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Under review as a conference paper at ICLR 2027

The Alignment Boundary in Cross-Subject Imagined-Speech EEG: Provable Limits of Pre-Alignment and In-Training Alignment

Abstract

Imagined-speech brain–computer interfaces (BCIs) promise a non-muscular communication channel, but they must generalize across people: a decoder trained on some subjects should work on an unseen subject without recalibration. Two families of remedies dominate practice—pre-alignment (fixed transforms applied before the decoder, e.g. Euclidean Alignment and its class-conditional refinements) and in-training alignment (objectives applied during training, e.g. adversarial or correlation-based domain adaptation, and episodic meta-learning). We prove that both families are fundamentally bounded, and we characterize the boundary precisely. On the pre-alignment side, we show class-conditional Euclidean alignment (CC-EA) is not an improvement over marginal EA but a catastrophe: it whitens each class covariance to the identity, equalizing the two class covariances and erasing the between-class contrast that Common Spatial Patterns (CSP) decoders read; accuracy collapses to chance (72.3%→49.3% on BCI IV-2a, replicated on Cho2017 with 49 subjects, p < 10⁻¹¹). A gauge-invariance argument then proves the CSP decoder is unchanged by any class-agnostic linear pre-alignment, making marginal EA optimal within the linear family up to a residual per-subject rotation we rule out empirically. On the in-training side, we prove that minibatch objectives such as DANN and CORAL carry zero expected cross-subject H-divergence signal, while episodic prototype alignment is a principled H-divergence surrogate; the predicted gradient alignment is confirmed on imagined-speech EEG across 29/30 proxy–dataset pairs (p < 0.001). Finally, we show these two bounds combine on imagined speech: on a new multilingual cross-subject benchmark (Telugu, Kannada, English; consumer-grade 8-channel EEG), cross-subject decoding is near chance for every method, adaptive or not—not a method failure but the quantitative prediction of the H-divergence bound at the available signal-to-subject ratio. Motor imagery serves throughout as a signal-present control where the same theory translates into measurable accuracy structure. Our analysis converts widely assumed "better alignment" heuristics into precisely characterized boundaries and tells the field where cross-subject gains cannot come from.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
cross-subject EEG, imagined speech, brain-computer interface, domain adaptation, domain generalization, Euclidean alignment, Common Spatial Patterns, H-divergence, meta-learning, transfer learning, learning theory

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_gHurOpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies the limitations of pre-alignment and in-training alignment for cross-subject EEG decoding. It combines theoretical analysis with synthetic and real EEG experiments, including a new multilingual imagined-speech benchmark.

Critical strengths
  1. The paper's topic is an important problem in cross-subject EEG decoding.

  2. The synthetic experiments are useful for understanding when alignment removes class information.

Critical weaknesses
  1. I believe the theoretical claims seem too strong. An upper bound on error does not directly imply that performance must be near chance.

  2. It is unclear how invariance under a shared transformation proves optimality when different subjects can receive different transformations.

Questions for authors
  1. How does the upper bound imply that performance must be near chance, rather than simply providing a loose guarantee?

  2. Why is the divergence “constant across the class-agnostic linear family” (Appendix G), given that subject-specific rotations can alter “the cross-subject geometry the pooled decoder reads” (Remark 2)?

Reviewer_abdBOpenReview ↗
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1
Confidence
2
Informativeness
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1
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Paper summary

I am not an expert in speech decoding.

Critical strengths

The paper tackles an important topic

The multilingual dataset is novel and an important new direction.

Critical weaknesses

Theorem 1 seems condraticted by Remark 2. The pooled decoder relies on across subject alignment and therefore the per individual spectr a is not enough. Remark 2 seems to agree with this view.

This seems to plaque Proposition 3 which states that the per person spectra, and not the pooling, is what matters. This seems false.

In many cases, ceiling bounds seems to be use to make claims about performance well below the bound. One cannot use a ceiliing bound to claim that chance performance is expected.

The claims of "provable limits" and fully mapped are exaggerated.

The novelty seems low as all the pieces (mostly) have been shown before. The multilingual results are novel.

Overall this is more of an empirical test than a "proof"

Questions for authors

Can Theorem 1 and prop 3 focus on the pooling results, which is what matters, rather tha the indiivuals?

