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Under review as a conference paper at ICLR 2027

Assess Consciousness from Long-Duration EEG Monitoring via Evidence Accumulation Transformer

Abstract

Assessing consciousness in patients with severe disorders of consciousness plays a critical role in diagnosis, prognosis, rehabilitation planning, and clinical decision-making. Reliable EEG-based assessment requires long-duration monitoring to capture consciousness-related patterns that may be sparse, intermittent, and evolving. Identifying nuanced signatures of consciousness from long-duration EEG remains challenging because evidence must be localized and accumulated across the recording, while supervision is available only through subject-level diagnoses. We propose EviFormer, the Evidence Accumulation Transformer, to assess consciousness from long-duration EEG. EviAttention applies attention along time and across electrodes, then models temporal patterns of different durations through a mixture of experts. EviMemory uses gated causal convolutions to accumulate recurring evidence across EEG chunks. EviLearning supervises subject-level evidence seeking by learning representations over evidence sets. We collect a sleep EEG dataset involving 140 subjects spanning different levels of consciousness, including 60 subjects diagnosed with disorders of consciousness. Across the collected cohorts and public datasets, EviFormer achieves state-of-the-art or competitive performance, while attribution analyses highlight delta-band and temporal evidence together with long-range anterior–posterior and bilateral electrode patterns.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Disorders of consciousness, Long-duration EEG modeling

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_ssDuOpenReview ↗
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Paper summary

The paper presents EviFormer for subject-level consciousness assessment from long-duration EEG, combining temporal/spectral embeddings, multi-scale attention, gated causal convolutions (EviMemory), and weakly supervised subject-level learning. Results are reported on two linked clinical cohorts and four public Alzheimer’s disease EEG datasets.

The clinical motivation and reported results are promising. However, the current evidence does not adequately separate long-range temporal modeling from the accumulation of local EEG information, and the fairness of key baseline comparisons remains uncertain. Stronger mechanism controls, MIL comparisons, and more transparent external validation would substantially strengthen the submission.

Critical strengths

1、Clinically meaningful task with a plausible motivation for accumulating intermittent EEG evidence. 2、A valuable self-collected clinical cohort and broad comparisons across EEG and time-series models. 3、Ablations, context-length analysis, synthetic sequence tests, and physiological interpretation are provided.

Critical weaknesses
  1. Limited Receptive Field of EviMemory Figure 2 indicates that MMSE-140 performance is strongest with roughly 30–60 minutes of EEG history, while EviMemory uses two causal convolutions with a local receptive field of seven 30-second chunks (3.5 minutes). Why was this setting chosen? Would longer receptive fields or larger dilations improve performance? Note that the model still aggregates the full history through cumulative averaging.
  2. Temporal Modeling versus Evidence Aggregation Table 2 shows a benefit from EviMemory over chunk-level mean pooling, but this could arise from improved local temporal features rather than long-range dependencies. Likewise, the history-length gains in Figure 2 might reflect the availability of more EEG evidence. The synthetic ordering task in Appendix D can potentially be solved using local transition patterns. Please compare history-length curves with and without EviMemory and consider controlled temporal-order perturbations.
  3. Baseline Reproduction and Evaluation Fairness ADformer, LEAD, and other established EEG models perform substantially below values reported in previous studies on the same underlying public datasets. The original protocols are not directly comparable, but the manuscript does not adequately explain these gaps. Please document official implementations, checkpoints, input adaptation, training budgets, and hyperparameter tuning, and clarify the reasons for the discrepancies.
  4. Missing External DoC Validation Despite Available Public Data Although publicly accessible UWS/MCS EEG datasets have been reported (e.g., Bai et al., NeuroImage 2021), the DoC assessment is evaluated only on the authors’ cohort, while the public-data experiments focus on Alzheimer’s disease. Why were existing public DoC datasets not considered for external validation? The authors should clarify whether recording duration, electrode montage, acquisition protocols, or access restrictions prevent their use. Even if these datasets are unsuitable for evaluating long-duration accumulation, shorter-context external validation could still test cross-cohort generalization.
Questions for authors

