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Under review as a conference paper at ICLR 2027

Measuring Model–Brain Alignment in Latent Spaces

Abstract

Evaluating neural network models as hypotheses of brain computation requires accurately quantifying the alignment between artificial and biological representations. Here, we propose measuring representational alignment within a shared latent space learned via a cross-modal multi-encoder–decoder architecture. By mapping network and brain representations into a common low-dimensional space, our framework enables direct comparison of both overall latent distributions and per-stimulus correspondences. To demonstrate the properties of our method, we construct two diagnostic benchmarks using fMRI data paired with reference and manipulated network representations: (1) structural "foil" models, which are mechanistically dissimilar to brain computation by design yet match its coarse high-level structure, and (2) reference model representations with systematically corrupted information. We show that linear ridge regression is nearly flat across these structural transformations, whereas commonly used similarity metrics – Representational Similarity Analysis (RSA) and Centered Kernel Alignment (CKA) – score the foil models close to, or above, the reference network. In contrast, metrics derived from our latent space (i) accurately capture progressive information loss under controlled corruption and (ii) reliably identify structural discrepancies between the foil models' representations and biological neural data, providing a new robust, structure-sensitive tool for brain–AI alignment.

Primary area:
applications to neuroscience & cognitive science
Keywords:
representational alignment, model-brain alignment, Variational Autoencoders, neuroAI

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

The paper proposes measuring model–brain alignment in a shared latent space learned by a multimodal VAE. The authors evaluate distributional overlap and image identification in this space, using ResNet representations and fMRI data. They test the approach on constructed representations that remove image details, swap category information, or rely on artificial shortcuts. The proposed scores generally penalize these constructions more strongly than the existing measures considered.

Critical strengths

I like the use of constructed controls. The networks trained to classify using planted squares provide a useful test of whether an alignment measure rewards a model that solves the task through an implausible strategy. The evaluation on held-out images and checks across training seeds, feature selections, and RSA variants also give some confidence that the reported patterns are reproducible.

Critical weaknesses
  1. I am not fully convinced that the corruption ladders establish a correct ordering that an alignment measure should recover. Removing image-specific detail loses information, but a fixed, one-to-one category swap can preserve category identity in a different code. A fitted decoder may reasonably undo that mapping. The constructions combine these different changes, and I think the authors need to explain more clearly which properties their measure should preserve or penalize. Positive controls using equivalent representations would also help establish that the method does not reject harmless changes.

  2. I am unsure whether the results establish an advantage over existing approaches. Appendix F reports that ridge already ranks every foil below both reference networks and detects every step of the corruption ladders. At each network’s best layer, RSA and CKA also rank every foil below the reference. Larger numerical differences on a different score scale do not by themselves establish a better measure. Meanwhile, a separate latent space is trained for each candidate model, so the brain representation used for evaluation changes across comparisons. I would like to understand how stable the conclusions are to latent dimension and reconstruction-loss weighting, and how much the VAE adds over simpler bidirectional or shared-space methods.

Questions for authors
  1. What transformations should leave the proposed alignment scores unchanged?

  2. Does the advantage remain against reverse predictivity or a simpler shared space method evaluated using the same image identification task? How sensitive are the rankings to latent dimension and the balance between model and brain reconstruction losses?

  3. The dCKA estimator corrects stimulus sampling but not feature sampling. Could the authors discuss whether the correction in Chun et al. (2025, arXiv:2502.15104) is applicable to their fMRI measurements and projected model features? I am unsure whether it would affect the comparisons, especially if only the brain side requires correction.

4 comments
AuthorsOpenReview ↗

Response to Reviewer ZxfB (1/4)

We thank the reviewer for the comments. Here are our responses to the two Weaknesses mentioned and the three Questions. Appendix, Table and Figure numbers refer to the revised paper.

1. Corruption ladders and why the measure should penalise them (added Appendix D1).

We agree that a one-to-one swap keeps category identity, and a fitted map can undo it. Here we show that every step down the Corruption ladders removes structure that RN50 shares with the brain: either the image-specific structure within a group, or the similarity structure between groups. The ladders contain two kinds of steps: steps that remove information, and steps that corrupt it, i.e., replace information about an image with the wrong information from another image.

  • Steps that remove information about the image: RN50 → CATownCAT_{own} or S-CATownS\text{-}CAT_{own} (the image keeps its group mean and ten principal components of its own detail)
  • Steps that relabel and corrupt information: In CATinCAT_{in} and CAToutCAT_{out} the 80 category means are exchanged one-to-one: every image of a category receives the mean of another category, a “sibling” category for CATinCAT_{in} and a randomly chosen one for CAToutCAT_{out}.

Two different questions can be asked about these manipulations:

i) Can the category of an image still be read out? The answer is yes, as all images of a category still share one mean, and different categories still have different means, so the swap only renames the categories. An invertible linear map can send every swapped mean back to the original one. A measure that fits a linear map therefore cannot see the swap, and ridge does not (0.294 for CATinCAT_{in}, 0.293 for CAToutCAT_{out}, Fig. 3 and Table 5).

ii) Are the same categories still alike? The answer is no. In RN50 some categories are close to each other and others are far apart: the images closest to cats are those of dogs, teddy bears, etc. After the random swap the cat images carry the mean of an unrelated category, and the images closest to them are different, e.g., benches, motorcycles, etc. The categories remain distinguishable, but which categories are neighbours has changed. We call this the similarity structure between categories.

Table 3 in App. D1 (also shown below) measures the second question with two numbers, both computed over pairs of categories (e.g. cat and dog).

  • RN50 similarity structure asks how much of RN50’s own structure survives the swap. For each of the 3,160 possible category pairs we take the cosine similarity between the two category means before the swap and after it, and correlate the two lists. A value of 1 means that every pair of categories is as alike as before the swap and a value of 0 means that how alike two categories were says nothing about how alike they are after the swap.
  • Agreement with the brain asks whether this structure is shared with the brain. We compute the same similarities between categories from each subject's responses and correlate them with the model's: a high value means that the categories that are alike in the model are also alike in the brain.
RN50 similarity structure keptagreement with the brain
no swap1.000.63
sibling swap (CATinCAT_{in})0.770.54
random swap (CAToutCAT_{out})-0.02-0.02

Without a swap, the categories that are alike in RN50 tend to be alike in the brain (0.63), e.g., in both the categories closest to cats are dogs, teddy bears and bears. The sibling swap keeps most of RN50’s structure (0.77) and most of its agreement with the brain (0.54). The random swap keeps none of either (-0.02): which categories are alike in the manipulated model representations no longer has anything to do with which are alike in the brain, although the category of every image can still be read out by a linear map.

