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Under review as a conference paper at ICLR 2027

BIT BUDGET: HOW MUCH INFORMATION DOES EEG ADD BEYOND A FROZEN LANGUAGE PRIOR?

Abstract

EEG-to-text systems can produce fluent language even when the underlying EEG signal is corrupted, raising a fundamental question: how much text-specific information does the neural signal contribute beyond a language prior? We introduce Bit Budget, a calibrated framework that treats neural-to-language decoding as a communication-channel measurement problem and quantifies evidence dependent information beyond a frozen language prior. On the ZuCo corpus, gaze provides a significant information lower bound of 0.107 bits/token, while the evaluated EEG representation yields 0.000 bits/token with no significant evidence dependence. On the independent COFETT corpus, the same framework recovers an injected text-dependent signal of 0.149 bits/token, whereas real EEG remains within ±0.004 bits/token across the evaluated conditions. Notably, EEG still decodes four-way task/session identity with 82.1% balanced accuracy, indicating that the representation contains structured information that does not translate into detectable token-level linguistic evidence. These findings expose a gap between language-generation performance and dependence on neural evidence, and motivate calibrated information measures and explicit evidence-destruction controls as complementary tools for evaluating neural-to-language systems.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG-to-text decoding, Neural decoding, Information theory, Neural information, Eye tracking, Language models

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_KaRyOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

EEG-to-text systems produce fluent output, but prior work shows performance often survives when EEG is replaced by noise, suggesting the prior from a strong language model rather than the neural signal does the work, specifically in typical settings with a closed pool of candidate sentences. The paper studies how many bits per token recorded evidence actually adds beyond a frozen LM.

Decoding is framed as a channel-capacity measurement. An evidence encoder (fixation-locked EEG band power) produces an embedding that that tilts a frozen LM prior (GPT-2, Qwen). An InfoNCE-style contrastive score yields a per-token lower bound on mutual information between evidence and token given context. The estimator is calibrated on synthetic channels of known capacity and tested against structured nulls that preserve non-linguistic structure while breaking text alignment. A structured pipeline (steps E0–E4) drives the evaluation on three different data sets.

The authors find that their framework recovers information from text biases and gaze, but EEG itself yields 0 bits/token, consistently across several different configurations. Further experiments show that the EEG signal still contains structural information (e.g., identifying tasks/sessions), which do not transfer to the sentence identification.

Critical strengths
  • The paper tackles an important, timely problem as it quantifies a fundamental flaw in EEG-to-text evaluation that fluency metrics (BLEU, BERTScore) cannot detect, and quantifies existing skepticism in the field.
  • Through frozen prior, exact zero anchor, exact partition function, structured nulls, synthetic calibration, pre-specified hypotheses, gated pipeline, text-disjoint splits, provenance logs, and released code, the authors go beyond a simple real-vs-noise comparison with .
  • The reported positive control shows that another biosignal in gaze provides a positive information rate and that EEG contains decodable information beyond the text prediction, showing that the negative result is not just the result of a broken pipeline.
  • The authors do their best (but see also weaknesses) to triangulate the results through cross-corpus (ZuCo, COFETT, OneStop), cross-language, and cross-subject evaluation, and all results point in a similar direction.
  • The paper provides transparent reporting, honest disclosure of limitations, and a conservative interpretation, which is important for a negative main result (but also see below).
  • The paper is well-structured and written in a human-understandable fashion, with some leakage of AI jargon.
Critical weaknesses

Weaknesses:

  • The paper mentions multiple times "pre-registered" hypotheses, but those do not make an appearance. This concerns me deeply. A paper, specifically one which carries a negative result, should be structured along hypotheses which drive the expectation of the analysis. If there are pre-registed hypotheses, they need to be disclosed and made an integral part of the paper, irrespectively of the observed outcome.
  • Calibration (E1) shows the estimator saturates near ~0.1 bits/token fails to detect synthetic channels below roughly 0.25–0.5 bits/token. Gaze is reported at 0.107, but EEG is framed as "0.000" although this is not a tight bound on EEG mutual information beyond the established detectability threshold. The text acknowledges that correctly, but the abstract's "0.000 bits/token" does not. Is also unclear why the positive gaze result is treated differently when lying under the detection threshold and warrants a discussion of how reliable the estimates from the calibration are for real data (or can there be a gaze-specific calibration with a tighter threshold?).
  • The results are by design limited to the specific chosen representation, using only fixation-locked, word-level band power, which says nothing about raw waveforms, source-localized signals, temporal dynamics, or learned EEG encoders. The per-token likelihood-ratio framework does not rule out that EEG might carry information about higher-level structure (sentence meaning, discourse). The authors acknowledge this limitation properly, but it limits the scope. Ideally, the paper would at least outline how subsequent analysis could be conducted to extend the scope while staying as comparable as possible to the current pipeline. In that sense, the reproduction analysis in appendix H might actually deserve a more prominent role, as it provides some level of pipeline-independence. Why did the main analysis not rely on an established pipeline in the first place?
  • Minor: Figure 2 is not scaled properly
Questions for authors

