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Under review as a conference paper at ICLR 2027

AdaRelate: Learning to Acquire Multiscale Evidence for EEG Emotion Recognition

Abstract

Emotion-related EEG structure spans individual channels, geometry-defined regions, and relations between regions, yet the useful scale and target change with each recording. Existing static and sample-adaptive graphs generally instantiate a broad relational representation in one pass, before the value of its constituent computations is known. AdaRelate instead formulates recognition as reliability-anchored sequential hierarchical evidence acquisition. A training-fitted low-order anchor supplies initial class logits. A graph-constrained actor–critic then selects a REGION, CHANNEL, RELATION, or STOP action; only the selected shared expert is evaluated, and its evidence conditions the next decision. A strictly forward accumulator incorporates preceding windows within each trial. Across four datasets, the complete system exceeds the strongest reproduced mean for Accuracy, balanced accuracy, and macro-F1. A matched three-seed evaluation yields 66.81% Accuracy, against 65.87% for one-shot top- and 65.64% for no-RL routing. Removing the anchor reduces Accuracy by 7.42 points, while forward history contributes 6.06 points. Evidence-nulling diagnostics show that acquired evidence changes subsequent actions and stopping decisions, and four-dataset maps reveal distinct channel, region, and relation allocations. The results establish a hierarchical EEG interface in which a reliable prediction base and sequential reinforcement learning jointly support sample-conditioned emotion recognition.

Primary area:
learning on graphs and other geometries & topologies
Keywords:
EEG emotion recognition, adaptive computation, multiscale evidence acquisition, graph learning, reinforcement learning

Reviews

Among:
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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_Gpv8OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

EDIT: Given the additional evidence provided in the rebuttal, I have decided to raise my score.

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AdaRelate formulates EEG emotion recognition as reliability-anchored sequential evidence acquisition rather than one-shot graph inference. A linear "anchor" classifier fitted on low-order, training-standardised channel descriptors supplies a zero-action logit prediction; together with a learned low-cost overview readout it forms a "prediction base" that is frozen for evaluation. A graph-constrained actor–critic then iteratively selects one legal action from a typed vocabulary: REGION (open one of 8 fixed sensor-geometry groups), CHANNEL (query one of 62 electrodes inside an opened region), RELATION (compare one of 28 opened region pairs), or STOP, invoking only the selected parameter-shared expert. Acquired evidence updates a gated GRU state (which conditions the next decision) and a bounded logit residual on top of the anchor. A strictly-forward accumulator then fuses window predictions within each trial (dataset-frozen exponential decay; cumulative mean plus uncertainty-scaled prior on MPED). Classification supervision is applied at every prefix; the actor is rewarded by the detached reduction in prefix cross-entropy minus a measured action cost.

The system is evaluated on SEED, MPED, SEED-IV, and SEED-V under personalised (within-subject) splits using 62x10x5 differential-entropy inputs, subject-level metrics (Accuracy, BAcc, macro-F1), subject-bootstrap CIs. AdaRelate exceeds the strongest reproduced mean on all 12 dataset-metric margins. Ablations on MPED attribute +7.42 pp to the fitted anchor, +6.06 pp to forward history, +1.65 pp to the uncertainty prior, and +0.55 pp to dual quality scoring. A matched three-seed MPED study gives 66.81% for Full vs 65.87% one-shot top-k (+0.93 pp) and 65.64% no-RL/static (+1.17 pp). Beyond the benchmark tables, the authors audit whether the mechanism works as intended: they zero out the acquired evidence to check whether it actually changes the policy's subsequent decisions; they replay each trajectory with a fixed number of acquisitions (0 to 6) to measure what each step adds; they replace the policy's selected targets with random or unselected alternatives of the same type; they map onto the scalp which channels, regions, and relations are used and how much each helps; and they measure inference latency and throughput.

Critical strengths

S1: The evaluation is overall rigorous. The subject, not the window or the fold, is the unit of every statistical test. Confidence intervals come from bootstrap resampling over subjects. Paired tests use 100k permutations with Holm correction. A check on 857,808 perturbed windows proves that the model never reads future data. Intervention tests that remove or replace acquired evidence measure what each component does.

S2: The formulation is genuinely novel. The model does not build the full graph in one pass. It makes a sequence of decisions: open a scalp region, query one channel in that region, compare two open regions, or stop. An action is legal only after its prerequisites. Only the selected computation runs. The model learns when to stop. This differs from one-shot adaptive-graph methods such as DGCNN and IAG/V-IAG, and from generic glimpse-selection methods. The decision path is an execution record rather than a post-hoc attribution: for each sample it shows which expert ran, on which target, and in which order.