Table 4 in App. D1 in the paper, splits the agreement with the brain value from the Table above into a part between groups (similarities between group means) and a part within groups (similarities between two images of the same group, group mean removed) and shows that each step of the ladders deteriorates at least one of the two. The agreement between the model's and the brain's similarities within groups falls .167 → .033 → 0 on the category ladder and .153 → .043 → 0 on the supercategory ladder. We argue that this supports that any alignment metric should score CATinCAT_{in}, CAToutCAT_{out} and S-CATdonorS\text{-}CAT_{donor}, S-CATswapS\text{-}CAT_{swap} lower than the CATownCAT_{own} and S-CATownS\text{-}CAT_{own}.

The ordering we defend is: references (RN50, RN50sc) > (CATownCAT_{own}, S-CATownS\text{-}CAT_{own}) > CATinCAT_{in}, CAToutCAT_{out} and S-CATdonorS\text{-}CAT_{donor}, S-CATswapS\text{-}CAT_{swap}. While also (CATownCAT_{own}, S-CATownS\text{-}CAT_{own}) > foils.

AuthorsOpenReview ↗

Response to Reviewer ZxfB (2/4)

2. i) Advantage over existing approaches

We do not claim that our method is superior because of larger differences on another scale, but that it expresses different aspects of alignment, i.e., distributional and stimulus-specific, that the standard metrics do not capture. This leads to the foil models scoring low in our method's metrics, while they reach most or all of the reference RN50's score on the standard measures.

Specifically, the issue that we show with the paper’s constructed cases and RSA’s and ridge’s performance on them is that the foils still manage to get a high score. Even in Ridge, the foils score up to 77% of RN50’s and 82% of RN50sc’s r, and 61% of RN50’s, and 71% of RN50sc’s R2R^{2} and they are scored at the level of CATownCAT_{own} and S-CATownS\text{-}CAT_{own}. For the per-layer RSA, both CATownCAT_{own} and S-CATownS\text{-}CAT_{own} score above both references, and Carrier-B is level with RN50sc (88% and 87% of RN50 on RSA; Appendix N, Table 19). The table below places the best foil score on each measure as a % of what score RN50 achieves in the same metric.

measurebest foil, % of RN50's scorewhere it falls on the training-degradation ladder
RSA121%above the trained RN50
ridge r77%above α = .25
ours, top-19%at the untrained network

If foil model representations that haven’t been fed the images, or solve the task in mechanistically dissimilar ways with the brain (e.g., from planted pixels shortcuts) can achieve most of RN50’s and RN50sc’s alignment score and all of CATownCAT_{own} and S-CATownS\text{-}CAT_{own} (RN50 representations that have some information removed, but still contain substantial RN50 information), doesn’t this make RN50 and RN50sc high alignment score less meaningful?

In the distributional and stimulus-specific alignment that our method measures, RN50’s and RN50sc’s score cannot be achieved with a foil. So, our thesis is not that our method is superior, but that it expresses different aspects of alignment, which in some cases are more difficult to achieve a high score on, and this is why the foil models fail. We believe these aspects are meaningful and could potentially be what is needed to distinguish candidate models (architectures, training objectives etc.) regarding their alignment with the brain in cases where other metrics saturate.

2. ii) Comparison with CCA (added in Appendix I)

CCA also places model and brain in a common space and in addition to its own metric (canonical correlation r), we can compute the metrics we proposed in this work in their aligned space. CCA common space identifies images well (RN50 top-1 0.568; full results in Table 9, latent visualisation of CCA space in Fig. 8, App. I). However, CCA whitens each side (model and brain). Every retained direction (after PCA cut) is rescaled to unit variance, so how much of the model representation a direction carries is discarded, and only the directions that correlate best with the brain are kept in the common space. Thus, CCA gives a model credit for whichever part of it correlates best with the brain, even when that part is only a small fraction of the model's representation. Our method works differently, since the latent space must also reconstruct the model's features (model→model and brain→model pathways), so a part of the model that carries a lot of its variance needs to be represented in the common space.

To test exactly that, namely if CCA score can be maximised if a model representation contains a brain-like subspace, no matter how small the part of the model representation that aligns with the brain is, in Appendix I.2, we constructed representations in which the model representation is controlled to be consisted of a meaningful RN50 signal and Null’s signal. We take Null (RN50's response to a different image) and add RN50's response to the true image at a gain that sets its share of the variance. When the true image's RN50 code is 8% of the mixed representation and the other 92% is about another image (Null), CCA scores it at 56% of the top-1 and at 82% on its own measure r of what RN50 itself achieves; when RN50 code is 11% of the share, at top-1 is at 80% and r at 93% of what the actual RN50 representation achieves. Our method's top-1 metric scores both at 1% of RN50, and rises only when the code is a large part of the representation (top-1 at 30% of RN50 at a 38% share, and RN50's level at 71% share) (Table 11, App. I.2). The reason is whitening: CCA rescales every retained direction to unit variance, so a direction that holds 1% of the variance counts as much as one that holds 50%. This is a known property: a measure that is invariant to invertible linear maps ignores the scale of directions and gives the same score to representations that match only in their small principal components (Kornblith et al., 2019). Our latent must also reconstruct the model's features, so a code enters it in proportion to its share.

AuthorsOpenReview ↗

Response to Reviewer ZxfB (3/4)

2. iii) Impact of model vs. brain loss weights and Latent dimensions number

In our method, every training image pairs the model features with the one subject who saw it, so the model encoder sees all 62,551 training images and each subject's encoder 7,400–8,100. Thus, each subject's own encoder and decoder receives fewer examples than the shared model encoder/decoder. However, over the eight subjects the brain contributes as many examples as the model, since each image has been seen by exactly one subject. Thus, at least in respect to the number of the samples, the model and brain representation samples equally contribute to shaping the latent space.

