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Under review as a conference paper at ICLR 2027

Organize Once, Adapt Efficiently: Target-Conditioned Hypergraph Retrieval for Few-Shot Motor Imagery EEG Adaptation

Abstract

Rapid deployment of motor imagery–based brain–computer interfaces (BCIs) requires reliable decoding for new users with few calibration trials. Prior source-selection methods reuse historical electroencephalography (EEG) data through subject-level screening, trial-level scoring, or pairwise graph propagation. However, exploiting higher-order relations among trials for budget-constrained, target-conditioned source-trial retrieval remains challenging. To address this, we view transfer utility not as an intrinsic pointwise property but as a target-dependent structural quantity jointly determined by local discriminative coherence and cross-domain reproducibility, and propose a neural retrieval framework over a reusable dual-relation source hypergraph. Following an organize-once, retrieve-per-target paradigm, we build this hypergraph offline with local semantic and cross-domain consensus relations. Online, we query this hypergraph with a small target support set to construct a subhypergraph and select transferable trials through structural propagation and budget-constrained ranking. Cross-subject and cross-dataset experiments on BNCI2014-001, Cho2017, and Lee2019-MI show that, in some settings, our method matches or outperforms the All-source training reference while using as little as 2.35% of the available source trials for target adaptation.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Brain–computer interfaces, motor imagery, few-shot learning, transfer learning

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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.
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Paper summary

TETHER formulates few-shot motor-imagery EEG adaptation as target-conditioned, fixed-budget source-trial retrieval. A source-supervised encoder embeds covariance/tangent-space and bandpower features. Local semantic and cross-domain consensus hyperedges organize the source repository; a small labeled target support set retrieves and attaches to relevant hyperedges. Two HGNN branches, a relation gate, and a trial scorer are trained using source-only pseudo-target episodes and a differentiable weighted-ridge utility objective. At deployment, exact class-balanced selection provides a source subset, and a selected-source-fitted tangent/bandpower logistic classifier is trained with target support. Evaluation covers four-class BNCI2014-001 LOSO and binary cross-dataset LODO on BNCI-LR, Cho2017, and Lee2019-MI. The paper emphasizes adaptation accuracy, small selected-source budgets, and sub-second online processing.

This assessment concerns the 22-page manuscript and the supplied TETHER_code archive. It includes static inspection, a passing subset of 18 supplied tests, and limited synthetic checks of core retrieval functions, not reproduction of the reported EEG experiments. The archive explicitly omits recordings, checkpoints, and experimental outputs.

Critical strengths

1. A coherent task-specific retrieval formulation with an implemented learning mechanism. Reusing source-side organization while conditioning selection on a small labeled support set addresses a concrete adaptation problem. The local/consensus relations and downstream-utility supervision form a connected design rather than unrelated feature modules. The inspected implementation contains the stated normalized hypergraph propagation and differentiable ridge solve. Limited synthetic checks confirm agreement with the propagation equation, gradient flow through the utility mechanism, and feasible exact class-balanced selection; these checks do not validate benchmark accuracy.

2. Useful data-isolation provisions and informative controlled ablations. The final classifier fits its tangent reference and scalers on selected sources, and its fitting API excludes real target-query data. The retriever removes the pseudo-target domain from episode graphs/candidates while transparently allowing its earlier source-encoder pretraining. The release provides nested-support/trial-ID checks and documents seed-within-subject aggregation. Table 3 and its runner use the same final decoder for the main method and structural/utility ablations. The README is unusually explicit about comparison and preprocessing limitations. These are meaningful strengths, even though the principal comparisons and efficiency claims remain unresolved.

Critical weaknesses

1. The principal comparisons change the downstream model and adaptation weighting, so they do not establish the claimed benefit of source-trial retrieval.

The README explicitly states that traditional selector baselines use EEGNet with a fixed per-target-sample weight of 2, whereas the final TETHER results use tangent/bandpower features and logistic regression with 50% of the total training-weight mass assigned to target support (README.md, lines 279–295). This is confirmed by tether/lodo_training.py, lines 41–76, and tether/tangent_decoder.py, lines 83–112 and 124–177. The documented two-stage binary workflow first generates selections and intermediate EEGNet scores, then uses scripts/run_tangent_binary.py for the reported TETHER classifier; the README explicitly says the intermediate TETHER scores are not the reported results (lines 92–101).

For balanced binary B=500, the neural baselines' nominal target-weight fractions are 3.85%, 7.41%, and 13.79% at 5/10/20 shots per class, rather than 50%. These are nominal sample-weight fractions, not an assertion about exact gradient contributions under batch-normalized losses. Nevertheless, representation, classifier, optimization, and target emphasis all change together with selection. Thus, the large gaps in Tables 1–2 and Figure 4 cannot be attributed specifically to higher-order retrieval. Complete-system comparisons can be useful, but should be labeled and interpreted as such; the README acknowledges that they do not isolate the selector. The decisive missing comparison is to pass random, similarity-based, pairwise, and TETHER-selected subsets through the same final feature map/classifier, target-weight policy, and development budget. Native end-to-end methods such as RSSDA can remain additional system-level references.

The binary All-source reference is also inconsistent between manuscript and implementation. Appendix C.1 (p. 17) says it uses all source trials plus a fixed target reference support set. In the supplied runner, tether/lodo_bnci_seed0.py, lines 455–476, passes an empty target-index array and explicitly records baseline_protocol="source_only" and target_trials_used=0. README.md, lines 288–290, confirms this is not an all-source version of the target-adapted classifier. Consequently, comparisons with that row do not establish that selecting 2.35% of sources improves on equivalently adapted all-source learning. The percentage itself is a correct selected-subset ratio, but it is not the total historical data used to learn the encoder, graph, and retriever. An all-source reference using the same support and final decoder is needed; the source-only reference should be retained under an accurate label. The support definition underlying the shot-independent four-class All-source row also needs to be made explicit.

Table 3 provides more relevant within-pipeline evidence and should not be dismissed. However, removing HGNN propagation changes Macro BA from 0.5196/0.5407/0.5781 to 0.4948/0.5266/0.5618, substantially smaller changes than the headline cross-system gaps. Their importance should be assessed with paired subject-level effects and uncertainty, not inferred from marginal standard deviations. The no-utility ablation deliberately removes both utility training and the learned scorer, as disclosed in the paper, and is therefore not a one-factor isolation of a loss term. A non-hypergraph or pairwise retriever with the same frozen encoder and utility supervision would better distinguish the specific structural contribution. There is also a surrogate/deployment gap: training evaluates soft sample weights through ridge regression in frozen embeddings, whereas deployment uses hard selections and refitted tangent features with logistic regression. This is not an algebraic error, but evidence that the surrogate ranks subsets usefully for the final classifier would strengthen the central utility claim.

2. The efficiency and preprocessing claims are not aligned with the supplied measurement and execution paths.

Runtime boundaries. Section 4.2 and Appendix E.2 define the approximately 0.64-second online cost as source retrieval plus target adaptation, excluding query forward inference. In scripts/run_tangent_binary.py, selections are read and checked before timing (lines 398–434); the timer begins at line 439, includes feature-map/classifier fitting and query prediction, and ends at line 448. The recorded training_seconds therefore excludes retrieval and includes query inference. Baseline runtime fields include validation-stage and final-stage selection/training (tether/lodo_bnci_seed0.py, lines 949–960), and the compared classifiers are different. README.md, lines 307–318, explicitly warns that these fields cannot be compared directly as end-to-end online latency. This does not prove that Table 11 was computed from those exact fields, but the supplied timing path does not substantiate its advertised boundary or the approximately 9x retrieval/adaptation speedup. The table-producing script and measured phase-level logs, matched cache conditions, hardware/synchronization details, and the offline amortization denominator are needed.