see above.

4 comments
AuthorsOpenReview ↗

Author's response to Reviewer's comment

W1. Pre-registered hypotheses

You are right, and we thank you for raising it. "Pre-registered" overstated what we did. We committed the hypotheses H1–H5 locally on 8 August 2026, four days before the first access to the test split on 12 August, but without third-party registration, so the revised paper calls them pre-specified. We should also have been open about test-split use during development: earlier versions accessed it at least 11 times between 12 August and 17 September and computed E4 results. One change followed a test run: on 15 August we found that the N∗N^\ast predictor used validation bits instead of E2 bits, contrary to its documented rule, so we corrected it and reran E4. The bits/token results (E2) use validation data only and are unaffected, but the revised paper no longer calls the E4 results at N∗N^\ast a clean held-out test. The revised Appendix J gives the full timestamped access log (Table 18), and Table 2 now lists every hypothesis with its outcome:

HypothesisGazeEEGEEG + gaze
H1: information beyond the prior under both nulls (E2)passfailpass
H2: accuracy at N∗N^\ast within 1.5× (in bits) of the E2 predictionfailfailfail
H3: ITR within 1–60 bits/minpassfailpass
H4: partial AUC > 0.5 and dominates the cheap-confidence baselinepassfailpass
H5: every noise arm equivalent to chance (TOST ±2 pts)not decidablenot decidablenot decidable

H5 was not decidable at N∗N^\ast because the smallest margin 133 pools can resolve is 6.2 points; at N = 64, 15 of 30 controls are formally equivalent to chance.

W2. The abstract's 0.000, and why gaze and EEG are treated differently

We agree that the abstract overstated the EEG result. The revised abstract now states that no reliable token-level information was detected in the band-power representation, and reports 0.38 bits/token as the capacity at which 9 of 10 synthetic seeds are detected, not as an upper bound on real EEG. The different treatment is deliberate: our estimate is a lower bound, so a significant positive value (gaze) establishes at least that much information, whereas a non-detection (EEG) shows only that no information was detected. Gaze is robust across five retrained models (0.265 ± 0.025 bits/token) and GPT-2 sizes from 124M to 1.5B (0.17–0.30). Following your suggestion, we ran a gaze-matched calibration (Appendix N, Table 25):

bblocalb_{\mathrm{local}}N = 2,000: bound [seed range] · detectedN = 15,131
00−0.0004 [−0.0011, 0.0000] · 0/3−0.00004 · no
0.050.034−0.0005 [−0.0013, 0.0002] · 1/3—
0.10.0690.0047 [0.0021, 0.0071] · 2/30.0119 · yes
0.250.1750.0174 [0.0142, 0.0224] · 3/30.0434 · yes
0.50.3570.0535 [0.0411, 0.0690] · 3/30.0969 · yes
10.7370.1505 [0.1284, 0.1700] · 3/3—
21.4680.3051 [0.2989, 0.3123] · 3/3—

All seeds are detected from a true capacity of 0.18 bits/token at 2,000 sentences, and the single real-size seed from 0.07. A bound of 0.271 corresponds to a true capacity of 0.74–1.47 bits/token at 2,000 sentences and above 0.37 at the real size, so the gaze value is, if anything, an underestimate.

