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Under review as a conference paper at ICLR 2027

Towards Interpretable Brain-Region Similarity Benchmarks

Abstract

Comparing Deep Neural Network (DNN) representations to neural activity is a common way of evaluating computational models of the brain. Yet, design choices such as the alignment measure critically influence conclusions drawn from such benchmarks, which is a problem if we have no ground truth to validate a benchmark against. We propose to first sanity-check whether the benchmark is sensitive to the axes that differentiate the brain region under study, using region matching as a diagnostic test, and to require feature specificity of the similarity measure if the goal is to infer functional or mechanistic similarity from benchmark scores. We evaluate 10 similarity measures on both criteria using two large-scale fMRI datasets, the Natural Scenes Dataset and BOLD Moments. We find that region matching performance varies substantially by brain region and dataset. Region matching exposes preprocessing and measure implementation choices that degrade measure sensitivity. For example, applying PCA impairs performance of some measures and using Pearson-correlation distance reduces matching accuracy with RSA. Further, the test surfaces that region identification on fMRI data strongly depends on the univariate signal component, a component that has questionable relevance for identifying functional similarity to DNNs. Also, many commonly used measures lack feature specificity: They cannot distinguish a region from overcomplete supersets or incomplete subsets of the region. We recommend region matching as a sanity check before interpreting brain-DNN similarity scores, and to test for feature specificity when searching for precise model–region matches.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Brain-DNN similarity benchmark, alignment, similarity measure

Reviews

Among:
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1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_iCj2OpenReview ↗
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4
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Paper summary

This paper looks at two 'sanity-check' measures to help validate similarity metrics when it comes to interpreting brain-DNN model alignment. The two features are region-matching and feature specificity. The authors show that region-matching exposes a varying set of factors that can have a dramatic impact across benchmarks, and therefore becomes a primary focus to help serve as a base from which further analyses and conclusions can be made. In other cases, other metrics would give artificially high scores while the region-matching baseline is low, showing an artificial inflation of performance that the region-matching metric would surface.

I like papers that take aim at consolidating and applying a scientific battering ram to preconceived notions and which try to reinforce the interpretations many papers claim to make on a much more shaky ground. Many papers try to do this in pieces, with either too large and incomplete goals, or really specific claims that don't directly affect a lot of the research. This paper finds that middle-ground, I feel, in being only large enough to have good analyses contained within it and for it to tell a coherent story without overcomplicating the issue.

The submitted paper also has a nice overview of the literature. I thought I spotted a few gaps sometimes, but when searching for the principal authors, I did find the citations in a related section, so I am satisfied with that aspect. I also appreciated the (brutal) honesty of the limitations section, which increases my confidence in the scientific considerations of the authors and the overall submission.

I think it might be a bit of a stretch to imagine a world where all brain-DNN similarity results have an expected region-matching/feature-specificity result to be done as a baseline, but if not, I can imagine it being a diagnostic test as to whether something "unexpected" might be going on in some other spurious analysis. I think a lot of work went into thinking about this and it's on-topic for the themes of ICLR over the past few years and would be well-received by many of the participants.

Critical strengths

The main strengths of the paper is the presentation of a suite of alignment metric performances in relation to the proposed sanity checks. Scientists working in the field have something tangible to consult and look at varying metrics across varying dimensions. It will cause pause for thought, consideration on preprocessing methods, extra testing, relying not just on single pieces of evidence to make strong (incorrect) conclusions. It also brings together a lot of the recently used methods critiquing the often (bad, IMHO) practice of just fishing for high-alignment scores and making faulty post-hoc deductions about what brain-model alignment actually means.

It's a dense piece of work and I was originally quite irritated by the length of the supplementary material (almost 6 times the length of the main submission) and obviously I couldn't give it the attention it deserved as I only have scarce review time and I budgeted for about 10-ish pages of supplementary material for each paper. Most of the titles I did scan, though, did seem to be more in terms of completeness and carefully stating some assumptions and I could understand a bit better why the authors felt this was necessary.

