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Under review as a conference paper at ICLR 2027

Centered Kernel Distance: Dimension-Free Error Bounds for Comparing Neural Representations

Abstract

The asymptotic error of representational similarity metrics such as CKA and RSA has been well-characterized, but there are no realistic bounds on how estimates of representational similarity depend on the number of sampled neurons () and experimental conditions (). We study the natural metric counterpart of CKA and RSA, which we call the Centered Kernel Distance (CKD). We show that CKD can be studied via an unbiased estimator, whereas several popular similarity measures including CKA have no unbiased estimator. Under mild assumptions, we show that estimation error of CKD decays in proportion to . Strikingly, the rate in this bound does not depend on the dimensionality of the space of experimental conditions. Thus, similarity estimation does not suffer from the curse of dimensionality, which plagues similar problems in high-dimensional statistics. We verify our results empirically in random shallow neural networks, trained neural networks, and macaque visual cortex data. Ultimately, this paper advances a framework for studying the error of similarity estimators, and our theoretical and empirical predictions produce specific prescriptions on how to most efficiently estimate the similarity between multiple neural systems.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Representation Similarity, Similarity Metrics, Error Bounds

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_2W6oOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The presented work proposes the Centered Kernel Distance (CKD) to evaluate the similarity between neural representations and studies its theoretical properties, showing that CKD can be studied as an unbiased estimator, and providing an error bound on its variance, depending on the number of sampled neurons and experimental conditions. The experimental evaluation supports the proposed theoretical bound and covers a range of examples comparing one layer neural networks with random weights, deep convolutional networks trained on ImageNet, and neural representations from the THINGS Veneral Stream Dataset across brain regions of different monkeys.

Critical strengths
  • The scope of the work to study statistical properties and error bounds of the centered kernel distance is well articulated and described in connection to related work. The authors provide a clear description of results, do appropriately acknowledge substantial LLM use, and with the aid of LLMs provide both relevant theoretical and empirical results, which support their main claims. Overall, I believe this is a solid contribution to understanding the estimation error of the proposed Centered Kernel Distance (CKD).
Critical weaknesses
  • The statement that CKD² does not suffer from the curse of dimensionality seems overstated. Just because one can find a dimension-free bound, this might not necessarily imply that the empirical estimate might not still practically be impacted by varying dimensionality or varying numbers of samples.
  • Figure 1 only validates the results in relatively low dimensions d=1,5,9 rather than providing extensive verification across higher-dimensional settings.
  • The experimental evaluation covers a range of examples including convolutional neural networks trained on ImageNet and monkey brain data. Nevertheless, the evaluation could be strengthened through further empirical evaluation, e.g. by verifying the results across a wider range of image datasets, different neural network architectures, and a wider range of varying dimensionalities. Overall, as it stands the empirical evidence is limited to relatively few experimental settings.
  • In general, the scope of the work is focused on proposing CKD and evaluating the error bound in Thm 3.1, which is a solid, but perhaps not a very novel or impactful contribution. This can of course be argued about, but for example the results do not demonstrate why CKD would be a more useful representational similarity metrics than existing methods beyond its theoretical study.
  • Further discussion and comparison both in terms of the theoretical properties and empirical performance of existing representational similarity metrics, out of which there exist a wide range of alternative methods (see Klabunde et al. (2025)), would strengthen the motivation of proposing and using CKD in the first place.
  • The way the theoretical results are structured could benefit from further formalisation and clear separation into theorems and proofs etc., to clarify which of the statements rely on which assumptions, distinguish novel results, and clarify how each statement is derived.

Minor comment:

  • CKA and RSA are first mentioned in the abstract but not defined there.
  • The quality and resolution of the illustrations is low and could be improved by e.g. using vector graphics.
  • The language is difficult to follow at parts.
  • Typo in line 471(?) - “providea”
  • missing word in line 474 “, bootstrapping would still be constrained ill-parameterized experiments”

Reference: Max Klabunde, Tobias Schumacher, Markus Strohmaier, and Florian Lemmerich. Similarity of neural network models: A survey of functional and representational measures. ACM Computing Surveys, 57(9):1–52, 2025.

Questions for authors
  • How confident are you really in the statement that your estimator does not at all suffer from the curse of dimensionality in practice?
  • How would the results from Figure 1 behave in truly higher dimensional settings, for example d=100 and d=1000?
  • Could you verify the results on the image datasets for different neural network architectures and different image datasets?
1 comment

Thank you for your helpful comments.

