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Under review as a conference paper at ICLR 2027

MoRSE: Distilling EEG Foundation Models into a Single Montage-Robust Multi-Task Encoder

Abstract

Electroencephalography (EEG) foundation models are pre-trained across many electrode montages, and several accept any number of channels by construction. However, they are typically deployed after fine-tuning on a task recorded with a single montage, which largely removes this montage flexibility. Existing remedies, such as channel interpolation or montage-sampled fine-tuning, still leave one large model per task. To address this, we propose MoRSE (Montage-Robust Student for EEG), which distills fine-tuned EEG foundation models into a single small multi-task encoder that remains accurate on electrode subsets. In this asymmetric distillation, teachers observe the full montage while the student observes a random electrode subset resampled each step, and so learns to infer the full-montage representation from the electrodes available. Having found that fine-tuning typically compresses representations to an effective dimensionality that tracks the class count, we align the student with a never-fine-tuned backbone. We evaluate MoRSE on eight tasks spanning seizure detection, sleep staging, emotion recognition, motor imagery and dementia diagnosis, where a model fine-tuned without montage variation loses 0.142 balanced accuracy when electrodes are removed. Across 30 task-by-montage cells, a single 1.97M-parameter encoder retains 95% of the balanced accuracy of the per-cell specialists, with 89× fewer deployed parameters. Against eight montage-sampled specialists that are 24× larger in aggregate, it retains 98%. It also transfers zero-shot to unseen electrode layouts and to two external sleep-staging datasets. Thus, one encoder a third the size of a single specialist can replace multiple task-specific foundation models across tasks and layouts. Anonymous code is available via the Reproducibility Statement.

Primary area:
applications to neuroscience & cognitive science
Keywords:
lightweight EEG models, EEG foundation models, knowledge distillation, representation learning, montage robustness, multi-task learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_qUa7OpenReview ↗
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3
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Paper summary

MoRSE trains a shared 1.97M-parameter EEG student across eight tasks while randomly varying the available electrode subset. Full-montage teachers provide task logits and token representations, with feature alignment taken from a never-fine-tuned backbone. The method combines labeled multi-task training with alignment on an additional unlabeled corpus. Evaluation includes 30 task-by-montage cells, held-out hardware layouts, comparisons with montage-sampled specialists, and two external sleep cohorts. The experiments measure accuracy, aggregate parameter storage, and performance when electrodes are removed. Its extensive ablations locate most of the distillation benefit in feature alignment rather than logit transfer.

Critical strengths
  1. A practically meaningful robustness and consolidation result, tested against relevant alternatives. The same student handles eight tasks and multiple electrode budgets, with mean balanced accuracy of 0.6044 versus 0.6335 for the LaBraM per-cell specialists. The paper also compares against eight montage-sampled specialists, a stronger and more relevant baseline than specialists trained only at fixed montages. On 42 hardware-layout cells, montage sampling improves the student from 0.5143 to 0.5670. The unchanged sleep head also transfers to ISRUC and PhysioNet 2018; the largest sampling gains occur with two electrodes, where training electrodes are missing. These experiments directly address the claimed deployment problem.

  2. Extensive, informative ablations and transparent negative findings. The appendix distinguishes teacher family from student initialization, separates feature alignment from additional unlabeled data, compares multi-task and single-task students, and reports unsuccessful interventions. Table 15 establishes that feature alignment helps even without the auxiliary corpus, while explicitly treating logit distillation's incremental gain as indistinguishable from zero. This level of analysis substantially increases the value of the work beyond presenting a compact model.

Critical weaknesses
  1. The teacher-role explanation is stronger than the causal evidence for it. The abstract motivates never-fine-tuned alignment features through the effective-rank reduction after task fine-tuning, and the recipe is described as distillation from fine-tuned task experts. However, effective rank tracking class count does not by itself show that those representations are unsuitable alignment targets. The direct experiment needed for that explanation is a matched feature-alignment teacher comparison before versus after task fine-tuning, holding the teacher family, student, corpus, and losses fixed. Separately, Table 15 gives 0.6016 for feature-only training and 0.6044 for the full recipe, with the logit increment carried by one seed; the authors appropriately acknowledge this. The evidence therefore supports asymmetric feature distillation with montage sampling more strongly than a necessary dual-teacher transfer mechanism. I would accept a narrower explanation consistent with these results; demonstrating the stronger teacher-role claim would require the matched control above.

  2. Aggregate retention ratios conceal meaningful task-level costs, and seed variation does not establish patient-level reliability. Retaining approximately 95% of raw balanced accuracy can sound closer to specialist performance than the absolute drop or chance-adjusted headroom warrants. The appendix already supplies headroom analyses, which is a strength, but they should be reflected in the main result: some full-montage tasks lose appreciably more than the mean, while others benefit from sharing. The 89× figure also concerns aggregate stored parameters for the specialist collection, not an 89× reduction in the cost of one inference; the separate runtime measurements are the relevant evidence for that claim. Finally, paired tests across five seeds quantify training variability on fixed test cohorts, not uncertainty over patients or sites. Please elevate the existing per-task/headroom results and add participant-level paired uncertainty for the principal robustness and external-cohort comparisons where feasible. This would clarify when the compact shared model is an acceptable replacement rather than imply a uniform trade-off across tasks.

Questions for authors
  1. Is there a matched comparison using the same alignment teacher before versus after task fine-tuning? If not, will the authors frame effective-rank observations as motivation and remove claims that the never-fine-tuned teacher is required by those observations?

  2. Can the main results show absolute per-task losses and chance-adjusted headroom next to the aggregate retention ratio, together with paired subject-level uncertainty for the external sleep and held-out-layout comparisons?

  3. What behavior is expected for electrodes outside the trained slot vocabulary, or for reference changes beyond those evaluated? Please distinguish unseen subsets/layouts of supported electrodes from arbitrary unseen electrode coordinates and acquisition systems. A clear limitation is sufficient; a new broad benchmark is not required.

4 comments
AuthorsOpenReview ↗

Response to Reviewer qUa7 (1/2): W1 and Q1

Thank you for the clear review and for stating which narrower explanation you would accept. We answer each weakness (W) and question (Q) below. Changes are in blue in the revised PDF.