Critical weaknesses

When such papers aim to showcase a better method and identify how other methods can be unreliable, it's usually very informative to show how previous published research has been incorrect and to help us course correct a bit better in identifying any spurious conclusions from faulty analyses. A great way for this submission to solidify its relevance and applicability would be to identify 2+ examples where region-matching, applied to a previous analysis, shows that previous results do not hold and that these sanity benchmarks would have stopped the analysis from preceding. I can appreciate it's difficult to 'call-out' other papers and directly target an analysis and claim it's based on shaky principles, but this is the goal of science and my worry is that this trend is allowing incorrect conclusions based on shaky analyses to permeate our field and it's becoming more and more difficult to separate out the signal from the noise.

You had a great chance here to directly show how, had your method been applied to previous works, that it would have raised a red flag earlier in the process. Also, it would give us a direction for which styles of analyses (specific metrics etc.) were being used in research that should come under more scrutiny (by not passing the sanity checks you propose). It's a bit of an oversight to not include something about this in the paper to strengthen the point I feel the authors wanted to make. There's a tiny bit of this, with Thobani and Finzi papers, but it's weak and stuffed into the (gigantic) appendix.

Questions for authors
  1. What thoughts are there to use potentially cheaper and lighter assumptions for a similar method that can be more generalised and not so engrained within specific contexts?

  2. In your discussion you argue that things like the specifics of the DNN architecture are an "orthogonal concern", which surprised me and I think I'd be tempted to disagree with as it's so key to the interaction with some of the alignment techniques. In fact, you do specify a bit about this with the Layer Normalization point in the appendix, removing mean activity from previous layers and how this interacts with the univariate signal in e.g. fMRI. -- I feel like you're trying to answer a question you have, but without saying a lot, and then claiming it's an orthogonal question in the discussion to pre-empt a (potential) criticism that enough thought hasn't gone into that topic. My question is - is that the case?

  3. If you were to take a careful analysis of the current leaderboards like Algonauts or Brain Score and apply these metrics to each of the entries there, do you imagine the rankings would stay moderarely intact, or fall to pieces? significantly re-order? What (informally) are your suspicions of what this would do? (I'm trying to get a sense of how disruptive you think your proposal would be to the state of current research, and more disruptive is not a bad thing at all).

1 comment

Dear Reviewer,

Thank you for taking the time to review our paper. We are delighted that you found our paper to apply “a scientific battering ram to preconceived notions”, to “have good analyses contained within it and [telling] a coherent story without overcomplicating the issue” and believe it would be “well-received” by many ICLR attendees.

Q: “A great way for this submission to solidify its relevance and applicability would be to identify 2+ examples where region-matching, applied to a previous analysis, shows that previous results do not hold.”
A: Thank you for this suggestion. We refer to our general comment for additional experiments that we ran. In short, we find that poorly identifiable regions indeed give less stable model rankings. Thus, we hope our analysis prompts more caution in interpreting benchmarking results with fine grained region sets. .Region matching can tell in advance which regions a dataset cannot distinguish, so that they can be merged or benchmarked jointly instead. We expect this to give less fine-grained but more robust benchmark results. We also hope to raise awareness of what is needed to increase this 'resolution' of benchmarks.

Q: “What thoughts are there to use potentially cheaper and lighter assumptions for a similar method that can be more generalised and not so engrained within specific contexts?”
A: Thank you for this interesting question. We believe that our assumptions are explicit and relatively well-defined in the context of computational neuroscience, which is the main context in which the investigated measures are applied. Regarding costs of evaluating this check, want to point out that region-matching uses the same (training) dataset as the main benchmark would, and that runs are generally cheap - in particular compared to model-brain benchmark evaluations which require running DNN models on the stimulus set.

