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Under review as a conference paper at ICLR 2027

Does Attention Matter in Motor Imagery EEG Decoders? Diagnosing and Repairing Attention Failure

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Abstract

Attention is widely used in hybrid motor-imagery (MI) EEG decoders to dynamically select and integrate evidence for each trial. However, performance gains of the complete decoder and its attention maps do not reveal whether this trial-specific weighting actually contributes to classification. At frozen checkpoints, we replace attention with cross-sample or training-set-mean weights while holding the current trial's Value tensors and all parameters fixed; uniform replacement provides an additional fixed-route control. Across eight decoders on BCIC-IV-2b and BCIC-IV-2a, no architecture shows jointly supported dependence on the two empirical replacements in both datasets. Probes and controlled perturbations trace this failure to token convergence, Value-space equivalence, and downstream bypass or compensation. We therefore develop SOAMNet, which preserves multi-scale temporal trajectories, separates class queries, and forces evidence through one sample-conditioned attention path. Across four MI datasets and three seeds, SOAMNet achieves the highest mean balanced accuracy and Cohen's among 12 baselines. Cross-sample and training-set-mean replacement consistently reduce its balanced accuracy on every dataset; the weaker mean decrease ranges from 18.61 to 40.95 percentage points, and both participant-bootstrap intervals exclude zero throughout. Replacing attention with a matched trainable non-attention head lowers balanced accuracy by 3.51–5.22 points. SOAMNet thus realizes functional reliance on sample-conditioned attention weights while achieving competitive classification performance.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Motor imagery EEG, Brain–computer interfaces, Attention mechanisms, Functional dependence, Attention failure, Neural decoding

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_gJBSOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper studies whether attention weights in motor-imagery EEG decoders contribute to predictions in a trial-specific way. The authors replace the weights at frozen checkpoints with weights from other trials or with training-set averages, while keeping the current trial’s Value tensors and model parameters fixed. They find that several existing decoders are relatively insensitive to these replacements and discuss how token similarity, the Value representation, and downstream processing can account for this behavior. They then propose SOAMNet to make predictions depend more strongly on sample-conditioned attention. Across four datasets, they report competitive classification performance, improvements over a matched non-attention head, and substantially larger performance drops when SOAMNet’s attention weights are replaced. The paper presents these results as a diagnosis and repair of attention failure.

Critical strengths
  1. The replacement audit makes a useful distinction between the performance of a complete decoder and its reliance on the current trial’s attention weights. Holding the Value tensors and parameters fixed is a reasonable way to examine that distinction, and the results caution against inferring functional importance from attention maps or overall accuracy alone.

  2. The authors provide substantial empirical analysis, including classification comparisons, replacement interventions, and controls that examine the source of SOAMNet’s sensitivity. I particularly appreciate the global-context controls in Table S19: they provide evidence that is important for interpreting what the proposed model actually does. These are useful contributions, even though I do not think they support the central repair claim.

Critical weaknesses
  1. The paper does not establish that replaceable attention weights constitute a functional failure. The audit shows that, at these checkpoints, replacing the current trial’s attention weights with cross-sample or training-set-mean weights changes balanced accuracy only slightly. This shows that the trial-specific weights are not necessary for these predictions, but it does not show that the decoders are deficient. If the class-relevant information is already captured by global statistics, or remains available through residual or downstream paths, low sensitivity to replacement may reflect a reasonable solution to the task, redundancy, or robustness. To call this a failure, the paper would need to show what is lost because of it, for example in accuracy, generalization, robustness, or a clearly specified faithfulness requirement. Without such a criterion, the target of the repair is defined by the expectation that attention should be used. SOAMNet is then designed to force evidence through one sample-conditioned attention path, and the large drops under replacement confirm that its predictions depend on that path. However, greater sensitivity to replacing an internal component is not, by itself, evidence of a better model, and could equally indicate fragility. This is the main reason for my recommendation, because the diagnosis-and-repair framing organizes the whole paper.