Four-class preprocessing. Appendix D (p. 18) describes a common fourth-order zero-phase Butterworth pipeline and 0.5–3.0-second, 625-sample epochs. The documented four-class final configuration uses tmin=0.5, tmax=4.0 (configs/bnci2014_001_final.yaml, lines 20–29). Its extraction path uses raw.filter(method="fir", phase="zero") and passes those epoch limits directly to MNE (tether/data.py, lines 153–222). Thus the supplied four-class entry point does not implement the universally stated window/filter combination. The binary preprocessing path does implement the stated 0.5–3.0-second crop; this discrepancy should not be generalized to every task. The authors should identify the exact configuration/cache version underlying each table and reconcile filtering, referencing, trial normalization, and source-statistic fitting.

Signal-level partition dependence. For Cho2017, complete continuous class recordings are filtered/resampled before epochs receive reconstructed run labels (tether/lodo_data.py, lines 110–152 and 258–307); support/query partitioning occurs subsequently in tether/lodo_splits.py, lines 39–58. README.md, lines 297–305, acknowledges that the bidirectional preprocessing can couple signals across a partition boundary and that its effect has not been measured. Trial-ID disjointness is a useful check, but does not by itself establish strict signal-level independence. I have not established the size of this effect or demonstrated performance inflation. Partition-wise preprocessing or a targeted boundary-dependence check is needed to resolve this limited risk, without assuming that the complete test set contaminated training.

Finally, the code/report discrepancies cannot be resolved from aggregate means alone. Rechecking 170 displayed recall-to-Macro-BA rows found agreement within rounding, which is a positive internal consistency check; it does not verify the subject-level predictions, standard deviations, or Holm-adjusted tests. Result-matched configurations, prediction/selection outputs, and the statistics/timing scripts would allow the main comparisons to be audited. Omission of raw outputs is not by itself a reason for rejection; their importance here follows from the concrete protocol mismatches.

Overall assessment. I recommend rejection in the current form. The main concern is not an intrinsically invalid hypergraph algorithm or implausibly high accuracy: the current evidence does not separate source selection from different downstream learners and adaptation weights, and the advertised efficiency/protocol definitions are not established by the supplied paths. The archive's transparency and working core functions are appreciated. I found no direct evidence of fabricated data or deliberate target-query-label use in model fitting. Matched-decoder comparisons and reconciled, independently auditable execution/timing records could materially change the assessment.

Questions for authors

1. Matched-selector evaluation. Can the existing random, similarity-based, pairwise, and TETHER-selected subsets be decoded with exactly the same selected-source-fitted tangent/bandpower map, logistic classifier, target mass, and tuning policy? Please provide paired subject-level changes. Which Tables 1–2/Figure 4 comparisons were intended as complete-system rather than selector-only comparisons?

2. All-source information budget. Why does Appendix C.1 describe target reference support for binary All-source while the runner passes an empty target set? Please identify the result-producing configuration and report all-source with the same k-shot support and final decoder. What support set produced the single four-class All-source reference?

3. Timing provenance. Which script and measured records produced Table 11? Please separate cached/source-side preparation, support encoding, source retrieval, decoder fitting, and query prediction, with identical measurement boundaries for competing methods. What offline cost and number of reuses define the amortized values, and are validation/development costs handled equivalently?

4. Preprocessing correspondence and isolation. Did the four-class results use the documented 0.5–4.0-second FIR configuration or the manuscript's 0.5–3.0-second Butterworth pipeline? Please provide configuration hashes, epoch shapes, and preprocessing manifests. For Cho2017, has partition-wise processing or a signal-boundary dependence test been performed?

5. Structural contribution and result traceability. Please provide paired effects for the existing ablations and, if available, a retriever with matched utility supervision but no hypergraph/pairwise-only structure. How well does the soft ridge utility correspond to performance of the hard-selected logistic decoder? Please identify the subject–seed prediction outputs and aggregation/statistics code underlying the principal means, uncertainty, and significance annotations. These requests concern the reported claims and existing datasets, not a new application domain.

10 comments
AuthorsOpenReview ↗

Response to Reviewer HAqy [1/N]

We sincerely appreciate your careful and technically detailed review, as well as your positive comments on our data-isolation safeguards and controlled ablations. Your questions helped us identify aspects of the experimental scope, implementation, and result traceability that required clearer explanation and validation. In response, we have added new analyses and revised the manuscript accordingly. Below, we address each point in turn and welcome any further questions or suggestions.


[W1] The principal comparisons change the downstream model and adaptation weighting, so they do not establish the claimed benefit of source-trial retrieval.

Thank you for your question, and we sincerely apologize for the confusion. The original experiments primarily evaluated the overall performance of the complete TETHER framework relative to existing methods. To further clarify the independent contributions of the retrieval strategy and its structural design, we have added retrieval comparisons under a common downstream decoding protocol (Q1), further clarified the target support set and information budget used by the All-source reference method (Q2), and further examined the roles of hypergraph structure and utility supervision through subject-level paired analyses of the existing ablation configurations, comparisons of different retrievers under the same utility supervision, and an analysis of the correspondence between the soft training surrogate and final decoding with hard selection (Q5). These additional analyses strengthen the original experimental evidence by addressing fairness in downstream evaluation, the contribution of retrieval structure, and consistency between training and deployment. The additional experiments further show that, under common downstream decoding conditions, TETHER maintains high mean Macro BA across the evaluated source-data budgets and support-set sizes. Meanwhile, the retriever comparisons under the same utility supervision provide more direct evidence for analyzing the additional value of the dual-relation hypergraph relative to unstructured retrieval and simple relation modeling. These results enable us to distinguish more carefully among full-system performance, the retriever's contribution, and the contribution of the structural design.


[W2] The efficiency and preprocessing claims are not aligned with the supplied measurement and execution paths.

Thank you for carefully examining this part of the work. To address the correspondence between the original timing records and the actual execution pipeline, we have reviewed the relevant execution entry points and retained records, established a staged timing protocol that distinguishes source-side preparation, target-side online calibration, and query inference, and explicitly described the scope of caching, the cost of building offline resources, and their actual reuse counts (Q3). To address the inconsistency in preprocessing protocols, we have rechecked the raw GDF data and processing configurations for the four-class task, corrected the descriptions of the filters, time windows, and epoch data shapes actually used, and added a boundary-dependence check for continuous-signal preprocessing in Cho2017 (Q4). In addition, we have further organized the prediction outputs at the subject and random-seed levels and their correspondence with metric computation, statistical aggregation, and significance testing to improve the traceability and verifiability of the reported results (Q5).

These checks clarify the actual measurement scope of the efficiency metrics in the paper, distinguishing online calibration time, query inference time, and source-side offline preparation costs. The preprocessing checks identify and correct inaccuracies in the original description of the four-class processing pipeline and quantify cross-boundary dependence in the original continuous-signal processing for Cho2017. Together with the organization of prediction outputs and statistical analysis records, this additional work further clarifies how the experimental results were obtained and the scope to which they apply, avoiding interpretations of runtime efficiency, data isolation, and statistical conclusions that extend beyond the available evidence.

AuthorsOpenReview ↗

Response to Reviewer HAqy [2/N]

[Q1] Matched-selector evaluation.

Thank you for your question. We have added four-class LOSO experiments on BNCI2014-001 and provide the following clarifications.

