acceptodds
Under review as a conference paper at ICLR 2027

Representational Similarity Analysis: Countering Incompleteness with Functional Neuronal Organization

Abstract

Stimulus representations are widely used in neuroscience and machine learning to compare neural systems, such as different brain regions, organisms, and deep learning models. These representations, analyzed with decoding (perceptual) manifolds and alignment metrics such as Representational Similarity Analysis (RSA), are used for claims of similar computation. This approach has a fundamental weakness: it is misleading to assume that representational geometry is representative of a neuronal population as a whole, when such representations may be shaped by a small subset of neurons. We show that the complementary encoding paradigm addresses this: it characterizes how neurons are organized globally in terms of their responses, providing insight into how the stimulus representation is implemented by neurons within a population. We demonstrate across experiments in biological systems and deep learning models that high representational alignment can arise from small, non-representative subpopulations of neurons. Further, alignment metrics are insensitive to encoding manifold topology (how function is distributed across neurons), despite this being a key signature of differentiation across biological systems. A controlled MNIST experiment provides causal evidence: alignment metrics change only marginally even when encoding topology is causally manipulated. Overall, similarity in stimulus representations, as measured by classic alignment metrics, does not imply similarity in function or computation, motivating the use of encoding manifolds as a complementary tool for comparing neural systems.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Representational Similarity, Neural Manifolds

Reviews

Among:
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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_YogfOpenReview ↗
Rating
3
Confidence
4(+1)
Informativeness
3
Presentation
2
Soundness
3
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Paper summary

This paper investigates a fundamental yet often overlooked blind spot in systems neuroscience and machine learning: traditional population-level decoding and alignment metrics tend to be dominated by a small subset of high-responding neurons and are insensitive to changes in the internal functional organization (encoding manifold) topology. The authors propose combining encoding manifolds with the Gromov-Wasserstein (GW) distance as a complementary diagnostic tool beyond traditional "behavioral alignment." Across multiple biological datasets, diverse deep learning architectures, and rigorous controlled MNIST causal experiments, the paper convincingly demonstrates that high decoding alignment does not imply identical internal functional organization or computational mechanisms.

Critical strengths
  1. The paper directly points out the limitations of the current neuro-AI field's over-reliance on single scalar alignment metrics, revealing the profound fact that "behavioral alignment does not equal functional alignment."

  2. The authors not only analyze complex biological electrophysiological datasets but also widely test various modern deep learning models, enhancing the generality of the conclusions.

Critical weaknesses
  1. The differences in regional sampling (High-PC vs. Low-PC) are primarily driven by neuronal response amplitudes. While this exposes the flaw of Euclidean distance metrics, the discussion remains thin on how to completely strip away amplitude effects to measure tuning organization purely. Furthermore, would employing different distance metrics, such as cosine similarity or angular distance, make the metrics less susceptible to response amplitude? Discussing or evaluating whether alternative metrics can isolate tuning topology from amplitude would greatly strengthen the diagnostic framework.

  2. The controlled experiments are based solely on a relatively shallow CNN architecture. For over-parameterized modern visual foundation models or large language models trained on complex natural images (e.g., ImageNet), it remains to be validated whether this causal decoupling still holds.

  3. The GW distance matches structures by comparing internal pairwise distances. Theoretically, if two populations share internal geometric structures but encode completely unrelated semantic contents, false positive matches (spurious alignment) could occur. The quantitative boundaries of such extreme failure modes are underexplored.

Questions for authors
  1. When dealing with new datasets, the specific selection criteria or rationale for the NTF decomposition order R and the IAN neighborhood parameters lack clear guidelines or explanation. The authors need to explicitly elaborate on how these hyperparameters are chosen and discuss their potential impact on the analysis results.

  2. In the Procrustes distance calculation detailed in Appendix B.2.1, when the number of neurons in a subpopulation is K < 15, the spatial dimension P is set to k, and the smaller manifold is zero-padded to 15 dimensions prior to alignment. To what extent does this zero-padding operation affect the final analysis results?

4 comments
AuthorsOpenReview ↗

Response Part 1

We thank the reviewer for summarizing the paper’s point that “high decoding alignment does not imply identical internal functional organization.” Following the reviewer’s question on false-positive matches, we quantified this blind spot of GW. It is complementary to the blind spots of RSA/CKA/Procrustes, which is why we propose GW alongside these metrics rather than as a replacement. We also compared naturally trained models with mouse V1 and address the comments on response amplitude, hyperparameters and zero-padding below.

W1 — Amplitude vs. tuning; cosine and angular distances

"the discussion remains thin on how to completely strip away amplitude effects to measure tuning organization purely. Furthermore, would employing different distance metrics, such as cosine similarity or angular distance, make the metrics less susceptible to response amplitude?"

We recomputed the decoding metrics after per-neuron normalization (max-normalization, the normalization of the encoding pipeline, z-scoring) and RSA with correlation distance (App. A.5). The FPS results of Section 4.3 hold under all of them. For Section 4.2, high-PC1 subpopulations still decode better than low-PC1 ones, but at 5–10% they no longer match random subsets, as the normalization removes the amplitude advantage of the few neurons that dominate the decoding metrics on raw responses. We now state this in the paper. Correlation distance normalizes each stimulus pattern rather than each neuron, and we only tested it on the FPS contrast, where the results are unchanged. The encoding manifold removes amplitude by construction, since each neuron is normalized relative to its preferred stimulus, which is why we use it to measure the organization of tuning.