W1. Narrower explanation. We adopt it. The submitted and revised wording, side by side:

LocationSubmittedRevised
Abstract"teachers observe the full montage while the student observes a random electrode subset ..., and so learns to infer the full-montage representation""Matched controls did not resolve an accuracy advantage for an alignment teacher that sees the full montage or was never fine-tuned"
Abstract"Having found that fine-tuning typically compresses representations ..., we align the student with a never-fine-tuned backbone"removed; the matched-control sentence above replaces it
Contribution 2"Teacher roles from a representation diagnosis ... To our knowledge this consequence of fine-tuning has not been drawn before""Matched controls of the teacher roles ... neither an alignment teacher that sees the full montage nor one that was never fine-tuned was resolved as more accurate, so we attribute the measured gains to feature alignment and montage sampling rather than to these teacher choices"
Section 2.2"Such a representation still carries the task decision but is a poor source of features. The two distillation targets therefore come from different models""... which motivated us to draw the per-patch targets from the never-fine-tuned backbone. The matched controls ... did not resolve an accuracy advantage for this choice on the eight tasks, so it is kept as a design choice"

Logit distillation stays in the recipe as specified but is no longer described as necessary, because its increment over alignment is not resolved (+0.0028, Table 15). Appendix G.2 reports its per-task values as exploratory.

Q1. Matched comparison. Yes. We aligned the student to the same Gram backbone before versus after task fine-tuning, holding the teacher family, student, corpus and losses fixed as you specified, and repeated the comparison in the feature-only configuration without the corpus (Section 3.5 and Appendix K). Neither resolves an advantage for the never-fine-tuned Gram (full recipe +0.0001 [−0.0117, +0.0119]; feature-only −0.0042 [−0.0143, +0.0060], and −0.0028 [−0.0105, +0.0049] with ten seeds), and for LaBraM, run in the same way, the estimate favours the fine-tuned teacher across seeds (−0.0082 [−0.0144, −0.0020]) but not across subjects or on validation. We also measured the effective rank of Gram itself before and after fine-tuning. It falls strongly on some tasks (Mumtaz 61 to 3.4, ADFTD 61 to 5.7) but not on others (HMC 53 to 54, CHB-MIT 64 to 61, SEED-V 56 to 67), while LaBraM falls on all eight (Table 12). A further test shows where the rank observation does and does not hold. Students aligned to fine-tuned teachers inherit their compression (student effective rank lower by 12 to 55, all fifteen seed pairs), yet neither accuracy on the eight tasks nor a linear probe on tasks not used in distillation shows a resolved cost (+0.0047 [−0.0086, +0.0179]). Following the rule we fixed before running the controls, effective rank is framed as motivation, and the claim that the observations require a never-fine-tuned teacher is removed.

Continued in the next comment (2/2).

AuthorsOpenReview ↗

Response to Reviewer qUa7 (2/2): W2, Q2 and Q3

W2 / Q2. Per-task costs, stored parameters and subject-level uncertainty.

  • Table 1 now gives chance-adjusted retention per task next to the absolute per-task differences and the aggregate, and the abstract leads with the absolute gap (0.029 balanced accuracy and 90% of the headroom above chance against the per-cell specialists, 0.010 and 96% against the eight montage-sampled specialists).

  • 89× now refers to stored parameters. Per-inference cost is reported separately in Table 11, which now adds CPU latency. On one CPU core a window takes 5.9 ms for MoRSE and 16.8 ms for a LaBraM specialist, so per inference MoRSE is about 2.9 times faster, far less than 89×, and the text keeps the two apart.

  • Subject-level paired intervals for the held-out layouts are in the table below (all tasks in Appendix P). For the external sleep cohorts, the sampling gain at two electrodes is +0.1267 [+0.1149, +0.1386] on ISRUC (82 subjects) and +0.1163 [+0.1072, +0.1254] on PhysioNet 2018 (150 subjects). At four and six electrodes the gains are small (+0.0017 to +0.0123). Their subject-level intervals exclude zero in three of the four cases, but their seed-paired intervals include zero in all four, so we describe them as small and not resolved across training seeds.

  • Five seeds describe training variability on fixed test cohorts, and Section 3.1 now says so.

ComparisonΔ BASubject 95% CI
Student vs 8 sampled specialists, 42 layouts−0.0255[−0.0452, −0.0046]
Sampling vs no sampling (student), 42 layouts+0.0528[+0.0365, +0.0671]

Q3. Electrodes outside the vocabulary and other references. We added the limitation in Appendix J.3. MoRSE is validated on unseen subsets and layouts of the electrodes in its training vocabulary and with the references of the training data. Its behaviour for arbitrary new electrode coordinates, other references and other acquisition systems is not established. Within that scope we added two controlled estimates (Appendix N). For electrode identities the student does not know, we withheld four electrodes from the student throughout training and mapped them at test time to trained sites at increasing distance (26 to 192 mm). The loss grows with distance, and leaving the electrodes out did better than mapping them (by 0.0095 to 0.0694 on the cells that contain them), so Appendix J.3 advises leaving such electrodes out. For references, re-referencing the test data to the common average or to a single electrode, without retraining, lowers balanced accuracy by 0.024 and 0.036 at the full montages and by 0.026 and 0.020 on the held-out layouts. These estimates cover sites of the 10-10 system and two reference changes, and Appendix J.3 does not extend them to new coordinates or acquisition systems.

We hope these results address your concerns, and we would be glad to clarify any remaining point.

Thank you for the detailed response and the revision. I'll keep my score

AuthorsOpenReview ↗

Thank you for your follow-up

Dear Reviewer qUa7,

Thank you very much for reading our responses and the revision, and for your continued positive assessment. Your review described the matched comparison and stated which narrower explanation you would accept, and the revised paper now reflects both. We sincerely appreciate the time and care you have given to our paper.

Best regards, The Authors

Reviewer_SH37OpenReview ↗
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Confidence
2
Informativeness
3
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2
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Paper summary

MoRSE distills EEG foundation models into a shared 1.97M-parameter encoder with task-specific linear heads. The student receives randomly sampled electrode subsets, while full-montage teachers provide task logits and contextual per-patch representations. The main configuration uses LaBraM initialization and fine-tuned logit teachers, together with an unfine-tuned Gram representation teacher. Supervised and distillation losses are supplemented by feature alignment on 524 hours of unlabeled EEG. Evaluation spans eight cross-subject tasks, 30 task/budget cells, 42 hardware-layout pairs, and two external sleep cohorts. The student achieves 0.6044 mean balanced accuracy versus 0.6335 for per-cell LaBraM specialists, and 0.6144 for eight montage-sampled specialists, with substantially fewer total deployed parameters.