1. Scope of interpretation of the original comparisons

The original Tables 1–2 and Figure 4 were intended to evaluate the overall performance of the complete TETHER framework and existing transfer methods under their respective experimental protocols. For the conventional selection baselines that use a common downstream EEGNet pipeline (Random, Subject-level Top-k + Random, Bandpower, Riemannian, Pairwise, MTS, and MEIS), the results can be used to compare the performance of different source-data selection strategies within that decoding pipeline. RSSDA is evaluated using its specialized adaptation pipeline. All-source and Subject-level Top-k + All Trials serve as reference methods unconstrained by a fixed source-data budget, providing performance references when all available source trials are used. Thus, the original experiments primarily support comparisons of the overall performance of different complete methods and their respective selection strategies. The additional experiments with common downstream decoding further control the feature mapping, final classifier, and target support sample weights to analyze the contribution of the source-trial selection strategy itself more directly.

2. Additional comparisons under a common downstream protocol

All methods use the same source-data budget, target support set, query set, and random seeds. The final Tangent Space / Bandpower feature mappings are fitted using the source trials selected by each method. All methods use Logistic Regression, the same proportion of total weight assigned to target support samples, and parameter configurations fixed in advance. Tables 1–2 report the comparisons for B=500 and B=1000, respectively. TETHER achieves the highest mean Macro BA in all evaluated 5-, 10-, and 20-shot settings. These results show that, under common downstream decoding conditions, TETHER's target-conditioned source-trial selection continues to provide favorable overall adaptation performance, offering further evidence for the effectiveness of its retrieval strategy.

Table 1 Retrieval comparisons with matched downstream decoders: four-class LOSO on BNCI2014-001, B = 500

ShotMethodLeft HandRight HandBoth FeetTongueMacro BA
5Class-balanced Random-B0.4438 ± 0.19180.5494 ± 0.18030.4086 ± 0.15180.4988 ± 0.29020.4752 ± 0.1418
5Bandpower Top-B0.3886 ± 0.20500.5324 ± 0.21550.3892 ± 0.15510.5296 ± 0.28000.4600 ± 0.1385
5Riemannian Top-B0.4404 ± 0.25350.5389 ± 0.22810.4457 ± 0.19470.5481 ± 0.29070.4933 ± 0.1595
5Pairwise kNN Graph Diffusion0.4481 ± 0.21210.4596 ± 0.19870.4623 ± 0.24730.4735 ± 0.30880.4609 ± 0.1514
5TETHER0.4830 ± 0.14170.5654 ± 0.16100.4691 ± 0.13580.5608 ± 0.22310.5196 ± 0.1425
10Class-balanced Random-B0.4972 ± 0.22840.5506 ± 0.22660.4627 ± 0.19500.5423 ± 0.26010.5132 ± 0.1556
10Bandpower Top-B0.4503 ± 0.25530.5660 ± 0.21520.4287 ± 0.18710.5528 ± 0.30230.4995 ± 0.1545
10Riemannian Top-B0.4836 ± 0.26860.5466 ± 0.24840.5046 ± 0.21680.5821 ± 0.27210.5292 ± 0.1617
10Pairwise kNN Graph Diffusion0.4873 ± 0.24100.4904 ± 0.22470.5136 ± 0.25940.5204 ± 0.29680.5029 ± 0.1551
10TETHER0.5457 ± 0.18920.5627 ± 0.19600.4849 ± 0.15580.5694 ± 0.24330.5407 ± 0.1440
20Class-balanced Random-B0.5049 ± 0.21530.5753 ± 0.24340.5404 ± 0.20010.5840 ± 0.26510.5512 ± 0.1533
20Bandpower Top-B0.4590 ± 0.27030.5852 ± 0.22830.5244 ± 0.23270.5932 ± 0.28370.5404 ± 0.1568
20Riemannian Top-B0.4821 ± 0.26050.5633 ± 0.27010.5769 ± 0.24400.6154 ± 0.25110.5594 ± 0.1631
20Pairwise kNN Graph Diffusion0.5056 ± 0.20900.5485 ± 0.21440.5420 ± 0.22850.5861 ± 0.26390.5455 ± 0.1493
20TETHER0.5485 ± 0.21030.5722 ± 0.23190.5673 ± 0.18980.6244 ± 0.22920.5781 ± 0.1301
AuthorsOpenReview ↗

Response to Reviewer HAqy [3/N]

Table 2 Retrieval comparisons with matched downstream decoders: four-class LOSO on BNCI2014-001, B = 1000

ShotMethodLeft HandRight HandBoth FeetTongueMacro BA
5Class-balanced Random-B0.4454 ± 0.22040.5614 ± 0.21240.4253 ± 0.16940.4830 ± 0.30310.4788 ± 0.1513
5Bandpower Top-B0.4136 ± 0.24060.5123 ± 0.24650.4198 ± 0.17890.5509 ± 0.27510.4742 ± 0.1558
5Riemannian Top-B0.4549 ± 0.28030.5198 ± 0.25950.4654 ± 0.22220.5182 ± 0.30470.4896 ± 0.1689
5Pairwise kNN Graph Diffusion0.4534 ± 0.22170.4883 ± 0.22400.4821 ± 0.23700.4602 ± 0.30820.4710 ± 0.1619
5TETHER0.5287 ± 0.19970.5127 ± 0.21010.4747 ± 0.15680.5769 ± 0.22180.5233 ± 0.1344
10Class-balanced Random-B0.4812 ± 0.22420.5645 ± 0.24290.4750 ± 0.20550.5373 ± 0.24800.5145 ± 0.1521
10Bandpower Top-B0.4682 ± 0.25720.5389 ± 0.25750.4676 ± 0.20610.5534 ± 0.28600.5070 ± 0.1629
10Riemannian Top-B0.4818 ± 0.28350.5327 ± 0.26280.5059 ± 0.24230.5571 ± 0.28990.5194 ± 0.1695
10Pairwise kNN Graph Diffusion0.4849 ± 0.24320.5130 ± 0.23000.5117 ± 0.24880.5244 ± 0.29520.5085 ± 0.1666
10TETHER0.5537 ± 0.20840.5463 ± 0.23370.5191 ± 0.19760.6111 ± 0.25150.5576 ± 0.1373
20Class-balanced Random-B0.5019 ± 0.21370.5787 ± 0.24570.5543 ± 0.19960.5830 ± 0.24690.5545 ± 0.1529
20Bandpower Top-B0.4852 ± 0.27280.5481 ± 0.26130.5457 ± 0.25520.5932 ± 0.25930.5431 ± 0.1613
20Riemannian Top-B0.4864 ± 0.27190.5636 ± 0.27790.5772 ± 0.26040.5920 ± 0.25970.5548 ± 0.1623
20Pairwise kNN Graph Diffusion0.5191 ± 0.22750.5611 ± 0.23350.5556 ± 0.22900.5731 ± 0.25200.5522 ± 0.1552
20TETHER0.5775 ± 0.20360.5716 ± 0.22710.5753 ± 0.23380.6873 ± 0.19700.6029 ± 0.1393

After controlling for the downstream learner, TETHER continues to achieve the highest mean Macro BA under the tested conditions, supporting the overall effectiveness of its retrieval pipeline.

Reviewer_GqG1OpenReview ↗
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Paper summary

The paper presents TETHER, a framework for selecting a compact, target-relevant subset of historical motor imagery EEG trials for few-shot adaptation. A source-trained encoder organizes trials into two reusable hypergraph relations: same-class local neighborhoods and cross-domain neighborhoods subject to domain-coverage and membership constraints. A small labeled target support set retrieves relevant hyperedges, attaches support nodes, and conditions two HGNN branches and a trial scorer. The retriever is trained through source-only pseudo-target episodes, using a differentiable weighted ridge estimator to supervise scores by downstream prediction utility. At deployment, the frozen retriever selects an exact class-balanced source budget, after which feature statistics are refitted and a logistic regression decoder is trained with the selected sources and target support. Experiments on three public datasets evaluate four-class cross-subject and binary cross-dataset adaptation, with comparisons under matched source budgets, component ablations, and runtime measurements.