W2 — Deeper, naturally trained models

"The controlled experiments are based solely on a relatively shallow CNN architecture. … it remains to be validated whether this causal decoupling still holds."

A causal test in large foundation models is beyond the scope of this paper, and we state this as a limitation. We added two analyses in this direction. First, we compared 20 layers of seven naturally trained vision and video models with mouse V1 (Section 4.5, App. A.8). GW orders the layers robustly differently from CKA and RSA and separates layers with practically the same CKA. Second, on MNIST we tested ten ordinary changes of architecture, objective and regularization, including an MLP instead of the CNN (App. A.10). None of these changes targets how tuning is arranged across units. GW stays stable while the decoding metrics change, so the dissociation in Section 4.4 is specific to rearrangements of tuning.

W3 — False positives of GW

"if two populations share internal geometric structures but encode completely unrelated semantic contents, false positive matches (spurious alignment) could occur."

We agree and now quantify this failure mode (App. A.11). If the stimuli are relabeled in the same way for all neurons, GW stays exactly at 1. RSA and CKA detect permuted stimuli, but barely a global shift of the directions. If a shared stimulus set exists, fused GW detects both kinds of differences. Conversely, RSA, CKA and Procrustes are invariant to rotations of the neuron axis, which change the encoding manifold. The blind spots are thus complementary, which is why we propose GW as a complement to the existing metrics and not as a replacement. We removed the sentence that called this failure mode unlikely.

Q1 — NTF rank R and IAN parameters

"the specific selection criteria or rationale for the NTF decomposition order R and the IAN neighborhood parameters lack clear guidelines or explanation."

R is chosen as the rank beyond which the reconstruction error does not improve substantially (Dyballa et al., 2024; 8–17 here). IAN has no neighborhood-size parameter, since it infers the kernel scale of each point from the data (Dyballa & Zucker, 2023). The encoding topology is stable for R ∈ {10, 15, 20} and for 50–100% of the neurons (Figure 9). We added these guidelines to App. B.3.

AuthorsOpenReview ↗

Response Part 2

Q2 — Zero-padding in Procrustes

"To what extent does this zero-padding operation affect the final analysis results?"

Padding only affects subpopulations with fewer than 15 neurons (below 2.4% of the smallest dataset), i.e. only the leftmost points in Figure 2. Zero columns do not add shape, so the padded R² is never higher than when both sides are truncated to k dimensions. Padding can therefore only lower the score and works against our claims. The difference is at most 0.01 for k = 13 (App. B.2.1, Table 21).

Summary. The reviewer’s concerns were the role of response amplitude, the restriction of the controlled experiment to a shallow CNN, and false-positive matches under GW. With per-neuron normalization, the FPS result holds, and the advantage of high-PC1 subpopulations in Section 4.2 is an amplitude effect on raw responses. The comparison of 20 layers of naturally trained models with mouse V1 shows that GW orders layers differently from CKA and RSA, although a causal test in large models remains open. The false-positive case occurs when stimuli are relabeled identically for all neurons, and fused GW detects it when the systems share a stimulus set. We hope these results strengthen the reviewer’s assessment and would be grateful if the reviewer would consider raising the score.

I thank the authors for their thorough and thoughtful responses. The additional experiments and clarifications have addressed my concerns regarding response amplitude, the generalizability of the proposed framework, and the potential limitations of GW. I also appreciate the additional analyses on hyperparameter selection and zero-padding. While some limitations remain open for future investigation, I believe the authors have adequately addressed the key concerns raised in my review. I will maintain my Weak Accept recommendation and increase my confidence in the assessment.

We thank the reviewer for the helpful review. We appreciate the positive assessment of our work and increasing the confidence after the rebuttal.

Reviewer_45PyOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
Paper summary

The authors present an argument that commonly used alignment metrics (e.g., RSA, CKA, Procrustes), which they call “decoding metrics”, summarize a neural population into a single scalar. As a result, one overlooks how function is organized across different neurons. To remedy this, they propose the use of an “encoding manifold”, wherein each neuron is represented as a point in stimulus-response space. Using the Gromov-Wasserstein (GW) formulation, one can compare the intra-population distance structure of two such manifolds. They show that small subpopulations can mimic full-population decoding scores, and that subpopulations with distinct coverage of the encoding manifold yield similar decoding scores on neural data from retina, V1, Allen Brain Observatory, as well as several ML models. Last, they train a shallow MNIST network with an auxiliary loss that clusters neurons by their preferred digit and report that GW shows substantial changes, while decoding metrics have minimal change.

Critical strengths

Alignment metrics are widely used by the community as evidence of similar underlying computational principles, and it is worth asking what information they miss about a representation. The paper raises an important question about how function is organized across neurons within a population.