Q1. EviMemory's effective receptive field is only ~3.5 minutes, much shorter than the 30–60 minute history window where performance peaks, and full history is aggregated by cumulative averaging. This makes it unclear whether the gains in Figure 2 come from long-range temporal modeling or simply from accumulating more local EEG evidence. Could you provide history-length curves with and without EviMemory, plus a controlled test (e.g., shuffling chunk order) to show whether global temporal order actually matters? Q2. ADformer, LEAD, and other baselines score well below previously reported results on the same public datasets, and the paper does not explain this gap. Please clarify whether official implementations/checkpoints were used, how inputs were adapted, and whether tuning budgets were comparable — do the relative rankings still hold under fair re-tuning?

2 comments
AuthorsOpenReview ↗

Response to Reviewer ssDu

R1. Choice of local receptive field (Weakness 1).

Thanks for your helpful comments. We use a local receptive field of 3.5 minutes to extract patterns across adjacent chunks. Increasing the receptive field produced no significant improvement in our experiment.

The model can still aggregate the 30–60 minutes of history shown in Figure 2 with this 3.5-minute local receptive field. The write gate controls how local information updates the current representation, while the running mean accumulates all updated representations up to the current time. The recording can therefore continue to grow while each step retains a bounded historical state.

We added an experiment on MMSE-140 that progressively increased the number of causal convolutional layers with dilation 2. Expanding the local receptive field to 11.5 minutes produced no significant improvement, supporting the two-layer configuration.

Convolutional layersLocal receptive field (chunks)Local receptive field (minutes)MMSE BAccMMSE AUROC
273.5.6650 ± .0798.6874 ± .0862
3115.5.6646 ± .0793.6877 ± .0862
4157.5.6630 ± .0797.6876 ± .0861
5199.5.6636 ± .0783.6876 ± .0856
62311.5.6651 ± .0786.6879 ± .0857

R2. Observation length and sensitivity to chunk order (Weakness 2, Question 1).

Thanks for your helpful comments. The results indicate that accumulating local EEG evidence can explain the benefit of longer observation periods.

To examine the respective roles of observation duration and EviMemory, we compared mean BAcc and AUROC with and without EviMemory at ten durations on MMSE-140. M denotes EviMemory.

Observation duration (minutes)BAcc w/ MAUROC w/ MBAcc w/o MAUROC w/o M
0.5.530.548.513.520
2.587.597.525.553
4.591.610.540.566
8.611.638.542.583
16.635.688.579.612
30.650.684.584.612
45.654.691.594.614
60.648.698.602.618
90.645.696.603.618
120.639.692.602.617

Extending the observation period from 0.5 to 60 minutes increased AUROC from .548 to .698 with EviMemory and from .520 to .618 without it, demonstrating the benefit of using a longer EEG history. EviMemory achieved higher mean values for both metrics at all ten durations, supporting the contribution of the memory module.

AuthorsOpenReview ↗

Response to Reviewer ssDu

R3. Baseline implementation, tuning, and comparability (Weakness 3, Question 2).

Thanks for your helpful comments. Differences in experimental settings can explain the performance gaps. The original LEAD study pretrained on multiple external datasets before downstream fine-tuning. Except for APAVA, which used a fixed split, it used 5 random seeds and assigned 80%, 10%, and 10% of subjects to training, validation, and testing, respectively.

ADformer's subject-independent experiments on ADSZ and ADFD assigned 60%, 20%, and 20% of subjects to these sets.

We trained LEAD and ADformer from scratch within each task dataset, evaluated them on held-out subjects, and reported mean BAcc and AUROC across 10 repetitions of subject-wise five-fold cross-validation.

R4. External validation on shorter DoC recordings (Weakness 4).

Thanks for your helpful comments. We did not include this dataset because its acquisition setting differs from long-term bedside monitoring. Each recording contains 10 minutes of resting-state EEG, which supports evaluation within that duration. Assessing evidence accumulation beyond 10 minutes requires longer recordings. In addition, the data from Bai et al. (2021) are no longer publicly accessible, and we are contacting the authors to obtain them.