  2. The paper’s own controls suggest that SOAMNet’s dependence comes mainly from a global class-conditioned pathway, rather than from better selection of temporal evidence. SOAMNet first forms a global class context and writes it into the attention scores through a fixed temporal carrier. In this design, attention can carry class information to the output without needing to identify which EEG time points are informative. Swapping attention across trials then partly amounts to attaching one trial’s class-related code to another trial’s evidence, so a large drop in performance is expected. Table S19 is consistent with this interpretation: the global-carrier-only model retains core replacement losses close to those of the full model (25.38/41.22/32.23/20.61 vs. 28.46/40.95/33.81/18.61 pp on 2b/2a/BNCI/Cho), whereas removing the content Q–K scores costs only 1.08–4.29 pp, and swapping attention after matching global evidence costs only 1.32–3.12 pp. The authors acknowledge the role of the global context, but the paper still presents the large dependence as evidence that attention failure has been repaired. A more accurate conclusion would be that the strong dependence arises mainly from a class-conditioned global pathway, while trial-specific temporal content contributes a small additional effect. The accuracy gains over the baselines and over the matched non-attention head are a practical contribution, but they do not show that these gains come from repairing attention failure, or that strong attention dependence is what produces them. Addressing this would require reframing the central claim, not only adding experiments.

Questions for authors
  1. Beyond the replacement results themselves, what concrete cost do you attribute to replaceable attention in existing decoders? Is there evidence that decoders with low replacement sensitivity perform worse in accuracy, cross-session or cross-subject generalization, robustness, or another clearly specified criterion? Evidence of such a cost would most directly affect my assessment, because it would give the diagnosis-and-repair framing an independent basis.

  2. Can the gains from the global class-conditioned pathway be separated from those of trial-specific temporal selection? For example, how does an independently trained model with matched capacity and information perform when the same global class context is provided directly to the classifier, or through a simple non-attention gate? If such a model matches SOAMNet’s accuracy without strong attention dependence, how would you interpret the repair claim?

  3. Clarification: please describe the matched non-attention head in more detail, including its inputs, whether it has access to the global class context, its parameter count, and its training procedure. This would make clear which comparison the reported 3.51–5.22 point difference reflects.

4 comments
AuthorsOpenReview ↗

Evidence for Attention Failure and Functional Route Repair

Thank you for the detailed review and comments.

Response to Critical Weakness 1 and Question 1: criterion and cost of attention failure

The attention failure identified in the paper is clearly established. We must start from a basic fact: an effective attention mechanism should make classification benefit from its trial-specific weights. Our results show otherwise. As shown in Figure 1, we fix current-trial Values and every model parameter. Across eight decoders, cross-sample and training-mean replacement changes mean BA by only −0.51-0.51 to +0.93+0.93 pp. Some replacements even increase mean BA for ATCNet, EEG Conformer, CTNet, and TCFormer. These results directly show that current-trial weights fail to provide the classification benefit expected from an effective attention mechanism.

Classifier accuracy and mechanism validity are separate questions. The concrete cost of this failure is false mechanistic attribution: observed gains cannot be credited to trial-specific weighting, and the attention maps lack a decision-level basis. This can misdirect architecture design toward attention blocks or downstream compensators without verifying route use. Accuracy, generalization, and robustness evaluate the complete system; our audit determines whether the advertised mechanism contributes to its performance.

Cross-sample replacement is an in-distribution mechanism counterfactual. It bijectively reassigns valid held-out attention tensors, preserving their marginal distribution and route activity while breaking only their pairing with current-trial Values. A task-level response is required to claim functional benefit from those weights.

SOAMNet establishes route dependence without sacrificing task performance. Uniform attention supplies an analytic null, while cross-sample and training-mean replacement provide empirical tests that the architecture does not guarantee: a single path can still learn static weights, nearly uniform routes, or route-insensitive Values. SOAMNet passes both empirical tests on all four datasets and achieves the highest mean BA and κ\kappa among the compared methods. It therefore satisfies both requirements of the repair: the route is demonstrably used, and the classifier remains the strongest on average.

Response to Critical Weakness 2 and Question 2: global context and temporal selection

The global-context result supports the repair claim by revealing how the repaired route carries class evidence. Our repair criterion is functional dependence on sample-conditioned routing; local-peak discovery is a separate, narrower property. In SOAMNet, global context conditions scores and Values and reaches the logits only through the audited readout. Replacement therefore disrupts a genuine sample-specific coupling in the sole decision path.

The controls also separate global and temporal contributions. Independently trained global-only variants lose 0.95--2.45 BA points on every dataset, with all participant-paired intervals excluding zero; removing content Q--K scores costs 1.08--4.29 points, and evidence-matched swaps cost 1.32--3.12 points. Global context drives the principal route, and trial-specific temporal evidence adds a consistent classification gain.