  1. The encoding manifold view is a neat complementary perspective, and is well-grounded in prior work on retina and V1.
  2. I really appreciate the breadth of neural datasets and ML models used for analysis, which makes the results more convincing
  3. The authors have been extremely thorough in their robustness checks in the appendix with respect to hyperparameters, comparisons with soft-matching distance etc.
Critical weaknesses
  1. My biggest issue is with the MNIST result in table 2, which is presented as causal evidence that decoding metrics are insensitive to encoding topology. The baseline column compares different baseline seeds, whereas the clustered column compares each clustered model to the baseline model with the same seed, i.e., the two models share their initial weights. As the authors show themselves in Appendix A.3, shared initialization substantially increases similarity (same-index unit correlation of 0.700.70 vs. 0.160.16). When this is controlled for (Table 8), RSA, CKA and Procrustes R2R^2 all decrease for the clustered model. So, per my understanding, the decoding metrics do detect the reorganization, just with a smaller effect size than GW. I think the main text, Table 2 and the abstract (“alignment metrics change only marginally”) should reflect this. Moreover, the claim should be that decoding metrics are less sensitive rather than insensitive. Relatedly, GW is only reported for same-seed pairs, which is the pairing the authors identify as confounded.

  2. A second problem with the MNIST experiment is that the auxiliary loss directly pulls together neurons with the same preferred digit based on their tuning profiles. This means that you are enforcing, via the objective, that these neurons be close to one another, which is essentially the space the encoding manifold is built from. Isn’t testing GW on this equivalent to checking whether the optimization works? It is also already known (and mentioned in the manuscript) that RSA, CKA and Procrustes are invariant to orthogonal transformations of the neuron basis. A more convincing test would use a manipulation that is not defined in terms of the encoding manifold, e.g., different architectures, objectives or regularizers, and ask whether GW distinguishes the models in this scenario while decoding metrics do not.

  3. I am also not sure why the two pipelines use different preprocessing. The encoding pipeline normalizes each neuron by its maximum response (Supp. B.3.1), whereas the decoding metrics are computed on raw responses with only a global shift (Supp. B.2). Supp. A.1 shows that the only consistent difference between the high- and low-PC1 subpopulations is response amplitude. The discussion (L443–444) acknowledges that RSA and CKA are dominated by high-amplitude neurons. This makes it possible that the dissociation in Sec. 4.1–4.2 partly reflects the preprocessing rather than a difference between the two views. Do the results hold if the same per-neuron normalization is applied before computing the decoding metrics? It is also not clear to me what “rescale by relative activation” in B.3.1 means. I wonder if this would reintroduce firing-rate differences?

  4. There also seems to be a circular argument in Sec. 4.3. The FPS subpopulations are constructed by tuning nn and mm to control breadth of coverage and local neighborhood density on the encoding manifold, and are then scored by GW similarity, which measures coverage of the same manifold. The GW difference in Fig. 4J is therefore expected by construction. The part of this experiment that is indeed informative is that the decoding metrics do not change much. More generally, in Sec. 4.1–4.3 the subpopulation’s points are taken from the full population’s embedding (L201), so GW similarity here measures how well a subset covers a fixed point cloud, rather than comparing two separately constructed manifolds. The motivating use case of comparing two systems, e.g., a model and a brain, is only tested in the MNIST experiment.

  5. Table 1 is presented as a strength (L239–242), but I think it cuts against the paper’s own argument. The paper argues that decoding metrics cannot tell which subpopulation was selected while the encoding view can. If GW changes less than the decoding metrics across the 1111 selection strategies, then GW is the measure that is less able to tell subpopulations apart. Comparing raw standard deviations across metrics with different ranges is also difficult to interpret. Perhaps it would be fairer to express each metric’s variability across selection strategies relative to its own variability across random subsets of the same size (e.g., the 1010 random draws in Supp. B.5)?

  6. Some of the statistics are also weak. In Fig. 3J, the Wilcoxon test pools 1212 pairs over 44 datasets ×3\times 3 fractions, but the fractions are nested (the top 11\\% of neurons by PC1 is contained in the top 55\\% and 1010\\%). Hence, there are effectively only 44 independent units.

  7. Finally, the paper was difficult to follow in places. It is often not clear which neural populations are being aligned. For example, in Sec. 4.1 each subpopulation is compared to its own full population, which is only stated in Appendix B.5. Stating this at the beginning of each section would help readability a lot. The paragraph at L405 is very dense, and quantities such as attribution entropy, attribution overlap and assortativity are not defined in the main text. Several key caveats (the seed pairing in A.3, the amplitude result in A.1, and the single seed in Table 5) only appear in the appendix, and I think they deserve a sentence in the main text.

Questions for authors
  1. L190 states that GW is computed in diffusion coordinate space, but Appendices B.6 and B.8 say that GW and FPS are using the first 33 MDS dimensions of the encoding manifold. I am confused as to which one of these is used?
  2. (minor) L192: since X\boldsymbol{X} and Y\boldsymbol{Y} are finite point clouds, it would be more accurate to say that μ\mu and ν\nu are uniform discrete measures over the points. It might be worth stating this explicitly
  3. L201 - L203: collapsing all points to their centroid yields a space with zero internal distances. So, GWmax\text{GW}_{\text{max}} is the root mean square pairwise distance of the full population. Does that mean that GWsim\text{GW}_{\text{sim}} can in principle be negative? Can the authors also clarify where the ε\varepsilon jitter enters? Is it added to the pairwise distance matrices?
  4. L215: what does "Proc. R2R^2 and trajectory metrics produce lower alignment scores only below 11\\% of neurons" mean? I assume these metrics only drop once <1<1\\% of neurons are kept? If that is the case, then the wording is a bit ambiguous
  5. Fig. 2 is hard to read with all the shaded bands, and also makes it a bit difficult to tell colors apart. What are the individual gray lines? Do they show alignment for different subpopulations?
  6. "IAN decoding manifold" (L376 + table 5) is not used elsewhere. Is this the same encoding manifold as in Sec. 3.2?
  7. In Fig. 5, how are the neuron tunings calculated? Are tuning mean and variance computed per unit across digits?
  8. The baseline-vs-baseline values differ slightly between Table 2 (RSA =0.958=0.958, GW =0.958=0.958) and Table 8 (RSA =0.955=0.955, GW =0.957=0.957). Are different pairs of seeds used?
  9. The selection strategies in Sec. 4.1 all rank neurons by within-population statistics. One could think of a complementary analysis where you select neurons by whether they have a functional counterpart in another system, e.g., using partial optimal transport methods such as partial soft-matching between the baseline and clustered MNIST models (or across animals or sessions). In this case, it would be interesting to see whether decoding metrics computed on matched versus unmatched units differ. It would also directly test whether neurons that are shared across systems are what drive the decoding scores, which would add to the results presented in the paper
5 comments
AuthorsOpenReview ↗

