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.