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Under review as a conference paper at ICLR 2027

Rogue Dimensions Mask a Learned Cortical Trajectory of Visual Tokens in Vision–Language Decoders

Abstract

Vision–language models (VLMs) process image tokens with an entire language decoder, yet brain-alignment studies usually score the visual encoder, one layer, or the final hidden state. We trace the representational geometry of image-token positions after every decoder block of 13 open checkpoints (256M–10B parameters) and compare it with seven visual-cortex regions in eight Natural Scenes Dataset (NSD) participants and, for 10 checkpoints, nine participants of the independent Natural Object Dataset (NOD). Two depth patterns hold under the frozen correlation-distance protocol and under three feature-scaling controls, and are absent from depth-matched untrained decoders: alignment with the lateral stream rises over the first three quarters of the decoder (+0.040 to +0.046 of the noise ceiling), and early-cortex alignment falls in the last quarter (negative in 13 of 13 NSD checkpoints; participant-by-stimulus intervals exclude zero in 7), as does alignment with the other streams. The large change at the returned final state, which at image positions no later computation reads, is instead a measurement effect: three channels carry a median 83% of the energy of the mean image token at the last read state and 34% after the output normalization, and standardizing features shrinks the final lateral gain from +0.030 to +0.005. Feature scaling also decides which checkpoints appear to move from early toward lateral geometry (6 of 13 raw, 11 standardized). Endpoint directions agree across datasets in 19 of 20 cells under the frozen metric and in 14 with standardized features, where the lateral rise transfers and the early decline is uncertain on NOD. The depth decomposition was defined after inspecting the curves and is exploratory. Layer-wise VLM–brain comparisons should standardize features and report the last read state alongside final-layer scores.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
representational similarity analysis, vision–language models, Natural Scenes Dataset, visual cortex, lateral visual pathway, brain alignment

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

This empirical study examines how visual representations change across the language decoders of 13 open-weight vision–language models (VLMs). The authors extract hidden states at image-token positions, apply mean pooling, and use representational similarity analysis (RSA) to compare the resulting representations with neural representational dissimilarity matrices (RDMs) from seven visual cortical streams in NSD. The study presents interesting findings through a carefully designed analysis informed by established practices in neural data analysis. However, several issues concerning effect-size interpretation, anatomical specificity, representation readout, and cross-dataset consistency require clarification.

Critical strengths
  1. Insightful experimental design and careful statistical analysis. The authors use subjects as the unit of inference, avoiding pseudo-replication from treating model–subject pairs as independent observations. Reporting both checkpoint-weighted and lineage-balanced summaries also addresses unequal representation of model families. The bootstrap analyses are particularly valuable for an empirical study whose conclusions depend heavily on statistical reliability.

  2. Convincing diagnosis of rogue dimensions. The energy share of the top three channels increases from 23% to 83% and falls to 34% after normalization. Complementary controls—including feature standardization, top-three-channel removal, and rank transformation—strengthen this analysis. Depth-matched, randomly initialized decoders further support the interpretation that the observed patterns depend on learned weights.

Critical weaknesses
  1. The practical magnitude of the effects is unclear. The main effects are approximately 0.03–0.05 in units normalized by the lower noise ceiling, but the main text does not provide absolute noise ceilings, alignment at llm.00, or alignment at the visual encoder output. These references are necessary to judge whether the changes are substantial relative to baseline alignment. For example, Figure 2 appears to show limited alignment for most models, with intermediate improvements concentrated in two Qwen models before declining again. Please report raw RSA scores alongside normalized changes and relevant baselines.

  2. The emphasis on the lateral stream exceeds the evidence for anatomical specificity. Section 4.1, Table 2, and Figure 11 show similar changes in other higher-order streams. Supporting a specifically lateral trajectory would require analyses such as partial RSA or variance partitioning across ROIs. Otherwise, the title and abstract should describe the broader early-to-higher-order contrast.

  3. Mean pooling may obscure spatial information relevant to early visual cortex. Early visual cortex is retinotopically organized, whereas averaging image tokens discards their spatial arrangement. The late-layer decline in early-cortex alignment could therefore partly reflect a depth-dependent interaction between pooling and spatial information, rather than a general loss of alignment in the underlying representations. A spatially preserving readout, such as patch-position concatenation or spatially resolved RDMs, would help distinguish these explanations. Additionally, trimming the top 1% of tokens by norm does not disentangle channel-concentrated activations from activations concentrated at attention-sink positions; these mechanisms warrant separate controls.

