When do measured representational distances reflect the neural representational geometry?

Reviewer #1 (Public review):

Summary:

This work presents a formalism for the relationship between neural signals and pooled signals (e.g., voxel estimates in fMRI) and explores why correlation-based and mean-removed Euclidean RDMs perform well in practice. The key assumption is that the pooled estimates are weighted averages, with i.i.d. non-negative weights. Two sets of simulations are used to support the theoretical findings: one based on fully simulated neural data and another that reverse-engineers neural data from an RDM estimated from real macaque data. The authors also discuss limitations of their simulations, particularly concerning the i.i.d. assumption of the weights.

Strengths:

The strengths of this work include its mathematical rigor and the clear connection that is drawn between the derivations and empirical observations. The simulations were well-designed and easy to follow. One small suggestion: a brief explanation of what is meant by "sparse" in Figure 3 would help orient the reader without requiring them to jump ahead to the methods. Overall, I found the work engaging and insightful.

Weaknesses:

Although I appreciate the effort to explore *why* certain dissimilarity measures perform well, it wasn't clear how these findings would inform the practical choices of researchers conducting RDM-based analyses. Many researchers likely already use correlation-based or mean-removed Euclidean distance measures, given their popularity. In that case, how do these results provide additional value or guidance beyond current practice?

Another aspect that could benefit from further clarification is the core assumption underlying the work - that channel-based activity reflects a non-negative weighted average of neural activity. Is this widely accepted as the most plausible model, or are there alternative relationships that researchers should consider? While this may seem intuitive, it's not something I would expect all readers to be familiar with, and only a single reference was provided to support it (which I unfortunately didn't have time to read). That said, I did appreciate the discussion of the i.i.d. assumption in the discussion section. Can more be said to educate researchers as to when the i.i.d. assumption might be violated?

I didn't find the "Simulations based on neural data" section added much, and it risks being misinterpreted. The main difference here is that neural data were reverse-engineered from a macaque RDM and then used in simulations similar to those in the previous section. What is the added value of using a real RDM to generate simulated data? Were the earlier simulations lacking in some way? There's also a risk of readers mistakenly inferring that human dissimilarities have been reconstructed from macaque data, an assumption that goes beyond the paper's core message, which focuses on linking neural and channel-based signals from the *same* source. If this section is retained, the motivation should be clarified, and the implied parallel in Figure 6, between the human data and simulated data, should be reconsidered.

Reviewer #2 (Public review):

Summary:

The paper is a methodological contribution to multivariate pattern analysis and, in particular, the analysis of representational geometry via pairwise representational distances, sometimes called representational dissimilarity analysis (RDA). The authors investigate through theoretical analysis and simulations how true representational distances (defined on the neural level) give rise to representational distances estimated from neurophysiological data, including fMRI and cell recordings. They demonstrate that, due to the way measurements sample neural activity, the activity common to all sampled neurons can be amplified in the representational geometry derived from these measurements, and therefore, an empirical representational geometry may deviate substantially from the true representational geometry. The authors propose to modify the obtained representational structure by removing the dimension corresponding to that common activity, and argue that such a removal of a single dimension does not relevantly affect the representational structure, again underpinned by mathematical analysis and simulation.

Importance:

The paper may at first sight be tackling a specific problem within a specific subfield of cognitive neuroscience methods. However, understanding the structure of representations is a fundamental goal of cognitive psychology and cognitive neuroscience, and the fact that methods of representational geometry are not yet routinely used by the wider community may at least partially be due to uncertainty regarding the reliability of these methods. This paper is an important step towards clarifying and improving reliability, and therefore towards more widespread adoption of representational geometry methods.

Strengths:

The paper makes its argument generally well, relying on previous work by the authors as well as others to support assumptions about neural sampling by neurophysiological measurements. Their main points are underpinned by both detailed mathematical analysis and simulations, and the latter also produces intuitively accessible illustrations of the authors' argument. The authors discuss in detail under which exact circumstances common neural activity distorts the representational geometry, and therefore, when exactly the removal of the common dimension is necessary to minimize that distortion.