Critical strengths
  1. A useful deployment result tested against a strong, simple alternative. The paper does not stop at comparing against fixed-montage models. Giving specialists the same montage sampler produces 0.6144 on the 30 budget cells versus 0.6044 for the single student, while eight specialists require approximately 24 times the deployed parameters (Appendix G.3). On held-out layouts, the stronger specialist baseline remains ahead by 0.0255, which the authors explicitly report. This establishes a meaningful trade-off between shared-model size and accuracy, rather than attributing all robustness to the student architecture. The 89-fold figure against 30 per-cell specialists is less deployment-general, but the eight-specialist comparison substantiates the core practical claim.
  2. Broad and carefully decomposed evidence. The paper retrains baselines with shared preprocessing, examines realistic clustered subsets, and transfers the unchanged sleep head to ISRUC and P2018. Sampling adds 0.1267 and 0.1163 balanced accuracy at two electrodes on those cohorts (Table 3). Table 15 separates feature alignment from the additional unlabeled corpus, and the appendix documents capacity trends, initialization effects, single-task students, and unsuccessful objective modifications. The explicit correction and testing of token-order conventions further improves reproducibility. These experiments make the empirical recipe informative beyond its average score.
Critical weaknesses
  1. The headline teacher-role and privileged-information explanation is only partly supported. Table 15 shows that feature-only distillation with the corpus reaches 0.6016 versus 0.6044 for the complete recipe; logit distillation alone is worse than the supervised baseline, and its incremental effect with alignment is not resolved across seeds. The paper acknowledges that the logits are retained mainly because they have no inference cost and were used for the other results (Appendix G.2). Thus, the successful student is not demonstrably dependent on distilling decisions from eight fine-tuned experts. Low effective rank after fine-tuning also does not by itself show that such features are inferior distillation targets; the reported rank analysis is diagnostic rather than a direct before/after target comparison. Finally, sampling versus no sampling does not isolate the value of giving the alignment teacher more electrodes than the student. A same-subset teacher control is needed for that specific causal explanation. These gaps weaken the methodological narrative, although they do not negate the recipe's measured benefit.
  2. Aggregate retention and seed statistics overstate how uniformly the result transfers. The main 95% retention figure is a ratio of mean balanced accuracies with different class-dependent chance floors. The paper usefully provides chance-adjusted task results in Figure 9, but the practical losses remain substantial on some tasks: BCI IV 2a falls from 0.5118 to 0.3862 averaged over budgets, while CHB-MIT improves from 0.7870 to 0.9100 (Table 1). Several tasks have few test subjects, including two for BCI IV 2a and four for CHB-MIT (Table 5). Five training seeds do not estimate uncertainty over those subjects, and layout cells within a task reuse the same recordings; a t-statistic over 42 cells should therefore not be interpreted as 42 independent cohort replications. The external sleep cohorts are a meaningful mitigation, but do not establish equally reliable transfer for the other task families. This limits how broadly “replacement” of specialists should be interpreted.
Questions for authors
  1. Assessment-changing control: With sampling, student initialization, corpus exposure, and optimization fixed, what changes when the representation teacher sees the same subset as the student rather than the full montage? Please make the referencing convention explicit so the comparison distinguishes contextual information from a reference change. This directly tests the proposed privileged-information mechanism.
  2. Clarification / assessment-changing ablation: Does aligning to an unfine-tuned backbone outperform aligning to its fine-tuned counterpart under a matched objective? Given Table 15, can the contribution be stated primarily as feature distillation plus montage sampling, or is there another demonstrated condition where the fine-tuned logit teachers are necessary? A direct experiment would strengthen the connection between the rank diagnosis and teacher assignment.
  3. Clarification / generalization uncertainty: Can you report subject-level paired intervals, or a hierarchical analysis respecting task/subject dependence, for the key specialist and held-out-layout comparisons? Please emphasize per-task absolute and chance-adjusted retention alongside the overall ratio. This would clarify whether the large gains on small cohorts and the losses on motor imagery are stable population-level trade-offs.
5 comments
AuthorsOpenReview ↗

Response to Reviewer SH37 (1/2): W1 (second and third points), Q1 and Q2 (first part), the two assessment-changing controls

Thank you for the careful review. Both assessment-changing controls are complete, so we answer them first, each W1 point with its matching question (points 3 and 2 here, point 1 next). Changes are in blue in the revised PDF.

Q1 / W1, third point. Same-subset representation teacher. Held fixed: sampling, initialization, corpus exposure, losses, optimization and seeds. Only the input of the Gram alignment teacher changes, on labeled and unlabeled steps alike, and the logit teachers keep the full montage. As in Appendix K, we write it as (electrodes, reference), with F the full montage and S the electrodes of the student.

Teacher inputGram teacher seesAverage reference computed over
(F, F), submittedall electrodesall electrodes
(S, F)the student's subset Sall electrodes, then cropped to S
(S, S)SS only

(S, F) is not fully context-free, because its reference still contains the mean of the withheld electrodes, which is why we also report (F, F) − (S, S).

Comparison30 cells Δseed-paired 95% CIsubject-level 95% CI42 layouts Δ
(F, F) − (S, F), more electrodes, same reference+0.0023[−0.0052, +0.0098][−0.0028, +0.0071]+0.0035
(S, F) − (S, S), reference change−0.0010[−0.0093, +0.0072][−0.0052, +0.0026]−0.0017
(F, F) − (S, S), no withheld information at all+0.0013[−0.0020, +0.0045][−0.0034, +0.0057]+0.0018

Neither context nor reference has a resolved effect on the 30-cell mean. Following the rule we fixed before running the controls, the privileged-information explanation and the sentence "This asymmetry is the method" are removed (Section 2.3), and the full-montage teacher remains a design choice. With four observed electrodes, the teacher's tokens at those electrodes keep a centred cosine of about 0.95 with its full-montage tokens (0.84 with the within-subset reference; about 0.99 at sixteen). Across budgets the difference grows as electrodes are removed, in the direction the mechanism predicts (+0.0053 for (F, F) − (S, S) at four electrodes, four of five seeds), but it is not resolved, and we report it as exploratory (Appendix K). On the 42 layouts, (F, F) − (S, F) has a subject-level interval excluding zero with five seeds but not ten, and a seed-paired one including zero in both.

Q2, first part / W1, second point. Never-fine-tuned versus fine-tuned alignment teacher. Under a matched objective we aligned the student to the same backbone before versus after task fine-tuning (each fine-tuned teacher on its own task), in the three settings below, five seeds each, paired with the existing runs. Held fixed: data, student and its initialization, losses and their weights, montage sampler, training steps, selection rule and seeds. Only the alignment teacher changes; on corpus batches of the full recipe it is the fine-tuned teacher of the same paradigm, a rule fixed before running.

