Differentiable Optimization of Similarity Scores Between Models and Brains

The claim between lines 267-270 is not detailed enough in the paper. The authors mention testing a hypothesis, but they simply state "we tested this hypothesis ... but this did not change the results" without further context. The results for that is not shared in the paper. Including these results in the appendix would enhance the paper's clarity.

Thanks for your suggestion. We added a new figure to support the claim (Supplementary Figure S3).

The joint optimization method in Section 4.4 and Appendix C.3 is unclear, as the details on experiments in this section are sparse. I think the paper can benefit from more details.

We added more details to Appendix C.3 and a new figure to explain the procedure (Supplementary Figure S4).

The term "Proof" in Appendix C.2 and Section 4.3 seems a bit strong without an accompanying theorem or lemma, especially since the assumption is only noted in the appendix. Revising the word "proof" might be appropriate.

We agree the term “proof” may be considered too strong here. We revised the title for this section.

What is the reason for using ridge regularization in the definition (in the numerator in line 208)? In that case, the numerator will not be the residual square and I do not see the rationale behind this.

Thanks for pointing this out. This was a typo in the manuscript, which is now corrected. The ridge regularization is only used to find the best linear mapping and not to evaluate it with $R^2$.

Why is line 512 specifically bold-faced, but not the next one? According to Figure 7, the relation that high value of angular Procrustes implies a high score for linear regression appears more established compared to the relation of angular Procrustes and CKA scores.

There are commonly used versions of both angular Procrustes and CKA and so the bolded statement is of general interest. We did not bold the statement concerning linear regression as we felt there are too many variations used in practice. Our analyses of linear regression illustrate the potential problems with even cross-validated and regularized versions of this similarity measure but we encourage practitioners to apply our method to their unique setup and choices for cross-validation, regularization, and dataset.

In light of these clarifications, would you consider increasing your score for our paper? If not, could you let us know any additional changes you would like to see in order for this work to be accepted?

Thank you for your assessment and suggestions. They were quite useful in revising the paper to better communicate the goals of our study. We address your concerns/suggestions below.

One premise stated in the abstract is that the paper offers a theoretical analysis to show how similarity metrics are dependent on the principal components of the dataset. However, this premise appears weak to me because: (i) it does not seem to be a novel analysis but rather a predictable outcome of using Frobenius and nuclear norms in metrics CKA and NBS; (ii) the assumption is introduced without sufficient context and is unclear; and (iii) the assumption is said to hold with large sample sizes, validated in a numerical experiment, yet I did not see a clear mention of dataset sizes in the paper. Including more details on the datasets and clarifying the underlying assumptions would be helpful.

It is true that the quadratic and linear dependence of CKA and NBS sounds intuitive from the difference between the Frobenius and nuclear norm. However, it is not straightforward to relate it to our empirical results showing the dependence of the scores to the principal components of one of the two datasets being compared. In particular, the numerator in the matrix norm formulation of CKA and NBS is the norm of the product $X^T Y$, meaning it is the sum of the singular values of $X^T Y$ (squared for CKA). However, we want to analyze the dependence with respect to the singular values of only one of the two matrices. In our analysis, we show how to do that using the formulation of CKA in terms of a weighted sum of inner products between left singular vectors from Kornblith et al. (2019). NBS doesn’t have such an alternative formulation but we show that with our assumptions on the perturbation on $X$, we can derive a similar expression. So even though the results are expected, our contribution is to explicitly show the dependence on the principal components of one of the two datasets and to quantitatively validate it on neural datasets.

Thanks for your suggestions to clarify this section. We added additional details to the revised paper.

The introduction and related work section suggest that prior research lacks practical guidance on metric selection given a dataset. However, I am uncertain if this paper proposes such a guidance. Suppose I have a neural dataset and model representations to compare. How should I choose the most suitable metric based on this paper? My understanding is that I can optimize a synthetic dataset using various metrics, observe the optimization dynamics, and then choose a similarity metric for and . Is that correct? I am asking this since I am struggling to understand how this paper offers a method for selecting an appropriate metric for a given task, if indeed it is promising.

Given the findings, the main takeaway seems to be that similarity metrics are highly sensitive to different data aspects and may be mutually independent. How, then, would the authors suggest selecting the best similarity metric for a given dataset?