Critical strengths
  1. A coherent solution to a practically important adaptation problem. Sections 3.1–3.5 integrate reusable source organization, support-conditioned structural retrieval, utility-based retriever training, and exact budgeted selection into a complete workflow. The local and cross-domain relations provide a concrete way to combine neighborhood similarity with domain diversity. This coordinated retrieval mechanism offers a practical contribution to adapting historical EEG resources to new users with limited labeled calibration data and supports acceptance.
  2. Consistent gains under matched source budgets across several transfer settings. TETHER reports the highest mean MacroBA among the evaluated fixed-budget methods in all six four-class LOSO and nine binary LODO conditions (Tables 1–2 and 8–10). At B=500 and 20 shots, four-class MacroBA is 0.5781 versus 0.3938 for MTS-Top-B; on binary BNCI-LR it reaches 0.7483 using 500 of 21,320 eligible source trials. Class-balanced Random-B is an appropriate basic comparator for the value of selection under the same budget and target support. Table 3 also reports higher means for the full model than for each component-removal variant. Together, these results support the usefulness of the complete approach across subject and dataset shifts. The 2.35% source-usage figure concerns the selected subset for downstream adaptation; source-side representation learning still uses the historical source pool.
Critical weaknesses
  1. The useful range of source budgets and the performance–cost trade-off are insufficiently characterized. The binary experiments use only B=500, while the four-class experiments evaluate B=500 and B=1000 (Section 4.1; Tables 1–2 and 5). These results establish performance at the reported budgets but do not show whether substantially smaller subsets retain the gains, where performance begins to deteriorate, or where additional source data cease to help. Moreover, the initial retrieval depth M changes from 64 to 128 as the per-class budget increases from 125 to 250 (Table 6), so the comparison also changes the initial candidate-retrieval scope. Appendix D explains that structural settings are fixed in advance, but does not report a broader budget or sensitivity analysis. Because compact and efficient source reuse is a central motivation, this leaves the deployment trade-off and minimum useful budget unclear. A representative lower-budget sweep, reporting accuracy and online cost with an explicit M policy, would substantially strengthen the practical contribution.
  2. The distinctiveness and complementarity of the two relations are not directly established. Both relations use the same embeddings and same-class similarity neighborhoods; Eq.2 permits cross-domain neighbors, while Eq.3 adds domain-coverage and per-domain membership constraints. The two relations can therefore share many members, and some hyperedges may coincide, but their actual overlap is not reported. In Table 3, local-only and consensus-only MacroBA differ by just 0.14/0.33/0.25 percentage points at 5/10/20 shots. The full model has higher means, by 1.23–2.75 points over the individual single-relation variants, but this does not isolate structural complementarity from extra branch capacity or an ensemble effect. Similar single-branch means also do not prove redundancy. The statement in Section 4.3 that the ablations suggest complementarity rather than interchangeability is consequently stronger than the available mechanism evidence. Since the dual-relation design is a central contribution, overlap analysis and a matched-capacity duplicate-relation control would make its interpretation more convincing.
Questions for authors
  1. The binary experiments evaluate only B=500, while the four-class experiments consider B in {500,1000}. How do accuracy and online adaptation cost change at smaller source budgets? A budget sweep on a representative cross-dataset task would help establish the useful operating range. Please specify how M is adjusted at the additional budgets and whether the same trained retriever is reused.
  2. Since both relations use the same embeddings and the local relation already permits cross-domain neighbors, how different are the retrieved local and consensus hypergraphs in practice? Hyperedge-overlap statistics and a capacity-matched control, such as two independent local-relation branches with comparable candidate scope and training, would help distinguish complementary structures from additional model capacity. Subject-paired performance differences would also clarify the consistency of the gains.
  3. For the single-relation ablations in Table 3, are the remaining retriever components retrained, and is the candidate pool reconstructed after removing a relation? In addition, how much does the refinement stage improve over coarse hyperedge retrieval alone (Eq. 5)? A budget-matched control could select a class-balanced random subset of B trials from the same coarse candidate pool, followed by the identical downstream fitting protocol. Does the “w/o HGNN Propagation” variant in Table 3 correspond to the coarse-only, budget-matched control described above? If so, please describe its configuration in detail, specifying which modules are retained and which are removed.
  4. The evaluation covers binary and four-class MI tasks, with cross-dataset transfer limited to binary left/right-hand classification. Could the authors provide evidence on a task with a larger label space or finer-grained MI distinctions, examining whether the retrieval gains persist and how the two relations contribute in that setting? This would clarify the method's applicability beyond the tested task configurations.
9 comments
AuthorsOpenReview ↗

Response to Reviewer GqG1 [1/N]

We sincerely thank you for carefully reading our work and providing valuable feedback. We are pleased that you recognize the contributions of our work. In this rebuttal, we aim to address each of the key concerns and questions you raised.


[W1] The useful range of source budgets and the performance–cost trade-off....

Thank you for raising this concern. To address it, we have added a cross-dataset budget sweep over a wider range, using both fixed M and variable initial M, and reusing the same trained retriever across budgets for a given source-training configuration and random seed. The experimental settings and results are provided in [Q1], where we report both accuracy and runtime. The results show that:

  • Under the small-budget conditions tested, the variable-M strategy retains advantages over fixed M in both mean accuracy and runtime.

  • Accuracy decreases gradually as the budget is reduced, with no clear threshold for an abrupt performance drop between the tested budget points. In the larger-budget range, the variable-M strategy shows diminishing returns per additional source sample, although accuracy continues to improve.


[W2] The distinctiveness and complementarity of the two relations are not....

Thank you for these thoughtful and insightful suggestions. We have added analyses of membership overlap, duplicated-relation two-branch controls, and subject-level paired comparisons, and have accordingly narrowed our conclusion: the two relations provide different structural constraints, but structural differences do not guarantee consistent predictive gains. Please see [Q2] for details and [Q3] for the training and candidate-pool settings of the single-relation ablations. The results show that the directions of subject-level changes are generally consistent. The overlap statistics support the presence of different structural constraints in the two relations, while the duplicated-relation controls support performance gains from combining the relations at some support-set sizes.

AuthorsOpenReview ↗

Response to Reviewer GqG1 [2/N]

[Q1] The binary experiments evaluate only B=500, while the four-class experiments....

Thank you for this question. As shown in Table 1, reducing the budget lowers runtime at the cost of accuracy. Setting the initial retrieval depth according to the budget yields a more favorable combination of mean accuracy and runtime in this sweep.

  • Regarding retrieval depth, we use two strategies: fixed M and variable initial M. The fixed strategy keeps M=1024, whereas the variable strategy adjusts the initial M as B increases; the specific mapping is given in Table 1. When the variable strategy does not yield enough candidates to meet the class quotas, the retrieval depth is expanded according to a predefined doubling rule, without adjustments based on target-query performance.

  • Regarding retriever reuse, for each random seed, all six budget settings B∈{50,100,250,500,1000,2000}B\in\{50,100,250,500,1000,2000\} and both M strategies reuse the same retriever trained with a budget of B=500 and then frozen. The source encoder, HGNN, relation gate, and trial-scoring module are neither retrained nor fine-tuned for different budgets. Only the source-trial budget B and retrieval-depth settings are adjusted during retrieval; the downstream feature mapping and classifier are fitted to the currently selected source subset using the same protocol.