Comparison (never-fine-tuned minus fine-tuned)30 cells Δseed-paired 95% CIsubject-level 95% CI42 layouts Δ
Gram, feature-only without corpus (primary)−0.0042[−0.0143, +0.0060][−0.0165, +0.0080]−0.0065
Gram, full recipe+0.0001[−0.0117, +0.0119][−0.0073, +0.0060]−0.0039
LaBraM, full recipe−0.0082[−0.0144, −0.0020][−0.0231, +0.0066]−0.0009

No arm resolves an advantage for the never-fine-tuned teacher, so under a matched objective we found no evidence that it is the better target on these tasks. For LaBraM the estimate favours the fine-tuned teacher across seeds but not across subjects or on validation (−0.0004). Following the rule we fixed before running the controls, the claim that a never-fine-tuned teacher is required is removed, and the second contribution becomes these matched controls (Section 3.5, Appendix K). Gram's own effective rank falls after fine-tuning on some tasks but not others (Mumtaz 61 to 3.4, HMC 53 to 54; Appendix K), whereas LaBraM's falls on all eight (Table 12). A student aligned to a fine-tuned teacher does inherit its compression (student effective rank lower by 12 to 55 across the three pairs, on all fifteen seed pairs), but a linear probe on tasks not used in distillation shows no resolved transfer cost (+0.0047 [−0.0086, +0.0179] for the primary pair). We added the rule excluding a task on which every student is at chance on validation after a one-seed check; keeping that task gives +0.0013 [−0.0066, +0.0092]. We therefore present the rank analysis as an observation, not as evidence that a fine-tuned teacher is an inferior target, which is the point of your W1.

Ten seeds. As fixed before the runs for unresolved results, the two primary comparisons, (F, F) − (S, F) and the feature-only Gram comparison, were extended to ten seeds: +0.0018 [−0.0039, +0.0075] and −0.0028 [−0.0105, +0.0049], decisions unchanged (Appendix K).

Continued in the next comment (2/2).

AuthorsOpenReview ↗

Response to Reviewer SH37 (2/2): W1 (first point) and Q2 (second part) on logit teachers, W2 and Q3

Q2, second part / W1, first point. Logit teachers. We accept the framing. The contribution is now stated as feature distillation plus montage sampling (abstract, contribution 2, Section 3.5). Logit distillation stays in the recipe as specified, and its aggregate increment remains unresolved (+0.0028 over five seeds, Table 15). Per task it ranges from −0.0198 (MentalArith) to +0.0184 (ADFTD), and no task remains significant after correction for eight tests, so we report these values as exploratory (Appendix G.2) and do not claim a condition in which the fine-tuned logit teachers are necessary.

W2 / Q3. Subject-level uncertainty and per-task costs. We resampled test subjects within each task (10,000 draws, each draw shared by all cells, arms and seeds of that task, stratified by class where labels are subject-level). TUEV is resampled by its 158 recordings because the official evaluation set does not identify patients, so its interval is recording-level.

ComparisonΔ BASubject 95% CIChance-adjusted retention
Student vs 8 sampled specialists, 30 cells−0.0100[−0.0235, +0.0049]96.4% [91.7, 101.9]
Same, 42 held-out layouts−0.0255[−0.0452, −0.0046]89.0% [81.5, 97.9]
Sampling vs no sampling (student), 42 layouts+0.0528[+0.0365, +0.0671]

The gap to the sampled specialists lies within subject-level uncertainty on the 30 cells and is resolved on the layouts, while the sampling gain is robust. For BCI IV 2a (2 test subjects), SEED-V (3) and CHB-MIT (4) we give no interval and list per-subject differences instead (Appendix P). CHB-MIT improves for all four subjects and BCI IV 2a declines for both, which we describe as results on these cohorts rather than population-level trade-offs. On the remaining points of W2:

  • The headline now gives the absolute gap and chance-adjusted retention (0.029 and 90% against the per-cell specialists, 0.010 and 96% against the sampled specialists), and Table 1 shows both per task.
  • Seed-paired and subject-level intervals are reported separately, and the t over 42 layouts is no longer used for inference.
  • Other task families. We applied the matching head of MoRSE and of the LaBraM specialists, unchanged and with nothing fitted, to three cohorts outside sleep (Appendix Q). On neonatal seizure detection (Helsinki, 34 neonates, CHB-MIT head), the montage-sampled specialist transfers weakly (balanced accuracy 0.58 to 0.60) and MoRSE barely (0.52), 0.060 to 0.075 below it on all five seeds, with subject-level intervals that exclude zero. On depression (TRDEP, 47 subjects labelled under DSM-5; ds003478, 121 subjects labelled by questionnaire), neither MoRSE nor either specialist is resolved above chance in any condition; only the student trained without sampling is, slightly, at four electrodes on TRDEP (0.532). On the two sleep cohorts MoRSE is above the sampled specialist on ISRUC (+0.048 to +0.083) and within 0.016 of it on P2018. Transfer is therefore established for sleep only, and Appendix J.3 and Appendix Q state the neonatal result as a measured cost of the shared student relative to the specialist.
  • "Replace" is narrowed to a measured trade-off between accuracy and stored parameters.

We hope these results address your concerns, and we would be glad to clarify any remaining point.

AuthorsOpenReview ↗

Gentle follow-up to Reviewer SH37, with a brief summary

Dear Reviewer SH37,

Thank you again for your careful review, and in particular for identifying the two assessment-changing controls. Both are complete, and their results changed how the paper explains the method. The revised PDF, with changes in blue, adds Section 3.5 and Appendices K to Q, including 19 new tables and 3 new figures. Below is a brief summary of the parts that answer your review, and the full answers are in our two responses above.

  • Q1 / W1, third point. Same-subset teacher. With sampling, initialization, corpus, losses and seeds fixed, the full-montage teacher was not resolved from a teacher that sees only the electrodes of the student on the 30 cells (+0.0023 [−0.0052, +0.0098], and +0.0018 with ten seeds), and the change of reference had no resolved effect either. We therefore removed the privileged-information explanation and keep the full-montage teacher as a design choice (Section 2.3, Section 3.5, Appendix K, Tables 20 and 21).
  • Q2, first part / W1, second point. Never-fine-tuned teacher. Under a matched objective, no comparison resolved an advantage for the never-fine-tuned teacher, so the claim that it is required is removed. Effective rank remains an observation that motivated the choice of alignment teacher, not evidence that a fine-tuned teacher is an inferior target (Section 3.5, Appendix K, Tables 20, 22 and 23).
  • Q2, second part / W1, first point. Logit teachers. As you suggested, we now attribute the gains to feature alignment and montage sampling. The per-task values of logit distillation are reported as exploratory, and we do not claim a condition in which the fine-tuned logit teachers are necessary (Appendix G.2).
  • W2 / Q3. Subject-level uncertainty and per-task costs. Subject-level intervals for the key comparisons are in Appendix P (Tables 34 to 37), and Table 1 now adds per-task chance-adjusted retention next to the absolute differences. "Replace" is narrowed to a measured trade-off between accuracy and stored parameters, and zero-shot transfer is stated as established for sleep staging only (Appendix J.3, Appendix Q, Table 38, Figure 18).