We have updated the abstract and main text to hopefully remove the confusion about our motivations. To clarify, the specific questions that motivated this paper are:

• What constitutes a “good” score? See Figure 3.
• What drives a high similarity score? See Figures 4, 5 and the analytic results in section 4.3 as well as Figure 6.
• Does a high similarity score for one measure imply a high score for the others? See Figure 7.

At this point in time we do not wholeheartedly recommend any of the current similarity measures without some reservations. That being said, not all similarity measures have the same drawbacks and we see angular Procrustes as a reasonable default. But see caveats in, for example, Ostrow et al. NeurIPS 2023 and Khosla & Williams UniReps 2023.

In terms of practical guidance, we advise to not just report similarity scores as our findings show that scores by themselves are hard to interpret and their meaning can greatly vary depending on the details of the dataset and the similarity measure. We argue that similarity scores require further interpretation before making any claim based on them. Here we show two concrete ways of doing so, that incorporate the context of the dataset and similarity measure, by optimizing synthetic datasets to determine:

1. How strongly task variables are encoded in order to reach the score (Figure 3).
2. How many PCs need to be captured in order to reach the score (Figures 4 and 5).

Thank you for your positive assessment and suggestions. We address your concerns/suggestions below.

Most discussions of similarity measures have focused on the special case where the similarity score is 1 (for example, what happens when response profiles X and Y are equivalent under some similarity measure such as CKA), so discussion of how intermediate values behave for different measures is a good contribution, especially since we are often dealing with intermediate levels of similarity in practice, e.g. when comparing models to brain data.

We completely agree. This is a great comment and a point we now emphasize in the paper.

In this paper, the regularization level for Ridge Regression is fixed to some chosen level (and the authors do consider results for different fixed levels of lambda). However it seems to me that, because of the probability of overfitting in high dimensional data settings, it is generally preferable to tune the ridge penalty through some cross-validation method (searching over a range of possible alpha values) such as k-fold so as to select the lambda that will maximize generalization performance on the chosen data.

Tuning the ridge penalty with cross-validation (CV) is indeed commonly used to select a ridge regression metric. The method we propose is complementary and addresses a different question. Once we have a given similarity measure (e.g. ridge regression with a specific value of lambda obtained with CV), how can we interpret and validate the scores it produces? In particular, is it possible to reach a high similarity score without capturing the relevant task variables or capturing only the first PCs?

Linear regression is only done in one direction, from the model to the reference neural dataset. This is good to know about, but it also would be useful to see what happens when linear regression is done in both directions

We focused on illustrating our method on commonly used similarity measures, and linear regression as a metric is mostly used in one direction. Our goal is to demonstrate the usefulness of our approach and give insights on commonly used similarity measures. We additionally provide tools to the community with, for example, open source code, to analyze and better understand present and future similarity measures.

RSA is also widely used as a similarity measure, but is not mentioned at all in the paper. It would be very useful if the paper included an analysis of RSA, especially since RSA is mathematically very closely related to linear CKA, but the formulas for RSA and linear CKA are not identical. It would be good to therefore have an analysis of the relationship between these two methods, as well as empirical simulations showing how the intermediate values compare for RSA and CKA (just as the authors did for other methods, like comparing CKA to NBS).

RSA is indeed widely used and interesting to consider as there are many existing variants. We have now included a new figure comparing common variants of RSA with CKA (Supplementary Figure S5). In particular, our new results confirm the equivalence between RSA with Euclidean RDMs and centered cosine similarity (see Williams UniReps 2024). However, they also show that other variations of RSA are almost independent of CKA, and that they might not even be equivalent to each other (as illustrated by comparing RSA with Euclidean RDMs using either cosine similarity or correlation to compare the RDMs).

Thank you for your helpful feedback.

This work is of expository nature, so by this nature its advancement in methodology and theory is less significant.

We noticed that your review primarily mentions the expository nature of our work as a reason for its lower score, but it does not provide further elaboration. To help us better understand and address your evaluation, could you please clarify which aspects of our work influenced your assessment?

What guidance will you provide to scientists in choosing a suitable similarity measure?

How will this work have impact in the way that similarity scores are applied in practice?

