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Under review as a conference paper at ICLR 2027

What Does a Channel Name Identify? Task Transfer Versus Channel Identity Across Neural Recording Sessions

Abstract

Successful decoding does not establish correct channel identity, and within-session matching need not remain reliable across recording sessions. We separate channel order, acquisition or registration identifiers, functional similarity, and decoder performance. In LINK, matching disjoint samples within a session recovers 88.4% of individual channels after an imposed permutation, but only 1.8% of complete 96-channel maps. These imperfect maps incur a mean loss of 0.0018 for one fixed decoder. Across chronological targets from two other macaques, behavior-conditioned recovery of electrode-channel identities falls from 44.8% in paired within-session controls to 4.7% across sessions. In an exploratory oracle analysis in one macaque, label-fitted reindexing raises mean held-out from 0.06 to 0.38. Across the three macaques, maps fitted on disjoint calibration halves agree on only 5–14% of channels. In 24 mice from the Allen Brain Observatory, repeated-stimulus profiles recover 20.7% of registered cells against a 1.2% random reference. A separate, prospectively frozen four-animal extension tests a locally fitted matcher across sessions. Mean false-match risk against stitched-sorting proxies is 25.66% at 62.55% source coverage, failing the prespecified requirement of at most 10% risk. Together, these experiments show that small decoder losses can coexist with incorrect channel assignments, while local matching competence does not ensure reliable cross-session matching. Identifier recovery, decoder utility, and cross-session matching risk require separate evaluation; acquisition and registered-cell identifiers do not establish biological continuity.

Primary area:
applications to neuroscience & cognitive science
Keywords:
neural recording shift, channel identity, distribution shift, neural decoding, cross-session matching, selective prediction

Reviews

Among:
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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_xVGmOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper argues that good cross-session decoding does not show a model has identified the same physical channels across sessions, and that matching channels within a session does not predict matching them across sessions. The main experiments compute features over raw neural activity, shuffle the channel identities, then solve the re-alignment problem. They find within-session recovery is high (though whole-map recovery is rare), cross-session recovery is near chance, and a baseline decoder is not affected by the errors in the recovered alignment. Follow-up experiments show that a permutation fitted with target labels can improve cross-session decoding without being stable across calibration splits (§5), and that a waveform-based unit matcher calibrated within one recording exceeds a prespecified false-match threshold when applied across sessions (§6). The paper concludes that identity recovery, decoder performance, and cross-session matching risk should be evaluated separately, and relates this to how POYO, NDT2, SPINT and LaBraM bind channels.The foremost weakness is that the paper is undigested AI output, and it is not possible to reproduce (or understand) the experiments from the text. AI use is acknowledged, but that is not an excuse, and there are indicators the author did not proofread.

Nearly every experiment is reported twice: a “frozen” version from an earlier iteration (presumably an earlier LLM session) and a “new” version with different settings and metrics (e.g. LINK 88.4% vs 86.3%, explicitly “not a revised estimate”; O’Doherty 4.7% vs 5.1%, “we retain both records”; Allen 20.7% retrieval vs 13.7% assignment recall with different denominators). §3 is titled “Analysis Status,” as if the work were unfinished. It is not explained what the new versions add beyond the old, and the duplication makes the paper difficult to understand.

It is not clear what model the primary findings (§4, Fig. 1) are evaluated under. The “fixed decoder” behind the headline 0.0018 R² loss is only inferable from an aside in §6 to be a one-bin ridge regression. The identity assay is described as “eight behavior-conditioned profiles from disjoint, behavior-balanced trial samples” with no statement of what the eight conditions are, what a profile contains, how balance is enforced, what distance is used, or what solver recovers the map.

Despite being framed against POYO, NDT2, SPINT and LaBraM (§7, Table 4), the results don’t say anything about whether the embeddings or performance of these models capture channel/neuron/unit identity. The experiments that shuffle activity channels and pair them back to their source are done on fingerprint statistics of the activity, not on any foundation model representation. The negative cross-session results show that these fingerprint statistics drift between sessions, a known property the authors themselves cite. I don’t think the results say anything about what a learned representation can or cannot identify, and I don’t think the work has implications for the design of the networks it references beyond what their multi-session mechanisms are already built to tolerate.

Critical strengths

The question of how permuting channel identity or perturbing activity affects the unit embeddings of POYO, or the read-in mechanisms of NDT2/LaBraM-style models, is interesting, and its answer could be mined for architectural improvements.