The discussion phase closes on November 18 (AoE). If you have any further questions or concerns, we would be glad to discuss them before then. If these results address your concerns, we would be grateful if you would take them into account in your final assessment.

Best regards, The Authors

Reviewer_59iZOpenReview ↗
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2
Confidence
3
Informativeness
2
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Paper summary

MoRSE distills task-specific EEG foundation-model experts into a single 1.97M-parameter multi-task encoder designed to operate across electrode subsets. During training, the student receives a randomly sampled subset of electrodes, while frozen teachers process the full montage. The objective combines supervised classification, logit distillation from fine-tuned experts, and per-slot representation alignment to a never-fine-tuned backbone. The authors evaluate eight tasks across 30 task-by-electrode-budget cells, seven held-out hardware layouts (42 eligible task-layout pairs), and two external sleep-staging cohorts. Across the 30 cells, MoRSE trails the per-cell LaBraM specialists by 0.0291 balanced accuracy while using 89× fewer deployed parameters. Montage sampling improves accuracy on the held-out layouts by 0.0528 over the corresponding no-sampling student. Ablations attribute the resolved distillation benefit primarily to representation alignment; logit distillation is not separable from zero in the reported experiments.

Critical strengths
  1. The paper evaluates a practical deployment setting: one shared model across multiple tasks and electrode configurations. Comparisons with per-cell specialists, retrained neural and foundation-model baselines, interpolation, montage sampling, and external sleep cohorts make the accuracy-versus-deployment-cost tradeoff concrete.
  2. The ablations separate the effects of montage sampling and distillation, and further isolate the loss terms. They show that representation alignment improves over the supervised student in the tested setup, while logit distillation does not provide a resolved benefit. The paper also clearly discusses limitations, including EEGNet’s competitive performance, the restricted scope of electrode robustness, and the lack of calibration improvement under electrode loss.
Critical weaknesses
  1. The comparison with compact supervised models does not establish how MoRSE compares with alternative compact multi-task architectures. The paper does include a supervised version of the same 1.97M student with montage sampling. This is useful evidence that alignment helps this particular student, but the paper does not report a TCN-style or other independently designed compact supervised multi-task encoder under the same evaluation protocol. EEGNet provides relevant context but is trained per task. Excluding BCI IV 2a reverses the eight-task ordering. Thus, the EEGNet result does not answer whether a shared compact supervised model with a different architecture could match MoRSE.
  2. The “full-montage representation inference” interpretation is stronger than the direct alignment supervision supports. The alignment loss matches teacher tokens only at electrode positions observed by the student; teacher tokens for withheld positions are discarded. Full-montage context can influence the teacher tokens at observed positions, but the objective does not directly supervise the student’s representations at missing positions. The paper reports representation-retention and retrieval analyses, and it tests an auxiliary completion head, but it does not report a direct measure of how well student tokens encode or predict missing-position teacher representations. Moreover, held-out layout evaluations use the layout electrodes that overlap with each task’s montage, requiring at least three overlapping sites. The paper does not quantify performance when an electrode identity outside the student’s vocabulary must be mapped to its nearest known site. These results support robustness to tested subsets and layouts, while leaving the broader representation-recovery and novel-electrode claims less directly established.
Questions for authors
  1. Table 4 includes a supervised version of the shared 1.97M student with montage sampling. Can you compare MoRSE with a compact TCN-style multi-task encoder, or another independently designed compact supervised architecture, using the same data splits, electrode-sampling protocol, and a comparable tuning budget? This would show whether the observed benefit extends beyond the selected student architecture.
  2. Can you report a direct measure of how much information about withheld electrodes is retained in the student representations—for example, prediction of withheld teacher tokens from the student’s observed-position tokens? The completion-head ablation reports its effect on downstream accuracy, but a token-prediction metric would more directly support the claim that the student infers the full-montage representation.
  3. Can you quantify how performance changes when an electrode identity is unavailable in the student’s vocabulary and must be mapped to a nearby known site? A controlled evaluation using held-out electrode identities and increasing mapping distances would clarify the scope of the layout-robustness claim.
  4. The paper discusses HEAR and LUNA as architecture-level approaches to montage heterogeneity. Could you evaluate a public LUNA checkpoint, and HEAR if a suitable checkpoint is available, on overlapping tasks and layouts under a comparable fine-tuning or linear-probe protocol? LUNA’s public model card provides checkpoint and fine-tuning information (LUNA model card). If a fair comparison is infeasible, please clarify the specific constraints. Such a comparison would contextualize MoRSE’s accuracy and deployment cost relative to models designed for heterogeneous electrode layouts.
5 comments
AuthorsOpenReview ↗

Response to Reviewer 59iZ (1/2): W1, Q1 and Q4

Thank you for the detailed review. We answer each weakness (W) and question (Q) below. Changes are in blue in the revised PDF.

W1 / Q1. Independent compact multi-task encoder. We agree that the supervised version of our own student does not answer this. We added a dilated TCN designed independently of LaBraM, with temporal convolutions shared across electrodes, one 200-d token per second, an electrode-identity embedding, mask-aware mean mixing across electrodes and one linear head per task. Held fixed between MoRSE and the sampled TCN: data splits, montage sampler, training steps, task sampling, label smoothing and the selection rule (mean validation balanced accuracy over the 30 cells); arms without sampling select on the full-montage cells, the only ones they train on. Size (1.18M, 2.02M or 2.87M parameters) and learning rate (three values) were chosen on validation at seed 0, a tuning budget no smaller than our student's, followed by five seeds.

Shared model, 8 tasks, mean of 5 seedsParams30 cells42 layouts
TCN, supervised, no sampling2.02M0.56940.5526
TCN, supervised, sampling2.02M0.56930.5653
TCN + our alignment and corpus, sampling2.02M0.60410.5796
Transformer from scratch, supervised, sampling1.97M0.54260.5434
MoRSE1.97M0.60440.5670

On the 30 cells MoRSE exceeds the supervised TCN with sampling by +0.0351 (seed-paired 95% CI [+0.0218, +0.0485], all five seeds; subject-level [+0.0112, +0.0592]); on the 42 layouts the difference is not resolved (+0.0017 [−0.0103, +0.0136]). Adding our alignment and unlabeled corpus to the same TCN, without logit distillation, raises it by +0.0348 [+0.0210, +0.0486] on the 30 cells and +0.0143 [+0.0026, +0.0261] on the layouts, on all five seeds. This TCN is then not resolved from MoRSE on the 30 cells (MoRSE − TCN +0.0003 [−0.0093, +0.0100]) and is ahead of it on the layouts by 0.0126 [0.0050, 0.0203]. We therefore attribute the gains to the training recipe, feature alignment with montage sampling, rather than to the LaBraM-initialized Transformer (Appendix L, Section 3.2). LaBraM initialization still matters for that Transformer: trained from scratch with labels and sampling it trails the TCN, and initializing it from LaBraM adds +0.0231 [+0.0030, +0.0431] on the 30 cells.