W3. Scope of the representation and established pipelines

We tested four further representations with the same pipeline (Appendix O, Table 27). The BrainTranslator encoder carries a negligible 3.0×10−73.0\times10^{-7} bits/token. LaBraM and CBraMod give 0.055 and 0.068, but structure-only controls reach 0.056 and 0.110, so neither carries token information beyond sentence structure. ERP features give 0.072, a third of it from which words were fixated; ERP + gaze exceeds gaze alone (0.342 vs. 0.267), but the intervals overlap and ocular artifacts may remain, so we treat ERP as a lead requiring ocular-corrected validation. Source-localized analysis would need head models that ZuCo lacks; the revised limitations state this, and that sentence-level meaning lies outside a token-level measure. Appendix O now gives a protocol for new extractors (same prior, splits, nulls and gain selection, with structure-only and injected controls), and Section 5.6 now discusses Appendix H: established pipelines give unchanged scores with real, shuffled or noise EEG, because the language model does the work, which is exactly what our measure separates.

W4. Figure 2

Agreed. The new Figure 2 uses a linear scale with b = 0 as its own point, shows every seed with the means and the exact capacity blocalb_{\mathrm{local}}, and plots detection rates with Clopper–Pearson intervals, including the ten-seed analysis; Figure 7 adds every seed's 95% interval, and Figure 4 is redrawn the same way.

Thank you for holding the paper to a high standard; we welcome further suggestions.

We would be glad to hear whether our response and the revised PDF address your concerns, and we are happy to clarify anything before the discussion period ends.

Thank you for your honest and critical re-analysis and addressing the "pre-registration". I adjusted my score to reflect this.

Thank you for your careful review and for reconsidering your score.

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

Bit Budget provides a calibrated framework for measuring text-specific information beyond a frozen language prior. Gaze on ZuCo and an injected text-dependent signal on COFETT yield positive estimates, while evaluated EEG shows negligible token-level gains despite strong task/session identity decoding.

Critical strengths

The paper measures how much text-specific information EEG adds beyond a frozen language prior. This helps assess whether decoding depends on neural evidence.

The framework detects information from gaze and recovers an injected text-dependent signal. These results support its ability to detect text-specific information.

The evaluated EEG representation achieves 82.1% balanced accuracy in four-way task/session identity decoding, but shows no detectable token-level linguistic evidence.

Critical weaknesses

The calibration fails to detect synthetic channels with injected capacities of 0.01–0.15 bits/token in any of the three seeds. Therefore, the near-zero EEG results cannot rule out weak text-dependent information.

The final candidate pools fail the pre-registered validity check, and equivalence testing is underpowered. These limitations weaken the evidence from the communication evaluation.

The EEG findings are limited to the tested band-power representations, and the COFETT analysis includes only two participants. This limits generalization to other EEG representations and broader participant populations.

Questions for authors
  1. Why was the evaluation gain fixed at 0.127 rather than the training value of 1, and how does this choice affect low-capacity detection?
  2. What validation rule selected N*=4 for gaze and N*=2 for EEG, given that larger pools (N=32 and 64) passed the pool-validity check?
6 comments
AuthorsOpenReview ↗

Author's response to reviewe's comments

W1. Weak channels are not detected

We agree that a near-zero estimate needs a calibrated detection limit. A pre-specified power analysis with ten new seeds per capacity (Appendix N, Table 24) detects a synthetic channel with a true capacity of 0.38 bits/token in 9 of 10 seeds, against 2 of 10 at 0.19. Band-power EEG is not detected under either null in any of five retrained models (largest bound 3.8×10−53.8\times10^{-5} bits/token in absolute value; Table 20), so it carries less than 0.38 bits/token beyond the prior. The revised paper now reports this upper bound rather than evidence of absence. The calibration uses 2,000 training sentences, against about 15,000 for real EEG, so the bound is conservative.

W2. Pool validity and equivalence testing

The validity check passes at N = 32 and 64, so we evaluated these sizes on the test split as a separate, logged access with the submitted checkpoints (Section 5.4, Appendix P, Table 28); an earlier development version had also run gaze at N = 32 on the test split (17 September), and the access log lists it. At N = 64 the pool set passes for all three seeds (best text-only rule at most 2.3%, chance 1.6%); gaze finds the true sentence in 33.8–39.8% of pools and EEG + gaze in 41.4%, while EEG stays at chance (1.5%). At N = 32, gaze reaches 47.4–50.4% (chance 3.1%), EEG + gaze 48.1% and EEG 3.0%; gaze seed 1 misses the check by one pool (7 of 133). Text features alone predict at or below chance (0.000–0.015).

