acceptodds
Under review as a conference paper at ICLR 2027

NeuroIntentFormer: Evidence-Conditioned Temporal Aggregation for Motor Imagery Decoding in Stroke Rehabilitation

Abstract

Decoding left- and right-hand motor imagery from stroke recordings can provide intention signals for rehabilitation-oriented interaction, but discriminative evidence varies across patients and trials. Beyond learning temporal representations, a decoder must determine how their content and class predictions should inform a joint decision. We formulate this step as evidence-conditioned temporal aggregation and introduce NeuroIntentFormer. The model constructs complementary temporal evidence and lets the evidence content and predictions jointly condition source aggregation and decision refinement. On seven held-out participants from a subject-disjoint 49-participant stroke cohort, NeuroIntentFormer achieves 85.53% subject-mean balanced accuracy (BAcc), with a participant-level bootstrap 95% confidence interval of [81.10%, 89.84%]. A parameter-matched ablation shows that evidence conditioning with joint decision refinement improves BAcc across all test trials by 1.76 percentage points (pp) over context-only routing. On OpenBMI, the same architecture reaches 82.03% subject-mean BAcc, with a 1.65 pp difference over MSVTNet. These results support the joint decision mechanism for offline motor imagery decoding.

Primary area:
applications to neuroscience & cognitive science
Keywords:
motor imagery decoding, stroke rehabilitation, brain-computer interfaces, EEG, Transformer, subject-disjoint generalization, healthcare machine learning

Reviews

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

The paper proposes an architecture NeuroIntentFormer for predicting left or right based on EEG signals in an individual generalization setting.

NeuroIntentFormer resembles an ensemble setup, with a difference that the aggregation function is an MLP with access to the experts predictions as well as some input statistics.

The model showed superior BAcc against Classical feature methods, Task-specific deep models and Pretrained EEG references. In those comparisons. Considering the 95% confidence intervals obtained via bootstrap, the model did not clearly outperform most of the models.

Additional experiments showed the model relied on both the input context and the evidence, and that each expert relies on a different time region of the signal (Early, Middle and Late).

Critical strengths

The paper presents well related works and describes in a precise way the high-level architecture proposed, cleverly comparing it to expert routing and ensemble.

The BAcc obtained is relevant, outperforming various models from previous works and the benchmark is broad, including Classical feature methods, Task-specific deep models and Pretrained EEG models.

Critical weaknesses

Figure 1 proposes using the pipeline of NeuroIntentFormer to predict uncertainty and conditionally pause and allow therapist review. This is not reanalyzed by the authors in experiments and their conclusions, being only presented in Appendix G. Similarly, it is not shown how the evidence based would be beneficial for interpretability, in the sense of what would be the meaning of each expert's prediction.

Some elements of Figures and Tables don't seem to be fully described in the paper or are described but under a different name in the text:

  • Shared Encoder
  • Local Conv.
  • Temporal Expert
  • Fixed temporal profiles
  • Homogeneous Transformers
  • Uniform mean fusion
  • channel/time consistency

It is unclear the relative importance of each of evidence sources.

Questions for authors

Were the baselines trained with the same channel-drop/time-shift views?

Could per-source ablations and the distribution of gate weights across patients and trials be run?

Can the elements described in Critical Weaknesses be better described in the text?

Reviewer_BsKGOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

NeuroIntentFormer addresses left- versus right-hand motor imagery decoding from multichannel recordings. It builds three learned soft temporal views and a global view, processes them with different encoders, and combines their predictions with a router conditioned on source features, logits, and signal context. A residual readout adjusts the combined prediction. The model is trained jointly with channel-drop and time-shift consistency losses. The authors train and evaluate the model separately on Stroke and OpenBMI, keeping participants separate across training, validation, and testing. They report subject-mean balanced accuracies of 85.53% and 82.03%. The experiments compare existing decoders, include component ablations, and test the interaction between routing and readout across four conditions.