Critical weaknesses

The foremost weakness is that the paper is undigested AI output, and it is not possible to reproduce (or understand) the experiments from the text. AI use is acknowledged, but that is not an excuse, and there are indicators the author did not proofread.

Nearly every experiment is reported twice: a “frozen” version from an earlier iteration (presumably an earlier LLM session) and a “new” version with different settings and metrics (e.g. LINK 88.4% vs 86.3%, explicitly “not a revised estimate”; O’Doherty 4.7% vs 5.1%, “we retain both records”; Allen 20.7% retrieval vs 13.7% assignment recall with different denominators). §3 is titled “Analysis Status,” as if the work were unfinished. It is not explained what the new versions add beyond the old, and the duplication makes the paper difficult to understand.

It is not clear what model the primary findings (§4, Fig. 1) are evaluated under. The “fixed decoder” behind the headline 0.0018 R² loss is only inferable from an aside in §6 to be a one-bin ridge regression. The identity assay itself is described as “eight behavior-conditioned profiles from disjoint, behavior-balanced trial samples” with no statement of what the eight conditions are, what a profile contains, how balance is enforced, what distance is used, or what solver recovers the map.

Despite being framed against POYO, NDT2, SPINT and LaBraM (§7, Table 4), the results don’t say anything about whether the embeddings or performance of these models capture channel/neuron/unit identity. The experiments that shuffle activity channels and pair them back to their source are done on fingerprint statistics of the activity, not on any foundation model representation. The negative cross-session results show that these fingerprint statistics drift between sessions, a known property the authors themselves cite. I don’t think the results say anything about what a learned representation can or cannot identify, and I don’t think the work has implications for the design of the networks it references beyond what their multi-session mechanisms are already built to tolerate.

Questions for authors

No question could materially affect my assessment.

Reviewer_weHJOpenReview ↗
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1
Confidence
2
Informativeness
2
Presentation
1
Soundness
1
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Paper summary

This paper introduces a conceptual framework distinguishing different concepts namely “transport”, “binding”, “function”, and “task”, providing a structured perspective to interpret channel identity and decoding performance across sessions. The main claim is that none of the concepts can fully explain the others and measurements regarding each concept should not be interpreted beyond that concept. As for results, the paper provides analysis on existing publicly available datasets and proposes that channel source identification could be independent from downstream decoder task performance and thus should have separate measurements and interpretation. It also suggests within-session channel matching does not guarantee good inter-session matching. Additionally, it concludes that channel/cell identifiers do not establish biological continuity.

Critical strengths

Multi-dataset and multi- species analysis is a critical strength in this paper

Critical weaknesses
  1. Structure: The absence of the typical structure (introduction, methods, relevant work and results) in the case of this paper is strongly affecting the clarity of the paper in terms of positioning in the current literature and introduces significant ambiguity in understanding the individual contributions of this paper and being able to separate that from already known results.

  2. The abstract is very dense in quantitative results yet very unclear in terms of the main message. As an example, you start by saying successful decoding does not establish correct channel identity and mention channel matching of 88.4% (not perfect but substantial) causes 0.0018 in R-squared loss. You use percentage for showing imperfect channel matching but absolute value for prediction loss. This makes it hard to understand whether this is a reasonable loss. Also, it’s unclear, but it seems like you are implying that this is a small loss given that channel identifiers were matched wrong, but this is a bad control a true effect size should be measured by fully shuffled identifiers to assess the effect of channel IDs on decoding, yet here channel matching was around 88% accurate, the remaining channels may have been irrelevant for the behavior prediction. Your claim is unclear, you have not presented your results in clear terms, and you have not connected the results clearly to your claims. Additionally, later in the same abstract, for your macaques dataset, you mention an improvement of R-squared from 0.06 to 0.38 which seems significant upon re-indexing channels which point towards the fact that channel indexing is important for behavior decoding. This is not unreasonable or necessarily contradictory to your earlier statement, but these results are not well reconciled with each other.

  3. using channel matching as a proxy for channel identity: It’s important to highlight that channel recovery using your channel matcher models is only a proxy and is not identical to channel identity, meaning it is dependent on the methods and parameters used for the matcher model and can not be directly used to estimate channel identity importance or quality.

  4. general ambiguity of terms: terms such as authority, storage action, transport binding, contracts, randomized-storage ladder etc. are terms used but not well defined. I believe you can use much clearer and standard terminology familiar to the field, than what you have used here.