We have found that CKA can achieve a high score on datasets that fail to encode task relevant information so we suggest that researchers do not rely solely on this commonly used similarity measure when making claims about model-data similarity. In addition, regardless of what similarity measure is used, we encourage researchers to accompany their reported scores with an analysis like the one in Figure 3 so readers know if the scores are “good” or not, i.e. if it is possible to obtain these scores without encoding task relevant variables. As we’ve demonstrated, a good value for a score isn’t fixed but depends on the similarity measure and dataset so this analysis is something that should be done every time these scores are reported to account for the unique aspects of a particular study.

In addition to this practical guidance for interpreting similarity scores, we also demonstrate a new tool for uncovering what drives high similarity scores. This has exposed shortcomings in some commonly used similarity measures which we see as a necessary first step in improving them! As these new similarity measures are developed it will be important to understand what drives them and our method can play an informative role here.

Given these clarifications, would you consider raising your score for our paper?

Thank you for your positive assessment and helpful comments. We have updated the paper based on your feedback.

Below are several related comments, along with our answers.

Ridge-Regression seems to be the most widely-used measure in the field although most of the comparisons focus on CKA vs Angular Procrustes. Would be nice to see more commentary on this especially in Figure 7 where it seems independent from angular Procrustes.

In the case of unregularized, uncross-validated linear regression compared to Angular Procrustes (Figure 7), our results are consistent with the invariance properties of these metrics. Angular Procrustes is invariant under orthogonal transformations, which is more strict than linear regression, which is invariant under invertible linear transformations. So it is expected that a high Angular Procrustes score implies a high linear regression score but not the other way around. Concerning regularized and cross-validated linear regression, the interpretation of our findings is less straightforward. In general, our method is designed to be widely applicable, i.e. to any differentiable metrics, but doesn’t replace careful theoretical work that studies differences between specific metrics. However, even in cases where there is an apparently straightforward mathematical relationship between canonical versions of two similarity measures, in practice, we find that implementation level details matter and change the allowable ranges of both similarity scores.

For example, our additional results with different variants of representational similarity analysis (RSA), as shown in appendix C.3, illustrate that a small difference in the implementation details can make two metrics independent from each other.

From the start of the paper it seems like it will answer the question: "What metrics should guide the development of more realistic models of the brain?" I would like the authors to comment more directly on what should be done.

We see the opening question from the abstract (referenced in your question) as one of the motivations for the field. However, at this point in time we do not wholeheartedly recommend any of the current similarity measures without some reservations. That being said, not all similarity measures have the same drawbacks and we see angular Procrustes as a reasonable default. But see caveats in, for example, Ostrow et al. NeurIPS 2023 and Khosla & Williams UniReps 2023.

We advise to not just report similarity scores as our findings show that scores by themselves are hard to interpret and their meaning can greatly vary depending on the details of the dataset and the similarity measure. We argue that similarity scores require further interpretation before making any claim based on them. Here we show two concrete ways of doing so, that incorporate the context of the dataset and similarity measure, by optimizing synthetic datasets to determine:

1. How strongly task variables are encoded in order to reach the score (Figure 3).
2. How many PCs need to be captured in order to reach the score (Figures 4 and 5).

We have removed the initial opening question from the abstract and updated the paper to hopefully alleviate the confusion about what we are trying to answer. Here are the specific questions that motivated this paper:

• What constitutes a “good” score? See Figure 3.
• What drives a high similarity score? See Figures 4, 5 and the analytic results in section 4.3 as well as Figure 6.
• Does a high similarity score for one measure imply a high score for the others? See Figure 7.

The datasets are all electrophysiology datasets whereas comparisons are often also done with fMRI datasets, will these results still hold for these datasets? Especially with the difference in sampling between the methods.

Since we find that our results on interpreting similarity scores can greatly vary depending on the dataset, we expect that they will be dataset-specific for fMRI data too. That's why we recommend practitioners to apply our analyses on their own datasets, and we provide open source code to facilitate it.

We are interested in seeing our method applied to fMRI, and also calcium imaging datasets as well, in follow-up work. We expect these analyses will also serve to highlight some potentially problematic cross-validation practices in model-data comparisons with fMRI data, for example, whether train-test splits are obtained by randomly shuffling the data or if contiguous blocks are used for testing. In this paper we wanted to show that there exists variability in good scores even across datasets collected using the same method, namely the five electrophysiology datasets that we analyzed.