The statement that CKD² does not suffer from the curse of dimensionality seems overstated.

Our original manuscript did not clearly define what we mean by the “curse of dimensionality”; we rectify this in our revision (Section 3.2). In high-dimensional statistics, the curse refers to cases where the dimensionality DD directly decreases the rate at which the data scale (here, MM and NN) reduces estimation error. In particular, it refers to cases where one needs to exponentially increase the number of samples to compensate for a linear increase in DD. Our results rule this out.

We agree that it is important to characterize how the dimension DD enters in the constant CC out front of our bound. We address this in detail in our common response (A) to reviewers. In short, we have revised the proof to show that CC only depends on the maximal fourth moment of the neural response, which — remarkably — is also bounded independent of the dimension under weak assumptions.

Thus, our results show that the hardness of the problem of estimating CKD stems from the maximal fourth moment of the neural responses rather than the dimensionality of the inputs, per se. Moreover, this quantity only impacts the hardness by a multiplicative constant, it does not impact the rate at which collecting more data (more MM or NN) improves the estimate.

How confident are you really in the statement that your estimator does not at all suffer from the curse of dimensionality in practice?

We are extremely confident that the estimator does not suffer from the curse of dimensionality. As detailed above and in our common response, our bound rules out the possibility that the rate of convergence of the variance degrades with dimension.

In terms of numerical validation, we have updated our Figure 1 on random neural networks, and have updated our analysis in Section 4.1 to accommodate new results regarding large-DD simulations in random neural networks.

Our results on natural images further verify our claims, as the dimensionality of the space of natural images is quite large, and much more complicated than random Gaussian inputs. We present new results in Appendix K to show that our results are independent of subclass within the space of natural images as well (see response (C) for details).

Could you verify the results on the image datasets for different neural network architectures and different image datasets?

We address these concerns in point (C) of our global response to reviewers. As mentioned above, our new Appendix K contains relevant results.

The results do not demonstrate why CKD would be a more useful representational similarity metrics than existing methods beyond its theoretical study… Further discussion and comparison both in terms of the theoretical properties and empirical performance of existing representational similarity metrics [...] would strengthen the motivation of proposing and using CKD in the first place.

We address these concerns in point (B) of our global response to reviewers.

We do not believe there is a single similarity measure that supercedes all others. Different measures quantify different things. For example, CKD is sensitive to the scale of neural responses while CKA is scale-invariant by design. Different applications or hypotheses will call for different measures in this regard.

We disagree that our paper does not highlight cases where CKD may be more useful. In particular, practitioners who are working with noisy, limited data (e.g. experimental neural recordings) and who want to use a method with theoretical guarantees should consider using CKD. For example, if an unbiased estimator is desired, we have given one for CKD while also proving that no such unbiased estimator exists for Procrustes and CKA (see discussion in Section 3 and proof in Appendix F). Furthermore, our main result on the variance of the CKD estimator provides a guarantee undemonstrated in other measures that error scales independently of DD.

Overall, we are aware of very few theoretical results that characterize how similarity measures behave when neurons and inputs are simultaneously subsampled. We focused on CKD because it is an exceptionally clean case with clear answers to this question. However, we ultimately hope that this paper will inspire similar investigations into other metrics.

The way the theoretical results are structured could benefit from further formalisation and clear separation into theorems and proofs.

We have revised the appendices for clarity and provided a guide to read the proof (Appendix A). Please let us know if there are particular sections or notation conventions that are confusing to you. We would be very grateful for specific suggestions that give us the opportunity to continue improving the manuscript.

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

This paper investigates the statistical reliability of neural representation comparisons under simultaneous stimulus and neuron subsampling, an important problem in computational neuroscience and deep learning interpretability. Focusing on Centered Kernel Distance (CKD), the authors develop a statistical framework for quantifying estimation uncertainty arising from both sources of subsampling. The key contributions include: (1) constructing an unbiased estimator of squared CKD using a multi-sample U-statistic; (2) deriving a signal-adaptive non-asymptotic variance bound with sampling dependence characterized by ε = 1/M + 1/N_X + 1/N_Y, without explicit dependence on ambient input dimension under the stated assumptions; (3) analyzing robustness to trial-to-trial noise; and (4) exploiting the Hilbert-space structure of CKD to enable metric repair and low-dimensional embedding for multiple neural representations. The authors evaluate their theoretical findings using synthetic random networks, trained deep neural networks, and real macaque visual cortex recordings.