Reviewer_atYPOpenReview ↗
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Paper summary

This paper proposes to analyze the level of consciousness in patients with Disorders of Consciousness (DoC) using long EEG recordings. The main challenge lies in the fact that the key patterns in signals are highly sparse and unpredictable, while annotations are provided only at the subject level rather than for individual EEG segments. The authors propose an EviFormer, which consists of four components. The authors curated a clinical sleep EEG dataset comprising 140 individuals, including 60 patients with DoC. EviFormer achieved SOTA performance across two in-house tasks and four public datasets related to Alzheimer’s disease.

Critical strengths
  1. The research addresses a clinically significant problem.
  2. The dataset represents the study's most substantial contribution. It comprises clinical sleep EEG data from 140 individuals. Such datasets are scarce and hold genuine practical value for the field.
  3. The evaluation rubric is rigorous. It employs a subject-wise five-fold cross-validation repeated 10 times, using a corrected repeated k-fold t-test.
  4. The paper is easy to follow.
Critical weaknesses
  1. The technical novelty is limited. Each module in the proposed method is essentially an existing method. For example, the dual-path patch encoding is similar to that used in LaBraM and CBraMod.
  2. The results on public datasets are suspiciously good.
  3. The two tasks overlap significantly, introducing confounding factors.
  4. The sample size is small, and the clinical conclusions are weak.
  5. The memory mechanism is not convincing.
Questions for authors

Please kindly refer to weakness.

2 comments
AuthorsOpenReview ↗

Response to Reviewer atYP

R1. Technical contribution relative to LaBraM and CBraMod (Weakness 1).

Thanks for your helpful comments. Relative to LaBraM and CBraMod, our technical contribution is to update representations across chunks through gating and learn both their means and distributions under subject-level diagnostic supervision.

For encoding, LaBraM trains a discrete tokenizer through spectrum prediction and then predicts the discrete codes of masked patches. CBraMod adds the temporal and spectral embeddings of each patch (its Eq. 3) and models temporal and electrode dependencies separately. EviEmbedding concatenates waveform and log-amplitude spectral representations and projects them into a fused representation (Eqs. 1–2). EviAttention then extracts local patterns within each chunk using windows of different durations. These design choices support our focus on long-duration EEG modeling.

Our contribution addresses how to update predictions as a long recording progresses and use differences among a subject's chunk representations when only subject-level diagnoses are available. EviMemory generates candidate updates from neighboring chunks, regulates each feature through a write gate, and computes a running mean of the updated representations. This mean predicts the subject's diagnosis, while the constituent representations also contribute to training. EviLearning treats them as an empirical distribution for each subject and uses maximum mean discrepancy (MMD) to compare subjects, encouraging distributions from the same class to be closer. Thus, even when two subjects have similar mean representations, the objective can use differences in their distributions. The original LaBraM and CBraMod methods did not propose this combination of gated cross-chunk updates and subject-level distributional supervision.

R2. Interpretation of performance on public datasets (Weakness 2).

Thanks for your helpful comments. EviFormer achieves BAcc/AUROC of .979/.997 on ADSZ and .842/.916 on ADFSU. Evaluation uses subject-wise splits within each dataset.

Learning a diagnosis from the full recording offers a possible explanation for EviFormer's advantage. EviMemory first updates representations using neighboring chunks, aggregates them across the recording, and supervises the resulting prediction with the subject's diagnosis. Group differences that are difficult to identify in a single short chunk can therefore jointly influence the diagnostic score when they recur across multiple intervals.

R3. Cohort overlap and potential confounding (Weakness 3).

Thanks for your helpful comments. The two tasks are trained and evaluated separately using their respective labels. DoC diagnoses are not provided as inputs to the MMSE classifier. This prevents the correlation between the task labels from directly entering the MMSE predictions through the DoC labels.

The tasks address complementary clinical questions that have also been studied in related literature. Bodien et al. (NEJM, 2024) found that, among 241 patients who did not exhibit command-following during bedside assessment, 60 (25%) exhibited command-following in task-based EEG or fMRI. The same team also found that severe cognitive impairment can persist after emergence from MCS (NeuroRehabilitation, 2020). These findings illustrate the distinct clinical questions addressed by the two assessments.