The bypass experiment provides direct causal support for this interpretation. Adding an external evidence path collapses RcoreR_{\mathrm{core}} from 18.61--40.95 pp to approximately zero while reducing clean BA by only 0.68--2.97 pp. Route dependence disappears precisely when the classifier regains unrouted access to class evidence, as the proposed bypass mechanism predicts. The repair claim is therefore supported by both the controlled information path and the resulting classification utility.

Response to Question 3: clarification of the non-attention control

The matched non-attention head is a valid control because it matches SOAMNet in encoder, source evidence, capacity, and training protocol. The reported 3.51--5.22 pp gap is obtained with a same-encoder nonlinear full-trajectory pooling head. For each participant and seed, it uses the same encoder checkpoint and receives the complete feature and class-evidence trajectories used by SOAMNet. The control receives the source evidence sequence from which SOAMNet derives gg and mm; its freshly trained head applies a token MLP, temporal mean/max pooling, and a logit MLP.

The control uses identical splits, seeds, optimization caps, and validation-based checkpoint selection, and has slightly more active parameters than SOAMNet (135,632 versus 130,474 on BCIC-IV-2a). These matched conditions largely rule out a weaker classifier, fewer source features, lower capacity, or a smaller training budget as explanations for its lower BA across all four datasets. The comparison therefore supports added classification utility from the attention-based readout.

Thank you for clarifying why mechanistic misattribution matters and how the pooling baseline was constructed. My main concern remains whether the reported classification gains can be attributed to the mechanism the paper claims to repair. The comparison shows that SOAMNet outperforms a pooling head given the same source trajectories, but it leaves open whether a direct readout given the same computed global class context could achieve similar accuracy. This distinction matters because the global-carrier-only model retains most of the replacement sensitivity, and adding a bypass largely eliminates that sensitivity with a much smaller change in clean accuracy. The response establishes that SOAMNet uses trial-specific routing; the evidence still leaves open what that routing adds beyond the construction and use of global class evidence.

AuthorsOpenReview ↗

Routing Utility Beyond Global Class Evidence

Thank you for the follow-up.

We agree that this is a valid concern, so we added a control that passes the global class context computed by SOAMNet directly to an independently trained classification head. SOAMNet outperforms this control on all four datasets, showing that attention routing provides additional classification gains beyond direct use of the same global class information.

For each participant and random seed, we froze the trained SOAMNet encoder, evidence aggregator, and global-context computation. The control's classification head uses only the global class context mm computed by SOAMNet before routing. It receives no attention scores, attention weights, Values, local temporal trajectories, or routed outputs.

We independently trained a three-layer residual MLP as the control's classification head. The control model's total active parameter count differs from SOAMNet's by no more than 1%. Both models use the same training, validation, and test splits, three random seeds, and training budget. Checkpoints are selected by validation BA for both models.

After averaging the three seeds within each participant, the test results are:

DatasetSOAMNet BADirect-readout BAPaired difference [95% CI]
BCIC-IV-2b80.1077.75+2.35 [1.35, 3.35] pp
BCIC-IV-2a69.4468.19+1.25 [0.60, 1.90] pp
BNCI2015-00185.5383.98+1.55 [0.85, 2.25] pp
Cho201772.7569.30+3.45 [2.72, 4.18] pp

SOAMNet achieves higher BA with each of the three random seeds and for 72 of the 78 participants. Cohen's κ\kappa also improves on all four datasets, with the confidence intervals for the paired differences excluding zero.

The earlier global-carrier and bypass controls showed that global context carries substantial class information. The new control uses that information directly, yet its BA remains 1.25--3.45 percentage points below SOAMNet's. These results show that attention routing can improve classification beyond direct use of the same global class information. We will include this control and its results in the revised manuscript.

AuthorsOpenReview ↗

Follow-up on Our Response

If you have had a chance to read our follow-up response, we would appreciate hearing your thoughts. Thank you for your time.

Reviewer_kMsROpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

In my view, this paper has a two-fold purpose: (a) shows that attention in many deep learning MI decoding approaches do not hold much information via a series of interventions and (b) introduce SOAMNet a new pipeline that has promises functional reliance on sample-conditioned attention.

Critical strengths

The paper is well-written and I find it a very timely contribution to the field as more and more deep learning MI decoders arise, this work provides a nice way to further test them. I particularly liked the first half of the paper that (as the authors say) answer the question: "does BA deteriorate when a frozen model does not use attention ?". The authors have put lots of attention into that with quantities like the ones in (3) and many results and experimental studies. The SOAMNet is also an interesting idea. Particularly the alignment with the 5-time windows as well as the class values. It seems as a well-thought architecture.