  4. Statistical resolution is limited. None of the 26 checkpoint-level tests survive Holm correction. The panel-level adjusted (p=0.0156) also appears to reach the minimum attainable value for a two-sided exact Wilcoxon signed-rank test with eight subjects and correction across two tests, highlighting the coarse resolution of the inference. The authors acknowledge that their joint bootstrap does not implement the variance correction of Schütt et al. (2023). Given its availability in rsatoolbox, please explain why this procedure was not used and, preferably, report it as a robustness check.

  5. The NSD–NOD differences need targeted analysis. Wider intervals on NOD are primarily attributed to its smaller stimulus set (120 versus 515 images), but the effects of stimulus count, signal quality, and other dataset differences are not separated. More importantly, standardization improves directional consistency on NSD—early-cortex endpoint decreases rise from 9/13 to 13/13 models—but reduces it on NOD, where only 6/10 models show decreases. Cross-dataset directional agreement also falls from 19/20 to 14/20 comparisons. This complicates the interpretation that standardization better reveals the relevant representational geometry. The absence of three models from NOD—PaliGemma2-10B, Idefics2-8B, and Qwen2-VL-7B—may further affect the comparison, as these models generally show pronounced early-cortex declines on NSD. Three analyses would help: (a) repeatedly subsample NSD to 120 images and assess interval widths and directional consistency; (b) report absolute ROI-level noise ceilings for both datasets; and (c) recompute NSD panel summaries using only the ten models shared with NOD.

Questions for authors

Please refer to the weakness.

2 comments
AuthorsOpenReview ↗

Response to Reviewer nLyM (1/2)

Response (1/2)

We thank the reviewer for a detailed and constructive review. Every request led to a new analysis, computed from the released artifacts and caches; the revised PDF marks all changes in red (new Sec. 4.5 and Appendix B). Part 1 covers W1–W3, Part 2 covers W4–W5.


W1. Practical magnitude: raw RSA, noise ceilings and baselines

Sec. 4.1 now states the raw scale, and Appendix B.1 gives ceilings for all seven streams in both datasets (Table 3), raw ρ\rho per stream (Table 4) and per checkpoint (Table 5). NSD panel means, 13 checkpoints:

streamllm.000.75peakL−1L-1LLceiling (lower / upper)
early0.1010.1000.1120.0840.0870.50 / 0.64
lateral0.1190.1380.1500.1190.1330.46 / 0.61
ventral0.2390.2680.2890.2330.2590.71 / 0.78

In raw units the lateral rise to 0.75 depth is +0.019+0.019 and the early last-quarter decline −0.016-0.016, each about 16% of the llm.00 value. Peaks reach 22–41% of the lower ceiling. NOD's lower ceilings are 3–4× lower (early 0.13, lateral 0.16, parietal 0.03); Appendix B.1 now notes that ceiling-scaled NOD parietal values are therefore not interpretable.

Baselines.

  • Vision-encoder output (new, Table 13). llm.00 is slightly above the last encoder layer (+0.036 early, +0.052 lateral, fraction of ceiling). The decoder's peak lateral alignment exceeds even the best encoder layer in 9/11 checkpoints (+0.045; standardized 10/11, +0.051). Early-cortex alignment is highest in intermediate encoder layers, about 0.10 above any decoder state, and is lost in the encoder's final layers.
  • Untrained depth-matched decoders (Sec. 4.4) show neither depth pattern.

On Fig. 2 and the Qwen models. The lateral rise is positive in 10/13 checkpoints; the largest rises are SmolVLM-2.2B, Qwen2-VL-2B, InternVL3-2B and SmolVLM-500M. Without the three Qwen checkpoints the panel still shows both patterns in 8/8 participants: lateral rise +0.035+0.035 raw / +0.052+0.052 standardized, early decline −0.024-0.024 / −0.014-0.014. The standardized early decline is about a third as large without Qwen, so the Qwen checkpoints do carry much of its size.