Q: (paraphrasing) “[Are the specifics of the DNN architecture really an orthogonal concern]?“
A: ‘Orthogonal concern’ refers to how our check is motivated. In brain-brain comparisons, we can define a benchmark-specific ‘ground truth’ in that we expect the same region to score the highest similarity. In DNNs, we can define a ground truth: We can test whether a measure assigns highest similarity to networks with the same architecture, but with different seeds, or to layers of the same depth. However, these networks might have found different solutions for solving the same problem. In both these tests and in region-matching, we pre-impose what we want to be scored as most similar. What differs is that in our setting, choosing regions as ground truth tests an assumption that is implicit in the benchmark. While these are clearly valuable and interesting experiments, there is no equivalent justification for any of the matching criteria in DNNs. This is what we mean by ‘orthogonal’. We here aim for an empirical evaluation of benchmarks against some kind of ground truth, which we believe can only be found convincingly on the brain side."

Q: “If you were to take a careful analysis of the current leaderboards like Algonauts or Brain Score and apply these metrics to each of the entries there, do you imagine the rankings would [change drastically]?”
A: Thank you for the interesting question. While we have not investigated the question in this work, it would constitute an interesting direction for further research. We do indeed speculate that changing the similarity measures underlying current leaderboards could drastically change their rankings.

References

[1] Finzi et al., 2023 - https://doi.org/10.1101/2023.12.19.572460 [2] Sartzetaki et al., 2025 - https://openreview.net/forum?id=LM4PYXBId5

Reviewer_MbDeOpenReview ↗
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Paper summary

In this paper, region matching is proposed as a prerequisite sanity-check for the Brain-DNN alignment studies, and further the feature specificity test for precise model-region matches. Multiple similarity measures were evaluated on two fMRI datasets, demonstrating the effects of preprocessing and measure choices on the performance benchmark.

Critical strengths

Sanity-check and feature specificity measures are proposed as a prerequisite step to identify meaningful similarity measures for the Brain-DNN alignment.

Critical weaknesses

Though performance on two fMRI datasets were evaluated with respect to multiple similarity choices, how the choices or conclusions would affect the downstream Brain-DNN study remains unclear and not validated.

Questions for authors
  1. For region-matching, only anatomical shifts of a region between subjects were accounted for. Regions within the same functional network (spatial distributed across association cortex, e.g., frontoparietal network) may share similar brain activity patterns for high-order cognitive function, how will these regions affect the region matching?

  2. Coarser target regions or region-merging were utilized to improve region matching performance. Will this decrease the region specificity? Increasing findings demonstrate significant inter-subject variations in spatial topography of functional parcellation, will individualized parcellation (e.g., fMRI based precision mapping) be better for region-matching and the brain-DNN alignment?

  3. Through the evaluation results on two fMRI datasets across multiple choices of preprocessing and similarity measures, is it possible to provide some general recommendations of choices for downstream Brain-DNN benchmark?

  4. The similarity benchmark was only evaluated between brain regions, how the choices or conclusions would affect the Brain-DNN benchmark remain unclear.

  5. Looks like the sections were not correctly labeled/numbered in the main text. Sometimes it is difficult to follow.

1 comment

We thank the reviewer for taking the time to review our paper, and for appreciating our work as being sound and informative. We are also grateful for the opportunity to clarify aspects of our methodology based on their questions.

Q1 and Q2:

  • “Regions within the same functional network (...) may share similar brain activity patterns for high-order cognitive function, how will these regions affect the region matching?”
  • “Coarser target regions or region-merging were utilized to improve region matching performance. Will this decrease the region specificity? Increasing findings demonstrate significant inter-subject variations in spatial topography of functional parcellation, will individualized parcellation (e.g., fMRI based precision mapping) be better for region-matching and the brain-DNN alignment?”

A: We thank the reviewer for this question and take the opportunity to clarify how region matching performance is intended to inform the design of the benchmarking setting. In fact, region matching accuracy is an indicator of region specificity in a given benchmarking setting. Design decisions, such as coarsening target regions and merging regions with poor identifiability, are meant to create a benchmark setting with higher region specificity. If regions of the same functional network share activity patterns, region matching might show that they are not well distinguishable from each other on the given data. This would tell the researcher that using this data to find models of those individual regions is unlikely to work well. It is an interesting avenue for future work to apply region matching to spatially distributed regions that are part of the same functional network.