AuthorsOpenReview ↗

Response to Reviewer atYP

R4. Cohort size and scope of the clinical conclusions (Weakness 4).

Thanks for your helpful comments. Collecting EEG data from patients with disorders of consciousness is challenging, and long-duration bedside monitoring requires extended recording time for each patient. Establishing a bedside EEG cohort of more than 100 participants therefore requires substantial data-collection effort. Our consciousness-state task includes 60 DoC patients, comprising 21 UWS and 39 MCS/EMCS patients. The cognitive screening task includes 140 participants with MMSE scores, comprising 90 with zero scores and 50 with positive scores.

Using these data, we conducted quantitative and qualitative experiments to evaluate classification performance and examine EEG features associated with the predictions. We also invited clinicians from a Grade III, Class A hospital to review the waveform interpretations of representative EEG segments and assess their consistency with clinical observations.

R5. Mechanism and contribution of EviMemory (Weakness 5).

Thanks for your helpful comments. We would like to highlight how EviMemory forms subject-level predictions through local contextual updates, selective writing, and accumulation across chunks. Equation 8 uses two causal convolutional layers to generate candidate updates from the current chunk and up to six preceding chunks, allowing the current representation to incorporate information from neighboring intervals. Equations 9–10 regulate each feature of the candidate update through a write gate and bound the update magnitude. This allows features from different chunks to influence the updated representations to different degrees while preserving information from the current chunk and preventing historical updates from dominating it. Equation 11 then computes a running mean of all updated representations up to the current time, progressively accumulating locally contextualized information into the subject-level representation. As the recording grows, the model can therefore use task-relevant patterns that recur over a longer observation period. Although the final aggregation uses a mean, the preceding contextual updates and gating allow the original chunks to contribute differently to the prediction.

Table 2 directly tests this mechanism. Replacing EviMemory with direct mean pooling reduces DoC BAcc from .737 to .626 and AUROC from .761 to .704. For MMSE, BAcc decreases from .650 to .584 and AUROC from .684 to .612.

Reviewer_LenDOpenReview ↗
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Paper summary

The paper addresses EEG-based consciousness assessment in DoC patients from long-duration recordings, where relevant signatures are sparse and intermittent and supervision exists only at the subject level. The proposed EviFormer splits recordings into 30-second chunks and has three components. EviAttention encodes each chunk with attention along time and across electrodes plus a multi-scale mixture of experts. EviMemory aggregates chunk embeddings into a subject-level prediction using gated causal convolutions. EviLearning combines self-supervised pretraining, which predicts handcrafted EEG features of future chunks, with a subject-level loss that aligns chunk-representation distributions by diagnosis. The authors collect a 140-subject sleep-EEG cohort including 60 DoC patients and evaluate UWS vs. MCS and MMSE = 0 vs. > 0 classification, along with public datasets, using repeated subject-wise cross-validation. EviFormer is reported to achieve state-of-the-art or competitive results, and attribution analyses highlight delta-band, temporal, anterior–posterior and bilateral patterns.

Critical strengths

The problem is clinically important and the setup is realistic. Behavioral assessment of DoC patients is unreliable, and an EEG tool that separates UWS from MCS would matter for prognosis and treatment decisions. I like that the authors work with long recordings and subject-level labels only, since that is how the data actually look in the clinic, rather than the usual short-epoch classification setup.

The dataset is a real contribution. 140 subjects with long sleep EEG, 60 of them DoC patients, is a decent cohort for a population that is hard to recruit and record. The code is also provided, which made it possible to check how the pipeline actually works. If the data can be released properly (de-identified, with appropriate approval), it could be useful to others since public DoC EEG data is scarce. That said, its value depends on how the release is handled, so it does not outweigh my concerns about the method and evaluation.

Critical weaknesses

The paper's premise is that consciousness-related signatures in long EEG recordings are sparse, intermittent events that need to be found and accumulated. This premise is assumed rather than shown. The paper gives no evidence, from the literature or from its own data, that such events exist or that they are what separates UWS from MCS. Many established EEG markers of DoC (spectral power, complexity, connectivity, sleep organization) are relatively global properties of a recording rather than rare events. If the signal is global, the evidence-accumulation framing is unnecessary. If it is truly sparse, the actual design undermines it, since averaging over all chunks dilutes sparse evidence. There is also a mismatch between the label and the signal. Consciousness in MCS patients fluctuates, and a single behavioral diagnosis taken at some point may not reflect the patient's state during the recorded night. The paper does not discuss how this label noise interacts with its weak-supervision setup.