Reviewer_C1xbOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
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1
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Paper summary

The paper studies cross-subject (leave-one-subject-out, LOSO) EEG decoding and claims to "provably bound" two families of alignment methods.

  1. Pre-alignment. Class-conditional Euclidean alignment (CC-EA), which whitens each class by its own mean covariance, maps both class covariances to the identity and erases the CSP signal (Sec. 4–5; Props. 1–2, Cor. 1). Accuracy drops to chance on BCI IV-2a (72.3% to 49.3%) and Cho2017. A "gauge invariance" lemma for CSP+LDA under GL(n_c) congruence (Lemma 1, Cor. 2, Thm. 1) is used to argue that marginal EA is optimal within class-agnostic linear pre-alignment (Prop. 3), up to a per-subject orthogonal residual that the authors rule out empirically.
  2. In-training alignment. Under pooled minibatch sampling, the expected prototype (linear-MMD) gradient is O(1/n) (Thm. 2). Under a shared-covariance Gaussian assumption, the prototype loss upper-bounds the linear-H-divergence (Thm. 3(i)). Under a "symmetric source prior", the CE gradient is orthogonal in expectation to the signed domain-classifier gradient (Thm. 3(ii)). From these the paper concludes that pooled DANN/CORAL "cannot systematically reduce cross-subject H-divergence" (Cor. 3).
  3. Empirics on imagined speech. Gradient-cosine experiments compare episodic with minibatch sampling (Table 1, 29/30 pairs positive). On a new 8-channel Telugu/Kannada/English imagined-speech benchmark, all methods sit near chance (Table 2). KaraOne and FEIS are also at chance under FBCSP (Sec. 9.3). The paper presents this as "the quantitative prediction of the H-divergence bound".
Critical strengths
  • The question matters and is well posed: why do cross-subject imagined-speech decoders fail, and which levers cannot help? A clearly argued negative result would be useful to the BCI community.
  • The CC-EA analysis is correct and easy to follow. Prop. 2's equalizing/distinctness-preserving dichotomy is a tidy way to classify class-conditional aligners. The synthetic COV-vs-MEAN control (Table 9, Fig. 2) illustrates well that the damage depends on where the signal lives.
  • The Cho2017 replication (49 subjects, paired Wilcoxon) gives the motor-imagery CC-EA result proper statistical power.
  • Most proofs are short and written out in full. The derivation of the O(1/n) minibatch bias (App. I) and the constant in Thm. 3(i) (App. J) check out. The paper is candid about several idealizations: Remarks 5–6, Limitation (2), and the admission in Table 3 that the conditional-CORAL oracle gain is label leakage.
  • The subject-aware ablation (Table 6) is a sensible control. It separates "P_S differs from P_Q" from the details of LOSO episodes.
  • The authors contribute new multilingual imagined-speech recordings, which are relevant for low-resource languages.
Critical weaknesses

W1. The pre-alignment "ceiling" (Thm. 1, Prop. 3, abstract claim "the CSP decoder is unchanged by any class-agnostic linear pre-alignment") does not follow from the gauge lemma, and the paper's own data contradict it.

  • Lemma 1(c) and Cor. 2 hold only when the same matrix A is applied to all training and test trials. EA is a per-subject transform A_s = C̄_s^{-1/2}. Per-subject transforms are not a single group action on the pooled LOSO dataset, so the lemma says nothing about them.
  • Thm. 1(i) shows only that each subject's own class-pencil spectrum is invariant to A_s. This is immediate, because congruence preserves generalized eigenvalues. But a pooled CSP+LDA trained on several subjects does not read per-subject spectra. It reads the pooled covariances, which depend on the relative registration of subjects.
  • The proof of Prop. 3 (App. G) asserts that "the within-subject class-pencil spectra [are] the only statistics CSP reads". For a pooled LOSO decoder this is false. If Prop. 3 were true, "Raw" (A_s = I, a member of the class-agnostic linear family) would match marginal EA. Table 7 shows 66.8% vs 72.3%.
  • Remark 2 describes the residual freedom as "per-subject orthogonal". That parametrization, A_s = M^{1/2} O_s C̄_s^{-1/2}, covers exactly the maps that send every subject's mean covariance to a common M. It excludes Raw and every other non-recentering map, which make up most of A_lin. The residual freedom is therefore all of GL(n_c) per subject, not O(n_c).
  • "Marginal EA is optimal within the linear family" is therefore not proved. It is supported only by a handful of baselines on 9 subjects (Table 3).
  • Even that empirical support is weak. "Discriminative reweighting" (72.76) and all EEGNet variants (up to 74.96) are numerically above EA. They are dismissed as "within the ±11 across-subject std", but that is the wrong criterion for a paired, within-subject comparison. No paired test is reported.
  • Ledoit–Wolf shrinkage toward a scaled identity is not GL-equivariant, so even the global-A statement is only approximate for the pipeline actually used (Sec. 3).