Table 1 Cross-dataset budget sweep: accuracy and runtime

BVariable initial MFixed M Accuracy (%)Variable M Accuracy (%)Fixed M Time (s)Variable M Time (s)
501661.54 ± 12.4662.18 ± 12.730.3120.078
1003261.56 ± 12.7962.88 ± 13.170.3540.120
2506462.04 ± 12.9663.21 ± 13.520.4400.232
50012862.56 ± 13.3863.75 ± 13.580.6320.436
100025663.24 ± 13.7864.50 ± 13.830.9860.815
200051264.60 ± 14.0365.25 ± 13.841.6981.584

These results show that, for this cross-dataset task and within the tested budget range, a single retriever trained offline can directly support multiple deployment budgets without separate training for each budget. This provides further experimental evidence for TETHER's principle of "Organize Once, Adapt Efficiently." We sincerely thank the reviewer for this insightful suggestion, which has provided valuable inspiration for further demonstrating and clarifying the practical value of this core principle from a new perspective.

AuthorsOpenReview ↗

Response to Reviewer GqG1 [3/N]

[Q2] Since both relations use the same embeddings and the local....

Thank you for raising this concern. We examine construction constraints, membership overlap, and predictive performance separately.

(1) The differences arise from neighbor constraints rather than different embedding spaces

Local selects same-class nearest neighbors in the shared embedding space and allows neighbors from other source domains. Consensus excludes neighbors from the anchor's own domain and imposes both a minimum domain-coverage requirement and a cap on the number of members from each domain. These constraints can alter hyperedge membership, descriptors, reliability weights, and retrieval rankings, but do not guarantee that the two relations are non-overlapping.

(2) Reporting overlap separately for source hyperedges and actual retrieval candidates

We measure overlap across 9 subjects and 5 random seeds on BNCI2014-001. The Jaccard coefficient is the ratio of the intersection size to the union size: J(A,B)=|A∩B|/|A∪B|, with larger values indicating more similar membership.

Table 2 Membership and domain-coverage statistics for source hyperedges sharing the same anchor

Source hyperedge statisticResult
Mean membership Jaccard for hyperedges sharing the same anchor0.5624
Mean neighbor Jaccard after removing the shared anchor0.5461
Proportion of hyperedges with identical membership0.2604%
Mean number of domains covered per hyperedge, Local / Consensus6.45/7.55
Proportion of cross-domain neighbors excluding the anchor, Local / Consensus82.15%/100%

Table 2 verifies the differences between Local and Consensus in structural construction through hyperedge membership, neighbor selection, and cross-domain coverage. These results indicate that the two relations do not simply duplicate the same higher-order structures; instead, they organize cross-domain relations differently through distinct neighbor constraints.

Table 3 Overlap of actual retrieval candidates driven by the support set

SettingCandidate-set JaccardLocal-only nodes as a proportion of the unionConsensus-only nodes as a proportion of the union
5-shot0.80168.22%11.63%
10-shot0.79918.57%11.52%
20-shot0.79548.83%11.63%

The results in Table 3 show substantial overlap between the actual candidate nodes retrieved by the two relations. However, the relations are not entirely redundant: while sharing some candidate nodes, they form different higher-order structures through distinct neighbor constraints.

(3) Duplicated-relation two-branch controls and subject-level paired analysis

We compare L+C, L+L, and C+C. The latter two each use two independent branches of the same relation type to control for the number of branches. The experiments use four-class BNCI2014-001 with B=500, 9 subjects, and 5 random seeds. We first average across seeds within each subject and then compute the mean and standard deviation across subjects.

Table 4 Mixed-relation and duplicated-relation two-branch comparisons

VariantRelation composition5-shot BA (%)10-shot BA (%)20-shot BA (%)
L+CLocal + Consensus51.96 ± 14.2554.07 ± 14.4057.81 ± 13.01
L+LTwo independent Local branches49.75 ± 14.5051.94 ± 15.1855.52 ± 15.63
C+CTwo independent Consensus branches50.34 ± 14.2452.37 ± 14.9455.51 ± 16.28

Table 5 Subject-level paired differences between L+C and the duplicated-relation controls

Subject5-shot ΔL+L5-shot ΔC+C10-shot ΔL+L10-shot ΔC+C20-shot ΔL+L20-shot ΔC+C
S1+1.389−0.139+0.694+1.181+0.278−0.278
S2+3.264+1.667+3.194+2.708+6.042+6.319
S3+2.083+1.944+1.458+1.042−0.556−2.431
S4+1.667+0.972+1.042+2.153+3.403+2.569
S5+2.778+1.736+3.958+2.014+5.972+6.806
S6+2.222+1.944+1.806+2.014+4.306+5.972
S7+1.528+1.250+4.028+1.458+0.972+1.458
S8+3.333+2.431+0.694+0.625+0.4860.000
S9+1.667+2.778+2.292+2.083−0.278+0.278
Mean Δ+2.21+1.62+2.13+1.70+2.29+2.30

As shown in Tables 4 and 5, the mixed-relation configuration achieves higher mean performance at all three support-set sizes. This trend is consistent with the hypothesis that the local and consensus relations may provide complementary information. The duplicated-relation two-branch controls offer an appropriate way to distinguish the effects of relation composition from those of branch count.

Reviewer_Bb8zOpenReview ↗
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Paper summary

This paper proposes TETHER, a target-conditioned hypergraph-based source-trial retrieval framework for few-shot motor imagery (MI) EEG adaptation. During offline preparation, it constructs a reusable dual-relation hypergraph consisting of local semantic hyperedges and cross-domain consensus hyperedges. A neural retriever is then trained using source-only pseudo-target episodes, where a differentiable ridge regression objective provides supervision based on downstream adaptation performance. During deployment, a small set of labeled target trials is used to retrieve a class-balanced subset of source trials, which is combined with the target support set to train a downstream classifier.

Critical strengths
  • The paper addresses an important challenge in cross-subject EEG decoding: identifying historical training samples that are useful for a specific target subject under a limited calibration and source-data budget.

  • The experimental results demonstrate substantial improvements over existing source-selection strategies under matched source-data budgets. On four-class BNCI2014-001, TETHER consistently outperforms the evaluated fixed-budget baselines across different target-shot settings.

Critical weaknesses
  • TETHER combines several established components, including similarity-based neighborhood construction, hypergraph neural network propagation, query-conditioned feature fusion, and differentiable utility-based selection. Although their integration is reasonable, the paper does not sufficiently establish that modeling higher-order relations provides a substantial advantage over simpler target-conditioned retrieval methods trained with the same downstream utility objective. The existing ablation studies remove individual hypergraph relations, HGNN propagation, or utility supervision. However, these experiments do not directly compare TETHER with a simpler learned pointwise or pairwise retriever using the same pseudo-target episodes, training objective, feature representations, and source-selection budget. This distinction is important because the ablation results indicate that utility supervision contributes substantially to performance. Consequently, it remains unclear whether the improvements primarily originate from the proposed higher-order structural modeling or from learning a target-conditioned selection policy using downstream adaptation feedback.

  • The current evaluation is restricted to motor imagery EEG with a shared label space between source and target datasets. It remains unclear how robust the learned retrieval strategy would be to substantial changes in source-domain composition, recording protocols, or newly added source datasets.

Questions for authors
  • Could the authors compare TETHER with a learned pointwise or pairwise source-trial retriever trained using exactly the same pseudo-target episodes and differentiable downstream utility objective, but without hypergraph construction or HGNN propagation? This would help isolate the contribution of higher-order structural modeling.

  • Can the authors provide a more systematic comparison between the proposed structural representations and simpler learned retrieval mechanisms under identical utility supervision?

  • How robust is the retrieval framework to source-domain heterogeneity?