EvidenceNText-only attackRealControls
Gaze (seeds 0/1/2)64.015/.023/.023.398/.361/.338.000–.023
EEG64.015.015.015–.023
EEG + gaze64.015.414.000–.023
Gaze (seeds 0/1/2)32.045/.053*/.045.504/.474/.474.008–.045
EEG32.045.030.015–.030
EEG + gaze32.045.481.015–.045

Test split, 133 pools; chance 0.016 (N = 64) and 0.031 (N = 32). Controls: range over six no-evidence arms. *Fails the validity check by one pool.

On equivalence testing, the problem was more basic than low power: with 133 pools, the smallest margin a TOST can resolve is 6.2 points at N = 4 and 7.1 at N = 2, so ±2 points could never be met there. At N = 64 it can (1.8 points), and 15 of 30 control results are formally equivalent to chance, the rest within 0.69 points (Table 29). The revised paper reports each arm's accuracy and resolvable margin instead of a pass/fail verdict.

W3. Only band power was tested; COFETT has two participants

We evaluated four further EEG representations with the same pipeline (Appendix O, Table 27). The BrainTranslator encoder carries a negligible 3.0×10−73.0\times10^{-7} bits/token. LaBraM and CBraMod give 0.055 and 0.068, but a structure-only control reaches the same or more (0.056 and 0.110), so neither carries token information beyond sentence structure. ERP features (0–500 ms) give 0.072, about a third of it from which words were fixated; ERP + gaze exceeds gaze alone (0.342 vs. 0.267), but the intervals overlap, and beyond ZuCo's MARA cleaning we applied no ocular correction, so we treat ERP as a lead, not a finding. COFETT is an external check, not a population estimate; the main analyses use 30 ZuCo readers.

Q1. Why γ = 0.127, and does it affect detection?

γ=0.127\gamma = 0.127 was the initial value of a gain gate not used during training (where the gain is 1), so it was never tuned. We now choose γ\gamma on held-out data (Section 3.2, Appendix L). This gives γ=0.5\gamma = 0.5; gaze rises from 0.107 to 0.271 bits/token, while EEG stays at zero at every gain. On synthetic channels it raises estimates at b≥1b \ge 1 by about 60–80% without lowering the detection floor or adding false positives. At γ≥1\gamma \ge 1 the bound shrinks, since for a fixed critic it peaks and then falls, but gaze beats both nulls at every gain (p≤0.001p \le 0.001; Table 19).

Q2. How were N* = 4 and N* = 2 chosen?

N∗N^\ast is the largest N∈{2,4,…,1024}N \in \{2, 4, \ldots, 1024\} for which the predicted accuracy 1/(1+(N−1) 2−I)1/(1 + (N-1)\,2^{-I}) is at least 0.5, with II the E2 information per sentence. Gaze gave 2.62 bits (0.107×24.60.107 \times 24.6 tokens), so N∗=4N^\ast = 4; for EEG (I≈0I \approx 0) the rule falls back to N∗=2N^\ast = 2. The rule was fixed before E4 and ignores the validity check, which is why the check could fail at N∗N^\ast; one implementation error (validation bits used instead of E2 bits) was corrected and E4 rerun (Appendix J). With the held-out gain, gaze carries about 6.7 bits per sentence and the same rule selects N∗=64N^\ast = 64, where the check passes. The rule is now stated in Section 3.2.

Thank you again for these questions. We hope the answers, the test results at N = 64 and the added EEG representations resolve your concerns, and we are glad to run anything further during the discussion.

Thank you for the additional calibration experiments and the evaluation with 64 candidates. The 9/10 detection rate at 0.38 bits/token helps characterize sensitivity for the simulated channels. Interpreting 0.38 bits/token as an upper bound for real EEG would require evidence that real EEG signals carrying the same amount of information are at least as detectable by this pipeline. I suggest revising the abstract to state that no reliable token-level information beyond the frozen language prior was detected in the tested EEG band-power representation and reporting 0.38 bits/token as a result of the synthetic calibration.

Thank you for acknowledging our response. If it answers your concerns, pl consider revising the score. We will upload the revised version at the earliest.

Reviewer_FbmJOpenReview ↗
Rating
2
Confidence
4
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper proposes Bit Budget, a framework to measure how much token-level information EEG provides beyond a frozen language model prior. The framework combines a prior-residual critic, contrastive information estimation, structured null controls, and synthetic calibration.