On EEGNet, we agree that it is a per-task baseline whose eight-task ordering depends on BCI IV 2a (Appendix D.3). One EEGNet per task trained with the same montage sampler and the paper's hyperparameters, over five seeds, reaches 0.5049 on the 30 cells and 0.4194 on the layouts with a presence mask as a second input plane, and 0.5368 and 0.4857 with missing electrodes filled with zeros, still below MoRSE by 0.0676 [0.0567, 0.0784] and 0.0813 on all five seeds. Its full-montage accuracy on BCI IV 2a falls from 0.7068 to 0.41 and 0.51, so under this protocol, which reuses the paper's hyperparameters, the sampled EEGNet does not retain that lead (Appendix L).

Q4. LUNA and HEAR. We fine-tuned the public LUNA-Base checkpoint (7.1M parameters) on each task with a recipe adapted from its released one, with the epoch chosen by validation balanced accuracy as for every model here and the learning rate chosen on validation from three values, with and without our montage sampler, over five seeds, and scored it on the same 30 cells and 42 layouts. MoRSE, one 1.97M model against eight LUNA models of 56.8M in total, is ahead of the sampled LUNA by +0.0697 [+0.0558, +0.0835] on the 30 cells and +0.0404 [+0.0316, +0.0492] on the layouts, and of LUNA trained on the full montage by +0.0951 and +0.0825, on all five seeds in each case. Excluding TUEV, which LUNA's pre-training corpus may contain, leaves the gap to the sampled LUNA on the cells at +0.0754. Per task, the sampled LUNA is ahead of MoRSE on HMC and Mumtaz and behind on the other six. Montage sampling also raises LUNA, by +0.0254 [+0.0023, +0.0485] on the cells and +0.0420 [+0.0296, +0.0545] on the layouts. Because the recipe counts epochs, our six smallest tasks get only about 100 to 800 optimizer steps, so we repeated them with batch 32, eight times the steps. This changed the sampled LUNA by +0.0095 [−0.0049, +0.0239] on the cells, and on BCI IV 2a its training loss stayed close to chance with either batch size. We did not identify the cause, so these BCI IV 2a numbers need not be the best LUNA can reach. With the batch size chosen per task on validation, MoRSE remains ahead of the sampled LUNA by +0.0625 [+0.0536, +0.0714] on the cells and +0.0303 [+0.0195, +0.0411] on the layouts, on all five seeds. Table 2 gains a LUNA-Base row (TUEV marked †), and Appendix O gives the protocol and per-task results. For HEAR we found no public pre-trained checkpoint, so a comparison from its pre-trained weights was not possible (Appendix A).

Continued in the next comment (2/2).

AuthorsOpenReview ↗

Response to Reviewer 59iZ (2/2): W2, Q2 and Q3

W2. What alignment supervises. We agree. Equation 10 matches teacher tokens only at the electrodes the student observes, and tokens at withheld positions are discarded. We rewrote the first contribution and Section 2.3 to describe exactly this, and the paper, including the abstract, no longer states that the student infers the full-montage representation.

Q2. Direct measure of withheld-electrode information. We added this measurement (Appendix M). A probe of 0.23M parameters, the same for every encoder, reads the frozen student's tokens at the observed electrodes together with a query for a withheld electrode and time step, and predicts the teacher's token there. It is fitted on training subjects, selected on validation subjects and scored on test subjects, and teacher tokens serve only as targets. Over the cells with withheld electrodes, the cosine between predicted and teacher tokens, each centred per electrode on the test windows, is 0.515 for MoRSE (scale-adjusted R² 0.28), against 0.175 for the supervised student with sampling and 0.169 for a randomly initialized encoder, while copying the full-montage teacher's token at the nearest observed electrode, a reference no deployed model has, gives 0.383. On the seven tasks with budgets of 16, 8 and 4 electrodes it falls from 0.612 to 0.538 and 0.427, and on HMC, the only two-electrode cell, it is 0.274. We centre on the test windows because the probe's loss leaves an arbitrary offset in its output. With the training-set centring of our original protocol, MoRSE, the supervised student, the random encoder and the nearest copy give 0.343, 0.111, 0.089 and 0.331, so the ordering holds but the margin over the nearest copy is small. The student aligned without montage sampling, however, gives 0.527, not resolved from MoRSE (+0.013 [−0.012, +0.037]), and the teacher itself, read by the same probe from the observed electrodes only, gives 0.573. Following the rule we fixed before running the probe, we therefore attribute this information to feature alignment rather than to montage sampling, and we no longer say that the student infers the withheld electrodes. Adding the completion term of Appendix I raises the probe value by 0.035 on all five seeds, yet that term did not raise accuracy in our ablation, so more decodable information about withheld electrodes did not translate into accuracy. We report all of this as decodable information and do not claim that the classifier relies on it; showing that would require an intervention on the representation, which we list as future work.

Q3 and the three-site condition. We ran the evaluation you describe, with held-out identities and increasing mapping distance. We retrained MoRSE over five seeds with four electrodes (F3, Cz, P4 and O1, one per region) withheld from the student during distillation and checkpoint selection, which Appendix N calls the withheld model. Their identity embeddings come from LaBraM pre-training, which has probably seen these sites, and received no gradient. At test time their signals are either left out or given the identity of a trained site 26 to 38 mm away (nearest 10-10 site), 56 to 74 mm away (nearest 10-20 site) or 106 to 192 mm away. On the 23 of the 30 cells that contain them, mapping lowers balanced accuracy relative to leaving them out by 0.0095, 0.0268 and 0.0694 at the three distances, on all five seeds each. On the 30 of the 42 layouts that contain them, the nearest mapping is not resolved from leaving them out (+0.0021 [−0.0044, +0.0086]) and the two farther ones are worse. With these electrodes left out, the withheld model trails MoRSE by 0.0071 [0.0008, 0.0135] on the cells that contain them, close to what MoRSE itself loses when they are left out (0.0076), although the experiment does not isolate identity exposure (Appendix N). Remapping electrodes the student did see in training, one at a time, leads to the same conclusion: leaving the electrode out was better than every mapping, and the farthest mapping did the most harm, also when all of them are remapped at once. Appendix J.3 therefore advises leaving an electrode outside the vocabulary out rather than mapping it, states that layout results require at least three electrodes shared with the task montage, and separates what is validated (unseen subsets and layouts of vocabulary electrodes, with the measured effect of identities withheld from distillation) from what is not (new coordinates, references and acquisition systems).