Critical strengths
  1. The reported Stroke comparison is a substantive strength, subject to resolution of the dataset correspondence below. Seven patients are excluded from training and validation, and subject-mean balanced accuracy weights patients equally. NeuroIntentFormer improves on MSVTNet by 3.62 percentage points, with a paired participant-bootstrap 95% interval of [0.92, 5.98]; six of seven patients benefit. OpenBMI provides a second, separately trained evaluation rather than a test of cross-dataset transfer.
  2. Table 9 already provides all four router/readout configurations. Figure 3 reports a patient-mean interaction of 5.44 percentage points, with a paired 95% interval of [2.66, 8.10]. This supports a positive interaction for the evaluated models. Appendix E.1 usefully distinguishes joint-training effects from the readout's immediate inference effect: in the jointly trained full model, base pooled BAcc is 86.02% and final BAcc is 85.95%, so the benefit is not simply an inference-time correction gain.
Critical weaknesses
  1. The controls do not isolate the added value of jointly using features and predictions. Patient/trial heterogeneity and the stated limitations of fixed or context-only fusion motivate adaptation, but do not establish that this particular combination is necessary. The parameter-matched context-only router removes source features and logits simultaneously. The uniform-fusion ablation also does not distinguish feature-only from prediction-only conditioning, or compare the design with a simple learned combiner using the same sources. With readout enabled, evidence-plus-context routing improves pooled BAcc by 1.76 points over context-only routing. The next useful evidence is a capacity-matched comparison of feature-only, logit-only, and joint routers, plus a simple learned combiner under the same sources, objective, and selection rule. Repeating the key configurations across independent training seeds would test whether the observed interaction persists beyond the selected models; participant bootstrap uncertainty alone does not answer that question.
  2. The Stroke data representation and event semantics need to be reconciled with the cited release. Appendix A.1 explicitly describes N × 34 continuous matrices, 32 signal columns, a time column, and event codes 1/2/3; it maps 1/2 to left/right classes and obtains 3,793 epochs from 49 participants. In contrast, the Data Records section of Liu et al. (2024a), Scientific Data 11:131 (doi:10.1038/s41597-023-02787-8), describes per-participant raw data arrays of 40 × 33 × 4000, with 30 EEG channels including the reference, two EOG channels, and a marker channel, plus separate left/right labels. Its processing description also uses marker values for trial phases. The manuscript does not document this correspondence or the potential transformation relationship.
Questions for authors
  1. Can the authors add or provide existing evidence for feature-only and logit-only routing, and a simple learned combiner, with the same sources and comparable capacity? Which benefit is specific to joint conditioning and residual refinement, beyond the adaptive-fusion motivation already given in Sections 1 and 2.3?
  2. Are independent training runs available for the principal comparisons and the four router/readout configurations? Please report their variability and consistency of the interaction.
  3. Please identify the exact Stroke release/version and conversion procedure, linking each derived epoch to an original participant, trial, and left/right label.
Reviewer_M6yQOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper addresses binary left/right-hand motor imagery (MI) decoding from EEG in stroke rehabilitation. The proposed NeuroIntentFormer constructs four temporal evidence views from a shared encoder: three learnable Gaussian soft-mask windows (early/middle/late) plus a global prototype-cross-attention view. A dense-softmax router conditions on source representations, source logits, and a context vector to produce per-sample mixing weights. An aggregated logit is then refined by a residual readout conditioned on a 20-dimensional deterministic evidence summary, trained end-to-end. The training objective combines multi-view cross-entropy, KL consistency, Brier loss, a variance-floor regularizer, per-source auxiliary cross-entropy, an entropy bonus, and a late-gate penalty (13 loss coefficients total). On 7 held-out stroke patients (from a 49-patient cohort, 35/7/7 split), the model achieves 85.53% subject-mean BAcc vs 81.91% for the best baseline (MSVTNet). On 8 OpenBMI subjects (from 54, 38/8/8), it achieves 82.03% vs 80.38%.

Critical strengths
  1. Clinically motivated problem with a scarce dataset. Acute-stroke MI decoding is a real clinical need, and the 49-patient dataset from Liu et al. (2024) is a valuable resource that is underexploited in the deep-learning MI literature.

  2. Systematic parameter-matched ablation with paired-bootstrap interaction analysis.The 2×2 router×readout experiment (Table 9) holds parameter count fixed across variants, and the interaction effect is reported with a patient-level paired 95% CI ([2.66, 8.10]). This is methodologically sound.

  3. Transparent limitation disclosure. Appendix D explicitly states that confidence intervals characterize "fixed trained models rather than repeated-training variability."

  4. Computational efficiency. At 1.9M parameters and 5.8 ms inference, the model is practical for real-time BCI deployment.

Critical weaknesses
  1. Underpowered test set × single training run × fixed split = unreliable conclusions. The stroke experiment tests on 7 patients and OpenBMI on 8 subjects. Every method is trained exactly once — there is no seed variance anywhere in the paper (Appendix D explicitly confirms this). The +3.62 pp stroke gain has a paired CI lower bound of 0.92; the +1.65 pp OpenBMI gain has no CI at all (subject SD ≈ 9.5). Despite having 49 and 54 participants available, the authors do not run LOSO or 5-fold cross-validation, nor do they justify the 35/7/7 or 38/8/8 split choice. With 7–8 test subjects and single training runs, differences of 1–3 pp cannot be reliably distinguished from noise or split-selection effects.