The abstract motivates the work with diagnosis, prognosis, and rehabilitation planning, but the experiments cover two binary tasks on a single-site cohort with 60 DoC patients, and no prognosis. The second task, MMSE = 0 vs. > 0, is not really a consciousness task: it mostly measures whether a patient can perform the test, which mixes in aphasia and motor impairment. Clinically, the most interesting case for EEG is the patient whose behavioral diagnosis is wrong, for example, covert consciousness, and this is not examined. Overall, the claims are broader than what the experiments can support.

The comparison with existing work is too narrow for the claims being made. The paper introduces a new EEG model, but the experiments do not include recent EEG foundation models such as REVE (El Ouahidi et al., NeurIPS 2025), which are now the natural reference point for any new EEG architecture. I don't think the authors necessarily need to build on a foundation model. But without these comparisons, it is hard to tell whether the gains come from the proposed design or whether an existing pretrained encoder with a simple aggregation head would do just as well. How these baselines are adapted also matters. Recent benchmarking such as NeuroAtlas (Kontras et al., 2026) evaluates foundation models with frozen-encoder probing and notes that fine-tuning may produce different rankings, so fine-tuned versions would be needed for a fair comparison. More broadly, I would like to see comparisons for each part of the method: other ways of aggregating chunks under subject-level labels (for example attention-based MIL pooling, Ilse et al., 2018), and a simple classifier on the same handcrafted features the model is pretrained to predict. These comparisons would make it much clearer which parts of EviFormer actually help.

The evidence is never defined or validated. There are no event labels and no experiment, synthetic or annotated, showing that the model localizes anything. The code also shows no explicit evidence mechanism. Every 30 s chunk is weighted equally, EviMemory is two causal convolutions with a receptive field of about 7 chunks (around 3.5 minutes), and the subject score is the mean over chunks. Training uses windows of 1 to 8 minutes, while testing uses the full recording.

Fine-tuning is very short. In trainers/finetune.py each epoch is one optimizer step, so with the default 5 epochs each fold gets 5 gradient updates. The memory gate and adapter start at identity and can barely move in that time, so the prediction is likely close to a linear readout on averaged pretrained embeddings. This makes me doubt the ablations that credit EviMemory.

The attribution results are largely built in. The encoder is pretrained to predict handcrafted features ( seen in trainers/expert_features.py) including delta power, anterior–posterior differences, left–right asymmetry, and interhemispheric correlation, which are the same patterns the attribution analysis reports.

The labels make the main task easier than it looks. EMCS patients are counted as MCS (found in code datasets/tasks.py), even though they have, by definition, emerged from MCS. How diagnoses were made (scale, number of assessments, timing relative to the EEG) is not described.

Possible confounds are not addressed. Some records use a different montage, and etiology, medication, and time since injury are not discussed. Any of these could correlate with diagnosis.

The evaluation protocol is weak. There is no validation set, hyperparameters differ per task (including the starting seed, 3 for DoC and 0 for MMSE), and it is unclear how they were chosen. Each test fold has about 12 DoC subjects, and the reported standard deviations are over correlated folds.

Pretraining is transductive. In the released code, it uses all subjects, including later test subjects, and fine-tuning loads one checkpoint for all 50 splits. This is not label leakage, but it should be disclosed, and it makes the comparison with externally pretrained baselines uneven.

The baseline code is not included, so it is not possible to check whether foundation-model baselines were fine-tuned or kept frozen.

Questions for authors
  1. What exactly is the "evidence" the model is meant to localize? Is it defined physiologically (sleep events, specific rhythms, state transitions), or is it purely latent? Are there any event-level annotations in the dataset?

  2. How were the FMs and other baselines adapted: frozen encoder with a linear head, or full fine-tuning? Did they use the same subject-level aggregation and the same splits as EviFormer?