Critical strengths
  1. Clear problem positioning and meaningful statistical contribution. The paper addresses an important limitation in neural representation comparison: the need to characterize estimation uncertainty arising simultaneously from stimulus and neuron subsampling. Both sampling dimensions are practically relevant in neuroscience and deep learning, where experimental resources and available observations are often limited. The unified statistical treatment provides a meaningful contribution to the literature.
  2. Solid theoretical framework and informative finite-sample guarantees. The construction of an unbiased estimator for squared CKD provides a principled statistical foundation. More importantly, the non-asymptotic variance analysis offers insights beyond conventional asymptotic consistency results. The signal-adaptive structure of the bound is particularly interesting, suggesting improved estimation accuracy when the underlying representations are close. The explicit dependence on stimulus and neuron sample sizes also provides useful guidance for experimental design.
  3. Useful connection between statistical estimation and representation geometry. The authors exploit the Hilbert-space structure of CKD to support geometrically consistent comparisons across multiple neural systems. The combination of pairwise estimation, positive-semidefinite Gram-matrix projection, and Euclidean embedding provides a coherent approach to multi-system representation analysis. This extends the practical usefulness of the statistical framework beyond individual pairwise comparisons.
  4. Empirical evaluation across complementary settings. The experiments cover random neural networks, trained artificial neural networks, and biological neural recordings. These complementary settings provide encouraging evidence for the predicted dependence of estimation variability on stimulus and neuron sample sizes. The inclusion of real macaque visual cortex data further strengthens the practical relevance of the work.
  5. Clear presentation and logical organization. The manuscript is well structured, progressing naturally from estimator construction and variance analysis to noise robustness and multi-system geometry. The theoretical motivation and main results are generally clearly explained.
Critical weaknesses
  1. The scope of the dimension-free guarantee requires further clarification. The dimension-free variance bound is one of the paper's central contributions. However, the absence of explicit ambient-dimensional dependence in the sampling rate does not necessarily imply that estimation difficulty is uniformly independent of dimension. The constants in the bound depend on response-scale and moment quantities, which may themselves vary with ambient dimension. In particular, Appendix B.4 introduces a uniformly bounded response-scale quantity, whereas Appendix G employs Gaussian inputs with unbounded support. For ReLU-type random features, the required uniform bound may be infinite without additional restrictions. This raises a question about whether the experimental setting directly satisfies the assumptions used in the theoretical analysis. Clarifying this relationship, or establishing whether weaker integrated moment conditions suffice, would strengthen the theoretical contribution.
  2. Experimental validation of dimension independence remains limited. Although the experiments provide useful qualitative evidence for the predicted variance dependence on stimulus and neuron sample sizes, the synthetic experiments cover a relatively limited range of ambient dimensions. Furthermore, varying network architectures or datasets may simultaneously change response scales and higher-order moments. Therefore, the experiments more directly support the predicted sampling-rate behavior than the stronger interpretation of dimension-independent estimation difficulty. Additional controlled experiments varying ambient dimension while maintaining comparable response statistics would make the empirical evidence more convincing.
  3. Limited robustness analysis under correlated neuronal responses and noise. The theoretical guarantees rely on independence assumptions that may not hold exactly in biological recordings. In practice, shared neural inputs and population-level fluctuations can induce correlations across neurons and trial-to-trial responses. Although the paper acknowledges correlated noise as a potential source of bias, it does not systematically quantify how estimation accuracy deteriorates when these assumptions are violated. A controlled sensitivity analysis would strengthen the practical applicability of the method.
  4. The statistical effects of metric repair are not fully characterized. The positive-semidefinite projection step guarantees that the repaired Gram matrix is no farther from the true positive-semidefinite Gram matrix in Frobenius norm than the original estimate. However, this guarantee does not automatically imply reduced variance or mean-squared error for every individual pairwise distance estimate. Moreover, the nonlinear projection may introduce estimation bias. The paper would benefit from explicitly distinguishing the global matrix-error guarantee from improvements in individual distance estimates and from quantifying the corresponding bias–variance trade-off.
  5. The trade-off between CKD and scale-invariant alternatives deserves deeper discussion. Unlike CKA, CKD is sensitive to differences in response amplitude. This may be desirable when absolute response magnitude carries meaningful biological information, but it may also complicate comparisons across systems with different firing-rate distributions or activation scales. For example, representations differing only by a multiplicative scaling factor can have identical CKA but nonzero CKD. More concrete guidance on the interpretation of such differences and possible normalization strategies would improve the practical usefulness of CKD.
Questions for authors
  1. Assumptions underlying the main variance theorem. The proof in Appendix B.4 appears to rely on a uniformly bounded response-scale quantity, while the random-network experiments in Appendix G use Gaussian inputs with unbounded support. Could the authors clarify whether these experiments satisfy the theorem's assumptions? If not, can the result be extended under weaker integrated moment conditions, and how would such an extension affect the dimension dependence of the constants?
  2. Empirical validation of dimension independence. Could the authors provide a more controlled experiment varying ambient dimension over a broader range while maintaining comparable response scales and moment conditions? This would help distinguish validation of the predicted sampling-rate dependence from validation of dimension-independent estimation difficulty.
  3. Robustness to correlated neural responses and noise. How sensitive is the proposed estimator to violations of independent neuron sampling and conditionally independent trial noise? Could the authors provide a simulation introducing controlled correlation strengths and quantify the resulting estimation bias and variance?
  4. Statistical consequences of metric repair. While positive-semidefinite projection guarantees non-increasing Frobenius error relative to the true Gram matrix, does it consistently improve the mean-squared error of individual CKD estimates? Could the authors quantify the bias–variance trade-off before and after projection under different subsampling settings?
  5. Practical guidance for selecting representation comparison metrics. Under which scientific scenarios should practitioners prefer CKD over alternatives such as CKA, RSA, or Procrustes distance? In particular, how should CKD be interpreted when comparing neural systems with substantially different response amplitudes, and how might normalization affect the proposed statistical guarantees?
2 comments