W2. Lateral specificity

We agree. Partial Spearman correlations per participant (model RDM vs one region's RDM, controlling for other regions' RDMs; 11 checkpoints; Sec. 4.5, Table 12):

target ∣\mid controlssteprawstandardized
lateral ∣\mid earlyllm.00→0.75+0.018+0.018, 8/8+0.024+0.024, 8/8
lateral ∣\mid early + ventralllm.00→0.75+0.001+0.001, 5/8+0.008+0.008, 7/8
early ∣\mid all six others0.75→L−1L-1−0.005-0.005, 7/8−0.011-0.011, 8/8

The rise is shared with the ventral stream, so it is a higher-order occipitotemporal pattern, not a lateral one. The abstract, introduction and discussion now say so; the title does not name the lateral stream. The late decline, by contrast, is specific to early cortex.


W3. Mean pooling, retinotopy and attention sinks

Retinotopy. We agree that mean pooling discards spatial layout. Sec. 3.2 and the Limitations now state that our early-cortex scores concern image-level geometry, not retinotopy. A spatially resolved readout needs per-token activations, which our caches do not store; we will add it for the checkpoints with fixed token grids in the final version. The readout dependence the reviewer suspects is real in one form we could test: at the generation position the late early-cortex trend reverses (Sec. 4.5). The claim is now restricted to the mean over image positions.

Channels vs positions. These are now separated (NSD panel; raw mean pooling gives lateral rise +0.040+0.040, early decline −0.032-0.032):

controltargetslateral riseearly decline
standardized featureschannel scale+0.046+0.046−0.038-0.038
top-3 channels removedchannel concentration+0.045+0.045−0.019-0.019
trimmed mean (top 1% tokens by norm dropped)high-norm positions+0.040+0.040−0.031-0.031
median poolingoutlier positions+0.041+0.041−0.027-0.027

Both patterns survive every control. Trimming selects positions by norm, not by attention mass; a sink definition based on attention mass is a better position control, and we will add it.

(continued in Part 2)

AuthorsOpenReview ↗

Response to Reviewer nLyM (2/2)

Response (2/2)

W4. Statistical resolution and the Schütt et al. (2023) bootstrap

We agree on both points. The panel pHolm=0.0156p_{\text{Holm}}=0.0156 is indeed the floor for an exact two-sided signed-rank test with n=8n=8 and two tests. It says only that all eight participants agree; magnitude comes from the bootstrap intervals. Checkpoint-level tests are now labeled descriptive and panel summaries confirmatory (Secs. 3.4, 4.1).

Why it was not used. The inference plan (signed-rank tests plus an ordinary crossed bootstrap) was frozen before the corrected analysis, and we listed the missing variance correction as a limitation rather than change the test after seeing results.

Result. We now report it (rsatoolbox eval_dual_bootstrap with its correction, participants and images resampled jointly, each checkpoint's readouts as fixed models, pairwise ρA\rho_A tests, 200 bootstrap samples; Appendix B.7, Table 14):

step (11 checkpoints)raw: claimed direction / p<0.05p<0.05 / Holmstandardized
lateral llm.00→0.758 / 7 / 69 / 9 / 4
early 0.75→L−1L-111 / 6 / 310 / 7 / 4

(Holm over 22 checkpoint × step tests per metric.) With this test, checkpoint-level effects become resolvable at n=8n=8. The early decline is never significant in the opposite direction. The lateral step is so in one checkpoint per metric: PaliGemma2-3B-mix (raw, Holm-significant) and Qwen2.5-VL-3B (standardized, not Holm-significant). The revised text reports this heterogeneity.


W5. NSD–NOD differences

(a) NSD subsampled to 120 images (1,000 random subsets, with brain RDMs, ceilings and model RDMs recomputed; Table 9):

  • Interval width. The panel's early last-quarter decline ranges across subsets from −0.046-0.046 to −0.017-0.017 (2.5–97.5%, raw). This range is as wide as NOD's participant interval (−0.051-0.051 to −0.016-0.016), but it never crosses zero.
  • Directional consistency. Subsets reproduce the full-NSD checkpoint signs of this step in a median of 9/10 checkpoints (95%: 7–10). NOD matches NSD in 6/10 under standardization, below that range.
  • Ceilings. NSD's lower ceiling is unchanged at 120 images (early 0.50 [0.46, 0.54]).