Critical weaknesses

The main points of weakness in this work are also my questions to the authors:

  1. I notice a lack of EEG foundation models in the results of Figure 1 (which should be included as most of them are transformer-based)
  2. The analysis does not include models that dynamically adapt to the input (which are relevant and should be mentioned)
  3. Although the authors say this is only MI for now, I think SOAMNet would be hard to scale to large multi-scale classification tasks

Minor: In the Appendix, I noticed many symbols which are not defined for example: H5. * or Table S19 cross-symbol

Questions for authors
  1. Can the authors include in their analysis EEG foundation models (pre-trained) and fine-tuned on MI ?
  2. How about dynamically adapted MI decoding frameworks like [1]: 10.1109/TNSRE.2023.3265304 and [2]: 10.1016/j.engappai.2025.113524 ?
  3. If class queries follow the number of classification classes, how does the network scale to multiple classes (above 4) ? Is there a saturation point ? Any ablation on this ?
2 comments
AuthorsOpenReview ↗

Audit Scope, Input-Adaptive Models, and SOAMNet Scalability

Thank you for the thoughtful and constructive review, for recognizing the paper's timeliness and technical soundness, and for offering concrete suggestions that help us clarify its scope and presentation.

Response to the paper summary

The paper summary should distinguish branch content from dynamic-weight dependence. Figure 1 fixes current-trial Values and all parameters, then tests whether classification benefits from the particular weights computed for that trial. Across eight decoders, the two empirical replacements change mean BA by only −0.51-0.51 to +0.93+0.93 pp. Some replacements even increase mean BA for ATCNet, EEG Conformer, CTNet, and TCFormer. The finding is functional replaceability of trial-specific weighting, with slight negative mean effects in several cases. Frozen-checkpoint replacement isolates the contribution of current-trial weights while retaining the branch representation; architecture-level ablation removes both and therefore answers a different question.

Response to the comments on EEG foundation models

We do not include EEG foundation models in the present study because our unified audit targets task-trained, subject-specific hybrid MI decoders. Foundation models pose a distinct experimental question: pretraining, backbone freezing or fine-tuning, and attention in the backbone or task head must be separated before functional dependence can be attributed. Adding a foundation model to the current audit matrix without separating these regimes would not provide a controlled comparison.

We will explicitly state that the present conclusions apply to the audited hybrid MI decoders and that EEG foundation models lie outside the current scope. In a future extension of this work, we will include foundation models and separately audit backbone and task-head attention under matched frozen-backbone and end-to-end fine-tuning regimes.

Response to the comments on input-adaptive MI frameworks

The audited models are input-adaptive at the object tested: all eight recompute QK-softmax routes for each trial. We additionally audit DBConformer's input-conditioned channel gate and SSTAF's spectral/spatial gates; their cross-sample and training-mean effects are only −0.12-0.12 to 0.21 pp. We will make this existing result more visible.

The two suggested studies adapt related but different objects. Barmpas et al. mix subject-specific convolutional kernels, so the appropriate counterfactual replaces their mixing coefficients while fixing the kernel bank. DAMT combines channel- and time-wise dynamic attention and can be tested with layer-matched route replacement. Dynamic kernels, vector gates, and token routes require mechanism-matched interventions; placing them as interchangeable rows in one matrix would conflate distinct mechanisms. We will clarify this distinction in Related Work.

Response to the question on scaling beyond four classes

SOAMNet uses class-to-token routes with linear class scaling. With CC classes, TT temporal positions, and key dimension dd, route scoring costs O(CTd)O(CTd) and stores O(CT)O(CT) weights. Keys and all five window encoders are shared across classes; adding a class adds one query and one route. The evaluated model has 130.5k parameters and 7.44 ms batch-1 latency on an RTX 2060, compared with 113.7k and 5.79 ms for ATCNet. Thus the architecture has moderate overhead in the evaluated setting.

The current experiments establish behavior for two and four classes. A dataset with genuinely distinct additional MI labels is the appropriate test of the saturation point because the limiting factor is class separability in the EEG representation.