  3. Was self-supervised pretraining done on all subjects, including those later used for testing? In the released code, it runs on all subjects by default, and fine-tuning loads one checkpoint for all splits.

  4. Fine-tuning in the released code is 5 epochs with one optimizer step each. Is this the setting used for the reported results? If so, how much do the EviMemory gates and adapter actually change from their initialization?

  5. How were hyperparameters chosen, given that there is no validation set? Why do they differ between tasks, including the starting seed (3 for DoC, 0 for MMSE)?

  6. How were diagnoses established (which scale, how many assessments, and how close in time to the EEG recording)? Why are EMCS patients included in the MCS class?

  7. What is the composition of the MMSE > 0 group? How many subjects are healthy or near-healthy, and how are locked-in or aphasic patients handled?

  8. Are montage, etiology, medication, and time since injury balanced across classes?

  9. How does EviFormer compare with recent EEG foundation models such as REVE, fine-tuned on the same task with the same subject-level aggregation?

  10. How does a pretrained encoder (yours or a foundation model) with simple aggregation, such as mean pooling or attention-based MIL pooling, compare with the full EviMemory and EviLearning pipeline?

  11. How does a simple classifier on the handcrafted pretraining features, averaged per recording, perform on both tasks?

  12. What happens to performance when EMCS patients are removed from the MCS class?

  13. Is there any evidence that the model localizes meaningful segments, for example on synthetic data with planted events, or by comparing high-attribution segments with annotated sleep events or clinician review?

5 comments
AuthorsOpenReview ↗

Response to Reviewer LenD

R1. Intermittent EEG patterns and subject-level supervision (Weakness 1).

Thanks for your helpful comments. We hypothesize that some consciousness-related signatures in long EEG recordings occur sparsely and intermittently, motivating their identification and the accumulation of their contributions across the recording. Studies on identifying disorders of consciousness support this hypothesis. For example, Malinowska et al. (2013) found that spindles were detected more frequently in MCS patients than in VS/UWS patients. In nonclinical sleep EEG, spindles were more likely to recur 3–6 seconds after a preceding spindle (Antony et al., 2018). Compared with other events, sleep spindles occur sparsely and intermittently.

To examine this hypothesis, we trained TinySleepNet on 3,503 30-second clips from 60 DoC patients and sequentially occluded each second of EEG in the training set. After ranking the absolute changes in classification scores induced by occlusion, the most influential 15 seconds accounted for approximately 80% of the total change within each window, on average. This indicates that the classifier's sensitivity is concentrated in particular intervals. Our model incorporates prior knowledge to identify and accumulate contributions from informative intervals.

Even when relevant patterns occur in only a few chunks, EviMemory can preserve their influence on neighboring chunks before averaging. EviMemory first extracts patterns across adjacent chunks using causal convolutions, and a write gate then regulates the update to each feature (original manuscript, page 4, lines 198–215, Eqs. 8–9). Transient patterns can therefore make different contributions to the final prediction. Task-relevant chunks, whose consciousness-related signals are learned through supervision, can influence both the current representation and those of subsequent neighboring chunks.

To address label noise under weak supervision, we use two loss functions. Equation 14 supervises classification at the subject level, accounting for variation in consciousness-related signals across overnight chunks. Equation 15 uses kernel similarity to compare the distributions of memory representations between subjects. This encourages subjects in the same class to have consistent distributions of the representations learned from consciousness-related chunks.

R2. Clinical endpoints and composition of the MMSE-positive group (Weakness 2, Question 7).

Thanks for your helpful comments. We include cognitive screening as a second task because cognitive function requires separate assessment even after a patient exhibits behavioral signs of emergence from MCS. Bodien et al. (2020) used the CRS-R to establish emergence from MCS and subsequently assessed cognition using the CAP, finding that patients could still exhibit an acute confusional state. Our use of the MMSE follows the same rationale. Alongside distinguishing UWS from MCS/EMCS, we examine whether long EEG recordings can predict whether a patient scores on at least one cognitive screening item.