Image count therefore does not explain the NOD differences, and Sec. 4.2 no longer attributes them to the smaller stimulus set.

(b) Absolute ceilings (lower, NSD vs NOD; Table 3): early 0.50 vs 0.13, lateral 0.46 vs 0.16, ventral 0.71 vs 0.25, parietal 0.36 vs 0.03. NOD's reliability is 3–4× lower in every stream. Together with its acquisition differences (scanner, field of view, preprocessing), this is the likely source of the NSD–NOD differences. Two datasets cannot separate these factors, and the text says so.

(c) NSD restricted to the 10 shared checkpoints (Tables 6–7) gives the same picture as the full panel. Raw: early endpoint 7/10 negative, −0.022-0.022 [−0.027,−0.017-0.027, -0.017]; lateral 8/10 positive, +0.037+0.037; last-quarter early decline 10/10, all 8 participants. Under standardization the early endpoint is negative in 10/10 on NSD but 6/10 on NOD for the same checkpoints. The three missing models therefore do not cause the divergence.

Standardization. We agree this complicates any claim that standardization "reveals" the right geometry, and we do not make it. Standardization is a control for channel scale. We claim only patterns that survive all four feature treatments, and recommend reporting a scale-invariant metric beside raw RSA, not instead of it. Under standardization the NOD last-quarter early step remains negative at the participant level (−0.024-0.024 [−0.038,−0.012-0.038, -0.012], 8/9), but its checkpoint signs agree with NSD in only 6/10. We report this as a genuine dataset difference, and Sec. 4.4 states that NOD does not replicate the checkpoint-level pattern.

We thank the reviewer again; these analyses sharpened the claims, especially on regional specificity, and we are happy to provide further detail.

Reviewer_pxVkOpenReview ↗
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Paper summary

The authors investigate how visual-token representations in VLM decoders align with different regions of human visual cortex, using representational similarity analysis (RSA) across 13 checkpoints and two datasets. The overall experiments provide useful empirical findings. However, early-cortex alignment decline is not well supported across datasets, and the depth decomposition is more about post-hoc analysis. Furthermore, the novelty, compared to existing layer-wise VLM-brain alignment studies, seems limited. The manuscript also has some formatting issues, e.g., the title's font does not match that from official ICLR template.

Critical strengths

The paper provides a systematic VLM-brain alignment analysis across different VLMs and two fMRI benchmarks, supported by multiple experimental controls. Some observations are insightful. E.g., the finding that rogue dimensions can distort final-layer alignment measurements.

Critical weaknesses
  1. Robustness of findings is limited across datasets. Late decline in early-cortex alignment is not supported on NOD. Furthermore, cross-dataset directional agreement drops from 19/20 to 14/20, after standardization, weakening the generalizability of the findings.
  2. Limited novelty and reliance on post-hoc analysis. Prior work has already studied layer-wise alignment between VLMs and brain responses (Bavaresco et al., 2026; Oota et al., 2025) , as well as how rogue dimension distort representational similarity measures in LLMs (Timkey & van Schijndel, 2021). This paper combines these existing points with a post-hoc depth decomposition, limiting its novelty.
Questions for authors
  1. What evidence can support the generalizability of the decline of early-cortex alignment, since it's not certain on NOD?
  2. What insights can the depth decomposition provide, rather than just verifying previous studies?
2 comments
AuthorsOpenReview ↗

Response to Reviewer pxVk (1/2)

Response (1/2)

We thank the reviewer for a critical and precise review. Both weaknesses point to real limits of the submission. Below we answer them together with the two questions, in two parts (W1/Q1 here; W2/Q2 in Part 2). All new analyses use the released artifacts and caches; the revised PDF marks every change in red (new Sec. 4.5 and Appendix B).


W1 / Q1. Is the late decline of early-cortex alignment general?

What we claim. The claim is the last-quarter step (0.75 depth → L−1L-1, the last image-token state that generation reads) at image-token positions. It is not a claim about the endpoint L−llm.00L-\texttt{llm.00}, which includes the unread final state that the paper shows is distorted by scaling. The evidence for this step:

(a) NOD, participant level. The step is negative under both metrics:

NOD, early cortex, 0.75 → L−1L-1panel mean [95% participant CI]participants < 0checkpoints < 0Wilcoxon pp
raw features−0.033-0.033 [−0.051,−0.016-0.051, -0.016]8/99/100.012
standardized−0.024-0.024 [−0.038,−0.012-0.038, -0.012]8/97/100.008

What is uncertain on NOD, as the abstract states, is the joint participant × stimulus interval, which includes zero.