Yet, there are other imbalances on the contribution of model vs. brain in shaping the latent space that come from training settings. In the per image loss, the model features carry ~51k variance units (model features are z-scored with variance 1) and the voxels ~11k on average (after the NSD and Algonauts preprocessing the brain features have variance ~0.5), so the model loss terms outweigh the brain and the model is effectively used as a scaffold in the latent space as the Reviewer suggests.

In Appendix H, to explore the effect of the model vs. brain losses in shaping the latent space and the sensitivity of our method’s metrics to the weight of the model vs. brain reconstruction losses, we retrained VAE with the two sides balanced (weights 1 for the model terms and 4.52 for the brain terms, KL weight scaled to keep its share comparable to the original one), everything else as in the paper. With this weighting the model and brain reconstruction losses contribute equally in variance. Table 8 in Appendix H gives the metrics for the paper’s main analysis vs. balanced weights comparison side by side and the visualization of the latent is in Fig. 7.

With balanced weights the brain shapes the latent space more than before, and the level of the scores changes. Identification of the references falls by almost half (RN50 top-1 0.321 to 0.179), because the latent now spends capacity on brain signal that the model does not explain. However, the ranking between the different cases of the main analysis (RN50, RN50sc, Ladders, and Foil models) remains unchanged (Table 8, App. H). On top-1, top-5, median rank and iLISI the order RN50 > RN50sc > CATownCAT_{own}, S-CATownS\text{-}CAT_{own} > foils is preserved. Despite the margins being narrower than with the paper's main analysis weights, the ordering does not depend on the model being the anchor in the latent space.

The ordering is the same with both weightings, so our conclusions do not depend on this choice. We view the weights of the model and brain losses as a hyperparameter, similarly to the latent dimensionality: when comparing different models regarding their alignment to a brain dataset, they should be compared with the same loss balancing between model and brain representations. We also view this parameter as a design choice, because it has a clear meaning: it sets how much the brain, relative to the model, shapes the common space. With the paper's weights the model works as a scaffold. With balanced weights, more brain signal is hold in the latent.

We note that the scaffold cannot create alignment by itself. With the correspondence between images broken (Null), every latent read-out of our method is at chance.

Latent dimension (Appendix G, Tables 6–7). After the reviewer's suggestion, we trained our VAE with different latent dimensionalities for RN50, RN50_sc, CATownCAT_{own}, S-CATownS\text{-}CAT_{own}, the three highest performing foils —Carrier-B, Carrier-P and LabelCode-N—and the Null. The ranking of these remained the same in 64 and 128 dimensions as it was in the originally trained 32-d VAE.

With 64 and 128 dimensions instead of 32, no representation moves by more than 0.02 on top-1, the order remains the same and the ordering contrasts remain significant on identification. The energy distance is built from Euclidean distances between latent points, and these grow with the number of dimensions over which they are summed. iLISI counts how well model and brain points are mixed among each point's nearest neighbours; with the same 872 images spread over more dimensions the neighbourhoods become sparser, and a small offset between the two clouds in each dimension adds up, so the neighbours of a point are more often from its own cloud. The values of these two metrics should therefore, because of nature of the metric, be compared between different model representations at one latent size, and not between latent sizes. Within each latent size the order RN50 > CATownCAT_{own}, S-CATownS\text{-}CAT_{own} > foils is preserved on both metrics (energy and iLISI), and all eight contrasts are significant at 32, 64 and 128 dimensions. The one change is on iLISI at 128 dimensions, where RN50sc (0.360) falls just below CATownCAT_{own} (0.379).

AuthorsOpenReview ↗

Response to Reviewer ZxfB (4/4)

Question 1. What transformations should leave the scores unchanged? (analysis added in Appendix K).

Changes that only re-express a representation should leave the scores unchanged (Appendix K, Table 15). We tested the following:

  • The training seed of our VAE: Over three seeds, top-1 of a representation varies by at most 0.007 (0.012 for RN50). This range is the reference for the two tests below.
  • A rotation of the feature space that keeps every feature's variance (we tested it in the following representations: RN50, S-CATownS\text{-}CAT_{own} and Carrier-P): For the rotation of the feature space, identification stays inside the range of the three VAE training seeds or within 0.010 of it (RN50 top-1 0.329 against 0.321–0.333), and the order RN50 > S-CATownS\text{-}CAT_{own} > Carrier-P is kept on every read-out in all eight subjects. iLISI is inside the range for RN50 and Carrier-P and above it for S-CATownS\text{-}CAT_{own} (0.536 against 0.460–0.496).
  • An independently trained copy of a network (RN50sc retrained from another initialisation): Every read-out is inside the range of training seeds (top-1 0.193 against 0.192–0.199).

What should lower the scores, and does: removing or replacing information about the image (the two Corruption ladders), undoing the network's training (the training-degradation ladder), and breaking the correspondence between images (the Null, at chance).

Lowered, as they should be: removing or replacing information about the image (the two Corruption ladders), undoing the network's training (the training-degradation ladder), and breaking the correspondence between images (the Null, at chance).

Question 2. Reverse predictivity, simpler shared-space methods, latent size and loss balance

Reverse predictivity does not keep the ordering. Ridge from voxels to model features rewards representations that are easy to predict: on the real brain the five foils score 2.0–2.7 times RN50 (0.43–0.57 against 0.22), and on the model-recovery study in Appendix Q, where synthetic brain is generated from RN50, the generator RN50 is ranked 11th of 18 (Tables 21–22). The comparison with a simpler shared-space method (CCA) is described above in Section 2.ii (Response 2/4) and in Appendix I. Latent size and loss balance analyses are described above in Section 2.iii (Response 3/4) and in Appendices G and H.

Question 3. Feature-sampling correction of Chun et al. (2025)

We applied feature-sampling correction to either the brain side or both sides, and it changes no comparison. In the estimator of Chun et al. (2025), only each system's self-term is corrected, by a factor that shrinks with the number of sampled features (about 20,700 voxels; 61,548 projected features).