Response Part 1

Introduction

We thank the reviewer for a very detailed and expert review that has led to new analyses and corrections that improve the paper. We agree with the reviewer's main point about the seed pairing in the MNIST experiment and have corrected it. With seed-controlled pairs, the decoding metrics do detect the reorganization, but they shift by at most 2.5 seed-to-seed SDs while GW shifts by 19, so we now describe them as far less sensitive rather than insensitive. On circularity, we now present the GW differences in the FPS and MNIST experiments as manipulation checks with a known ground truth. As the reviewer notes, the informative result is how little the decoding metrics change. We also added a model–brain comparison, in which GW orders layers differently from CKA and RSA. The reviewer's attention to detail also found several smaller issues, which we fix in the paper.

W1 — Seed pairing in Table 2

"the clustered column compares each clustered model to the baseline model with the same seed, i.e., the two models share their initial weights. … the decoding metrics do detect the reorganization, just with a smaller effect size than GW."

We agree with the reviewer: baseline and clustered models with the same seed share their initial weights. We recomputed all metrics, including GW, for seed-controlled pairs (Base_i vs. Clust_i+1 against Base_i vs. Base_i+1) with newly built encoding manifolds (Table 2, App. A.3). The decoding metrics do detect the reorganization (RSA, CKA and SMD in 20/20 pairs, Procrustes in 17/20), but with much smaller effects than GW: RSA, CKA and SMD shift by 1.7–2.5 seed-to-seed SDs and Procrustes by 0.9, while GW shifts by 19. We therefore no longer describe the decoding metrics as insensitive: the abstract, the contributions and Section 4.4 now state that they are far less sensitive than GW, and the conclusion that they change little. The same-seed comparison moved to the appendix (Table 8).

W2 — The auxiliary loss targets what GW measures

"the auxiliary loss directly pulls together neurons with the same preferred digit based on their tuning profiles. … Isn't testing GW on this equivalent to checking whether the optimization works?"

We agree that for the clustering loss the change in GW is a manipulation check. To test whether metrics detect a change in organization, the change needs to be known, so we defined the manipulation in terms of that organization. The informative result is that the decoding metrics change much less (W1). We now state this in Section 4.4 and limit the causal claim to rearrangements of tuning across units.

We also ran the suggested test with ten changes that are not defined on the encoding manifold: dropout, L1 on the activations, doubled width, tanh units, weight decay, label smoothing, augmentation, an MLP instead of the CNN, an MSE objective, and a contrastive loss over images (10 seeds each, compared across different seeds; App. A.10, Table 19). GW changes by at most 2 seed-to-seed SDs. The decoding metrics and SMD change by up to 10.8 SDs (e.g. MLP: CKA −8.0, SMD +10.8). None of these changes targets how tuning is arranged across units. GW does not detect them, while the decoding metrics do. We see this as the complementary blind spot of GW and report it in the paper. For a comparison between two systems that is not defined on the encoding manifold, see W4.

W3 — Different preprocessing

"Do the results hold if the same per-neuron normalization is applied before computing the decoding metrics? It is also not clear to me what "rescale by relative activation" in B.3.1 means."

"Rescale by relative activation" divides the response to each stimulus by its norm and multiplies it by the mean response to this stimulus in its best direction, relative to the neuron's preferred stimulus. This removes differences in firing rate between neurons instead of reintroducing them, and we now explain this in B.3.1.

We recomputed the decoding metrics with the same per-neuron normalizations (max-normalization, the normalization of the encoding pipeline, z-scoring) and RSA with correlation distance (App. A.5). The FPS results of Section 4.3 are unchanged under all of them. In Section 4.1, small subpopulations still reach high scores after normalization, but selective strategies mostly no longer beat random ones. In Section 4.2, high-PC1 subpopulations still decode better than low-PC1 ones in all datasets, but at 5–10% they no longer match random subsets. This is expected: the normalization removes the amplitude advantage of the few high-PC1 neurons that dominate the decoding metrics on raw responses, which is the mechanism Section 4.2 describes for decoding metrics as they are usually applied. We now state this in Section 4.2.

AuthorsOpenReview ↗

Response Part 2

W4 — Circularity in Section 4.3

"The GW difference in Fig. 4J is therefore expected by construction. … The motivating use case of comparing two systems, e.g., a model and a brain, is only tested in the MNIST experiment."