Response to the minor comment on appendix notation

We agree that the appendix must be self-contained. We will define the asterisk in Table S16 as the two empirical core interventions, the dagger in S19 as positive lower bounds for both bootstrap intervals entering RcoreR_{\mathrm{core}}, and expand labels such as “H5” at first use.

Reviewer_kMsROpenReview ↗

Response by Reviewer kMsR

I thank the authors for the clarifications to my questions and for fixing the appendix notations. The explanations in the "Related Work" would be very useful for the input-adaptive methods. I believe some EEG-FMs comparisons would further increase the value of the paper. Nevertheless, I maintain my "weak acceptance" rating.

Reviewer_rdCtOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper examines whether attention in motor-imagery (MI) EEG decoders genuinely relies on trial-specific weights. It applies seven frozen-checkpoint interventions to eight hybrid decoders, modifying attention while retaining the current trial's Values and all model parameters. Several models deteriorate when attention output is removed but barely change when weights are replaced across trials or by training-set averages. The authors attribute this to token consensus, Value-space equivalence, and downstream bypass. They propose SOAMNet, a multi-window network with class-conditioned routing and a single-path attention readout. It achieves the highest reported mean balanced accuracy (BA) among twelve baselines across four datasets and exhibits substantial degradation under empirical attention replacement.

Critical strengths
  1. freezing model parameters and current-trial Values while replacing only attention weights directly tests a property that architecture-level ablations cannot isolate. The large difference between zeroing and replacing weights in several baselines is a meaningful observation.

  2. the authors trace interventions through attention weights, Value representations, and logits, supported by probes and controlled Value-space and residual experiments (Tables S11–S15). These analyses make the diagnosis more informative than attention visualizations alone, even if the underlying mechanisms are not entirely novel.

Critical weaknesses
  1. Underperforming baselines undermine the representativeness of the attention-failure finding and the claimed classification advantage. On BCIC-IV-2a, the TCFormer repository reports 83.40% for ATCNet and 78.08% for CTNet, versus 67.93% and 64.87% here; the official ATCNet train–validation–test result is also 81.10%. FBCSP reaches only 42.94% in this paper. These discrepancies are too substantial to leave unexplained. On BCIC-IV-2b, using sessions 1–2 for training and session 3 for validation removes approximately 40% of the trials available for optimization under the common sessions 1–3 protocol, plausibly explaining part of that gap; it does not explain the BCIC-IV-2a results. Shorter training budgets, altered optimization schedules, and potentially different input preprocessing may affect architectures unequally. The baseline audits also primarily use one seed. Even if these protocol changes are legitimate, the results may not generalize to adequately trained checkpoints, weakening both the attention-failure claim and the reported SOAMNet advantage.

  2. Reliance versus utility. SOAMNet's uniform-attention collapse follows from Eq. 15, although its empirical replacement effects are not guaranteed. More importantly, adding a direct logit bypass reduces R_core from 18.61–40.95 pp to approximately zero while decreasing clean BA by only 0.68–2.97 pp (Table S19a). Using pre-routing aggregated class evidence m directly as logits, bypassing the final router, costs only 1.53–4.49 pp (Table S19b). Evidence-matched swaps cost 1.32–3.12 pp, versus approximately 31–42 pp for maximally dissimilar cross-sample swaps; perturbation magnitude also differs. Together, these results suggest that strong route dependence can largely reflect transmission of upstream class information, not necessarily better selection of local trial-specific evidence.

Questions for authors
  1. Which implementations, sampling rates, temporal windows, filtering, and training settings were used, and why are several BCIC-IV-2a baselines so weak, including FBCSP?

  2. Are the Figure 1 and Tables S2/S10 audit checkpoints the same as those evaluated in Table 2? If not, how do Tables S3 and S8 relate?

  3. What are the actual selected epochs and learning curves, and does the audit replicate on higher-performing, multi-seed checkpoints or with all three BCIC-IV-2b training sessions?

  4. How do the authors reconcile the direct-bypass and pre-routing-evidence results with the claim of improved local evidence selection? Could they report clean and replacement-route activity (rho_c) and logit distributions?

  5. How much do the two calibrated datasets change when beta is fixed to zero?

2 comments
AuthorsOpenReview ↗

Evaluation Protocol and Validity of the Attention Audit

Thank you for the careful and detailed review.