Thank you for your helpful comments.

The scope of the dimension-free guarantee requires further clarification.

This is a central question of our paper. In point (A) of our global response to reviewers, we describe how we refined our analysis to show that the constant factor is also independent of the input dimensionality (under weak assumptions). See Theorem 3.1 in our revised submission which characterizes the constant in terms of qq, a bound on the fourth moments of neural tuning curves.

This raises a question about whether the experimental setting directly satisfies the assumptions used in the theoretical analysis. Could the authors clarify whether these experiments satisfy the theorem's assumptions?

Our revised submission shows that, as you suggested, weaker conditions that do not assume boundedness are sufficient. See the bottom of page 5 in our revised manuscript for details.

Nonetheless, we have modified the random neural network experiments to avoid this confusion (Appendix J). We now include a normalization step so that inputs are uniformly distributed over the unit sphere. The boundedness of the input space guarantees that qq is finite. We recognize that there are possible extensions to account for full Gaussian inputs—as our prior results had suggested—but we focus on the core results on the rate as practical settings are covered by the current condition that inputs are bounded.

Experimental validation of dimension independence remains limited.

Could the authors provide a more controlled experiment varying ambient dimension over a broader range while maintaining comparable response scales and moment conditions?

Please see response (C) in the global response to all reviewers.

Our revised manuscript includes several additional experiments, including validation on random neural networks where the input dimensionality spans several orders of magnitude. Furthermore, natural images are high-dimensional with uncharacterized intrinsic structure. Yet, we observe the same scaling when comparing artificial networks with macaque visual cortex (new Appendix I) and when conditioning on individual image categories (new Appendix K).

Limited robustness analysis under correlated neuronal responses and noise.

You are correct in that handling noise correlations is important. We present an overview in response (D) on a new section of our proof accounting for this (Appendix E). Our U-statistic can be extended relatively simply to account for noise correlations, provided we have at least 2 presentations of the stimuli. Comparing across presentations is sufficient to account for noise correlations, fully debiases the CKD estimate, and the variance of this new estimator obeys a similar scaling law, with the rate ϵ=1NX+1NY+1M\epsilon = \frac{1}{N_X} + \frac{1}{N_Y} + \frac1M unchanged. For ease of presentation, we chose to keep the main body of the paper focused on the “standard” CKD estimator.

The statistical effects of metric repair are not fully characterized… this guarantee does not automatically imply reduced variance or mean-squared error for every individual pairwise distance estimate.

We thank the reviewer for this careful point. Because the original Gram matrix estimate is unbiased, the guarantee in eq. (18) implies that any bias introduced by the projection is more than offset by a reduction in variance, when errors are summed over the whole Gram matrix. We agree, however, that this is a guarantee about the matrix as a whole. It does not ensure that every individual entry, or every derived pairwise distance, is estimated more accurately. We have revised Section 3.4 to make this distinction more clear. Our original submission already noted that the metric repair step introduces bias.

The trade-off between CKD and scale-invariant alternatives deserves deeper discussion.