Q3: “Through the evaluation results on two fMRI datasets across multiple choices of preprocessing and similarity measures, is it possible to provide some general recommendations of choices for downstream Brain-DNN benchmark?”

  • General recommendations across benchmarks are difficult, since results depend strongly on the dataset and analysis settings; our main recommendation is to run the sanity checks for each new benchmark setting, and our Boxes give actionable recommendations on how to act on their results. One more general finding is that most measures rely on the univariate signal to identify regions, which points towards a need for more discriminative stimuli in fMRI experiments.

Q4: “The similarity benchmark was only evaluated between brain regions, how the choices or conclusions would affect the Brain-DNN benchmark remain unclear.”

  • We address this concern with two experiments reported in the general reply.

Q5: “Looks like the sections were not correctly labeled/numbered in the main text. Sometimes it is difficult to follow.”

  • We thank the reviewer for pointing this out; in the revised version of the manuscript, we will include numbered headers.
Reviewer_CnoiOpenReview ↗
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Paper summary

The paper studies sanity checks for similarity measures used in brain-model comparisons. Authors evaluate 10 measures on two fMRI datasets (NSD and BOLD Moments). First, they use region matching across participants. The idea is that a brain region should be more similar to the same region in other participants than to different regions. Then they test feature specificity or whether similarity decreases when unrelated features are added or matching features are removed.

The main contribution is a systematic evaluation of these checks across measures, brain regions, and preprocessing choices. The experiments show that region matching depends strongly on the dataset and analysis settings. Successful matching often relies on the average response across voxels for each stimulus. Several measures also fail to penalize added or missing features. Based on these findings, the authors recommend checking region matching and feature specificity before drawing region-specific conclusions from brain-model comparisons.

Critical strengths

The analysis of the univariate signal provides a useful diagnostic result on the two fMRI datasets studied. By comparing full responses, region-average responses, and responses with the mean removed, the paper shows what information supports successful region matching. This can help researchers using these datasets and similar analysis settings assess how much their results depend on the average response of a region. However, it remains unclear how strongly the finding depends on the stimulus sets, region definitions, and preprocessing. Its broader relevance to brain-model comparisons needs further validation.

Critical weaknesses
  1. It is unclear how the check helps evaluate brain models. Authors recommend region matching as a necessary check before interpreting brain-model comparisons. However, they do not show what passing or failing the check tells us about the quality of a model comparison. A failed match could also come from differences between people or from how brain regions are defined. The authors discuss these problems and run several controls, but the link to model evaluation is still unclear. Region matching has also been used in earlier work. Without a clearer demonstration of its practical value, the contribution mainly consists of the findings on the two datasets.

  2. Some statistical choices make the results harder to trust. Each participant is compared with an average of the other participants. The resulting scores therefore use overlapping data. The paper does not explain how this is accounted for when computing confidence intervals. Appendix K.4 also leaves out cases where confidence intervals could not be computed, including 49 of 140 cases for NSD. It is unclear whether leaving out these cases changes the conclusions. Finally, an accuracy interval that excludes zero does not show that a method performs better than random guessing. These issues make it harder to judge how reliable the proposed check is.

Questions for authors

Q1) Can you demonstrate how the proposed sanity check changes the interpretation of an actual brain-model comparison? An experiment with existing networks would be useful to clarify what passing or failing region matching tells about model evaluation. Simply reporting different model rankings would not establish which ranking is more meaningful.

Q2) Could you evaluate whether the main conclusions hold when including the following methods? Debiased CKA (Murphy et al., 2024), to assess the role of statistical bias related to feature and sample counts; Topological RSA (Lin and Kriegeskorte, 2024), which has already been evaluated on region identification across participants and addresses sensitivity to individual differences in representational geometry; WUC (Diedrichsen et al., 2021), to account for uncertainty and dependence between estimated distances when comparing RDMs. The Crossnobis and voxel-whitening experiments address a different stage of the analysis. These comparisons would help test specific explanations for the findings. I do not assume that they would necessarily perform better.