W2. Corollary 3 ("DANN and CORAL ... cannot systematically reduce cross-subject H-divergence, regardless of loss weight or architecture") rests on a mischaracterization of these methods.

  • Thm. 2 concerns a prototype loss whose "support" and "query" are two random halves of the same pooled distribution. Standard multi-source DANN (Ganin et al., 2016) trains a domain classifier on subject/domain labels. Its adversarial gradient explicitly uses the fact that subjects differ, so it is not a P_S = P_Q objective.
  • Deep CORAL in multi-source domain-generalization use aligns second-order statistics between source domains. It is also domain-aware.
  • Neither method's loss is the prototype loss. Thm. 2 says nothing about a domain-adversarial or covariance-matching objective.
  • The proof in App. K simply asserts that DANN/CORAL "operate entirely in the P_S = P_Q regime". If the authors implemented them by aligning two random halves of a pooled minibatch with no subject labels, that is a degenerate implementation, not "standard form".
  • The paper's own Table 6 shows that any P_S ≠ P_Q split (e.g., two distinct subjects) restores the signal. That is precisely what subject-labelled DANN/CORAL do.
  • As stated, Cor. 3 is either false (for the standard methods) or tautological (an objective that compares a distribution with itself carries no between-distribution signal).
  • The empirical "confirmation" (Table 2: DANN/CORAL "fall below MLDG") consists of sub-1 pp differences around chance. No variance or test is given, and MLDG is itself below "Normal" on 4/9 conditions (Tel.W, Kan.Ph, Kan.V, Eng.V). This is not evidence for the corollary.

W3. Thm. 3 is either vacuous by assumption or unaligned with what is measured.

  • Thm. 3(ii) assumes its conclusion. Assumption (S2′) posits an involution on source laws that negates the signed domain objective on a neighbourhood of θ0, and (S3) makes g_CE independent of P_S. Under these, E_π[G] = 0 is just the definition of a symmetric prior. Orthogonality with a fixed g_CE is immediate (see the "Special case" paragraph after Remark 4).
  • Remark 5 concedes that the result does not extend to ∇d_H, the unsigned divergence. Yet Fig. 1, Sec. 8 and Table 1 test against unsigned divergence proxies (Neural DC, KMMD, Energy). Thm. 3(ii) is therefore never tested.
  • Thm. 3(i) is a correct but standard Gaussian Lipschitz bound. Its assumption (B) requires the class-conditional feature covariance to be identical across subjects. In EEG, covariance shift is the dominant cross-subject shift; the paper's own pre-alignment half is built on this.
  • The proof sketch itself notes that with matched means and unequal covariances, L_proto = 0 while d_H > 0. That is exactly the regime the paper argues EEG lives in. So the "principled surrogate" claim is unsupported for the data at hand.

W4. "Near chance is the quantitative prediction of the H-divergence bound" (abstract, Sec. 9.2, Table 2 caption) misreads the bound.

  • Ben-David et al. (2010) give an upper bound on target error. With the reported d_H values of 0.80–1.00, the displayed bound is ε_S + 0.4–0.5 + λ. Whether this reaches 50% depends on ε_S + λ. In any case, an upper bound of this form supplies neither a lower bound on target error nor a prediction of chance-level performance; it is compatible with much lower target error.
  • The paper never derives a lower bound or a numerical prediction. The "signal-to-subject ratio" invoked in the abstract and Sec. 9.2 is never defined or computed.
  • The paper does not report d_H on IV-2a or Cho2017, where cross-subject transfer is reported to work (72%). Please provide this control and clarify whether the reported d_H values use the stated [0,2] definition or a normalized [0,1] convention. Without a scale-consistent comparison, the claimed quantitative prediction is difficult to assess.