  • Applied to brain side alone: dCKA rises by 0.03–0.06% for every representation.
  • Applied to both sides: at most 0.7% in the whole-network bases (RN50 0.1960 → 0.1972) and 2.% at the best layer.
  • The order of no pair of representations changes.
Reviewer_nfGGOpenReview ↗
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Paper summary

This paper concerns the alignment between brain representations (fMRI) and vision models, in the context of visual processing. An architecture is proposed where both representations are mapped to a common space and alignment is measured in this space. Elegant baseline models are created to normalize alignment measures.

Critical strengths

Important problem. Well argued approach and elegant baselines.

Critical weaknesses

The whole approach appear very similar to CLIP alignment, eg BrainCLIP: Liu, Y., Ma, Y., Zhou, W., Zhu, G. and Zheng, N., 2023. Brainclip: Bridging brain and visual-linguistic representation via clip for generic natural visual stimulus decoding. arXiv preprint arXiv:2302.12971.

Questions for authors

Please clarify the relation to BrainCLIP

5 comments
AuthorsOpenReview ↗

Response to Reviewer nfGG (1/3)

We thank the reviewer for pointing us to BrainCLIP (Liu et al., 2023). We have added an Appendix J: "Comparison with BrainCLIP" in the revised pdf. Here are the most important points summarized:

  • Aim. BrainCLIP is proposed for decoding images from fMRI, not for comparing different models with the brain. In the BrainCLIP paper, the alignment with CLIP serves this purpose (image decoding) and not the derivation of metrics to distinguish between different models regarding their alignment with brain data. However, for the efficient image decoding, BrainCLIP maps fMRI responses to CLIP’s feature space. Thus, we can repurpose its architecture as an alignment measure and conpute in its CLIP space the same metrics as from our method’s common space.
  • Architecture. The main difference in the architecture is that our method also reconstructs the brain from the common space, as it has four pathways; model→model, model→brain, brain→brain and brain→model. Thus, the low-dimensional representation of the brain in our method’s latent space preserves brain-related information that, importantly, is not necessarily aligned with the model representation. Contrary, BrainCLIP only maps the brain into the model's embedding space (brain→model pathway, the common space is entirely shaped by the model and is frozen during the brain mapping to it).
  • Consequence. BrainCLIP's space looks the same for a brain whose stimulus-related signal S is fully explained by the model and for a brain that carries additional private stimulus-related signal the model lacks (B=S+P), where B is the brain representation, S is the shared signal between model and brain representations and P is the private stimulus-related signal only the brain represents and the model lacks. Our latent retains that additional signal, and we show that it can be measured there.

Below in more detail:

1. Aim. BrainCLIP is an image decoding model. It is introduced as "a task-agnostic fMRI-based brain decoding model" that "transforms fMRI patterns into a well-aligned CLIP embedding space", and it is evaluated on zero-shot classification, retrieval and image reconstruction, with CLIP as its one target space. It does not compare networks as models of the brain, and we are not aware of work that uses a contrastive or joint-latent decoder of this kind as a score for ranking networks by their alignment with the brain. Model–brain comparison and benchmarks in the literature (Schrimpf et al., 2020; Conwell et al., 2024) rely mainly on linear mappings and on comparisons of representational geometry, which is why the submission is compared with ridge regression, RSA and CKA. Our paper asks whether a joint latent can serve as such a score: we define alignment read-outs in the latent and test them on representations whose relation to the reference network is controlled. A comparison with CCA/Procrustes, which are two methods that create a common space for model and brain representations and have been introduced in the literature as model-brain alignment measures has been done in Appendix I and described in point 1ii of the response to Reviewer Ybow. It shows that CCA gives a high score to a model representation of which only a small part is brain-like, which our method does not, and that Procrustes aligns model and brain only weakly.

AuthorsOpenReview ↗

Response to Reviewer nfGG (2/3)

As desribed also in our response Reviewer Ybow, our contribution, as stated in the Introduction, is not introducing an architecture that creates a common space between models and brains, but:

a) To propose the comparison of models and brains in a common space and derive metrics that quantify their alignment in a distributional and stimulus-specific level in that common space.

b) To show that this type of comparison (in a common space) and the derived distributional and stimulus-specific metrics are uncovering and expressing aspects of alignment that the standard metrics (ridge, RSA, CKA) do not capture. If constructed representations from foil models that haven’t been fed the images, or solve the task in mechanistically dissimilar ways with the brain (from planted pixels shortcuts, i.e., Carrier networks) can achieve most of RN50’s and RN50sc’s alignment score and all of CATownCAT_{own} and S-CATownS\text{-}CAT_{own} (RN50 representations that have some information removed, but still contain substantial RN50 information), doesn’t this make RN50 and RN50sc’s high alignment score less meaningful?

Our method uncovers and expresses different types of alignment compared to the standard metrics. In the distributional and stimulus-specific alignment that our method measures, RN50's or RN50sc's score cannot be achieved with a foil. Therefore, we claim that our introduced metrics express different aspects of alignment (in some cases more difficult to achieve a high score on, and this is why the foil models fail) that are meaningful and could potentially be what is needed to distinguish candidate models (architectures, training objectives) by their alignment with the brain in cases where other metrics saturate.

c) We have compared with other methods that create a common space and have been introduced in the literature as model-brain alignment measures (e.g. CCA/Procrustes). This analysis has been added in Appendix I and its key results are summarised in point 1 of the response to Reviewer Ybow.

2. Architecture. Our VAE trains four reconstruction pathways jointly (model→model, brain→model, brain→brain, model→brain) and places the model and all eight subjects in one 32-d latent. BrainCLIP-VAE trains two pathways, in sequence: an autoencoder of the model embedding is pre-trained and its decoder gets frozen (after this first training) and then one fMRI encoder per subject is trained so that its decoded output matches the model embedding (contrastive loss). Nothing reconstructs the brain, so a brain point can only take a position in the model's embedding space (512-d). This makes sense for BrainCLIP’s objective (image decoding) but for a model-brain alignment metric, the common space should also preserve stimulus-related brain structure that is not (necessarily) aligned with the model.