Q3) Could you provide an anonymized link to the repository? Please include the scripts and configurations needed to reproduce the main results

Q4) Each participant is compared with an average of the other participants. This means that the resulting scores share data. How do you account for this dependence when computing confidence intervals? Do you recompute the reference averages and scores during bootstrap resampling?

Q5) Why do you check whether accuracy confidence intervals include zero (Appendix K.4)? Under uniform random selection, chance accuracy is about 6.7% for BMD and 7.1% for NSD. Would using an appropriate chance baseline change the comparison with Cohen's standardized mean difference?

Q6) Why some confidence intervals for Cohen's standardized mean difference not be computed? This affects 27 of 150 cases for BMD and 49 of 140 for NSD. Could excluding these cases change your conclusions?

Q7) Apendix C states that the transport weights must be nonpositive, while their row and column sums must be positive. Is the inequality sign a typo? Please confirm that the implementation uses nonnegative weights.

Q8) Appendix C states that minimizing the transport cost is equivalent to minimizing the reconstruction error $ ||X-YP||_F^2 $ when the feature counts are equal. Could you explain this equivalence under the stated normalization and constraints on the transport matrix? A weighted sum of pairwise distances is generally different from reconstruction error after mixing features. Which objective was used in the experiments?

6 comments

We thank reviewer Cnoi for their thoughtful review, and for recognizing the practical usefulness of our univariate analysis. We further thank them for pointing us to a few issues that we resolve, as detailed further below.

The first set of core concerns of reviewer Cnoi center around the connection between our sanity check and actual brain-DNN benchmarks, and therefore its practical value. We have run brain-DNN benchmark experiments and will report added findings from them in the appendix, with reference from the main text. We there also test how removing the brain-side univariate signal affects model scores, which shows overall score changes but no strong rank changes. For our interpretation of this finding and for details of the other experiments, we kindly refer reviewer Cnoi to our first general comment.

We thank the reviewer for suggesting to test how the dependence on the univariate signal depends on stimulus set, region definition, and how it interacts with preprocessing. So far we observe this on two datasets with different stimulus sets (BMD and NSD). Studying this further is a potential avenue for future work, to narrow down how to choose a benchmark setting that has strong pattern-based region identifiability.

In order to ensure anonymity during the review phase, we will make the code available upon publication of the paper. This code can be extended to include new datasets, preprocessing methods, and measures, which we hope lowers the bar for applying the check to other benchmark settings.

We now address reviewer Cnoi’s remaining concerns about why our sanity check is relevant to brain-DNN benchmarks, when there are many potential reasons for a failed check. The reviewer points out that a failed match could also come from differences between people or from how brain regions are defined. This is correct and one of our main messages: Region matching tests a benchmark setting as a whole. How regions are defined and what stimuli are being used are part of that benchmark setting (see sec. 3.1 “A region matching sanity check”, Discussion, and Appendix Box 1, row ‘Region definition’). If a region is badly defined across subjects, or does not react distinctively to the stimulus set, then these issues equally affect a benchmark looking for models of that region on the same data.

Therefore, a failing check tells us that a benchmark setting has low sensitivity to the region in question, and that it cannot be expected to find region-specific DNN matches at the level of that region. A passing check in turn tells us that the benchmark is sensitive to the region - but not that its similarity scores are meaningful. (See section 3.1, “Limitations” and “Region matching is necessary and complementary to other criteria”. )

The practical value of region matching as sanity check is that it allows to adjust the benchmark - dropping or merging regions, rejecting a measure, iterating over preprocessing choices, or even moving on to a different dataset (Box 1, "Acting on region matching results") - to ensure that the benchmark setting allows to identify the region at all.

Reviewer Cnoi’s second set of concerns are about certain aspects of our statistical methods and how they are reported, some of which are true oversights on our part. We first address the three questions and corrections from point 2 in ‘critical weaknesses’, and answer those in the questions for authors separately below.