  2. Reported absolute accuracy systematically deviates from independent literature without protocol-difference analysis.** The original dataset paper (Liu et al., Nature Sci Data 2024) reports a best accuracy of 72.21% (TWFB+DGFMDM) on the same 49 stroke patients. This paper reports 85.53%, a 13 pp gap. More telling: this paper's own reimplemented MSVTNet baseline already achieves 81.91% — 9.7 pp above the original paper's best method — which strongly suggests that the protocol setting (longer analysis window, wider filter band, larger training set, different channel selection), rather than deep-learning architecture, is the dominant factor. Similarly, on OpenBMI, multiple independent reproductions cluster at 73–76% (IMH-Net 73.90%, MGCANet 73.68%, ATCNet reproduction 76.52%); this paper's baselines already reach 76–80%, and NIF itself claims 82.03%. The paper does not discuss these protocol discrepancies.

  3. The mechanism claim is undercut by the paper's own ablation, and the abstract selectively reports the most favorable comparison. In Table 9, evidence-conditioned routing without the readout achieves 82.34% pooled BAcc — worse than context-only routing without the readout (84.87%, a −2.53 pp gap). The evidence router only wins when the readout is also enabled (85.95% vs 84.19%). The abstract reports "+1.76 pp over context-only routing," which corresponds to 85.95 (evidence + readout) vs 84.19 (context + readout) — the most favorable pair. The honest net gain relative to the best ablated variant (context-only, readout off: 84.87%) is only +1.08 pp. The paper offers no explanation for why evidence conditioning alone hurts performance.

  4. Limited architectural novelty; terminology complexity masks simplicity. The core components are: (a) three learnable-but-sample-invariant Gaussian soft-mask windows, which are architecturally equivalent to fixed multi-scale temporal convolutions (not per-sample attention); (b) a dense-softmax router, which is a standard MoE gating mechanism without top-k sparsity or expert specialization; (c) a residual MLP readout, which is a learned stacking calibration layer. The paper's terminology (router / mask / gate / moe / evidence / expert) creates an impression of complexity that the architecture does not warrant. The distinction from MSVTNet (multi-scale vision Transformer with multi-branch fusion) is limited to the router input including evidence features and the addition of a readout module.

  5. Thirteen loss coefficients with no sensitivity analysis on a 7-patient validation set. The training objective combines seven loss terms with 13 total coefficients. The validation set contains only 7 (stroke) or 8 (OpenBMI) subjects. How these coefficients were selected and whether the results are sensitive to them is unreported. With such a small validation set, extensive hyperparameter tuning constitutes an implicit overfitting risk.

  6. Stroke framing without stroke-specific contribution or clinical-variable analysis. Despite the stroke-rehabilitation motivation, the paper reports no analysis of lesion side, NIHSS severity, time post-stroke, or Fugl-Meyer motor score in relation to decoding performance. No hemiplegic-side comparison is provided. The architecture contains no stroke-adapted design (e.g., accommodating reduced mu-suppression ipsilesionally or compensatory symmetry changes). The "confidence-aware review" is offline thresholding, not clinical decision support. The stroke dataset serves as an evaluation platform for a generic MI pipeline rather than driving any methodological contribution.

  7. Weak pretrained-model baselines and no code. CBraMod achieves 51.00% on OpenBMI (chance level), and BIOT 59.50%. These EEG foundation models typically perform substantially above chance in the published literature; the near-chance results suggest possible misconfiguration or input-format mismatch, which undermines claims of substantially outperforming foundation models. REVE-LP+LoRA (74.00%) is a reasonable pretrained reference.

Questions for authors
  1. Can you provide results across ≥5 random seeds for all methods? Are the reported conclusions robust to seed variance? (W1)
  2. Why not run 5-fold CV or LOSO? What is the rationale for the 35/7/7 and 38/8/8 splits? (W1)
  3. Your reimplemented MSVTNet baseline achieves 81.91% on the stroke dataset, 9.7 pp above the original dataset paper's best method (72.21%). Please explain the protocol differences (analysis window length, filter band, channel selection, training set size) and clarify whether deep-learning methods genuinely outperform classical methods under matched conditions. (W2)
  4. Independent OpenBMI reproductions cluster at 73–76%; your baselines already reach 76–80%. Please detail the protocol differences (window, filtering, channels, training set size) compared to the independent literature. (W2)
  5. Why does evidence-conditioned routing without the readout perform 2.53 pp worse than context-only routing without the readout (82.34 vs 84.87)? (W3)
  6. How were the 13 loss coefficients selected? Given the 7-patient validation set, how do you ensure reliable hyperparameter selection? (W5)
  7. CBraMod ≈ 51% on OpenBMI is far below published results. Was the fine-tuning protocol validated against the original paper? (W7)
  8. Can you provide any analysis relating decoding performance to clinical variables (lesion side, time post-stroke, NIHSS, Fugl-Meyer)? (W6)

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