3. Test: a brain with stimulus-related signal that the model lacks.

To compare our method with BrainCLIP-VAE repurposed as an alignment measure, we re-implemented BrainCLIP (its training code is not public), trained it with each candidate model's embedding in place of CLIP's and scored it with the metrics we proposed in our work in the common 512-d model-brain space BrainCLIP creates. Results can be found in Appendix J in the revised pdf.

The main difference between the architectures is the presence of the brain→brain and model→brain pathways in our method that BrainCLIP lacks. To test whether the common space preserves stimulus-related brain structure that is not aligned with the model we construct the following experiment. We built synthetic brains from the real data (This follows the style of Model Recovery experiment we implemented as required by Reviewer Ybow. For the Model Recovery experiment see point 4. in response to Reviewer Ybow and Appendix Q), per subject, out of four parts:

  • S, shared with the model: the subject's real responses as linearly predicted from RN50.
  • R: simulating noise -- the real residuals of that prediction, reassigned to other images (real brain noise structure, no image information).
  • P, stimulus-related brain signal but absent from RN50: we take a signal from CLIP ViT-B/32 that is not overlapping with the RN50 signal. To assure this, we take part of CLIP ViT-B/32 image embeddings that RN50 cannot predict linearly (32 dimensions), written onto random voxel patterns, with the same image values in every subject.
  • N: white noise of similar total variance, as a P.

Brains: BS=S+RB_S = S + R (the model explains all stimulus-related signal); BSP=S+R+PB_{SP} = S + R + P (the model explains about half of it); BSN=S+R+NB_{SN} = S + R + N. Two further brains test the case in which the signal the model lacks dominates: BS5PB_{S5P}, with PP at five times SS's variance in each of its directions (PP is then 47% of the brain's variance on average and SS about a fifth of the stimulus-related signal), and BS5NB_{S5N}, with white noise of exactly that PP's variance in every voxel. RN50 is the model throughout.

AuthorsOpenReview ↗

Response to Reviewer nfGG (3/3)

4. Is the additional signal recoverable from the comparison space? We attempt to decode P linearly from each method's brain points (cross-validated R²). From our latent it is recoverable: .55 for BSPB_{SP} and .75 at BS5PB_{S5P}. From BrainCLIP-VAE's output it is largely not: .08 and .23, respectively.

5. Does identification between model and brain register it? No, in either method and in either direction: P lowers the model→brain top1 but the equivalent case with white noise of matched variance (instead of P) lowers it more, at every amplitude (Table below). So on this score P cannot be told from noise.

6. Identification (e.g. top-1) between subjects latent representations does, in our method. Our latent holds all subjects, so the same identification score that we are computing between model and subject representations can be computed between two subjects' latent points. With P in the brains this score rises, from 0.074 for BSB_S to 0.089 for BSPB_{SP} and 0.178 for BS5PB_{S5P}, while the model–brain score does not rise. Importantly, with noise instead of P both fall (0.063 for BSNB_{SN}, and 0.044 for BS5NB_{S5N}). Thus, the signal P that the brains share and the model lacks is visible as better matching top-1 between brains without better matching top-1 between brains and model. In BrainCLIP-VAE's output P lowers identification between subjects (0.121 to 0.113 for BSPB_{SP} and 0.101 for BS5PB_{S5P}), as does noise (0.105 for BSNB_{SN} and 0.075 for BS5NB_{S5N}. So BrainCLIP common space does not register the signal P that the subjects share and the model lacks.

In our latent iLISI falls with P (0.745 to 0.698 and 0.634) and does not fall with noise (0.792 and 0.806). So iLISI in our latent registers the presence of P. In BrainCLIP-VAE's output it falls slightly with both (0.431 to 0.411 with P at five times, 0.380 with the matched noise). In the following table we present the results.

BSB_SBSPB_{SP}BSNB_{SN}BS5PB_{S5P}BS5NB_{S5N}
added part (P or N), share of the brain's variance–P, 15%N, 17%P, 47%N, 47%
ours: P decodable (R²)–.55–.75–
ours: top-1, model → brain.284.267.243.218.170
ours: top-1, brain → model.280.260.234.211.160
ours: iLISI.745.698.792.634.806
ours: top-1, brain → brain.074.089.063.178.044
ours: median rank, brain → brain after removing the model43430843362435
BrainCLIP-VAE: P decodable (R²)–.08–.23–
BrainCLIP-VAE: top-1, model → brain.370.353.335.321.262
BrainCLIP-VAE: top-1, brain → model.337.320.300.281.215
BrainCLIP-VAE: iLISI.431.428.412.411.380
BrainCLIP-VAE: top-1, brain → brain.121.113.105.101.075
BrainCLIP-VAE: median rank, brain → brain after removing the model383382385378401

The last row of each block isolates this signal: we subtract from each subject's brain points what the model's points predict, and identify images between subjects from what is left. In our latent this is at chance without P and with noise (median rank 433–435 of 872) and improves as P grows (308, 62). In BrainCLIP-VAE's output it does not respond to P (378–401 for all five brains).

7. Conclusion. Because our method reconstructs the brain as well as the model, its latent is a space of two-way bidirectional alignment: it holds what the model explains of the brain but, also, the most prominent stimulus-related brain signal that the model does not explain. The same space therefore gives a score for the model and a measure of what the model misses (e.g. top-1 between subjects). BrainCLIP-VAE's space only contains what the brain shares with the model. The detailed analysis is on App. J

8. With the brain and the model weighted equally, the model–brain score itself registers the signal. Our loss has separate terms for reconstructing the model and the brain, so their weights can be set [point 3 in Reviewer Ybow response and App. H]. Top-1 between the model and the brain did not register the presence of P in the analysis above for our method trained as in the main analysis of our paper (the loss weights used allowed for the model to contribute more in shaping the latent). However, with balanced weights (brain and model shape the latent equally) top-1 between model and brain falls by 20% with P (BSPB_{SP}) and by 1% with white noise of similar variance (BSNB_{SN}) and by 50% for BS5PB_{S5P} and 12% for BS5NB_{S5N}, and top-1 between subjects doubles with P (.029 to .057) and does not change with noise (App.J, Table 14). Thus, our method allows for the flexibility to use loss weights that allow the brain to have bigger influence on the latent. Then, the presence of P is also registered in model-brain top-1, in addition to brain-brain top-1. BrainCLIP has no term that reconstructs the brain, and so no such choice.