Q4, cost. Table 11 now includes LUNA-Base: one window takes 9.7 ms on one CPU core, against 5.9 ms for MoRSE.

We hope these results address your concerns, and we would be glad to clarify any remaining point.

AuthorsOpenReview ↗

Gentle follow-up to Reviewer 59iZ, with a brief summary

Dear Reviewer 59iZ,

Thank you again for your detailed review, and in particular for suggesting a concrete experiment with each of your four questions. We followed these suggestions, and together they made the paper more precise about what the alignment supervises and where the method applies. The revised PDF, with changes in blue, adds Section 3.5 and Appendices K to Q, including 19 new tables and 3 new figures. Below is a brief summary of the parts that answer your questions, and the full answers are in our two responses above.

  • W1 / Q1. Trained with labels and the same montage sampler, an independently designed TCN is 0.035 below MoRSE on the 30 cells (not resolved on the 42 layouts). Our alignment and corpus raise that TCN on the 30 cells by 0.035 on average, with a gain on all five seeds, so we attribute the gains to the training recipe rather than to our student architecture (Section 3.2, Appendix L, Tables 24 and 25). One EEGNet per task trained with the same sampler is at least 0.067 below MoRSE on the cells and 0.081 on the layouts (Table 26).
  • W2 / Q2. Section 2.3 and the first contribution now describe exactly what the alignment supervises, and the paper no longer says that the student infers the full-montage representation. A token-prediction probe shows that aligned students predict withheld teacher tokens far better than supervised or random encoders, which we attribute to alignment rather than to sampling (Appendix M, Table 27, Figure 16).
  • Q3 and the three-site condition. With four electrode identities withheld in training, no mapping to a trained site resolved a gain over leaving the electrode out, and the loss grows with the mapping distance (Appendix N, Tables 28 to 30, Figure 17). Appendix J.3 now states that such an electrode should be left out, that layout results require at least three electrodes shared with the task montage, and which conditions remain untested.
  • Q4. The public LUNA-Base checkpoint, fine-tuned per task with our montage sampler, is below MoRSE by 0.070 on the cells and 0.040 on the layouts, on all five seeds (Table 2, Figure 5, Appendix O, Tables 31 to 33), and Table 11 adds its CPU latency. We found no public pre-trained checkpoint of HEAR (Appendix A).

The discussion phase closes on November 18 (AoE). If you have any further questions or concerns, we would be glad to discuss them before then. If our responses have addressed your concerns, we would be grateful if you would take them into account in your final assessment.

Best regards, The Authors

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response and summary of revisions (1/2)

We sincerely thank the reviewers for their time and careful, constructive reviews, and the Area Chair for overseeing the review process. The additional controls prompted by the reviews have helped us refine our claims and strengthen the paper. We are encouraged that the reviewers valued the practical deployment setting (59iZ, SH37, qUa7), the comparison with montage-sampled specialists (SH37, qUa7) and the ablations, including their negative findings (59iZ, SH37, qUa7). The revised PDF is uploaded, with changes in blue. Tables 1–19 and Appendices A–J keep their numbers, new material is in Section 3.5 and Appendices K–Q, and the claims we removed or narrowed are listed in the next comment (2/2). New experiments use the original splits and five seeds paired with the original runs, and the MoRSE recipe is unchanged.

Summary. Montage sampling gives a robust gain, +0.046 balanced accuracy on the 30 cells and +0.053 on the 42 held-out layouts with subject-level intervals that exclude zero, and it also raises LUNA-Base. Under the same splits and sampler, MoRSE is ahead of per-task EEGNet and per-task LUNA-Base on the cells and the layouts, and of a supervised TCN on the cells. Our alignment and corpus raise that TCN by 0.035 on average, with a gain on all five seeds, so we attribute the gains to the training recipe rather than to the student architecture. The gap of MoRSE to the eight montage-sampled specialists lies within subject-level uncertainty on the cells and is resolved on the layouts (0.026). The matched controls did not resolve an accuracy advantage for an alignment teacher that sees the full montage or was never fine-tuned. We therefore describe the method as feature alignment plus montage sampling, the teacher choices as design choices, the efficiency claim as a trade-off between accuracy and stored parameters, and external transfer as established for sleep only.

ConcernRaised byWhat we addedOutcomeWhere
Same-subset representation teacherSH37teacher given only the student's electrodes, with the full-montage or the subset referencenot resolved on the 30 cells (estimates up to +0.0023, every seed-paired interval within ±0.01, also with ten seeds); privileged-information explanation removedSec. 3.5, App. K
Never-fine-tuned vs fine-tuned alignment teacherSH37, qUa7Gram (two recipes) and LaBraM aligned before vs after fine-tuning, effective rank of Gram, transfer probeno advantage resolved for the never-fine-tuned teacher (for LaBraM the estimate favours the fine-tuned one); students inherit its lower rank without a resolved accuracy or transfer cost; rank kept as motivationSec. 3.5, App. F, K
Independent compact multi-task encoder59iZTCN, four armsMoRSE ahead of the supervised TCN by 0.035 on the cells (layouts not resolved); with our alignment and corpus the TCN is not resolved from MoRSE on the cells and ahead on the layouts; gains attributed to the recipeSec. 3.2, App. L
EEGNet with montage sampling59iZ8 tasks × 5 seeds, presence mask or zero fillingat least 0.067 (cells) and 0.081 (layouts) below MoRSEApp. D.3, L
Comparison with LUNA59iZpublic LUNA-Base fine-tuned per task, with and without sampling, two batch sizes, 5 seedsbelow MoRSE by 0.070 (cells) and 0.040 (layouts) with sampling on every seed, also without TUEV and with batch 32; sampling raises LUNA tooTable 2, Fig. 5, App. O
Information about withheld electrodes59iZtoken-prediction probe on four studentsaligned students predict withheld teacher tokens far better than supervised or random encoders, with or without sampling (difference not resolved); attributed to alignment, "infers" removedApp. M
Electrodes outside the vocabulary, references59iZ, qUa7four identities withheld in training, remapping at three distances, test-time re-referencingno mapping resolved a gain over leaving an unknown electrode out, and the loss grows with distance; re-referencing costs 0.02 to 0.04App. N, J.3
Subject-level uncertaintySH37, qUa7subject bootstrap for cells, layouts and external cohortsgap to sampled specialists within subject-level uncertainty on the cells, resolved on the layouts; sampling gain robustTable 1, Sec. 3.2–3.3, App. P
Transfer beyond sleepSH37specialists scored zero-shot on 2 sleep and 3 other cohortssleep: MoRSE above or within 0.016 of the sampled specialist; depression: MoRSE and specialists not resolved above chance; neonatal seizure: sampled specialist better (0.58 to 0.60 vs 0.52)Sec. 3.3, App. Q, J.3
Per-task costs and headroom, 89×SH37, qUa7absolute and chance-adjusted results, CPU latencyheadline now 0.029 and 90% (per-cell), 0.010 and 96% (sampled); per window MoRSE is 2.9× faster than a LaBraM specialist on one CPU coreAbstract, Table 1, Table 11

Continued in the next comment (2/2).