Under which scientific scenarios should practitioners prefer CKD over alternatives such as CKA, RSA, or Procrustes distance?

We comment on this concern generally in (B). CKD measures something different from CKA, RSA, and Procrustes, so they are complementary tools. We focus our paper on highlighting the statistical benefits of CKD: that unbiased estimators exist and we can rigorously prove things about how estimator variance scales with respect to both MM and NN simultaneously. Practitioners who work with limited and noisy experimental data and desire these theoretical guarantees should consider using CKD. On the other hand, we note in our limitations section, CKD is not scale-invariant. If this is desired, then practitioners would favor a different measure.

Ultimately, we hope that this paper will inspire new investigations into the statistical estimability of representational similarity metrics. As noted in our paper, we are aware of very few results that cover the case where neurons and inputs are simultaneously subsampled.

Thank you for the follow-up. I find the authors’ response reasonable: the added Euclidean comparisons and clarifications address several of my concerns, and the theoretical proofs, revisions, appendices, and new experiments largely resolve the reviewer comments. Minor issues remain—some extended analyses (e.g., full validation for fully Gaussian inputs) are only discussed verbally without complete experimental evidence. I therefore maintain my original rating of 3 (Weak acceptance).

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

The paper considers the estimates of a metric-based measure of dependence of processes related to centered kernel alignment (and representational similarity analysis) with linear kernels that is unbiased. Theoretical bounds on the error as a function of the number of neurons (sampling points of the processes) and the experimental conditions.

Critical strengths

The paper is clear and easy to read. The result's are illustrative. The theoretical results are clear.

Critical weaknesses

While the paper positions CKD as an alternative to CKA, which does have an unbiased estimate, it is not clear to me what CKD offers compared to HSIC (line 1443 'it is no surprise that we demonstrate similar qualitative and quantitative results for HSIC as in CKD')? As HSIC the inner-product corresponding to CKD's squared norm, one can seemingly easily generate an L2 metric from HSIC and conduct similar analysis.

The discussion of unbiased HSCI versus unbiased CKA should cite "Partial Distance Correlation with Methods for Dissimilarities" by Gabor J. Szekely, Maria L. Rizzo.

Questions for authors

What am I missing in terms of the what CKD can do that HSIC couldn't do? From Figure 8 it appears that HSIC is better when NX≠NYN_X\neq N_Y.

I don't find the conclusion on line 1475 very satisfying: 'Hence, the difference in scale across multiple neural regions and models may be important in understanding multi-system relationships.' Especially since it is contradicted with discussion on line 1493: 'We attempt to isolate this effect by normalizing the scale of activations to have unit norm, and then finding the variance of similarity estimates on the normalized activations. This suggests that removing the effect of scaling can remove the overdependence of variance on one neural system over the other. In a neuroscience setting, where the constants cannot be well estimated until after the experiment, this improves a priori optimization of experimental parameters.'

Minor typo: line 472 "providea " -> "provide a"

1 comment

Thank you for your helpful comments.

While the paper positions CKD as an alternative to CKA, which does have an unbiased estimate, it is not clear to me what CKD offers compared to HSIC? As HSIC the inner-product corresponding to CKD's squared norm, one can seemingly easily generate an L2 metric from HSIC and conduct similar analysis.

This is correct: CKD is the L2 metric formed from HSIC. They have very similar properties. The main point of our paper is to analyze the statistical properties of CKD and HSIC when MM and NN are both subsampled. To our knowledge, no one has done this for either CKD or HSIC in the past.

Null hypothesis testing is one concrete reason someone may be interested in using CKD rather than HSIC. Suppose we record neural activity in two individuals and we want to test the null hypothesis that their representational geometry is equivalent up to orthogonal transformations and translations. The null hypothesis is that CKD = 0, but HSIC has no fixed value under the null.

A second situation where CKD may be preferred over HSIC is any analysis that requires a metric, such as clustering, nearest-neighbor methods (Section 4.3), or arguments relying on the triangle inequality (Sections 3.3–3.4).

I don't find the conclusion on line 1475 very satisfying [...] Especially since it is contradicted with discussion on line 1493.

We agree. It was a mistake to include these preliminary experiments as supplemental results in Appendix G. We do not believe this result matters for the central message of the paper, so we have removed them and abbreviated the supplemental figure to be clearer and focused on CKD.

The discussion of unbiased HSIC versus unbiased CKA should cite "Partial Distance Correlation with Methods for Dissimilarities" by Gabor J. Szekely, Maria L. Rizzo.