Weaknesses:

(1) The argument around the Johnson-Lindenstrauss lemma on pages 5 & 6 is somewhat confused, and also not really convincing.

First, the correct reference for the lemma seems to be not [20] = Johnson et al. (1986), but Johnson & Lindenstrauss (1984). Moreover, as far as I can tell, Johnson et al. (1986) do not discuss random projections, and while they play a role in Johnson & Lindenstrauss (1984), that is only as a proof device. The paper text suggests that the lemma itself is probabilistic, while actually it is a statement of existence.

Second, the authors correctly state that the lemma implies that "the number of measurement channels required for a good approximation does not depend on the number of neurons and grows only logarithmically with the number of stimuli", but it is not clear what the relevance of this statement for this paper is, considering that distances between N points can be exactly preserved within an N − 1 dimensional subspace, irrespective of the number of dimensions of the original space, and since in cognitive neuroscience the number of measurement channels is usually (much) larger than the number of experimental stimuli.

The actually centrally important statement is not the Johnson-Lindenstrauss lemma, but one about the metric-preserving properties of random projections with zero-mean weights. It is this statement that needs to be backed up by the correct references, which, as far as I can tell, are neither the cited Johnson et al. (1986) nor even Johnson & Lindenstrauss (1984) for the lemma.

(2) The detailed mathematical analyses and simulations focus on the effect of non-zero-mean sampling weights, and that is justified by the result that such sampling leads to a distorted representational geometry. However, there is another assumption which seems to be used almost everywhere in both mathematical analyses and simulations, and which I suspect may have a relevant effect on the observed representational geometry: statistical independence between weights. In particular, in fMRI, the existence of a naturally limited spatial resolution (due to MRI technology or vasculature) makes it unlikely that the weights with which a given neuron affects different voxels are independent.

Reviewer #3 (Public review):

Summary:

This manuscript investigates the conditions under which representational distances estimated from brain-activity measurements accurately mirror the true geometry of the underlying neural representations. Using a theoretical framework and simulations, the authors show that (i) random weighted sampling of individual neurons preserves representational distances; (ii) the non-negative pooling characteristic of fMRI stretches the geometry along the population-mean dimension; and (iii) subtracting the across-channel mean from each activity pattern removes this distortion, explaining the well-known success of correlation-based RSA. They further argue that a mean-centred, squared Euclidean (or Mahalanobis) distance retains this corrective benefit while avoiding some pitfalls of variance normalisation.

Strengths:

(1) Theoretical clarity and novelty:
The paper offers an elegant and convincing proof of how linear measurement models affect representational geometry and pinpoints the specific condition (non-zero-mean sampling weights) under which voxel pooling introduces a systematic bias. This quantitative explanation of why mean removal is effective in RSA is new and valuable.

(2) Simulations:
Experiments on both synthetic high-dimensional fMRI data and macaque-IT-inspired embeddings corroborate the mathematics, providing practical insights into the theoretical reasoning outlined by the authors.

(3) Actionable recommendations:
The work summarises the results into clear guidelines: random single-unit sampling is "safe" (the estimated geometry is undistorted); fMRI voxel data with unstructured or single-scale codes should be mean-centred; and multi-scale cortical maps require explicit forward modelling. These guidelines are clear, and useful for future research.

Weaknesses:

(1) Simplistic assumptions:
The assumption that measurement-channel weights are drawn independently and identically distributed (i.i.d.) from a univariate distribution is a significant idealisation for fMRI data. Voxels have spatially structured responses (and noise), meaning they do not sample neurons with i.i.d. weights. The extent to which the conclusions (especially the "exact recovery" with mean centring) hold when this assumption is violated needs more discussion. While the paper states that the non-negative IWLCS model is a best-case scenario, the implications of deviations from this best case could be elaborated.

(2) Random-subpopulation model for electrophysiology:
Similarly, the "random subpopulation model" is presented as an idealisation of single-cell recordings. In reality, electrophysiological sampling is often biased (e.g., towards larger, more active neurons or neurons in accessible locations). The paper acknowledges biased sampling as a challenge that requires separate modelling, but the gap between this idealised model and actual practice should be highlighted more strongly when interpreting the optimistic results.