Response to Critical Weakness 1: baseline performance and audit scope

We use a harder, stricter protocol than the TCFormer repository, so lower scores are expected. TCFormer's pipeline exposes the official E session during model development: checkpoints are selected on E across 1000 training epochs, and the same E session supplies the reported test performance. We never use E for training or model selection. We split official T 80/20 for training and validation, train up to 300 epochs, select strictly by validation BA, and evaluate E only after selection. The official ATCNet figure likewise follows a separate 500-epoch accuracy protocol. We can therefore state responsibly that our reported results are not inflated. On 2b, session 3 is likewise reserved for validation.

The audit is a within-checkpoint counterfactual, independent of absolute BA. It covers 72 participant checkpoints across eight architectures on 2b (clean BA 71.27--78.54%) and another 72 on 2a. Every test freezes the trained model and current-trial Values and replaces only the route. The attention audit therefore rests on 144 neural checkpoints; FBCSP, a non-attention comparator, enters only the classification comparison. Its configuration was validation-selected from eight candidates. Selected checkpoints were comfortably within the training budget: method-mean epochs are 26.8--40.2 on 2b and 92.2--141.2 on 2a, and every 2a checkpoint falls below the 300-epoch cap.

The audit comprises 144 participant checkpoints at seed 2026; Table 3 separately averages three seeds for classification. This defines the claim's scope and distinguishes the audit from a single aggregate run. Training on 2b sessions 1--3 would constitute a new protocol requiring inner validation to preserve sessions 4--5 as untouched tests.

Response to Critical Weakness 2: reliance versus utility

The audit asks whether classification benefits from the current trial's dynamic weights with its Values and parameters fixed. Across eight decoders, the two empirical replacements change mean BA by only −0.51-0.51 to +0.93+0.93 pp. Some replacements even increase mean BA for ATCNet, EEG Conformer, CTNet, and TCFormer. Thus the current-trial weights are functionally replaceable at the task level in the audited models.

Under these replacements, trial-specific weighting shows no supported decision benefit, so the attention maps lack a decision-level interpretation. Treating an attention block as evidence of functional dynamic attention encourages more attention, residual paths, or compensators without verifying route use. This is a consequential mechanism-design failure even when the classifier remains accurate.

The direct-bypass result provides positive evidence for the diagnosis. Exposing class evidence outside attention collapses RcoreR_{\mathrm{core}} from 18.61--40.95 pp to approximately zero while largely preserving BA. Route dependence therefore follows the information path, exactly as the proposed bypass mechanism predicts.

The repair target is dependence on sample-conditioned routing; local-peak discovery lies outside this claim. SOAMNet's global context remains inside the sole audited route. Local temporal information adds reliable utility: independently trained global-only variants lose 0.95--2.45 pp on every dataset with paired intervals excluding zero, and evidence-matched swaps lose 1.32--3.12 pp. Thus global context drives the principal route and temporal content further improves classification. Maximum-dissimilarity swapping quantifies stress-test sensitivity, whereas evidence-matched swaps quantify local utility.

Response to Questions 1--2: implementations, checkpoints, and training

No separate audit models were trained. Figure 1 and Table S10 use the seed-2026 2b checkpoints contributing to Table 2; S2 does the same for 2a. Table 2 averages seeds 2026/2036/2046; S3 records audit targets and S8 study-wide settings. We used pinned official/author implementations where available and only intervention adapters/hooks. Data are evaluated at 250 Hz; cue windows are 0.5--4/0--4/0--5/0--3 s for 2b/2a/BNCI/Cho, with 4--40 Hz filtering except SSTAF (8--30 Hz) and FBCNet's nine-band input. Normalization is training-only and checkpoints are selected by validation BA.

Response to Questions 3--4: route activity, logits, and β\beta

Cross-sample replacement is a bijection over evaluation trials, preserving the marginal distribution of attention tensors and route activity ρc\rho_c while breaking their pairing with current-trial Values. This design rules out global activity collapse as the source of the BA effect. Figure 2(c) already traces propagation from AA through AVAV to logits. Finally, fixing β=0\beta=0 lowers BA by only 1.31 pp on 2b and 1.10 pp on BNCI2015-001; SOAMNet still exceeds ATCNet by 1.84 and 3.32 pp, respectively.

For weakness 1. The stricter-protocol explanation is plausible, and the details provided on splits, checkpoint selection and training settings are consistent with it.

For weakness 2. The response clarifies the scope of the claim, namely functional reliance on sample-conditioned attention weights. Within this scope, my concern is addressed.

Overall, I am raising my rating to 3 (weak acceptance).

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

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