  5. in section 1 you mention you are introducing 4 different measurements in this paper without motivating why this is relevant and what is the main contribution and advantage of having these measurements? You are just mentioning what you are going to measure. The only thing you are motivating here is that these measurements might give you independent values (which makes sense) for example channel identity recovery does not guarantee good decoder performance since channels might carry channel-distinctive features but have no predictive value for the task being evaluated by the decoder. The question is why is that important? And how are you adding value here?

  6. underdefined mathematics: formula 1, lines 83 and 93 have mathematical expressions with undefined terms. That makes following the math very hard.

  7. the conclusion of the paper appears to be narrow, limited in novelty and not connected to any practical applications. As mentioned in section 8: this paper provides exploratory analysis on public datasets that proves that task transfer is not the same as source identification and inter-session matching is different from within-session matching. Both are valid points and trivial as mentioned before. Thus, the paper proposes to have separate measurements for the different questions, but fails to point out how this is helpful in this field or provide an example where papers made the mistake of confusing source identification and task transfer and how it can be improved by what has been proposed here in this paper.

  8. section 6: The frozen four-animal experiment's failure cannot be interpreted as evidence that channel identity is unrecoverable across sessions. The matcher was trained on a single development animal. The failure could be a methodological failure such as overfitting on the development mouse. In other words, failing to generalize a specific matcher across animals does not fully establish the lack of transferable attributes specifically when the training data consists of a single animal.

Minor: Placement of legend in figure 1 obstructs the histogram subfigure.

Questions for authors
  1. one of the main conclusions of your work is that correct channel identity and downstream decoder performance could be uninformative for each other and should be measured separately. As you said literature has well established the challenge of channel matching and session alignment when it interferes with the decoder performance. My question is, what does having an independent/separate identifier matching analysis add to our understanding of the underling neuroscience or in a practical case of BCI application?

  2. in line 107 can you explain how you are getting 500 maps?

  3. Section 4 line 155 you mention when 88.4% of channels are correctly matched by a channel matcher (so an imperfect yet very informative channel matching) it can lower the R-squared loss. What was the original R-squared with the correct map? How does this loss compare as a proportion of total decoder performance?

  4. section 4 line 195: “Stronger matchers do not remove the observed natural-session gap” as one of your findings you are showing it is harder to match channels between sessions rather than within-sessions across 3 datasets, yet the electrode coverage is not mentioned for all datasets analyzed here (only mentioned for O'Doherty), I believe this is informative when you are discussing channel matching between different datasets. Are these channels coming from a single brain region or distinctive and separate brain regions? Also, this finding is again well known and the reason why we have latent-alignment and fine-tuning when transferring a decoder to a new session, can you clarify what specific novel contribution this finding makes beyond restating a known limitation, and how it advances beyond what existing cross-session alignment methods already acknowledge?

Reviewer_FarUOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies the distinction between channel identity and task performance across neural recording sessions. It introduces an evaluation framework separating storage consistency, reference-identity recovery, functional stability, and decoder performance. Experiments on LINK, O'Doherty, Allen Brain Observatory, and UnitMatch example data show that incorrect channel assignments can preserve decoding performance, within-session matching does not ensure cross-session recovery, and locally fitted matching rules can fail a cross-session risk criterion. Additional analyses examine prediction-optimized permutations, matching stability, sensitivity to decoder choice, etc.

Critical strengths

The paper addresses a useful methodological issue (successful behavioral decoding does not establish that the same measurement sources have been identified across sessions). The evaluation spans several recording modalities and includes positive controls, stronger matchers, and decoder sensitivity analyses.

Critical weaknesses

(1) The practical contribution to neural representation learning needs stronger demonstration. The distinction is sensible, but the main identity-versus-task example uses a fixed linear decoder, while Table 4 provides an interpretive discussion of contemporary neural models. The decoder-history sensitivity in Section 6 already changes one repair conclusion. Applying the joint identity/task evaluation to a representative model with learned unit embeddings, such as POYO, would better demonstrate when the proposed framework changes a practical model assessment or scientific conclusion.

(2) The causes of unstable prediction-optimized maps remain unresolved. Appendix C notes that the split-half diagnostic changes both calibration observations and random solver starts, while within-source controls use different calibration budgets. Low map agreement therefore combines sampling effects, optimization variability, and possible assignment ambiguity. Repeating fits on identical data with different seeds, and comparing disjoint samples under matched calibration budgets, would make this finding more interpretable.

Questions for authors

Please see the weaknesses section above.

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