Experiments on ZuCo, COFETT, and OneStop show that gaze provides detectable information beyond the language prior, while the evaluated EEG representations provide almost no detectable token-level information. The paper also studies candidate selection and reproduces an EEG-to-text generation baseline to analyze evidence dependence.

Critical strengths
  1. The paper addresses whether EEG-to-text models actually use neural information or mainly rely on language priors. This is an important problem for evaluating brain-to-language decoding systems.

  2. The authors consider text-disjoint splits, shuffled and noise controls, synthetic calibration, and multiple datasets. These analyses are useful for identifying spurious performance and understanding the limitations of current EEG-to-text evaluation.

Critical weaknesses
  1. The synthetic calibration results in Table 11 show that the framework fails to reliably detect information below 0.25 bits/token and substantially underestimates even stronger injected signals. Therefore, the near-zero EEG results cannot provide strong evidence that EEG contributes little linguistic information. This limitation directly affects the main conclusion of the paper.

  2. The framework mainly combines existing contrastive information estimation, frozen language priors, and permutation-based controls. The new methodological contribution is not sufficiently clear. In addition, the candidate-pool validity test fails at the selected evaluation pool sizes, weakening the interpretation of the reported selection accuracy and communication metrics.

Questions for authors

What is the main methodological novelty compared with existing InfoNCE-based information estimators and evidence-shuffling evaluation methods?

4 comments
AuthorsOpenReview ↗

Pointwise reply to the reviewer's concern

W1. Can a near-zero EEG estimate support the conclusion, and why are strong signals underestimated?

We agree that a near-zero estimate cannot support the conclusion on its own. We therefore conducted a pre-specified power analysis with 10 additional seeds per injected capacity. The estimator detects a synthetic channel of 0.38 bits/token in 9/10 seeds, against 2/10 seeds at 0.19 bits/token (Appendix N, Table 24). We further evaluated band-power EEG across five independently retrained models. None was detected under either null test, and the largest absolute bound was only 3.8×10−53.8\times10^{-5} bits/token (Table 20). Band-power EEG therefore shows no reliable token-level information beyond the prior, and the revised abstract and conclusion now state this instead of 0.000 bits/token, reporting 0.38 bits/token as the synthetic detection level rather than as an upper bound on real EEG.

On the underestimation, we found three causes and corrected each of them (Table 23). First, because the synthetic text is drawn from the prior itself, the information available beyond the prior is about 0.73 b, not b; we now compute this exact value (blocalb_{\mathrm{local}}) and use it as ground truth. Second, γ=0.127\gamma = 0.127 was the initial value of a gain gate that is not used during training, so it was never tuned; choosing γ\gamma on held-out data raises the estimates at b≥1b \ge 1 by about 60–80%, with no false detection at b=0b = 0. Third, a coding error returned the last-epoch weights instead of the best-validation ones; after the fix, recovery at b=1b = 1 is 24% of the true value, compared with 10% in the submission (Appendix Q). The remaining gap is what we would expect from a lower bound. We also trained four other estimators (NWJ, MINE, SMILE and Jensen–Shannon) on the same channels, and all of them level off at 0.15–0.21 bits/token, just as InfoNCE does (Table 22). The gap is therefore not specific to our estimator.

W2. What is new compared with existing methods?

We agree that contrastive estimation, frozen language priors, and permutation-based controls are established techniques; our contribution is not to introduce these components independently, and we do not claim a new general-purpose mutual-information estimator. Our contribution is a calibrated framework for measuring how much token-level information recorded evidence adds beyond a frozen language prior. It rests on three design choices: (i) the evidence contribution is a token-level log-likelihood ratio against the prior, with exact full-vocabulary normalization; (ii) removing the evidence gives exactly zero contribution for every token, so the measure has a true zero point; and (iii) structured null distributions together with synthetic channels of known capacity check both false positives and detection sensitivity. The resulting estimate can therefore be read as detectable evidence-dependent information under specified controls, rather than as generation quality or an uncalibrated matched-minus-mismatched score. The revised introduction now states this, and a new appendix (Appendix R, Table 30) compares the framework point by point with contrastive MI estimators and evidence-corruption tests.