5 comments
AuthorsOpenReview ↗

Response to Reviewer Bb8z [1/N]

Thank you for your detailed and insightful suggestions. We are pleased that you recognize the contributions of our work. In this rebuttal, we address all the key questions and points you raised, one by one.


[W1] TETHER combines several established components, including similarity-based neighborhood construction, hypergraph....

Thank you for raising this issue. We fully agree with your suggestion and have added analyses at two levels:

  • Structural comparisons under the same supervision. We also train simpler learned retrievers using pseudo-target tasks and differentiable downstream utility supervision, with a common downstream evaluation pipeline. This makes the comparison more directly reflect the modeling differences among independent scoring, learned metrics, standard pairwise graphs, and dual-relation hypergraphs, reducing the influence of differences in supervision on the interpretation of the results.

  • Single-relation and dual-relation analyses. Local semantic relations focus on neighborhood associations among trials of the same class, whereas cross-domain consensus relations focus on patterns that recur across source domains. The two relations are designed to serve different roles. Retraining each of the two single-relation configurations allows us to examine the performance of each relation when learned on its own and assess the value of combining them, rather than merely testing the full model's dependence on a particular branch.

These two sets of additional experiments examine the role of structured retrieval from the perspectives of retrieval mechanisms and relation combinations, respectively. The results show that dual-relation hypergraph retrieval achieves higher average performance under the same utility supervision. In addition, the full dual-relation model outperforms the single-relation configurations in all three target calibration settings. These findings provide further empirical support for higher-order relational modeling and the joint use of the two relations in TETHER. The detailed experimental settings and results are provided in [Q1] and [Q2].


[W2] The current evaluation is restricted to motor imagery EEG with....

Thank you for drawing our attention to this point. In light of the emphasis on source-domain differences in existing cross-dataset MI studies [1, 2], we have added experiments varying the source composition and label sets to examine TETHER's robustness to source-domain heterogeneity and clarify the scope of generalization supported by the current experiments.

  • Label-set variation. The comparison between Closed-set and Partial Label-set extends the evaluation from identical source and target class sets to cases in which the target classes form a subset of the source classes. The latter allows additional classes in the source domain while retaining source-label semantics corresponding to the target classes. It does not represent completely disjoint source and target label spaces, nor does it establish transferability to unknown target classes or other EEG paradigms.

  • Source-composition variation. The additional single-source and mixed-source experiments vary the data sources while holding the source data size, retrieval budget, and target evaluation protocol fixed, separating the effect of source composition from that of increasing the amount of data. We retrain the encoder and retriever for each composition while keeping the architecture and hyperparameters unchanged. These experiments therefore support the applicability of the same method configuration across different source compositions, rather than the invariance of a single frozen model to changes in the source distribution. Each single-source dataset still contains multiple subject domains.

The detailed experimental settings and results are provided in [Q3]. The additional experiments show limited variation in TETHER's average performance across the tested source compositions. Moreover, the additional source classes do not cause a consistent performance decline across the shot settings. These findings support a degree of robustness to these two forms of source-domain heterogeneity. For cases in which the source and target label spaces only partially overlap and the target domain contains classes not covered by the source domain, we will further clarify the method's applicability limits and the need for further validation in the summary.

AuthorsOpenReview ↗

Response to Reviewer Bb8z [2/N]

[Q1] Could the authors compare TETHER with a learned pointwise or....

Thank you for your valuable suggestion. We have added the following three comparison methods, none of which uses hypergraph construction or HGNN propagation:

  • Pointwise-U [3]: Computes a target-conditioned score for each source trial independently, without constructing relations between trials.

  • Pairwise-U [4]: Uses a standard pairwise graph and graph message passing to model pairwise relationships.

  • Learned-Metric-U [5]: Learns metric-based matching between source trials and the target, without graph-based propagation.

All four methods use the same input features and encoder, pseudo-support/pseudo-query tasks, Soft Selection, differentiable ridge regression, and query cross-entropy objective. They also share the same source budget, final feature fitting and Logistic Regression decoding procedures, and parameter selection and evaluation protocols. The experiments use the four-class leave-one-subject-out (LOSO) setting on BNCI2014-001 with B = 500. The corresponding results are presented in Table 1.

Table 1 Comparison of retrieval methods under the same utility supervision

ShotMethodLeft-hand RecallRight-hand RecallBoth-feet RecallTongue RecallMacro BA
5Pointwise-U0.4846 ± 0.16990.5605 ± 0.21470.4883 ± 0.21370.4568 ± 0.24270.4975 ± 0.1450
5Pairwise-U0.5062 ± 0.20600.5667 ± 0.20790.5046 ± 0.20760.4515 ± 0.24710.5073 ± 0.1526
5Learned-Metric-U0.4849 ± 0.17760.5590 ± 0.19580.4972 ± 0.19530.4562 ± 0.23660.4993 ± 0.1439
5TETHER-U0.4830 ± 0.14170.5654 ± 0.16100.4691 ± 0.13580.5608 ± 0.22310.5196 ± 0.1425
10Pointwise-U0.5738 ± 0.23170.5108 ± 0.21890.4994 ± 0.25600.5265 ± 0.15760.5276 ± 0.2050
10Pairwise-U0.5571 ± 0.24150.5281 ± 0.23520.4858 ± 0.25650.5325 ± 0.15820.5259 ± 0.2148
10Learned-Metric-U0.5577 ± 0.22640.5256 ± 0.20170.5006 ± 0.23260.5279 ± 0.14880.5279 ± 0.1792
10TETHER-U0.5457 ± 0.18920.5627 ± 0.19600.4849 ± 0.15580.5694 ± 0.24330.5407 ± 0.1440
20Pointwise-U0.5728 ± 0.22470.5769 ± 0.26640.5543 ± 0.23850.5250 ± 0.25090.5573 ± 0.1572
20Pairwise-U0.5787 ± 0.24070.5670 ± 0.27490.5657 ± 0.24250.5256 ± 0.26000.5593 ± 0.1659
20Learned-Metric-U0.5608 ± 0.21460.5633 ± 0.24880.5704 ± 0.21490.5429 ± 0.26040.5593 ± 0.1560
20TETHER-U0.5485 ± 0.21030.5722 ± 0.23190.5673 ± 0.18980.6244 ± 0.22920.5781 ± 0.1301

These results show that, with the same pseudo-target tasks and downstream utility supervision mechanism, TETHER-U achieves the highest mean Macro BA in all three target calibration settings. Compared with simpler learned retrieval mechanisms such as Pointwise, Learned-Metric, and Pairwise, dual-relation hypergraph retrieval exhibits a more consistent overall performance advantage. These findings further support the value of higher-order structural modeling within the utility-supervised retrieval framework, indicating that local semantic associations and cross-domain consensus relations can provide additional structural information for target-conditioned source-trial retrieval. We have also added this important supplementary experiment to the revised manuscript (see the main text of Section 4.2 MAIN RESULTS and Table 3). Thank you again for your suggestion. These additional experiments allow us to assess more directly the gains of the proposed structured retrieval design over simpler retrieval mechanisms.

AuthorsOpenReview ↗

Response to Reviewer Bb8z [3/N]

[Q2] Can the authors provide a more systematic comparison between the....

Thank you for your valuable suggestion. To further examine the individual roles of local and consensus relations and the effect of using them jointly, we separately retrained the Local-only model, which retains only local relations; the Consensus-only model, which retains only consensus relations; and the Dual-relation model, which uses both types of relations, under the same training and evaluation protocol. The configurations are detailed below, and the results are summarized in Table 2. Local-only retains only the local semantic relations and their HGNN branch, Consensus-only retains only the cross-domain consensus relations and their branch, and Dual-relation uses both branches together with the Relation Gate. The two single-relation configurations were retrained separately, rather than evaluated by zeroing out the other branch of the full model at inference time.