Reviewer_YbowOpenReview ↗
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Paper summary

The paper proposes an idea for measuring representational alignment between brain and neural network models in the latent space of a variational autoencoder, jointly trained on representations extracted from both brain data and model. The validity of the method were examined under the setting of natural scene perception, specifically, via a published human fMRI dataset and an ImageNet-1K-trained ResNet-50, whose feature representations were artificially manipulated. Brain-model alignments were analysed using both the latent space and traditional methods, with their alignment readouts for different model manipulations compared using both latent-space metrics and traditional methods. The authors conclude that their latent-space alignment metrics are more sensitive to structural discrepancies between the brain data and model representations.

Critical strengths

The problem is well-posed, addressing an important open question in the field. Brain dataset selected here is well-suited for the purpose of this study. Different model manipulations applied here (training degradation, synthetic categories, foil models) are a nice design.

Critical weaknesses
  1. The basis of the paper, that is, analysing brain-model alignment in a shared brain-model latent space, has been purposed in earlier works. Notably, Papathanasiou et al. (2026) used the same autoencoder architecture with similar latent learning objectives, the same ResNet-50 reference model, and the same NSD dataset as brain data. The methodological overlap here seems substantial, yet not much was discussed in the paper. The authors should discuss prior works on latent-space brain–model alignment analysis in more detail and state clearly what is new here.
  2. The preprocessing of brain data was not clearly described in the paper. The authors stated that brain data are from the Algonauts 2023 dataset, yet key data cleansing details before latent space training, such as z-scoring, response averaging, hemodynamic function selection, etc., if any, are not explicitly explained.
  3. The latent space derived from VAE training is likely to be biased. During latent space learning, the model carries more training datapoints than the brain (~60k versus ~7k), and the model datapoints also have higher weights as training objectives than the brain datapoints due to their higher dimensionality (50k versus 20k). This effectively made the ResNet-50 model a scaffold in the shared latent space, which may affect the sensitivity of the alignment metrics applied.
  4. The validation experiments in the paper assumes that the ResNet-50 aligns better with the brain than any of its artificially manipulated variants, and the authors here argued that the latent-space metrics are valid because they reproduced the expected misalignments led by these artificial manipulations. This design does not truly justify that the latent-space metrics are useful, because the true representational structure of the human brain is not known. To rigorously show that the latent-space metrics are sensitive to discrepancies in representational structures, one should instead perform a model-recovery study, in which the brain data should be replaced by a known reference model with additional noise, and test whether the latent-space metrics can correctly identify that known model among its artificially manipulated variants or other models with different structures.
Questions for authors
  1. In the paper, only one brain dataset and one reference model were used for alignment analysis. Have the authors tested their latent-space metrics on other datasets and models?
8 comments
AuthorsOpenReview ↗

Response to Reviewer Ybow (1/4)

We thank the reviewer for their comments. Here are our responses to the four weaknesses mentioned and the extra analyses the reviewer’s comments prompted. Appendix, table and figure numbers refer to the revised paper.

1.i. Papathanasiou et al. (2026) and prior shared-space work

We build upon Papathanasiou et al. (2026), which used a multi-Encoder multi-Decoder VAE to align subjects with each other. In that work, the pretrained network was used as a common scaffold to overpass the need for common stimuli across subjects. Importantly, that work proposes no measure of how well a model matches the brain representations and is not introduced as a measure to compare model with brain representations. We are not aware of any work that proposes a multimodal VAE to bring model and brain representations into the same space with the aim of ranking different networks there regarding to their alignment with the brain. Usually architectures that create model-brain common spaces have different purposes, e.g., cross-subject alignment (Papathanasiou et al. 2026) and image decoding from fMRI signal (BrainCLIP, Liu et al., 2023). Model–brain comparison literature and benchmarks (Schrimpf et al., 2020; Conwell et al., 2024) rely mainly on linear mappings and on comparisons of representational geometry, which is why this work was compared with ridge regression, RSA and CKA.

The present work's contribution is to ask whether such a joint latent can serve as that measure: we define metrics in the common space that quantify the model-brain alignment. We construct cases where the standard metrics underperform and show what advantages (and extra notions of “alignment”, i.e., distributional and stimulus-specific) the comparison in a common representational space can offer and how this enables distinguishing between models that standard metrics score equally. The revision is stating this positioning in Related Work.

Thus, our contribution, as stated in the Introduction, is not introducing an architecture that creates a common space between models and brains, but:

a) To propose the comparison of models and brains in a common space and derive metrics that quantify their alignment in a distributional and stimulus-specific level in that common space.

b) To show that this type of comparison and the derived distributional and stimulus-specific metrics are uncovering and expressing aspects of alignment than the standard metrics (ridge, RSA, CKA) do not. If constructed representations from foil models that haven’t been fed the images, or that solve the task in mechanistically dissimilar ways with the brain (from planted pixels shortcuts, i.e., Carrier networks) can achieve most of RN50’s and RN50sc’s alignment score on a standard metric and all of CATownCAT_{own} and S-CATownS\text{-}CAT_{own} (i.e., RN50 representations that have some information removed, but still contain substantial RN50 information), doesn’t this make RN50 and RN50sc’s high alignment score less meaningful?

In the distributional and stimulus-specific alignment that our method measures, RN50’s and RN50sc’s score cannot be achieved with a foil. So, our thesis is not that our method is superior, but that it expresses different aspects of alignment, which in some cases are more difficult to achieve a high score on, and this is why the foil models fail. We believe these aspects are meaningful and could potentially be what is needed to distinguish candidate models (architectures, training objectives etc.) regarding their alignment with the brain in cases where other metrics saturate.

c) We have now compared with other methods that create a common space and have been introduced in the literature as model-brain alignment measures (e.g. CCA/Procrustes) and show that our method achieves superior results. This analysis has been added in Appendix I and some key results are summarised below.