The Introduction also describes advances in automated EEG-based DoC assessment (lines 58–60). Building on this motivation, our study explores automated assessment from long-duration bedside EEG by accumulating consciousness-related information across the recording. This approach could support ongoing monitoring and flag changes that may indicate recovery, prompting targeted clinical reassessment without requiring continuous expert observation of the EEG. Such alerts could help clinicians prioritize further diagnostic evaluation and inform subsequent treatment and rehabilitation planning.

The MMSE-positive group comprises 50 participants. Of these, 15 had normal or near-normal cognition. The remaining 35 included patients with cognitive impairment, language-related cognitive impairment, or locked-in syndrome.

R3. Baseline adaptation and code availability (Weakness 3, Weakness 11, Question 2).

Thanks for your helpful comments. The baselines were fully fine-tuned. We will release the baseline code upon acceptance.

For a fair comparison, the baselines used the same data-splitting strategy as the proposed method. Our evidence-accumulation modules aggregate information from long recordings to produce subject-level classifications. The baselines follow their original training settings by dividing long recordings into chunks of the required duration, classifying each chunk, and combining the predictions through majority voting. We found this to be a practical approach to adapting these methods to DoC classification from long recordings.

AuthorsOpenReview ↗

Response to Reviewer LenD

R4. Comparison with REVE (Weakness 3, Question 9).

Thanks for your helpful comments. We added REVE following the reviewer's suggestion. We use -F to denote full fine-tuning. In -A, chunk representations are averaged for each subject, and a linear classifier is fitted to the resulting subject-level representations. In -M, gated attention-based MIL learns the contribution of each chunk to the subject-level prediction. The table reports BAcc and AUROC for both tasks as the mean ± standard deviation across folds.

ModelDoC BAccDoC AUROCMMSE BAccMMSE AUROC
REVE-F.576 ± .124.615 ± .191.577 ± .083.629 ± .118
REVE-A.576 ± .133.599 ± .169.610 ± .084.643 ± .097
REVE-M.642 ± .132.703 ± .185.564 ± .095.567 ± .110
EviFormer.737 ± .094.761 ± .132.650 ± .066.684 ± .085

EviFormer achieves higher mean BAcc and AUROC than all three REVE variants on both tasks. A possible explanation is that REVE was designed and pretrained for short-duration EEG decoding, which may limit its advantage on long recordings.

R5. Comparison with simpler aggregation methods (Weakness 3, Question 10).

Thanks for your helpful comments. Table 2 shows that replacing EviMemory with direct averaging of chunk representations reduces DoC BAcc from .737 to .626 and AUROC from .761 to .704. For MMSE, BAcc decreases from .650 to .584 and AUROC from .684 to .612.

R6. Classification using handcrafted pretraining features (Weakness 3, Question 11).

Thanks for your helpful comments. Following the reviewer's comments, we directly computed the 45 pretraining descriptors and fitted a simple logistic regression classifier. The resulting BAcc/AUROC was .585/.650 for DoC and .597/.640 for MMSE, demonstrating predictive information in these descriptors. Two factors can explain the lower performance. First, the descriptors incorporate expert knowledge through statistical measures of interest, but their values are fixed and cannot be fine-tuned using task labels. Second, the simple classifier does not model long contexts to accumulate task-relevant evidence. Our model addresses both aspects and outperforms this baseline.

R7. Definition and validation of EEG evidence (Weakness 4, Question 1, Question 13).

Thanks for your helpful comments. We define evidence as latent chunk representations that contribute to subject-level predictions. The dataset has no temporal annotations. We therefore learn evidence from the data under weak supervision and assess the learned evidence through interpretability analyses and expert review.

For each 30-second chunk, EviAttention extracts features along the temporal and electrode dimensions and integrates patterns at multiple temporal scales to obtain a chunk representation (Eqs. 3–7). EviMemory uses causal convolutions to generate candidate updates from neighboring chunks (Eq. 8), controls the update through a write gate (Eq. 9), and bounds its magnitude (Eq. 10). Equation 11 averages the updated representations, allowing different original chunks to contribute differently to the prediction.