Critical weaknesses

W1: The gains are small. When the system is forced to acquire no evidence at all (budget K0), its accuracy already equals the full system on SEED and SEED-V, is slightly better on SEED-IV, and only on MPED does acquisition help, by 0.63 points, with p = 0.1763. The gains attributed to the sequential routing policy itself are measured on MPED alone. What carries the results instead are the frozen anchor (+7.42 points) and the forward-history accumulator (+6.06 points): both are generic add-ons that could be attached to any baseline, and without the anchor the acquired-evidence system scores below a reproduced DGCNN on MPED (59.43% vs 65.75%). The remaining evidence points the same way: removing the RELATION level costs almost nothing, replacing the policy's chosen targets with random alternatives of the same type costs 0.03 points, and deleting all acquired evidence changes the next decision in only 1.45% of cases.

W2: The evaluation cannot exclude that the reported gains reflect memorisation and trial-context effects rather than emotion decoding. Every model is trained and tested on the same subject, and there is no LOSO or even fully held-out session result: the authors' own split puts "trials 1-3 from session 3" into selection training while "session-3 trials 4–15 form the outer partition" on SEED, and places "the first session-3 trial of each class" in training on SEED-IV/V (Appendix B.1). A within-subject model can therefore exploit subject- and session-specific idiosyncrasies instead of transferable emotional structure, and the protocol never tests this. Emotion labels are constant within a trial, and the forward-history accumulator, the second-largest measured effect at +6.06 points, profits directly from this persistence: once the first windows of a trial are correct, later predictions are smoothed toward the same label. Because the reproduced baselines run without the anchor and the accumulator, part of every reported margin may measure trial-context exploitation rather than better decoding.

Questions for authors

Q1: Can you report a fully held-out session-3 evaluation, and ideally a LOSO result? The model is personalised by design, but the paper motivates it through inter-individual variability, so even within the personalised setting, a clean held-out-session split is needed to show the gains reflect more than subject and session-specific patterns.

Q2: Can you report the matched three-seed routing contrasts on SEED, SEED-IV, and SEED-V, not only on MPED? Tables 7 and 8 indicate that acquisition gains are almost 0 or negative outside MPED; if confirmed, the central claim should be narrowed.

Q3: Substituting the policy's targets with random or unselected same-type alternatives costs only 0.03 points. What evidence shows that which target is selected matters, rather than merely that some legal action is taken?

A. (Suggestion) Report the accuracy and latency of a variant that runs every expert on every sample: all regions, all channels, and all relations. This gives the dense upper bound on performance and a concrete reference for the efficiency claims.

B. (Suggestion) It would be interesting if you could test the method with fewer electrodes: for example, keep only 32, 16, or 8 of the 62 channels, or even use a low-cost EEG dataset with 4 channels. If sequential acquisition is what drives the improvement, its advantage should grow as the number of possible targets grows; if it stays near zero at every channel count, the gains come from the prediction base. Low-cost devices also produce noisier channels, which is the setting where the channel-reliability scoring should help most.

Reviewer_VeLJOpenReview ↗
Rating
3
Confidence
4
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes AdaRelate, a sequential evidence-acquisition framework for EEG emotion recognition. The method begins from a low-order prediction anchor and uses a graph-constrained actor–critic policy to sequentially select REGION, CHANNEL, RELATION, or STOP actions. Only the expert corresponding to the selected action is evaluated, and the acquired evidence updates both the recurrent state and the class logits. A forward accumulator additionally incorporates preceding windows within a trial. The method is evaluated on four EEG emotion datasets with comparisons against reproduced baselines, routing controls, component ablations, statistical tests, and analyses of the learned acquisition behavior.

Critical strengths

The paper formulates multiscale EEG processing as a sequential evidence-acquisition problem rather than another static or one-shot graph construction. The typed action grammar and learned stopping mechanism provide a coherent connection between the motivation and the algorithm. The experimental analysis is unusually comprehensive. The matched one-shot and non-RL controls, repeated-seed evaluation, subject-paired comparisons, stopping diagnostics, and evidence-nulling analyses provide more insight than a conventional benchmark comparison.

Critical weaknesses

1.The evidence that reinforcement-learning-based sequential routing is responsible for the main performance improvement is limited. The reported difference from matched one-shot top-k and non-RL routing is approximately one percentage point, whereas the anchor and forward-history components contribute much larger gains. This makes it unclear whether the central RL mechanism is necessary. 2.The method uses preceding windows within the same trial, while emotion labels and stimulus conditions are often persistent at the trial level. The current results do not completely separate improved EEG representation from exploitation of trial-level temporal continuity.