We agree with the reviewer that "the part of this experiment that is indeed informative is that the decoding metrics do not change much". Therefore, the experiment and its conclusions stay valid. We now present the GW difference in Section 4.3 as a manipulation check with known ground truth, and state at the start of Section 4 that in Sections 4.1–4.3 GW measures how well a subpopulation covers the manifold of its own population.

We added a model–brain comparison (Section 4.5, App. A.8): across 20 layers of seven pretrained models compared with mouse V1, GW orders the layers robustly differently from CKA and RSA, and it clearly separates layers with practically the same CKA (in 30/30 resamples). CKA and RSA also disagree with each other, so GW adds a view that is not redundant with them rather than a unique one.

W5 — Table 1

"If GW changes less than the decoding metrics across the … selection strategies, then GW is the measure that is less able to tell subpopulations apart."

We ran the suggested normalization (App. A.6): relative to the variability across random subsets, GW still varies least across strategies. We agree with the reviewer that GW is therefore less able to tell the strategies apart. GW measures the coverage of the encoding manifold, which every selective strategy reduces: all 38 selected subpopulations cover less of the manifold than random subsets of the same size, clearly so in 33 (5%) and 36 (10%) of them, including most strategies that beat random on decoding. We keep Table 1 with a neutral description.

W6 — Nested fractions in Fig. 3J

"In Fig. 3J, the Wilcoxon test pools … but the fractions are nested"

We agree. With a single fraction (5%), all 12 biological datasets and a null from 50 random subsets, high-PC1 subpopulations are not reliably closer to the full population than low-PC1 ones (8/12 datasets, p = 0.18; App. A.7), and we withdraw this claim, since the sign of the difference varies between datasets. Both subpopulations cover less of the manifold than random subsets in all 12 datasets.

W7 — Readability

"It is often not clear which neural populations are being aligned. … Several key caveats … only appear in the appendix, and I think they deserve a sentence in the main text."

Thank you, we adopted these suggestions. Section 4 now starts by stating what is compared with what, the dense paragraph is split and the attribution measures are defined in the main text, and the caveats on the seed pairing, the response amplitude and the single seed in Table 5 are now in the main text.

AuthorsOpenReview ↗

Response Part 3

Questions

  • Q1. "L190 states that GW is computed in diffusion coordinate space, but Appendices B.6 and B.8 say that GW and FPS are using the first … MDS dimensions"

    GW uses the first three MDS coordinates of the diffusion map embedding (five for MNIST). We corrected L190, and B.8, which wrongly stated that FPS uses all 10 dimensions for the neighbors.

  • Q2. "it would be more accurate to say that … are uniform discrete measures over the points"

    We changed this as suggested.

  • Q3. "Does that mean that … can in principle be negative? Can the authors also clarify where the … jitter enters?"

    Yes, GW<sub>max</sub> is the RMS pairwise distance of the full population, so GW<sub>Sim</sub> can be negative. For subpopulations, we clip it to [0, 1], and the clip was not active at 5%. The jitter is added to the coordinates of the collapsed point cloud. We now state all of this in the paper.

  • Q4. "I assume these metrics only drop once … of neurons are kept?"

    Yes, we reworded this to say that these metrics fall clearly below ceiling only when fewer than 1% of the neurons are kept.

  • Q5. "What are the individual gray lines?"

    These are the individual selection strategies; we now explain them in the caption. We are happy to remove them for readability if the reviewer prefers.

  • Q6. "Is this the same encoding manifold as in Sec. 3.2?"

    Yes, and we renamed the label accordingly.

  • Q7. "In Fig. 5, how are the neuron tunings calculated?"

    Per unit, as the mean and variance across the 10 digit-averaged activations. We added this to the caption.

  • Q8. "The baseline-vs-baseline values differ slightly between Table 2 … and Table 8 … Are different pairs of seeds used?"

    Yes, Table 2 averaged over all 190 baseline pairs and Table 8 over the 20 consecutive pairs. Both now use the consecutive pairs.

  • Q9. "select neurons by whether they have a functional counterpart in another system, e.g., using partial optimal transport methods"

    Thank you for this suggestion, we ran it (App. A.9) with partial optimal transport (half of the mass) between Base_i and Clust_i+1. Units with a counterpart reproduce the decoding scores as well as random subsets, while units without a counterpart score lower (p = 0.008, n = 10). The same holds between two baseline models, so this reflects which units are shared across networks and not the clustering loss.

Summary. The reviewer’s main concern was the seed pairing in Table 2. With seed-controlled pairs, the decoding metrics do detect the reorganization, but they shift by at most 2.5 seed-to-seed SDs while GW shifts by 19, and the paper now describes decoding metrics as much less sensitive rather than insensitive. The GW differences in Sections 4.3 and 4.4 are now presented as manipulation checks, and for ten MNIST changes not defined on the encoding manifold, GW stays stable while the decoding metrics change. The FPS result holds under per-neuron normalization, while the advantage of high-PC1 subpopulations in Section 4.2 is an amplitude effect on raw responses, as the reviewer suspected. The new model–brain comparison tests the use case the reviewer found missing: GW orders layers differently from CKA and RSA and separates layers that CKA does not. We withdrew the claim of Fig. 3J and no longer present Table 1 as an advantage of GW. We hope these results address the reviewer’s concerns about soundness and would be grateful if the reviewer would reconsider the assessment.