Table 2 Descriptive comparison of single-relation and dual-relation configurations

ShotMethodLeft-hand RecallRight-hand RecallBoth-feet RecallTongue RecallMacro BA
5Local-only0.4843 ± 0.16330.5660 ± 0.20580.5031 ± 0.20900.4429 ± 0.23270.4991 ± 0.1423
5Consensus-only0.4926 ± 0.16590.5691 ± 0.21270.4880 ± 0.20010.4549 ± 0.23170.5012 ± 0.1422
5Dual-relation0.4830 ± 0.14170.5654 ± 0.16100.4691 ± 0.13580.5608 ± 0.22310.5196 ± 0.1425
10Local-only0.5429 ± 0.17750.5552 ± 0.22270.5164 ± 0.22200.4914 ± 0.24630.5265 ± 0.1489
10Consensus-only0.5318 ± 0.17170.5639 ± 0.21880.5256 ± 0.22000.5015 ± 0.23980.5307 ± 0.1493
10Dual-relation0.5457 ± 0.18920.5627 ± 0.19600.4849 ± 0.15580.5694 ± 0.24330.5407 ± 0.1440
20Local-only0.5844 ± 0.20180.5702 ± 0.23870.5748 ± 0.22420.5396 ± 0.26440.5673 ± 0.1580
20Consensus-only0.5754 ± 0.19740.5804 ± 0.24940.5730 ± 0.22680.5489 ± 0.26930.5694 ± 0.1616
20Dual-relation0.5485 ± 0.21030.5722 ± 0.23190.5673 ± 0.18980.6244 ± 0.22920.5781 ± 0.1301

Tables 1 and 2 examine differences between retrieval mechanisms and the role of combining relations, respectively. In Table 1, dual-relation hypergraph retrieval achieves higher mean Macro BA than the pointwise, pairwise, and metric-based retrieval baselines across all three shot settings. In Table 2, the full model consistently achieves higher Macro BA than the single-relation configurations. Together, these results show favorable overall performance of dual-relation hypergraph retrieval under the same utility supervision and provide empirical support for jointly modeling local semantic relations and cross-domain consensus relations.

Comments on the paper

6 comments
AuthorsOpenReview ↗

Global Response and Revision of the Paper

We thank all reviewers for their careful assessment and constructive feedback. We appreciate their recognition of the practical importance of adaptation with limited calibration data (Bb8z, GqG1), the coherent formulation of target-conditioned source-trial retrieval (GqG1, HAqy), and the reported performance improvements under matched source budgets (Bb8z, GqG1). We also appreciate the positive comments on the data-isolation provisions and controlled component ablations (HAqy).

We acknowledge the reviewers’ concerns regarding the contribution of hypergraph-based retrieval, generalization beyond binary cross-dataset evaluation, the definition of reference methods, and inconsistencies between the experimental descriptions and implementation. In this rebuttal, we have addressed these concerns through additional comparative experiments, detailed technical explanations, and corrections to the manuscript. This represents the best effort we can achieve within the limited timeframe allocated for the rebuttal.


We have revised the manuscript as follows:

  1. Added a utility-supervised retrieval comparison.

    Under matched utility supervision and downstream decoding, TETHER achieves higher mean Macro BA than Pointwise-U, Pairwise-U, and Learned-Metric-U across the evaluated support sizes. These results provide more direct evidence for the contribution of the proposed structured retrieval mechanism. (Section 4.2)

  2. Added the experimental setup for four-class cross-dataset generalization.

    We describe the bidirectional transfer settings between BNCI2014-001 and ZJU-MI-EEG, together with the source-training and target-evaluation protocols. (Section 4.1)

  3. Added evaluation on an additional four-class dataset.

    We have added a description of ZJU-MI-EEG and updated the dataset documentation to reflect its use in the four-class cross-dataset generalization experiments. (Appendix A)

  4. Revised the All-source reference description.

    We clarify its experimental definition, target-support usage, and intended role in the comparisons. (Appendix C.1)

  5. Corrected the preprocessing descriptions.

    We distinguish the preprocessing protocols used in the cross-subject and cross-dataset experiments and clarify their respective filtering, channel selection, epoch windows, and standardization procedures. (Appendix D)

  6. Added four-class cross-dataset generalization results.

    TETHER achieves the highest mean Macro BA among the evaluated fixed-budget selection methods in both transfer directions across the tested support sizes. These results extend the empirical evidence beyond the original binary cross-dataset setting. (Appendix F)

  7. Updated the abstract.

    We revise the descriptions of the datasets and experimental coverage to reflect the expanded evaluation. (Abstract)

  8. Updated the introduction.

    We revise the overview of the experimental settings and datasets, aligning the presentation of the empirical contributions with the additional cross-dataset evaluation. (Introduction)

  9. Added source-pool usage information for the newly introduced dataset.

    We report the source-pool size and the proportion of source trials selected for adaptation in the additional four-class cross-dataset experiments. (Appendix A)

  10. Revised the discussion of limitations and future work.

    We clarify the scope of the current evidence and update the directions for further investigation. (Conclusion)


We thank the reviewers for helping us strengthen the experimental evidence and improve the clarity of the paper. We hope that the revised manuscript provides valuable insights into reusing historical EEG resources through target-conditioned source-trial retrieval for motor-imagery adaptation with limited labeled calibration data.

For a more detailed account of the revisions, please refer to the newly uploaded revised manuscript. We have made improvements throughout both the main text and the appendices, with all revisions highlighted in blue. We sincerely welcome the reviewers' feedback and constructive insights to further refine and enhance our study.

AuthorsOpenReview ↗

Second-Round Response to Reviewer HAqy [1/N]

Dear Reviewer HAqy,

Thank you for your further valuable feedback and for acknowledging our newly added comparisons with a common decoder and comparisons among utility-supervised retrievers. This response focuses on the three remaining issues you raised. We provide additional comparisons with a common decoder for binary cross-dataset transfer, a full performance evaluation under partitioned preprocessing on Cho2017, and further corrections and checks of the All-source implementation. We report the corresponding changes and results below.


1. Comparisons with a Common Decoder for Binary Cross-Dataset Transfer

We have added comparisons with a common downstream decoder on three leave-one-dataset-out (LODO) tasks: BNCI-LR, Cho2017, and Lee2019-MI. All fixed-budget methods use B = 500 source trials and share the same target support sets, query sets, and five random seeds. Each method selects source trials using its own retrieval strategy and then performs adaptation using the same Tangent Space / Bandpower feature mapping, Logistic Regression classifier (C = 0.01), and proportion of total training weight assigned to target support samples (50%). This allows a more direct comparison of different source-trial selection strategies.

Tables 1–3 report the binary classification comparisons with a common decoder on the three datasets. Bold and underlined values indicate the highest and second-highest reported means, respectively, for each metric within each shot setting. Under the common downstream decoding protocol, TETHER achieves the highest mean Macro BA across all nine combinations of task and shot setting in the three binary cross-dataset tasks. These results provide further support for the benefits of TETHER retrieval in binary cross-dataset transfer, in addition to the evidence from four-class cross-subject transfer.