  1. Lack of independence of source feature maps, which are leave-one-out mean (LOOM) over remaining subjects, and potential issues for analyzing variance over these comparisons: We thank the reviewer for this point. The source LOOM is not independent across target subjects, in fact it approximates a mean over the general population - a single comparison feature map across all subjects. Since our sample size is small, we omit the target subject from the mean, as this might have falsely inflated results. We therefore treat the LOOM as the same model across all subjects we compare against. This mirrors what is typically done in model-brain benchmarking: One model is compared to multiple target subjects, and variability is computed across these target subjects only. To answer Q4: No; accordingly we do not recompute the reference averages during bootstrap resampling. We see the source-side LOOM as 'one' reference model, and our variance estimate is computed across the target subject side.

  2. Appendix K.4 does not show CIs where they could not be computed: Our implementation so far used scipy.optimize.brentq to search scipy.stats.nct.cdf within −30 to 30 for the noncentral-t parameter (∆) (see also appendix K.1). This had numerical instabilities, so that the algorithm sometimes did not find a solution. We now change to scipy’s scipy.special.nctdtrinc function which is robust, so that we can provide all CIs. The missing CIs were mostly around values below visible range, as indicated by the cross marks drawn mostly at zero, the lower end of the range shown. Their CI’s often reach up to small positive values or below, therefore the plots do not change considerably.

  3. Chance level of accuracy is 1/R, so confidence intervals should be compared to whether they cross chance level, not zero, to mirror what we do for d_z: We thank reviewer Cnoi for pointing out this error in the appendix, section K.5, “Comparing Cohen’s dz and region matching accuracy”. We now report instead how often accuracy CIs include the chance level, which is 1/15 for BMD and 1/14 for NSD. The number of region/measure pairs with CIs including chance are, for accuracy: 30/150 (20%) for BMD (instead of 14/150) and 52/140 (37%) for NSD (instead of 37/140). Since we also change to a robust CI computation for Cohen’s dzd_z, as described above, we can now report the corresponding numbers for dzd_z across all region-measure pairs, which are: 67/150 pairs (45%) for BMD and 80/140 (57%) for NSD. (Previously missing CIs were typically for values of dzd_z below zero.) So overall, more CIs include chance level than we had stated before, still less frequently for accuracy than for dzd_z. These counts are meant as a descriptive summary of the plots, which are hard to read by eye, not as a statistical test.

Answers to the reviewer's questions to authors

Q1) Can you demonstrate how the proposed sanity check changes the interpretation of an actual brain-model comparison? An experiment with existing networks would be useful to clarify what passing or failing region matching tells about model evaluation. Simply reporting different model rankings would not establish which ranking is more meaningful.

  • Yes; we refer to our answer to the first set of concerns above and to our general comment.

Q2) Could you evaluate whether the main conclusions hold when including the following methods? Debiased CKA (Murphy et al., 2024), to assess the role of statistical bias related to feature and sample counts; Topological RSA (Lin and Kriegeskorte, 2024), which has already been evaluated on region identification across participants and addresses sensitivity to individual differences in representational geometry; WUC (Diedrichsen et al., 2021), to account for uncertainty and dependence between estimated distances when comparing RDMs. The Crossnobis and voxel-whitening experiments address a different stage of the analysis. These comparisons would help test specific explanations for the findings. I do not assume that they would necessarily perform better.

  • We thank the reviewer for this suggestion. For the camera-ready version, we will add debiased CKA, WUC, and RGTM-based topological RSA, with its two parameters, to our codebase and report results of region matching accuracy, feature specificity and results under removal and reduction to the univariate signal in the appendix. We note that for WUC, the combination of whitening and crossvalidation might lead to similar decreases in performance as we find with crossnobis (see fig. 20).

Q3) Could you provide an anonymized link to the repository? Please include the scripts and configurations needed to reproduce the main results

  • We are not able to ensure anonymity when sharing a link to the repository at this moment, but we will make the code for all region matching and feature specificity experiments public upon publication. The brain-DNN experiments added during the rebuttal rely on a benchmark codebase that we cannot release; we will describe their setup in the appendix in sufficient detail.

Q4) Each participant is compared with an average of the other participants. This means that the resulting scores share data. How do you account for this dependence when computing confidence intervals? Do you recompute the reference averages and scores during bootstrap resampling?