Reviewer_tGV7OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper argues that decoding-based alignment metrics, such as RSA, CKA, k-NN accuracy, Procrustes, and their trajectory-based variants, are insensitive to how a neural population is internally organized. As a complementary view, it proposes encoding manifolds, which represent neurons as points in stimulus-response space, and the Gromov-Wasserstein (GW) distance as a measure for comparing them. Using mouse retina, V1, ten Allen Brain Observatory datasets, and several machine learning models, the authors show that decoding metrics reach near-ceiling values with 5% of neurons or fewer, that subpopulations matching full-population decoding occupy only small regions of the encoding manifold, and that subpopulations with clustered or continuous encoding topology yield similar decoding scores. In a controlled experiment, an auxiliary loss clusters the hidden neurons of an MNIST CNN by preferred digit, which changes encoding topology and GW similarity while leaving accuracy, RSA, CKA, and Procrustes scores unchanged.

The paper claims three contributions: that a small, selective subset of neurons can replicate full-population decoding performance; that representational alignment metrics inherit this blind spot; and that encoding and decoding topology can be manipulated independently, providing causal evidence that decoding metrics are insensitive to internal functional organization. In my reading, the paper is timely. There has been a recent wave of critical work on RSA and other metrics for comparing representations across neural systems, the field is moving towards a multi-metric approach, and this paper adds to that literature. It is also clearly motivated and written. However, the insensitivity of RSA and CKA to neuron-level organization largely follows from invariances these metrics have by design, and the encoding manifold pipeline and GW distance are existing tools. The paper does not compare against existing metrics that are sensitive to single-neuron tuning, and it gives little guidance on how decoding and encoding measures should be used together. I am therefore not convinced that the contribution is sufficient for ICLR in its current form.

The experiments cover a broad range of biological and artificial systems, and the MNIST experiment is evaluated over 20 seeds with appropriate statistics. However, in the biological analyses, subpopulations are selected or constructed on the encoding manifold, and GW is then computed on the same manifold, so its sensitivity to these differences is partly expected by construction.

Critical strengths

Timely question, clearly presented: The paper addresses an active debate about the limits of representational similarity metrics and argues for a complementary, neuron-level encoding view. The motivation is clear, and the claims and experiments are stated precisely.

Clean controlled experiment and broad evaluation: The MNIST experiment shows directly that two networks can match on accuracy, RSA, CKA, and Procrustes while differing in internal organization, with measurable differences in tuning, attribution structure, and robustness. The biological analyses extend the pattern across many datasets and stimulus types.

Critical weaknesses

Limited novelty and missing comparison to neuron-level metrics: RSA, CKA, and Procrustes are invariant to neuron identity and to rotations of population space by design, so their insensitivity to neuron-level organization is a known property rather than a new finding. That a small fraction of neurons can match full-population decoding is likewise expected given redundancy in neural populations. The encoding manifold pipeline follows Dyballa et al. (2024), and GW is widely used for neural alignment. The paper’s specific claim is that encoding manifolds are needed to detect differences in internal organization, but it does not compare against existing metrics that are sensitive to single-neuron tuning, most directly soft matching distance (Khosla & Williams, 2024), or against a simple comparison of tuning-curve distributions. In addition, the subpopulations in Sections 4.2 and 4.3 are defined on the encoding manifold, and the auxiliary loss in Section 4.4 directly targets the clustering that the encoding manifold measures, so GW detecting these differences is expected.

Insufficient guidance on interpretation and combined use: The paper shows that decoding metrics miss differences in encoding topology and recommends complementing them with encoding manifolds and GW, but it does not show how the two should be used together. It does not specify how combinations of decoding and GW scores should be interpreted, what magnitude of GW difference is meaningful (for example, relative to differences between individuals), or whether combining the measures changes any conclusion in an actual model-brain comparison. In addition, as the authors acknowledge, GW compares only within-population distances, so two populations with similar topology but different stimulus tuning can appear similar. In model-brain comparisons with a shared stimulus set, this limitation is critical, and it means GW alone captures topology rather than function.

Questions for authors

Does soft matching distance, or a direct comparison of tuning-curve distributions, also distinguish the conditions in Sections 4.3 and 4.4? If so, what does encoding-manifold GW capture that these measures do not?

How should decoding and GW scores be interpreted jointly? What magnitude of GW difference is meaningful, for example relative to the GW similarity between the same area in two individuals?

Have the authors applied both measures to an actual model-brain comparison? Does adding GW change any conclusion, for example the ranking of models that are matched on CKA?

Since GW compares only within-population distances, how would a model with the same encoding topology but different stimulus tuning be distinguished from a functionally aligned model?

Table 1 presents the lower variability of GW across selection strategies as an advantage. Why does this indicate robustness rather than lower sensitivity of the measure?

3 comments
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Response Part 1

Introduction

We thank the reviewer for the careful review, and in particular for asking whether adding GW changes any conclusion in an actual model–brain comparison. We ran this comparison for 20 layers of seven pretrained models against mouse V1. GW orders the layers differently from CKA and RSA, and it separates layers that CKA does not. For example, the FNN output layer, which is trained to predict mouse visual-cortex responses, and CORnet-S V2 differ in CKA by only 0.02. GW is higher for the FNN output in all 30 resamples, by about ten times the variability between two halves of the V1 population. We agree that the invariances of RSA, CKA and Procrustes are known from theory. The paper tests whether they matter on real data, and it provides a measure that does not share them. Below, we also report the requested comparison with neuron-level measures, quantify the blind spot of GW, and describe how the two families of measures should be read together.