AuthorsOpenReview ↗

Response to Reviewer Ybow (2/4)

1.ii Comparison with CCA (added in Appendix I)

CCA also places model and brain in a common space and in addition to its own metric (canonical correlation r), we can compute the metrics we proposed in this work in their aligned space. CCA common space identifies images well (RN50 top-1 0.568; full results in Table 9, latent visualisation of CCA space in Fig. 8, App. I). However, CCA whitens each side (model and brain). Every retained direction (after PCA cut) is rescaled to unit variance, so how much of the model representation a direction carries is discarded, and only the directions that correlate best with the brain are kept in the common space. Thus, CCA gives a model credit for whichever part of it correlates best with the brain, even when that part is only a small fraction of the model's representation. Our method works differently, since the latent space must also reconstruct the model's features (model→model and brain→model pathways), so a part of the model that carries a lot of its variance needs to be represented in the common space.

To test exactly that, namely if CCA score can be maximised if a model representation contains a brain-like subspace, no matter how small the part of the model representation that aligns with the brain is, in Appendix I.2, we constructed representations in which the model representation is controlled to be consisted of a meaningful RN50 signal and Null’s signal. We take Null (RN50's response to a different image) and add RN50's response to the true image at a gain that sets its share of the variance. When the true image's RN50 code is 8% of the mixed representation and the other 92% is about another image (Null), CCA scores it at 56% of the top-1 and at 82% on its own measure r of what RN50 itself achieves; when RN50 code is 11% of the share, at top-1 is at 80% and r at 93% of what the actual RN50 representation achieves. Our method's top-1 metric scores both at 1% of RN50, and rises only when the code is a large part of the representation (top-1 at 30% of RN50 at a 38% share, and RN50's level at 71% share) (Table 11, App. I.2). The reason is whitening: CCA rescales every retained direction to unit variance, so a direction that holds 1% of the variance counts as much as one that holds 50%. This is a known property: a measure that is invariant to invertible linear maps ignores the scale of directions and gives the same score to representations that match only in their small principal components (Kornblith et al., 2019). Our latent must also reconstruct the model's features, so a code enters it in proportion to its share.

2. Preprocessing of the brain data (added in Appendix C)

We did no preprocessing as the fMRI data was already preprocessed by NSD and by the Algonauts 2023 Challenge organisers. The revision describes it in full in Appendix C.

  • NSD (Allen et al., 2022): single-trial amplitudes estimated with GLMsingle. For every voxel the hemodynamic response function is selected from a library of 20, GLMdenoise noise regressors are added, and the amplitudes are regularised by ridge regression; the estimates are resampled to the fsaverage surface.
  • Algonauts 2023 (Gifford et al., 2023): visual-cortex vertices; every vertex z-scored within each scan session; the repeats of an image (one to three) are averaged.
  • Our use: we keep the ventral, lateral, midventral and midlateral streams (20,726–20,736 vertices per subject) and use the responses as distributed, with no further z-scoring, averaging, clipping or vertex selection. An image a subject did not see is not imputed, it is masked in that subject's encoder and decoder loss. Training uses the images each seen by one subject and every score is computed on the 872 images seen by all eight subjects, none of which is used in training.

3. "The ResNet-50 effectively becomes a scaffold" (added in Appendix H)

In our method, every training image pairs the model features with the one subject who saw it, so the model encoder sees all 62,551 training images and each subject's encoder 7,400–8,100.

Thus, each subject's own encoder and decoder receives fewer examples than the shared model encoder/decoder. However, over the eight subjects the brain contributes as many examples as the model, since each image is seen by exactly one subject. Thus, at least in respect to the number of the samples, the model and brain representation samples equally contribute to shaping the latent space.

Yet, the reviewer is right and there are other imbalances on the contribution of model vs. brain in shaping the latent space that come from training settings. In the loss per image, the model features carry ~51k variance units (model features are z-scored with variance 1) and the voxels ~11k on average (after the preprocessing the brain features have variance ~0.5), so the model loss terms outweigh the brain and the model is effectively used as a scaffold in the latent space as the Reviewer suggests.

AuthorsOpenReview ↗

Response to Reviewer Ybow (3/4)

3. Continuation of "The ResNet-50 effectively becomes a scaffold"

In Appendix H, to explore the effect of the model vs. brain losses in shaping the latent space and the sensitivity of our method’s metrics to the weight of the model vs. brain reconstruction losses, we retrained VAE with the two sides balanced (weights 1 for the model terms and 4.52 for the brain terms, KL weight scaled to keep its share comparable to the original one), everything else as in the paper. With this weighting the model and brain reconstruction losses contribute equally in variance. Table 8 in Appendix H gives the metrics for the paper’s main analysis vs. balanced weights comparison side by side and the visualization of the latent is in Fig. 7.

With balanced weights the brain shapes the latent space more than before, and the level of the scores changes. Identification of the references falls by almost half (RN50 top-1 0.321 to 0.179), because the latent now spends capacity on brain signal that the model does not explain. However, the ranking between the different cases of the main analysis (RN50, RN50sc, Ladders, and Foil models) remains unchanged (Table 8, App. H). On top-1, top-5, median rank and iLISI the order RN50 > RN50sc > CATownCAT_{own}, S-CATownS\text{-}CAT_{own} > foils is preserved. Despite the margins being narrower than with the paper's main analysis weights, the ordering does not depend on the model being the anchor in the latent space.

The ordering is the same with both weightings, so our conclusions do not depend on this choice. We view the weights of the model and brain losses as a hyperparameter, similarly to the latent dimensionality: when comparing different models regarding their alignment to a brain dataset, they should be compared with the same loss balancing between model and brain representations. We also view this parameter as a design choice, because it has a clear meaning: it sets how much the brain, relative to the model, shapes the common space, and our method allows to control this. With the paper's weights the model works as a scaffold. With balanced weights, more brain signal is hold in the latent.

We note that the scaffold cannot create alignment by itself. With the correspondence between images broken (Null), every latent read-out of our method is at chance. The size of the latent does not change the order either (Appendix G, Tables 6–7). With 64 and 128 dimensions instead of 32, no representation moves by more than .02 on top-1, and the ordering contrasts remain significant on identification.

4. Model recovery (added in Appendix Q)

We have added the model-recovery study as the reviewer describes, and the latent-space metrics pass it. They identify the known model among its manipulated variants and the foil models, and their scores fall step by step as a representation departs from that model (Appendix Q, Tables 21–22, latent visualisation in Fig. 12).