W3. The candidate pools fail the validity check

We agree that the results at N* = 4 and 2 are not validated, and the revised paper now treats them as secondary. We conducted an additional, logged test-split evaluation with larger candidate pools, N = 32 and 64, using the submitted checkpoints (Section 5.4, Appendix P, Table 28). One earlier development version had also run gaze at N = 32 on the test split (17 September); the revised access log lists that run.

At N = 64, all three gaze seeds satisfy the pre-specified validity criterion: the best text-only attack achieves at most 2.3% accuracy against 1.6% chance, while gaze achieves 33.8–39.8% and EEG + gaze 41.4%. EEG alone remains at chance (1.5%). Fifteen of the 30 no-evidence controls are formally equivalent to chance by TOST, and the rest lie within 0.69 points of it (Table 29). At N = 32, gaze achieves 47.4–50.4% against 3.1% chance, and EEG + gaze 48.1%; EEG remains at chance (3.0%). One seed fails the validity check marginally: for gaze seed 1, the best text-only attack identifies 7/133 pools (5.26%), slightly above the 5.125% threshold, while the other two seeds pass (6/133, 4.51%).

A conditional logit on text features alone scores 0.000–0.015, at or below chance, whereas adding the gaze score raises cross-validated accuracy to 0.31–0.41 at N = 64; likelihood-ratio tests agree (p < 10⁻⁴² for gaze, 0.76–0.95 for EEG). The selection therefore comes from the evidence rather than from the text. The revised paper reports this evaluation separately from the original E4 results and states the seed-1 failure explicitly.

Thank you again for a careful review. We hope these changes address both weaknesses, and we are happy to run anything further during the discussion.

We would be glad to hear whether our response and the revised PDF address your concerns, and we are happy to clarify anything before the discussion period ends.

Thank you for your detailed rebuttal and the additional experiments. I appreciate your efforts to address my concerns, particularly the clarification of the estimator's detection sensitivity and the revised interpretation of the EEG results.

While these revisions help clarify the scope and limitations of the findings, my main concerns regarding the estimator's sensitivity and the methodological novelty are not fully resolved. Therefore, I will maintain my original rating.

Thank you for reading our response and the revised paper so carefully, and for acknowledging the changes.

We agree that sensitivity remains a real limitation. The revised paper now states it directly: the estimator detects synthetic channels reliably only from about 0.38 bits/token (0.18 for the EEG-like channels), so the EEG result is reported as an absence of detectable information, not as a bound on real EEG (Section 5.1, Appendix K).

On novelty, we accept that the individual components are known. Our aim is a calibrated measurement protocol rather than a new estimator, and we have tried to state that contribution plainly in the introduction and Appendix R.

We appreciate your time and constructive review.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of revisions

We thank all reviewers. Reviewer KaRy has raised their rating to weak acceptance after the revisions. The revised PDF addresses each concern; earlier revisions are in red, and the change requested by Reviewer WoEp in the discussion is highlighted in yellow.

  • EEG claim (all reviewers). A pre-specified ten-seed power analysis characterizes sensitivity: synthetic channels of 0.38 bits/token are detected in 9 of 10 seeds. Band-power EEG is not detected in any of five retrained models. Following Reviewer WoEp, the abstract now states that no reliable token-level information was detected and reports 0.38 bits/token only as a synthetic calibration result, not as a bound on real EEG.
  • Underestimation (FbmJ). Three causes corrected: exact conditional ground truth (blocalb_{\mathrm{local}}), a gain chosen on held-out data, and a checkpoint-selection bug; four other estimators level off at the same level (Appendices L, M, Q).
  • Pool validity (FbmJ, WoEp). A separate, logged test evaluation at N = 32 and 64, where the validity check passes: gaze finds the true sentence in 34–40% of pools at N = 64 (chance 1.6%), EEG stays at chance, and TOST resolves equivalence at N = 64 (Appendix P).
  • Pre-specification and test access (KaRy). "Pre-registered" is corrected to "pre-specified"; Appendix J discloses every test-split access, and Table 2 lists all hypotheses with outcomes.
  • Scope (WoEp, KaRy). Four further EEG representations (Appendix O), a gaze-matched calibration (Appendix N), a protocol for new feature extractors, and a redrawn Figure 2.
  • Novelty (FbmJ). Stated in the introduction, with a point-by-point comparison in Appendix R.

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