Scope of the comparisons

"it does not compare against existing metrics that are sensitive to single-neuron tuning, most directly soft matching distance (Khosla & Williams, 2024)"

We already compare to soft matching distance in the paper (see Related Work and Appendix A: Comparison with the Soft-Matching Distance, Table 8). We make this more prominent in the paper and extend it to the FPS results (see Q1 below).

"the subpopulations in Sections 4.2 and 4.3 are defined on the encoding manifold"

This is true for Section 4.3, but in Section 4.2 the subpopulations are defined on the decoding side. Our own wording likely caused this misunderstanding, and we now clarify this in the paper. In Section 4.3, we present a manipulation check on the encoding manifold, to have a known ground truth, and we make this clearer in the paper.

Novelty

One key weakness the reviewer mentions is the novelty of the paper:

"RSA, CKA, and Procrustes are invariant to neuron identity and to rotations of population space by design, so their insensitivity to neuron-level organization is a known property rather than a new finding."

We agree that from theoretical analyses the invariances and shortcomings of decoding metrics are known in the literature; we do not claim to discover them. However, the presence of these invariances in theory does not guarantee that they matter in practice. Our analyses test whether they matter on several recorded and model datasets, using the encoding manifold as a description of the population that does not share these invariances. Specifically, a rotation of the neuron axis that mixes the neurons in a population has no effect on RSA/CKA/Procrustes, but it directly impacts the encoding perspective. We make this clearer in the paper (Related Work and Section 3.2).

"GW is widely used for neural alignment."

GW has been used for neural alignment (e.g. Thual et al., 2022; Takeda et al., 2025; Takahashi et al., 2026), but by matching stimuli or cortical locations between systems. To our knowledge, GW has not been used to match neurons as we propose in our paper. We would be grateful for references if we have missed such work.

Q1 / W1b — SMD and tuning-curve distributions

"Does soft matching distance, or a direct comparison of tuning-curve distributions, also distinguish the conditions in Sections 4.3 and 4.4? If so, what does encoding-manifold GW capture that these measures do not?"

We agree that, by construction, the FPS experiment does favor GW. We use it as a manipulation check with known ground truth. As expected, GW cleanly separates the smooth vs clustered conditions. The key finding is that decoding metrics do not, and we now checked that SMD on the tuning curves, and distance between tuning curve distributions, are also inconsistent here. Similarly, in the MNIST experiment, the decoding metrics and SMD are a lot less sensitive to the changes of the encoding manifold than GW. We agree that our framing here was too strong, we now clarify that these are manipulation checks, and that decoding metrics are not insensitive but a lot less sensitive in the MNIST experiment. The encoding manifold describes how tuning curves are arranged relative to each other across the population, and GW compares this arrangement without needing a shared stimulus frame. Overall, we conclude from this that our encoding perspective is a useful complement to the existing metrics.

AuthorsOpenReview ↗

Response Part 2

W1c — The auxiliary loss targets the encoding manifold

"the auxiliary loss in Section 4.4 directly targets the clustering that the encoding manifold measures, so GW detecting these differences is expected."

We agree that the clustering loss in Section 4.4 acts directly on the organization that the encoding manifold measures, so the change in GW is expected. This is intended: to test whether a metric detects a change in organization, we need a manipulation with a known ground truth, and this requires defining the manipulation in terms of that organization. The change in GW is therefore a manipulation check, and the key result is how little the decoding metrics change. We now state this in Section 4.4 and limit the causal claim to rearrangements of tuning across units.

Following a suggestion of reviewer 45Py, we also tested ten ordinary training changes that do not target the encoding manifold, for example dropout, an MLP instead of the CNN, or an MSE objective (App. A.10). Here GW barely changes (at most 2 seed-to-seed SDs), while the decoding metrics change by up to 8.0 SDs (CKA for the MLP) and SMD by up to 10.8 SDs. None of these changes targets how tuning is arranged across units, and the two families of metrics have complementary blind spots. For a comparison that is not defined on the encoding manifold, see W2 / Q2 / Q3 below.

W2 / Q2 / Q3 — Joint use, magnitude and model–brain comparison

"How should decoding and GW scores be interpreted jointly?"

Decoding metrics describe what a population represents and the encoding manifold how it is organized. We now discuss in the Discussion how the two should be read together. Similar decoding scores with different GW indicate the same read-out with a different implementation (Section 4.4). Different decoding scores with similar GW indicate either a blind spot of GW (Q4) or a change at the read-out level (App. A.10). A similar GW alone does not establish a similar implementation.

"What magnitude of GW difference is meaningful, for example relative to the GW similarity between the same area in two individuals?" "Have the authors applied both measures to an actual model-brain comparison? Does adding GW change any conclusion, for example the ranking of models that are matched on CKA?"