W5. The gradient-alignment evidence (Table 1, "the paper's strongest imagined-speech result") is close to tautological and statistically mis-specified.

  • Under pooled minibatching, Thm. 2 describes an expected prototype gradient of order O(1/n). Does this justify treating it as zero-mean at the reported finite batch sizes? Please distinguish finite-sample bias from variability when interpreting the cosine comparisons.
  • Under episodic sampling, g_proto is the gradient of a linear-kernel MMD between S and Q. It is compared with the gradient of an RBF-kernel MMD (KMMD, σ=1) or an energy distance between the same S and Q. These are closely related discrepancy objectives, so a positive cosine is expected regardless of whether any class information transfers.
  • The "29/30 pairs, p < 0.001" appears to treat the 200 episodes as independent samples. The subjects (4–14) are the actual units of replication.
  • Limitation (5) argues that "a broken pipeline would not produce the theory-predicted gradient-alignment signal". This does not follow: the alignment between two divergence gradients is independent of the class labels and would appear with permuted labels. A label-permutation control is needed.

W6. Several pre-alignment results are near-definitional, and the CC-EA target is a straw man.

  • Prop. 1(i) and Prop. 2(i) say that mapping both classes to N(0, I) makes them indistinguishable. Table 4's "Marginal EA leaves the contrast identical to four decimals" is the affine invariance of the AIRM distance, not an empirical finding.
  • I am not aware of published cross-subject EEG work that whitens each class to the identity as a proposed improvement. Existing class-aware alignments, e.g., Label Alignment (He & Wu, 2020, IEEE TNSRE, to my knowledge), map source class statistics onto target class statistics. They are distinctness-preserving under the paper's own Cor. 1(b).
  • The "collapse" therefore refutes a construction few would use. The paper should cite and test the class-aware methods that actually exist.
  • The oracle CC-EA at 63.4% (Table 8) also needs explanation. With true labels on both sides, Prop. 2(i) predicts Bayes error 1/2 for every covariance-based decoder. The synthetic oracle in Table 9 is indeed at 49.85%. Above-chance real-data performance therefore suggests label-dependent test-time preprocessing (leakage). It does not show an "intrinsic cost". The same concern applies to the pseudo-label variants.

W7. The imagined-speech experiments are too thin to support "intrinsic property of cross-subject imagined speech".

  • Table 5 lists 4–14 subjects per condition, as pre-screening totals. Several conditions have "fewer than 4 usable subjects" (Table 1 †), e.g., Telugu Words with 6 listed. The screening criteria are not given.
  • Trial counts, stimulus protocol, epoch windows, artifact handling and device per condition are missing. Two different devices (Enobio, UNICORN) are mixed. Within-subject accuracies, from which the "19.7 pp gap" is computed, are not shown.
  • Table 2 gives 5-seed means with no standard deviations, confidence intervals or tests.
  • KaraOne and FEIS are evaluated with an 8–30 Hz FBCSP pipeline designed for motor imagery (Sec. 9.3). Chance-level LOSO with a mis-specified pipeline is weak evidence of an intrinsic limit.
  • Other imagined-speech benchmarks are not used, notably the BCI Competition 2020 Track 3 imagined-speech dataset (Jeong et al., 2022, review of the 2020 International BCI Competition).
  • The dataset release status is unclear: only code "upon acceptance" is promised. That weakens the "first multilingual benchmark" contribution, and I cannot verify the "first" claim.

W8. Missing related work on the limits of in-training alignment. The headline "provable limits of in-training alignment" should engage with:

  • Zhao et al. (2019, ICML), "On learning invariant representations for domain adaptation", on the impossibility of invariant representations when label distributions differ.
  • Johansson, Sontag & Ranganath (2019, AISTATS), on support and invertibility in domain-invariant representations.
  • Multi-source DA bounds (Mansour, Mohri & Rostamizadeh, 2009; Zhao et al., 2018).
  • Riemannian Procrustes Analysis (Rodrigues, Jutten & Congedo, 2019, IEEE TBME), which is directly relevant to the "Procrustes" baseline and to Remark 2.

Without these, the novelty of the theoretical boundary is overstated.