Thank you for the catch! We have integrated the paper from Szekely and Rizzo and highlight how we build on the work—namely, simultaneous debiasing for both number of stimuli presented (which is in Szekely and Rizzo) and the number of neurons recorded (which is of importance in neuroscientific settings).

Comments on the paper

1 comment
AuthorsOpenReview ↗

Global Response to Common Questions

Thank you to all the reviewers for their helpful comments. We address the four main concerns below and respond to specific comments in reviewer threads.

(A) How does the bound relate to dimensionality in practice?

A key result is that the variance of the CKD estimator is at most C(1/M+1/N)C (1/M + 1/N), where CC does not depend on the number of sampled neurons NN or inputs MM. When CKD=0\mathrm{CKD} = 0, the variance decays even faster at a rate proportional to (1/M+1/N)2(1/M + 1/N)^2. Notably, these rates do not deteriorate as the input dimension DD grows. This contrasts with the "curse of dimensionality," under which the error would decay like (1/M+1/N)1/D(1/M + 1/N)^{1/D}, requiring exponentially more neurons and inputs to compensate for an increase in DD, as in many high-dimensional estimation problems.

Reviewers rightly asked whether DD affects the constant CC. We now write this constant explicitly in terms of qq, a bound on the fourth moment of the tuning curves (revised Theorem 3.1 and Section C.4): q=max⁡(sup⁡uEf[(f(u)−fˉ)4], sup⁡uEg[(g(u)−gˉ)4])q = \max \left ( \sup_u \mathbb{E}_f\big[(f(u) - \bar f)^4\big], \ \sup_u \mathbb{E}_g\big[(g(u) - \bar g)^4\big] \right ) where f,gf, g are randomly sampled tuning curves. The remaining constant is absolute and does not depend on any experimental factors.

Does qq grow with DD? Weak assumptions rule this out. Biological firing rates are bounded: rescaling responses to [0,1][0, 1] (minimal to maximal firing rate) gives q≤1q \leq 1 regardless of the input dimension or distribution. The revised paper now discusses two further conditions that do not require boundedness (see page 5).

Reviewer EgXU noted that our random-network experiments (Appendix J) used Gaussian inputs and ReLU activations, which technically fall outside these assumptions (the supremum over u can make qq infinite). First, it is encouraging that the theory nonetheless fits the empirical scaling well, and indeed we are confident that a similar bound can be proved rigorously for Gaussian inputs. Second, as discussed in the revised paper, adding a normalization layer to the network (as is commonly done in practice) is sufficient for the theory as stated to rigorously apply.

(B) How does CKD compare to other similarity measures (e.g. HSIC, CKA, Procrustes)?

While CKD has some advantages (e.g. CKA and Procrustes admit no unbiased estimators), our main goal is to study an under-appreciated statistical problem: how accurately can representational similarity be estimated when MM and NN are simultaneously subsampled? This is difficult in general; our preliminary analysis of the Procrustes distance suggests a much more complicated picture.

We focus on CKD because the analysis is exceptionally clean, and we have revised the Introduction to clarify this. We do not claim CKD is always superior, only that it is unusually easy to estimate from limited data. We also agree with Klabunde et al. (2025) that interpreting several measures together is useful (e.g. large CKD but small CKA suggests that scale drives the dissimilarity).

(C) Can you verify these results in more diverse settings?

Our core contribution is theoretical, and our experiments are meant to illustrate and validate the bounds rather than survey all settings. Nonetheless, we have added comparisons between systems with very different architectures and response scales: artificial networks versus macaque visual cortex (new Appendix I), and all pairs of macaque regions within and across subjects (Appendix H). We also expanded the random-network experiment (Fig. 1) to vary the input dimension over three orders of magnitude. Because the macaque image set is fixed, we instead condition on different image categories (new Appendix K). In every case, we observe the evenly spaced, L-shaped level curves predicted by our theory. Our random-network experiments verify the theory where the input distribution can be explicitly controlled, while natural images provide the standard high-dimensional input space of practical interest, one whose structure is largely uncharacterized.

(D) Handling correlated noise

Prompted by Reviewer EgXU, we added Appendix E, which extends our theory to noise that is correlated across neurons, a case of practical importance to experimentalists. The standard estimator becomes biased in this setting, but a natural extension using two repeated trials per stimulus recovers an unbiased U-statistic. Its variance retains the same rate, 1/M+1/NX+1/NY1/M + 1/N_X + 1/N_Y; the constants change but remain dimension-independent.

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

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