(3) Noise as an "orthogonal issue":
The theoretical derivations largely ignore measurement noise, treating it as an orthogonal problem solvable by cross-validation. Although bias from noise is a well-known problem, interactions between noise and sampling-induced distortions (especially the down-scaling of orthogonal dimensions) could complicate the picture. For instance, if a dimension is already heavily down-scaled by averaging, it might become more susceptible to being obscured by noise. Addressing or highlighting these points more explicitly would make the limitations of this theoretical framework more transparent.

(4) Simulation parameters and generalizability:
The random ground-truth geometries were generated from a Gaussian mixture in 5-D and then embedded into 1,024-D, with ≈25 % of the variance coming from the mean dimension. The sensitivity of the findings to these specific parameters (initial dimensionality, geometry complexity, proportion of mean variance, and sample size) could be discussed. How would the results change if the true neural geometry had a much higher or lower intrinsic dimensionality, or if the population-mean component were substantially smaller or larger? If the authors' claims are to generalise, more scenarios should be considered.

(5) Mean addition to the neural-data simulation:
In simulations based on neural data from Kiani et al., a random mean was added to each pattern to introduce variation along the mean dimension. This was necessary because the original patterns had identical mean activation. However, the procedure might oversimplify how population means vary naturally and could influence the conclusions, particularly regarding the impact of the population-mean dimension. While precisely modelling how the mean varies across conditions is beyond the manuscript's scope, this point should be stated and discussed more clearly.

(6) Effect of mean removal on representational geometry:
As noted, the benefits of mean removal hold "under ideal conditions". Real data often violates these assumptions. A critical reader might ask: What if conditions differ in overall activation and in more complex ways (e.g., differing correlation structures across neurons)? Is it always desirable to remove population-mean differences? For example, if a stimulus truly causes a global increase in firing across the entire population (perhaps reflecting arousal or salience), subtracting the mean would treat this genuine effect as a nuisance and eliminate it from the geometry. Prior literature has cautioned that one should interpret RSA results after demeaning carefully. For instance, Ramírez (2017) dubbed this problem "representational confusion", showing that subtracting the mean pattern can change the relationships between conditions in non-intuitive ways. These potential issues and previous results should be discussed and properly referenced by the authors.

Appraisal, Impact, and Utility:

The authors set out to identify principled conditions under which measured representational distances faithfully reflect the underlying neural geometry and to provide practical guidance for RSA across modalities. Overall, I believe they achieved their goals. Theoretical derivations identify the bias-inducing factors in linear measurement models, and the simulations verify the analytic claims, demonstrating that mean-pattern subtraction can indeed correct some mean-related geometric distortions. These conclusions strongly rely on idealised assumptions (e.g., i.i.d. sampling weights and negligible noise), but the manuscript is explicit about them, and the reasoning from evidence to claim is sound. A deeper exploration of how robust each conclusion is to violations of these assumptions, particularly correlated voxel weights and realistic noise, would make the argument even stronger.

Beyond their immediate aims, the authors offer contributions likely to shape future work. Its influence is likely to influence both analysis decisions and the design of future studies exploring the geometry of brain representations. By clarifying why correlation-based RSA seems to work so robustly, they help demystify a practice that has so far been adopted heuristically. Their proposal to adopt mean-centred Euclidean or Mahalanobis distances promises a straightforward alternative that better aligns representational geometry with decoding-based interpretations.

In sum, I see this manuscript as a significant and insightful contribution to the field. The theoretical work clarifying the impact of sampling schemes and the role of mean removal is highly valuable. However, the identified concerns, primarily regarding the idealized nature of the models (especially for fMRI), the treatment of noise, and the need for more nuanced claims, suggest that some revisions are necessary. Addressing these points would substantially strengthen the paper's conclusions and enhance its impact on the neuroscience community by ensuring the proposed methods are robustly understood and appropriately applied in real-world research settings.