Minor Issues

  • d_H is defined with a factor 2 (range [0,2]), but the values reported (0.80–1.00) are not put in context. Please state the scale.
  • Table 3's footnote points to "Section 6" for the shuffled-label control, but no such control appears there.
  • The main evidence (Tables 3, 4, 7, 8, 9) is all in the appendix while the main text cites it constantly. Please reorganize.
  • The rhetoric is overclaiming ("catastrophe", "fully mapped", "provably exhausted", "tells the field where gains cannot come from"), given that the proofs cover linear CSP+LDA, prototype losses and symmetric priors.
  • Prop. 2(ii)'s final sentence ("may match or underperform marginal EA but cannot exceed it in general") is not proved in App. B.
  • In Fig. 1, "g_CE orthogonal in expectation to the signed domain-classifier gradient" conflicts with the figure's use of g_dH, the unsigned quantity.
  • The Zanini et al. citation is listed as 2017; the TBME issue is vol. 65(5), 2018.
  • Cho2017 has 52 subjects. Please state the screening rule that yields 49.
  • Theorem 2 relies on the exchange of ∇ and E (A2). Please state whether the batch-norm/dropout encoders used satisfy the independence assumption (A3).

Justification of Rating

The paper's organizing claim is that both alignment families are provably bounded and that near-chance imagined-speech decoding is predicted by theory. None of the three pillars carries that weight:

  • The pre-alignment ceiling (Thm. 1, Prop. 3) confuses global-A invariance with per-subject alignment and is contradicted by Raw vs EA in the authors' own Table 7.
  • The in-training "impossibility" (Cor. 3) applies only to a domain-label-free implementation of DANN/CORAL that is not their standard form. Thm. 3(ii) assumes its conclusion and is never tested.
  • The "quantitative prediction" of chance is not established by an upper bound on target error.

What remains correct is mostly near-definitional: CC-EA erases class covariance contrast, and the pooled-sampling analysis describes an expected prototype gradient of order O(1/n), which does not by itself establish an exactly zero finite-sample expectation. The imagined-speech evidence is small-sample, without variance, and uses pipelines not designed for the paradigm.

I would raise my score if the authors:

  • reformulated the pre-alignment result as a correct statement about per-subject maps, e.g., an invariance characterization within the recentering family plus a proper empirical comparison against Riemannian Procrustes;
  • re-ran DANN/CORAL with subject-labelled domains;
  • removed or substantiated the "prediction" claims with an actual lower bound;
  • added label-permutation controls, subject-level statistics and full benchmark documentation and release.

Even then, the contribution would likely be a careful empirical/diagnostic paper rather than a set of provable limits.

Questions for authors
  1. Please reconcile Prop. 3 and the abstract claim ("the CSP decoder is unchanged by any class-agnostic linear pre-alignment") with Raw (66.8%) vs marginal EA (72.3%) in Table 7. Both are per-subject class-agnostic linear maps. Which precise statement about per-subject maps does Thm. 1 prove, and how does it imply EA's optimality for a pooled LOSO decoder?
  2. How exactly were DANN and CORAL implemented? Did the domain discriminator or the CORAL loss use subject identities? If not, why is this the "standard form"? If yes, how does Thm. 2, which concerns a prototype loss on a random split, apply to them?
  3. What precisely is "CC-EA, honest (target fallback)"? How is the test subject whitened without labels? For the oracle and pseudo-label variants, are test trials transformed with label-dependent matrices? If so, why is the 63.4% not label leakage, as you concede for conditional CORAL?
  4. What d_H do you measure on BCI IV-2a and Cho2017, where cross-subject decoding works? Using the same stated scale, in what sense does d_H ≈ 0.8–1.0 "predict" chance on imagined speech? Can you give any lower bound or explicit numerical prediction?
  5. Does the Table 1 gradient-alignment gap persist with permuted class labels? Are the reported p-values computed over episodes or over subjects?
  6. Please report per-condition standard deviations and paired tests for Table 2, within-subject accuracies for the benchmark, trial counts per subject and class, screening criteria, and the device used for each condition. Will the raw dataset be released?
  7. Were the EEGNet hyperparameters ("tuned") selected using the held-out subjects? Please give a paired test of EA vs EEGNet+both and vs discriminative reweighting on IV-2a.
  8. Why use an 8–30 Hz FBCSP pipeline for KaraOne and FEIS? Do imagined-speech-appropriate pipelines and frequency bands (e.g., tangent space over broader bands, or EEGNet) also give chance under LOSO?

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