  • No, we do not recompute the reference averages during bootstrap resampling. See our answer to the concern on independence (point 1 above).

Q5) Why do you check whether accuracy confidence intervals include zero (Appendix K.4)? Under uniform random selection, chance accuracy is about 6.7% for BMD and 7.1% for NSD. Would using an appropriate chance baseline change the comparison with Cohen's standardized mean difference?

  • We thank the reviewer for pointing us to this, this was an error, which we now fix. Details and corrected numbers are given above under point 3. The correction does not change the comparison with Cohen’s dzd_z. As noted there, these numbers are a descriptive summary of the plots, not a statistical test.

Q6) Why some confidence intervals for Cohen's standardized mean difference not be computed? This affects 27 of 150 cases for BMD and 49 of 140 for NSD. Could excluding these cases change your conclusions?

  • We again thank the reviewer for pointing this out and refer to our answer in point 2 above.
Reviewer_5XQVOpenReview ↗
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Paper summary

The paper evaluates the sensitivity of 10 similarity measures for neural data across two large-scale fMRI datasets. They explore the impact for both region matching (correct region versus incorrect) and feature specificity (robustness to unrelated features). The paper also explores the impact of preprocessing choices.

Critical strengths

-The investigation is well controlled a thorough with the experimental framing, with well thought out decisions for investigating statistical valididty. -The authors come to meaningful conclusions from their investigation and frame those conclusions around practical considerations for practitioners. -The investigation of feature specificity is, to my knowledge, novel---I have not seen it pursued in other works---I found these findings particularly interesting. I think this is an important consideration for future works to keep consider and would like to see it widely adopted as a consideration.

Critical weaknesses

-While the paper is framed as a preliminary investigation/sanity check, it would still have been nice to see some experiments with DNNs themselves and how these findings generalize beyond brain-to-brain. Especially considering the explicit framing of the problem as being most meaningful for that comparison. One thing that would be particularly interesting would be comparing DNNs to one other using the same set of experiments and seeing what properties hold. -The title implies a grander effort than what we are getting this this paper, particularly the use of the word 'interpretable' -The authors rely on an averaged reference model for each dataset, following standard practice--however, this mutes the influence of a 'feature specific' analysis since the averaging itself is suppressing feature noise. -Several of the experiments are conceptually interesting but in reality simply confirm known properties of metrics--often due to the mathmatical guarentees of how the measure itself works, which thus negates the need for exhaustive experimentation, e.g., "lack of feature specificity is expected" when adding feature dimensions.

Questions for authors

-Even a modest set of experiments comparing DNNs with the neural data would meaningfully ground the relevance of this work. For example, how much does a standard DNN-brain score change when a univariate component is removed from the brain data? -Is there ever a case where single-subject findings deviate from multi-subject reference model findings for things like region matching?

1 comment

We thank reviewer 5XQV for highlighting the rigor of our investigation and the novelty of our feature specificity analysis, and for their suggestions for DNN experiments. We share their hope that feature specificity will be taken into consideration more widely.

To address the requests for showing connections to brain-DNN benchmarks more explicitly, beyond our theoretical considerations, we run additional experiments, for which we present preliminary results in the general comment. They include an experiment how dropping brain-side univariate information affects model scores (questions to authors, Q1): It only affects model rankings slightly. We discuss this further in the general comment.

Regarding reviewer 5XQV’s suggestion to run similar experiments for DNN comparisons: This has been done ([1-4]), and is, as we mention, an orthogonally motivated direction of research. By this we mean: Region matching has a direct connection to an assumption that benchmarks make implicitly, this leads us to a ‘ground truth’ to compare against. In DNNs there are many interesting axes of comparison (layer depth, architecture, train data, … see e.g. [5] ), but even networks that only differ by random seed might learn completely different solutions to the same task. So we believe there is no equivalent justification to consider any pair of DNNs as ‘true’ match.