Before the model-recovery study, the order we assumed in the main analysis was checked by comparing the raw real brain representations with the RN50's and its artificially manipulated variants' representations. We showed that the similarity of category structure between the artificially manipulated variants and the brain representations decreases for every next step of the artificial manipulations, e.g., CATownCAT_{own}→ CATinCAT_{in}→ CAToutCAT_{out}. We computed similarities between categories, separately in the model and in the brain, and correlated them, asking two questions:

Are the categories that are alike in the model also alike in the brain? (For example, are cats closer to dogs than to balls in both?) For RN50 they are: the correlation with the brain's similarities between categories is 0.63. Swapping the categories lowers it to 0.54 when a category is exchanged with a related one (CATinCAT_{in}) and to −0.02 when it is exchanged with a random one (CAToutCAT_{out}) (Table 3, App. D.1).

Within one category, are the images that are alike in the model also alike in the brain? For RN50 the correlation is 0.167. It falls to 0.033 when only ten components of each image's detail are kept in CATownCAT_{own}, and to 0 when the detail comes from another image (either CATinCAT_{in} or CAToutCAT_{out}) (Table 4, App. D.1). The second ladder, built on supercategories, gives 0.153, 0.043 and 0 for RN50 → S-CATownS\text{-}CAT_{own} → S-CATdonorS\text{-}CAT_{donor}.

So every step of the ladders removes structure that RN50 measurably shares with the brain. More info on Appendix D.1 and point 1. in respone to Reviewer ZxfB.

Next, we take the model-recovery approach the reviewer suggested to rigorously show that the latent-space metrics are sensitive to discrepancies in representational structures. The brain data are replaced by a known reference model, namely RN50 with additional noise, and we test whether the latent-space metrics can correctly identify that known model among its artificially manipulated variants.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General summary response for the Area Chair and all Reviewers

We thank the reviewers for their comments, which prompted extra analyses that helped us improve the paper. This note briefly summarises our main responses, details are in the individual responses.

1. Advantage of our method (raised by Reviewer ZxfB). Our method expresses different types of alignment compared to the standard metrics. Aligning with the NSD, foil models (models mechanistically dissimilar to the brain computation) reach >100% of RN50's score on RSA, 77% on ridge and 76% on mixed RSA, against 9% on our method's top-1. Our method's metrics express different aspects of alignment, on which, in cases, a high score is harder to obtain (e.g., foil models failing on them). We believe these aspects are meaningful and may be what is needed to distinguish candidate models (architectures, training objectives, etc.) and address the saturation of other metrics, which is a well-reported problem in literature (Storrs et al., 2021; Conwell et al., 2024) or even to flag reward-hacking instead of real alignment (e.g. RL agents in videogames).

2. Novelty: Papathanasiou et al. (2026) and BrainCLIP (Reviewers Ybow and nfGG; App. J). We build upon Papathanasiou et al., who introduced a similar architecture to align subjects with each other. There, a pretrained network was used as a common scaffold to overpass the need for common stimuli across subjects. However, this work proposes no measure of how well a model matches the brain representations. Similarly, BrainCLIP is an image-decoding model. Neither of the two is proposed as a measure of model–brain alignment. For a direct comparison with BrainCLIP, we repurposed it as an alignment measure and constructed a case that shows our method's advantage. More in Appendix J.1 and response to Reviewer nfGG.

The present work's contribution is to ask whether a multimodal VAE's joint latent can serve as that measure: we define metrics in the common space that quantify the model-brain alignment. We construct cases where the standard metrics underperform and show what advantages (and extra notions of “alignment”, i.e., distributional and stimulus-specific) the comparison in a common representational space can offer and how this enables distinguishing between models that standard metrics score equally.

3. CCA and Procrustes (Reviewers Ybow and ZxfB; App. I). Both place model and brain in a common space. CCA whitens each side, so it credits the part of a model that correlates best with the brain, however small. When RN50's code for the image is only 8, 11 or 17% of a NULL representation (so the rest is about another image) CCA scores it at 56, 80 and 86% of RN50's top-1; our method at 1, 1 and 3% (Appendix I.2, Table 11; more in response 2/4 to Reviewer Ybow).

4. Loss weighting and latent size (Reviewers Ybow and ZxfB; App. G and H). Indeed the paper's weights make the model anchor the latent. We retrained with the model and brain loss terms balanced: the levels change (RN50 top-1 0.321 to 0.179), but the ranking of the paper's constructed cases is the same (Table 8, App. H). The latent size does not change the order either (App. G, Tables 6–7). We view the loss weights and the latent dimensionality as hyperparameters. When comparing different models, they should be compared with the same loss balancing between model and brain and latent dimensions. More on response 3/4 to Reviewer ZxfB

5. Model recovery (Reviewer Ybow; App. Q and R). We ran the study the reviewer asked for, in two forms. In both, the brain is replaced by synthetic data generated from a known network plus real noise, so the correct answer is known.

  • Among RN50's manipulated versions (Appendix Q). Our read-outs rank RN50 first of the 18 representations, in all eight subjects. RSA and dCKA rank it third, behind two foils. Mixed RSA and ridge identify it, but barely register the loss of image detail (they fall by 2% and 4% where our top-1 falls by 86%), and the best foil still reaches 66% and 70% of RN50's score (against 7% on ours) and CATownCAT_{own}, SCATownSCAT_{own} are scored below some of the foils (Table 21-22 App. Q, response 3-4/4 to Reviewer Ybow).
  • Among different architectures (Appendix R). Each of RN50, CLIP-RN50 and CLIP ViT-B/32 generates a brain, and all three are scored on each. Our method's metrics recover the generator on every brain, as do mixed RSA and ridge

6. Why each step of the corruption ladders should be scored lower (Reviewer ZxfB; App. D.1). For RN50 and each ladder rung, we measured how similar images are to each other in the model and in the brain, and correlated the two, between categories and within a category (are categories, or images of a category, that are alike in the model also alike in the brain?). Every step down the ladders lowers this model–brain agreement at one level or both, so it removes structure RN50 shares with the brain and should be scored lower. More on reply 1-2/4 to Reviewer ZxfB

7. 2nd dataset replication (BOLD5000, App. S).

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