Questions for authors

1.Can the authors report a complete matched-budget comparison among the full RL router, one-shot top-k routing, non-RL routing, and a fixed or random legal routing policy on all four datasets? This would directly test whether sequential policy learning provides benefits beyond the action vocabulary and expert architecture. 2.Please provide a full factorial ablation of the anchor, forward-history accumulator, and RL router, if available. In particular, does RL routing remain beneficial when the anchor and history components are held fixed? 3.Can the authors report the accuracy–computation curve as the maximum number of acquisitions varies? The learned STOP action is a central contribution, but its benefit should be demonstrated against fixed-step policies at matched average computation. 4.Please clarify how train/test splits interact with trials and temporal windows. Are all windows from a trial or recording kept within a single split? If not, a trial-disjoint re-evaluation would materially affect my assessment. 5.A useful diagnostic would be to shuffle preceding windows across trials while preserving the number of available historical windows. Can the authors provide this control, or explain from existing results why the history gain reflects meaningful temporal evidence rather than trial identity or stimulus persistence?

Reviewer_btZHOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes AdaRelate for EEG emotion recognition from DE features. A linear anchor fitted on low-order channel statistics gives the initial logits. An actor–critic policy then picks REGION, CHANNEL, RELATION or STOP actions one at a time, and each selected expert adds a bounded residual to the logits. Window predictions are finally averaged with the preceding windows of the same trial. Subject-dependent experiments on SEED, MPED, SEED-IV and SEED-V report gains of 1.1–6.6 points over eleven reproduced baselines.

Critical strengths
  1. The statistical reporting is careful, with subject-level paired tests, bootstrap confidence intervals and Holm correction, and the code is released.
  2. The appendix includes budget sweeps, relation controls, evidence interventions and runtime profiles, which makes it possible to check where the gains come from.
Critical weaknesses
  1. According to the paper's own appendix, the core contribution, sequential RL acquisition, has almost no effect. Table 7 shows that with no expert called, accuracy already equals the final result on SEED and SEED-V, is slightly higher on SEED-IV, and is only 0.63 points lower on MPED, a difference that is not significant. Table 10 shows that replacing the selected target with a random one of the same type changes accuracy by 0.03 points, and Table 9 shows that removing RELATION actions changes nothing. The routing gains of 0.93 and 1.17 points are measured against controls that fall below the anchor-only result. The margins over baselines therefore come from the linear anchor and the trial-history averaging, not from learned multiscale acquisition.

  2. The benchmark numbers are not comparable to the literature. The split follows no standard protocol for these datasets, and all baselines are re-run by the authors. Several reproductions are close to chance: CADD-DCCNN reaches 25.9% on 5-class SEED-V and DGC-Link 34.2% on 4-class SEED-IV. DGCNN reaches 64.3% on SEED, against about 90% in its original subject-dependent setting. Cross-subject methods such as PR-PL, CADD-DCCNN and EmT are forced into a subject-dependent setting. AdaRelate also benefits from trial-history averaging, worth 6.06 points on MPED, which the baselines do not appear to receive, and its row in Table 1 is a single selected seed.

  3. The most directly related methods are not compared. The paper's central argument is that existing sample-adaptive graphs build the relational structure in one pass. Yet IAG and V-IAG by Song et al., which the paper itself cites as representative instance-adaptive graphs, are missing from the comparison, although IAG was originally evaluated on SEED and MPED. APAGNN, which progressively combines global, region and channel experts, and VPR, which performs adaptive pathway selection, are also close in spirit. Also absent are region and relation models such as RGNN, BiHDM and LGGNet; recent work the paper cites, such as FreqDGT, MSGM and TAS-Net; EEG foundation models such as LaBraM and CBraMod; and a simple SVM or MLP baseline with the same trial-level averaging.

  4. The motivation does not hold up. The paper argues that one-shot graphs waste computation before its value is known, but the whole model costs about 2.7M MACs. Table 11 shows that adaptive inference is slower than the anchor-only path, 23.2 ms against 18.2 ms, and five times slower than evaluating all 28 relations at once. Learned stopping only shows up on MPED, with 2.19 actions per sample; on the other three datasets the policy uses 5.2 to 6.0 of the 6 allowed actions. Inter-subject variability is cited as motivation, yet every model is trained per subject.

  5. Reproducibility and presentation are weak. The method stacks many dataset-specific parts, including anchor views, the decay ρD\rho_D, an uncertainty prior, teacher distillation, a safety loss and a checkpoint guard, and their values appear only in the repository. The way the baselines were adapted is not described. The writing relies on self-made terms such as "execution contract" and "claim–evidence ledger", and Section 3.6 and Table 2 repeat the same summary. The most informative negative results are left in Appendix G.

Questions for authors

Mostly as in Weaknesses. In particular:

  1. What are the results under the standard protocol of each dataset, so they can be compared with published numbers?
  2. How does AdaRelate compare with IAG and V-IAG under the same protocol, given that these are the sample-adaptive graphs the paper argues against?
  3. How do the baselines perform with the same trial-history averaging, and how does the anchor alone with this averaging compare to the full system on all four datasets?
  4. Why do the one-shot and no-RL controls fall below the anchor-only result, and how were the reproduced baselines tuned?

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

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