Does averaging reduce ‘feature specificity’ in a different sense, by smoothing out spatial and individual differences? It is true that we might be erasing fine-grained structure in this way. However, we focus on brain-region benchmark settings, where the information preserved through averaging seems sufficient for identifying a brain region, and any loss of fine-grained features is offset by the averaging out of noise and subject-specific idiosyncrasies. Empirically, preserving this fine-grained structure would lead to worse identifiability across subjects.

To answer reviewer 5XQV’s related second question for authors (Q2), “Is there ever a case where single-subject findings deviate from multi-subject reference model findings for things like region matching?”: Single-subject-pair comparisons differ in the errors they make - which regions are confused with which. But they rarely are correct when the comparison to averaged data is wrong: Across 10 measures (we here only use Euclidean variants of veRSA and RSA), on our standard set of 15 regions on BMD (14 on NSD), this was the case in around 4% (4%) of comparisons, while in 29% (17%) of cases, matching with averaged sources was successful while single-subject matching failed. We will add this to the appendix section discussing our reasons for choosing averaged sources instead of single subject ones.

Experiments partially confirm known properties of measures: Our experiments reproduce known properties of metrics where those are known, and we see this as a sanity check of our method. Additional unexpected findings include the low empirical feature specificity of (Pearson-correlation) RSA, a drop of linear predictivity’s region identification with PCA preprocessing, and that noise-whitening hurts Procrustes’ performance. We think that our empirical checks are a valuable complement to theoretical considerations: They can help discover theoretical properties that are not yet known, and even where they reflect known properties, they might help a non-expert discover some of the intricacies of a measure and its interaction with preprocessing methods. Our empirical checks are lightweight to run, and they can be applied to new metrics that a researcher is still unfamiliar with.

Paper title: Finally, we agree that ‘towards interpretability’ can be read as overclaiming, since we are still far from knowing how we should interpret such benchmarks. We will change our title to: "Sanity-checking brain-alignment benchmarks with region matching and feature specificity".

References

[1] Kornblith et al., 2019 - https://arxiv.org/abs/1905.00414
[2] Bo et al., 2024 - https://arxiv.org/abs/2411.14633
[3] Han et al., 2023 - https://arxiv.org/abs/2302.06677
[4] Ding et al., 2021 - https://arxiv.org/abs/2108.01661
[5] Conwell et al., 2024 - https://doi.org/10.1038/s41467-024-53147-y

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Comment to all reviewers: Added brain-DNN benchmark experiments

In this paper, we introduce two procedures for sanity checking brain-alignment benchmarks: region matching and feature specificity. All reviewers appreciated the systematicity of our approach, and asked for experiments that demonstrate the implications of our results for brain-DNN alignment benchmarks. We address this point below based on two experiments; concerns raised by individual reviewers are addressed below in the individual reviewer replies. We will include these results in the appendix of the final version of the paper, with a short section in the main text discussing these results.

First, (i) we find that brain regions that are harder to identify (as assessed by region matching) give less stable model rankings, even when controlling for noise levels. Second, (ii) while removing the univariate component from brain data makes it harder to identify regions in the brain-brain setting, the same procedure leaves model-brain alignment rankings nearly unaffected for most measures and only changes absolute model alignment scores.

In other words, the (univariate) component that helps distinguish regions contributes about equally to every model’s alignment score, while differences in model alignment scores stem from the remaining (multivariate) pattern information, which our sanity check shows to distinguish regions less well. Further, model rankings are often similar across regions for commonly used measures, in line with recent findings of shared top-performing models across different brain regions (Tang et al. 2025 [1], Hoefling et al. 2026 [2]). Differences in alignment between models therefore may partially reflect properties of the models that a measure rewards regardless of the brain data, such as the effective dimensionality (e.g., Canatar et al. 2023 [3]). One implication for the field is that future brain data collection efforts should aim at experimental designs that increase the region-distinguishing signal beyond the univariate component.

[1] Tang et al. (2025). https://doi.org/10.1101/2025.07.22.664908
[2] Hoefling, L., et al. (2026). https://arxiv.org/abs/2604.21780
[3] Canatar, A., et al. (2023). https://doi.org/10.52202/075280-2038

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