To answer both the magnitude and the model–brain question, we compared 20 layers of seven pretrained models with mouse V1 (new Section 4.5, App. A.8). Each layer is subsampled to the number of V1 neurons and compared with halves of the V1 population (30 resamples), and since the spread of an encoding manifold depends on the number of neurons, each manifold is scaled to unit spread. Two halves of one V1 population define the noise floor (GW similarity 0.80, SD 0.013). Differences between models are large relative to this floor, and they change the ranking of models that are matched on CKA. The FNN output layer, which is trained to predict responses of mouse visual cortex, and CORnet-S V2 have practically the same CKA (difference 0.02), but differ by 0.13 in GW, about ten times the variability of the floor, with a higher GW for the FNN output in all 30 resamples. Likewise, MouseNet VISl2/3 has the same CKA as PredNet layers 2 and 3, but a GW that is lower by 0.15 in all 30 resamples.

Q4 — Same topology, different tuning

"Since GW compares only within-population distances, how would a model with the same encoding topology but different stimulus tuning be distinguished from a functionally aligned model?"

We agree that this is a blind spot of GW, and we now quantify it (App. A.11). If the stimuli are relabeled in the same way for all neurons, all neuron-to-neuron distances stay the same and GW stays exactly at 1. RSA and CKA detect permuted stimuli, but barely a global shift of the directions, since the set of directions is symmetric. Conversely, RSA, CKA and Procrustes are invariant to rotations of the neuron axis, which change the encoding manifold. The blind spots of the two families are thus complementary, and we propose GW alongside decoding and neuron-level metrics, not as a replacement. If a shared stimulus set exists, fused GW, which adds a tuning term to the GW cost, detects both kinds of differences (App. A.11). We discuss this in the limitations.

Q5 — Table 1

"Table 1 presents the lower variability of GW across selection strategies as an advantage. Why does this indicate robustness rather than lower sensitivity of the measure?"

Table 1 shows how much each metric depends on the criterion that is used to select a subpopulation. GW measures the coverage of the encoding manifold, and every selective strategy reduces it: at 5% and 10%, all 38 selected subpopulations cover less of the manifold than random subsets of the same size, clearly so in 33 and 36 of them (App. A.6). Therefore, we now show Table 1 with a neutral description.

I thank the authors for the above clarifications and changes, which have addressed many of my concerns. I will raise my score to 3.

Comments on the paper

1 comment
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General Response

We thank all reviewers for careful and constructive reviews. As the reviewers noted, metrics like RSA, CKA, and Procrustes are by design insensitive to how a population is organized at the level of neurons, which Reviewer Yogf calls “a fundamental yet often overlooked blind spot.” Our contribution is not in identifying these known blind spots, but in testing whether they matter on recorded and model data, and in proposing the encoding manifold and GW distance as tools for complementary use alongside these metrics. We now stress this contribution more clearly in the paper. Following the reviewers’ suggestions, we compared 20 layers of seven pretrained models with mouse V1. GW orders the layers differently from CKA and RSA and separates layers that CKA does not distinguish, so it adds information that the decoding metrics do not provide. The main changes are summarized below, and the individual responses contain the details.

Main points

Seed pairing in the MNIST experiment (45Py). With seed-controlled pairs, RSA, CKA and SMD detect the reorganization in 20/20 pairs, but they shift by at most 2.5 seed-to-seed SDs, while GW shifts by 19. We now describe decoding metrics as far less sensitive than GW instead of insensitive.

Circularity (45Py, tGV7). Only the FPS subpopulations (Section 4.3) and the clustering loss (Section 4.4) are defined on the encoding manifold. This is intended, since a controlled test needs a known change in organization, and there the GW difference is a manipulation check. For ten MNIST manipulations that are not defined on the encoding manifold, GW stays stable while the decoding metrics change, so the two families have complementary blind spots. We limit the causal claim to rearrangements of tuning across units.

Model–brain comparison (tGV7, 45Py; related to Yogf). Across 20 layers of seven pretrained models compared with mouse V1, GW orders the layers robustly differently from CKA and RSA and separates layers with practically the same CKA. CKA and RSA also disagree with each other, so GW adds a view that is not redundant with them (Section 4.5, App. A.8).

Corrections (45Py). We withdraw the claim of Fig. 3J. The advantage of high-PC1 subpopulations in Section 4.2 is an amplitude effect on raw responses. Table 1 is no longer presented as an advantage of GW.

Overview of changes to the paper

  • Main text. "Insensitive" → "much less sensitive" (abstract, contributions, Section 4.4, conclusion). Section 3.2: GW is not invariant to rotations of the neuron axis, precise GW definition, GW does not establish a neuron-to-neuron correspondence. Section 4: opening sentence on what is compared. Section 4.1: Table 1 described neutrally, per-strategy lines in Figure 2 explained in the caption. Section 4.2: renamed, Fig. 3J claim withdrawn, normalization result. Section 4.3: GW difference as manipulation check, neuron-level baselines. Section 4.4: new Table 2 with seed-controlled pairs, scope of the causal claim, MNIST control experiments, caveats, attribution measures defined. New Section 4.5: model–brain comparison. Discussion: joint use of both families, complementary blind spots.
  • Appendix. New sections with methods, results and tables: neuron-level measures on the FPS contrast (A.4), per-neuron normalization (A.5), variability across selection strategies (A.6), high- vs. low-PC1 subpopulations in all 12 datasets (A.7), model–brain comparison (A.8), units with and without a functional counterpart (A.9), MNIST manipulations not defined on the encoding manifold (A.10), and the blind spot of GW with fused GW (A.11). Table 8 with GW for both seed pairings, zero-padding in Procrustes (B.2.1), normalization and hyperparameter guidelines (B.3), corrected FPS and GW methods (B.8, B.9).

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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