Figure 3c shows representative 2-second EEG waveforms selected through perturbation attribution for their contribution to each class prediction. Clinical experts from a tertiary hospital reviewed these segments and endorsed their waveform interpretations. Representative waveforms from the UWS and MMSE-zero groups showed slower fluctuations, whereas those from the MCS and MMSE-positive groups showed denser fluctuations. This suggests that the model uses local rhythmic differences in both tasks. Subject-level analysis also showed higher spindle density in MCS, consistent with the experts' clinical observations.

R8. Fine-tuning budget and parameter changes (Weakness 5, Question 4).

Thanks for your helpful comments. We use 5 gradient updates per fold by default, whereas the DoC and MMSE results in Table 1 used 20 and 3 updates per fold, respectively. Under the default setting, the relative displacements of the write gate and adapter from initialization were 14.99% and 4.07%, respectively.

Table 2 directly compares EviMemory with mean pooling of chunk representations. Replacing EviMemory with mean pooling before classification reduces BAcc/AUROC from .737/.761 to .626/.704 for DoC and from .650/.684 to .584/.612 for MMSE.

AuthorsOpenReview ↗

Response to Reviewer LenD

R9. Influence of pretraining targets on attribution (Weakness 6).

Thanks for your helpful comments. Pretraining introduces statistical features of interest to human experts as potentially useful representations. These features are interpretable and can be assessed by experts, which motivates their use as pretraining descriptors. The model learns to select and adapt task-relevant information during fine-tuning. The pretraining targets span multiple frequency bands and spatial features, and their sensitivity in the final diagnostic prediction is examined after fine-tuning. For example, the targets include alpha, beta, and delta bands, while the fine-tuned DoC model is most sensitive to posterior and temporal delta activity (Fig. 3a).

R10. Diagnostic assessment and inclusion of EMCS (Weakness 7, Question 6, Question 12).

Thanks for your helpful comments. We grouped EMCS patients with MCS patients because both groups exhibit behavioral signs of consciousness and the individual subgroups have limited sample sizes.

Both performance metrics decreased after excluding EMCS patients. After removing 10 EMCS patients, we retained the main-table pretrained weights and fine-tuning settings and repeated subject-wise five-fold cross-validation 10 times on 21 UWS and 29 MCS patients, including 18 MCS− and 11 MCS+ patients. BAcc was .715 ± .129 and AUROC was .731 ± .144, compared with .737 ± .094 and .761 ± .132 in the original 60-patient task. This decrease may reflect the smaller sample size.

CRS-R assessments were collected after EEG recording, with some patients assessed during follow-up within one year. Each patient was assessed once.

R11. Montage and clinical confounders (Weakness 8, Question 8).

Thanks for your helpful comments. We standardized the input montage and compared the etiological distributions between groups to address potential confounders. All recordings used electrode placement according to the international 10–20 system. We selected the same 16 channels, and all recordings had an original sampling rate of 256 Hz. These input specifications were identical across participants and therefore did not vary as potential confounders.

Using the diagnostic text in the original clinical records, we classified etiology into five broad categories: trauma, hemorrhage, hypoxia, ischemia, and other causes. The etiological distributions did not differ significantly between groups (two-sided Fisher–Freeman–Halton exact test, p=.627).

R12. Hyperparameter selection and repeated cross-validation (Weakness 9, Question 5).

Thanks for your helpful comments. We selected hyperparameters using task-specific sensitivity analyses. Different random seeds were used to characterize performance variability across random runs. The starting seeds, 3 and 0, were selected at random.

R13. Pretraining exposure to held-out subjects (Weakness 10, Question 3).

Thanks for your helpful comments. The main experiment used transductive pretraining, including unlabeled EEG from subjects subsequently used for testing. We added an inductive experiment in which the encoder was pretrained using only unlabeled EEG from the training subjects in each fold. The table reports performance under the same data splits as the mean ± standard deviation across folds.

PretrainingDoC BAccDoC AUROCMMSE BAccMMSE AUROC
Transductive.737 ± .094.761 ± .132.650 ± .066.684 ± .085
Inductive.721 ± .131.757 ± .145.640 ± .068.688 ± .075

The changes in the means of all four metrics were at most 1.6 percentage points, smaller than their respective fold-level standard deviations. The small increase in MMSE AUROC from .684 to .688 may reflect stochastic optimization.

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

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