AuthorsOpenReview ↗

General response and summary of revisions (2/2)

Removed or narrowed claims. Following the reviewers' suggestions, we removed or narrowed the claims below, and every statement about the teachers is now tied to a matched control (Section 3.5, Appendix K).

  • "This asymmetry is the method" and the privileged-information account of the gain are removed; the full-montage teacher is described as a design choice.
  • "Teacher roles from a representation diagnosis", "a poor source of features", "fine-tuning collapses the structure that representation distillation must transfer" and "To our knowledge this consequence of fine-tuning has not been drawn before" are replaced by the matched controls of the teacher roles. The never-fine-tuned backbone is kept as a design choice rather than a requirement, and effective rank as the observation that motivated it.
  • "learns to infer the full-montage representation" (abstract), "distillation becomes inference of the full-montage representation" (first contribution, Conclusion) and "asks it to infer the contribution of the missing electrodes" (Section 2.3) are removed; the student is now described as aligned to the teacher's tokens at the electrodes it observes.
  • "retains 95% ... with 89× fewer deployed parameters" now reports the absolute gap and chance-adjusted retention, and 89× refers to stored parameters.
  • "can replace multiple task-specific foundation models" now reads as a measured trade-off between accuracy and stored parameters.
  • "an electrode outside the vocabulary is mapped to the nearest known site" and "we do not measure how performance degrades with that distance" are replaced by the measured effect of mapping and of leaving such electrodes out.
  • "A direct comparison would require pre-training each architecture" is replaced by the LUNA comparison.

Corrections. Table 5 and Appendix B.1 now report TUEV by its 158 test recordings, because its official evaluation set does not identify patients, so its intervals are recording-level. The future-work paragraph (Appendix J.4) no longer lists external cohorts as untested.

Code. The core code of the experiments added in this revision is now in the anonymous repository linked in the Reproducibility Statement, in a new folder additional_experiments/ whose README maps each file to its appendix. The method code is unchanged; only the top-level README now points to the new folder.

AuthorsOpenReview ↗

Summary of the discussion and revisions

Dear Area Chair, Senior Area Chair and Program Chairs,

Thank you for overseeing the review of our submission, and we thank the three reviewers again for their careful and constructive reviews. The revised PDF adds Section 3.5 and Appendices K to Q, with 19 new tables and 3 new figures, and changes are in blue.

Main result. One 1.97M-parameter encoder, a third the size of a single specialist, serves eight tasks spanning seizure detection, sleep staging, emotion recognition, motor imagery and dementia diagnosis.

  • Lightweight. It stores 89 times fewer parameters than the 30 per-cell specialists and needs 2.9 to 23 times less time per window on one CPU core than the foundation-model specialists.
  • Close to the specialists. It trails the per-cell specialists by 0.029 balanced accuracy, retaining 90% of their improvement over chance. Its gap to eight montage-sampled specialists, 24 times larger in aggregate, is 0.010 on the 30 cells, within subject-level uncertainty, and 0.026 on the held-out layouts, where it is resolved.
  • Robust and transferable. It transfers zero-shot to seven hardware layouts never drawn during training and to two external sleep-staging cohorts. Montage sampling adds 0.053 balanced accuracy on these layouts, with a subject-level interval that excludes zero, and 0.127 and 0.116 on the two cohorts with two electrodes.

Strengths noted by the reviewers. The three reviews list the same two strengths. On the result, 59iZ describes "a practical deployment setting: one shared model across multiple tasks and electrode configurations", SH37 "a useful deployment result tested against a strong, simple alternative", and qUa7 "a practically meaningful robustness and consolidation result, tested against relevant alternatives". On the evidence, SH37 notes "broad and carefully decomposed evidence", qUa7 "extensive, informative ablations and transparent negative findings", and 59iZ that "the ablations separate the effects of montage sampling and distillation".

Concerns and what we added.

ReviewerMain concernsWhat we added (where)
59iZan independently designed compact multi-task baseline, information about withheld electrodes, electrodes outside the vocabulary, LUNA and HEARTCN and montage-sampled EEGNet (Appendix L), token-prediction probe (Appendix M), withheld electrode identities and mapping distance (Appendix N), LUNA-Base (Table 2, Appendix O), no public HEAR checkpoint found (Appendix A)
SH37the teacher-role explanation (logit teachers, never-fine-tuned teacher, same-subset teacher), with two assessment-changing controls, subject-level uncertainty and per-task costs, transfer beyond sleepboth controls, with ten seeds for the primary comparisons (Section 3.5, Appendix K), per-task logit values (Appendix G.2), subject-level bootstrap (Appendix P), per-task chance-adjusted retention (Table 1), three cohorts outside sleep (Appendix Q)
qUa7a narrower explanation of the teacher roles, per-task costs and the meaning of 89×, references and new electrodesnarrower explanation adopted (abstract, Section 3.5, Appendix K), per-task chance-adjusted retention (Table 1), CPU latency (Table 11), limitations and measured estimates (Appendices J.3 and N)

Under the same splits and sampler, MoRSE is ahead of per-task EEGNet and per-task LUNA-Base on average over the cells and the layouts. The matched controls did not resolve an accuracy advantage for the teacher choices, so we removed the claims that depended on them, as listed in our general response (2/2), and attribute the gains to feature alignment and montage sampling. We also report one unfavourable result, on neonatal seizure transfer (Appendix Q). The core code of the added experiments is in additional_experiments/ of the anonymous repository linked in the Reproducibility Statement.

Outcome of the discussion. Two of the three reviewers, SH37 and qUa7, now favour acceptance. Both replied "Thank you for the detailed response and the revision", and SH37 raised the rating from 2 to 3. Reviewer 59iZ thanked us for the additional results and described the paper as borderline while keeping the rating, but wrote "I'm not strongly against acceptance". The remaining concerns of 59iZ were that the TCN results could not be verified without source code, and whether the additional training time and computation of distillation are worth it. In our reply, to which the reviewer has not yet responded, we linked the code and acknowledged that distillation adds training computation. For this one-time cost, MoRSE is 0.035 higher in balanced accuracy than the supervised TCN of similar size on the 30 cells, a gain that our alignment and corpus also give the TCN itself, and against the foundation-model specialists it keeps the advantages summarized above.

We would be glad to answer any further questions. Thank you again for your time and consideration.

Best regards, The Authors

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