Table 1. BNCI-LR binary classification comparison (B = 500)

DatasetShotMethodLeft-hand Recall ↑Right-hand Recall ↑Macro BA ↑Macro F1 ↑
BNCI-LR5-shotClass-balanced Random-B0.5933 ± 0.21260.7318 ± 0.17920.6626 ± 0.16580.6467 ± 0.1812
BNCI-LR5-shotBandpower Top-B0.6229 ± 0.19360.6641 ± 0.20840.6435 ± 0.16930.6287 ± 0.1836
BNCI-LR5-shotRiemannian Top-B0.6416 ± 0.15450.6947 ± 0.17510.6682 ± 0.15070.6579 ± 0.1612
BNCI-LR5-shotPairwise kNN Graph Diffusion0.6208 ± 0.20230.7167 ± 0.15210.6688 ± 0.15060.6571 ± 0.1626
BNCI-LR5-shotTETHER0.6722 ± 0.19590.7414 ± 0.18850.7068 ± 0.16760.6853 ± 0.1876
BNCI-LR10-shotClass-balanced Random-B0.6121 ± 0.19190.7374 ± 0.16110.6747 ± 0.15890.6664 ± 0.1674
BNCI-LR10-shotBandpower Top-B0.6398 ± 0.17390.6855 ± 0.21730.6626 ± 0.16570.6551 ± 0.1728
BNCI-LR10-shotRiemannian Top-B0.6258 ± 0.17300.7326 ± 0.16730.6792 ± 0.14990.6720 ± 0.1555
BNCI-LR10-shotPairwise kNN Graph Diffusion0.6156 ± 0.23500.7519 ± 0.13670.6838 ± 0.16060.6732 ± 0.1735
BNCI-LR10-shotTETHER0.6929 ± 0.17220.7688 ± 0.19010.7309 ± 0.16620.7222 ± 0.1734
BNCI-LR20-shotClass-balanced Random-B0.6395 ± 0.17080.7422 ± 0.16140.6908 ± 0.15670.6854 ± 0.1612
BNCI-LR20-shotBandpower Top-B0.6766 ± 0.17080.6828 ± 0.24840.6797 ± 0.16310.6702 ± 0.1743
BNCI-LR20-shotRiemannian Top-B0.6327 ± 0.19150.7423 ± 0.17850.6875 ± 0.15730.6786 ± 0.1656
BNCI-LR20-shotPairwise kNN Graph Diffusion0.6158 ± 0.21730.7566 ± 0.14430.6862 ± 0.16480.6766 ± 0.1751
BNCI-LR20-shotTETHER0.7235 ± 0.14640.7731 ± 0.19470.7483 ± 0.16080.7399 ± 0.1684
AuthorsOpenReview ↗

Second-Round Response to Reviewer HAqy [2/N]

Table 2. Cho2017 binary classification comparison (B = 500)

DatasetShotMethodLeft-hand Recall ↑Right-hand Recall ↑Macro BA ↑Macro F1 ↑
Cho20175-shotClass-balanced Random-B0.5502 ± 0.15780.5977 ± 0.17170.5740 ± 0.12190.5628 ± 0.1276
Cho20175-shotBandpower Top-B0.5287 ± 0.13230.5743 ± 0.14730.5515 ± 0.09810.5359 ± 0.1054
Cho20175-shotRiemannian Top-B0.5380 ± 0.15830.5895 ± 0.16270.5637 ± 0.11140.5482 ± 0.1194
Cho20175-shotPairwise kNN Graph Diffusion0.5372 ± 0.15090.5864 ± 0.14920.5618 ± 0.10930.5471 ± 0.1178
Cho20175-shotTETHER0.6033 ± 0.15040.6313 ± 0.15590.6173 ± 0.11210.5986 ± 0.1211
Cho201710-shotClass-balanced Random-B0.5603 ± 0.16420.6076 ± 0.17170.5840 ± 0.12750.5750 ± 0.1329
Cho201710-shotBandpower Top-B0.5480 ± 0.13860.5946 ± 0.15200.5713 ± 0.11560.5622 ± 0.1207
Cho201710-shotRiemannian Top-B0.5496 ± 0.17330.6042 ± 0.15790.5769 ± 0.12240.5667 ± 0.1270
Cho201710-shotPairwise kNN Graph Diffusion0.5600 ± 0.16000.5978 ± 0.14560.5789 ± 0.12050.5709 ± 0.1247
Cho201710-shotTETHER0.6249 ± 0.16460.6463 ± 0.16210.6356 ± 0.12180.6213 ± 0.1303
Cho201720-shotClass-balanced Random-B0.5725 ± 0.16640.6223 ± 0.16140.5974 ± 0.13050.5913 ± 0.1347
Cho201720-shotBandpower Top-B0.5546 ± 0.16050.6178 ± 0.14540.5862 ± 0.12420.5794 ± 0.1286
Cho201720-shotRiemannian Top-B0.5601 ± 0.19080.6254 ± 0.15030.5927 ± 0.12880.5844 ± 0.1353
Cho201720-shotPairwise kNN Graph Diffusion0.5614 ± 0.17420.6276 ± 0.12620.5945 ± 0.12460.5883 ± 0.1293
Cho201720-shotTETHER0.6341 ± 0.17160.6699 ± 0.15640.6520 ± 0.12790.6420 ± 0.1337

Table 3. Lee2019-MI binary classification comparison (B = 500)

DatasetShotMethodLeft-hand Recall ↑Right-hand Recall ↑Macro BA ↑Macro F1 ↑
Lee2019-MI5-shotClass-balanced Random-B0.5628 ± 0.18960.6457 ± 0.19000.6042 ± 0.12900.5864 ± 0.1407
Lee2019-MI5-shotBandpower Top-B0.5276 ± 0.16190.6107 ± 0.17390.5691 ± 0.10540.5489 ± 0.1179
Lee2019-MI5-shotRiemannian Top-B0.5944 ± 0.20230.5939 ± 0.21650.5942 ± 0.12410.5696 ± 0.1440
Lee2019-MI5-shotPairwise kNN Graph Diffusion0.5584 ± 0.18290.6136 ± 0.18380.5860 ± 0.12050.5625 ± 0.1356
Lee2019-MI5-shotTETHER0.6128 ± 0.19750.6856 ± 0.19340.6492 ± 0.12870.6196 ± 0.1454
Lee2019-MI10-shotClass-balanced Random-B0.5759 ± 0.19340.6381 ± 0.20300.6070 ± 0.13290.5901 ± 0.1441
Lee2019-MI10-shotBandpower Top-B0.5507 ± 0.17850.6182 ± 0.19050.5844 ± 0.11690.5668 ± 0.1280
Lee2019-MI10-shotRiemannian Top-B0.6172 ± 0.20620.5865 ± 0.23670.6019 ± 0.13160.5786 ± 0.1509
Lee2019-MI10-shotPairwise kNN Graph Diffusion0.5984 ± 0.19050.5979 ± 0.21390.5982 ± 0.12580.5754 ± 0.1419
Lee2019-MI10-shotTETHER0.6244 ± 0.20480.6902 ± 0.21160.6573 ± 0.13570.6294 ± 0.1527
Lee2019-MI20-shotClass-balanced Random-B0.5864 ± 0.20280.6498 ± 0.21370.6181 ± 0.13800.6005 ± 0.1516
Lee2019-MI20-shotBandpower Top-B0.5548 ± 0.21510.6426 ± 0.22010.5987 ± 0.12890.5789 ± 0.1461
Lee2019-MI20-shotRiemannian Top-B0.6226 ± 0.21350.6081 ± 0.25210.6154 ± 0.13590.5936 ± 0.1578
Lee2019-MI20-shotPairwise kNN Graph Diffusion0.5965 ± 0.20620.6192 ± 0.23770.6078 ± 0.13410.5866 ± 0.1519
Lee2019-MI20-shotTETHER0.6380 ± 0.21430.7006 ± 0.22630.6693 ± 0.13880.6408 ± 0.1575

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