puts it questionable about the finding 4 on whether RIVER's native electrode design is helpful.
  2. Table D.7: The authors confirmed that alignment-weight-zero should not affect zero-shot predictions under the same checkpoint. However, the AUROC differs substantially from Full RIVER (e.g., 0.666 vs. 0.789 in cross-time settings). This raises concerns about whether the ablation runs use controlled checkpoints and settings.

Thanks again for the detailed response. I will take these results into account in my final assessment.

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