(b) NOD's uncertainty is not explained by its image count. We cut NSD to NOD's size: 1,000 random 120-image subsets, with brain RDMs, noise ceilings and model RDMs recomputed on each (Appendix B.2, Table 9).

  • The panel's last-quarter early decline is negative in 100% of subsets under both metrics (median −0.031-0.031 raw, −0.037-0.037 standardized).
  • NSD's lower ceiling is unchanged at 120 images (early 0.50 [0.46, 0.54]).
  • NOD's lower ceilings are 3–4× lower in every stream (early 0.13; Table 3).

NOD's wider intervals therefore track its lower reliability, together with its other differences (scanner, field of view, preprocessing). Two datasets cannot separate these factors, and the Discussion now says so.

(c) The step is robust across checkpoints, statistics and analysis choices (NSD unless stated):

  • Checkpoints. The step is negative in 13/13 checkpoints (raw) and 12/13 (standardized).
  • Per-checkpoint tests. We ran the variance-corrected dual bootstrap of Schütt et al. (2023), resampling participants and images jointly (Appendix B.7, Table 14). The step goes in the claimed direction in 11/11 checkpoints (raw) and 10/11 (standardized), and is never significant in the opposite direction.
  • Specificity. The step is specific to early cortex: it survives partialling out all six other streams (−0.005-0.005 raw, 7/8 participants; −0.011-0.011 standardized, 8/8; Sec. 4.5, Table 12).
  • Pooling. It is unchanged under trimmed-mean pooling (which removes attention-sink tokens) and median pooling, on both datasets (Table 11).
  • Boundary. It holds for every boundary from 0.50 to 0.90 (Table 10).
  • Trained weights. It needs trained weights. In depth-matched untrained decoders the step is −0.001-0.001 raw and −0.003-0.003 standardized, against −0.026-0.026 and −0.039-0.039 for the same trained checkpoints (Sec. 4.4).

(d) A limit we now state. The decline is a property of image-token positions. At the generation position of the same forward passes, early-cortex alignment rises over the last quarter: +0.013+0.013 raw and +0.019+0.019 standardized, in all 8 participants, for the eight checkpoints up to 3B (Sec. 4.5, Table 15). The revised abstract and Sec. 4.5 restrict the claim accordingly.


W1 (cont.). Cross-dataset agreement drops from 19/20 to 14/20 after standardization

This is correct, and we now report agreement for every step, not only the endpoint (Appendix B.2, Table 8):

early + lateral cells, 10 shared checkpointsrawstandardized
endpoint L−llm.00L-\texttt{llm.00} (paper)19/2014/20
last read state L−1−llm.00L-1-\texttt{llm.00}16/2013/20
claimed patterns (lateral llm.00 → 0.75; early 0.75 → L−1L-1)18/20 (9 + 9)14/20 (8 + 6)

Where the drop comes from. Under standardization, the lateral rise transfers in 8/10 checkpoints but the early decline in only 6/10. SmolVLM-256M, InternVL3-2B, PaliGemma2-3B and InternVL3-8B show a small positive early step on NOD.

Why this is a real dataset difference. 120-image NSD subsets reproduce the full-NSD sign of this step in a median of 9/10 checkpoints (95% of subsets: 7–10). NOD's 6/10 lies below that range, so the disagreement is a genuine NSD–NOD difference for these checkpoints, not image-sampling noise.

How the paper now treats it:

  • The panel-level decline is present in both datasets; the checkpoint-level pattern does not replicate on NOD.
  • Checkpoint-level directions are presented as descriptive and participant-level panel tests as the confirmatory evidence (Secs. 3.4, 4.1).
  • Sec. 4.4 and the Discussion now say explicitly that NOD does not replicate the checkpoint-level pattern.

(continued in Part 2)

AuthorsOpenReview ↗

Response to Reviewer pxVk (2/2)

Response (2/2)

W2. Novelty relative to Bavaresco et al. (2026), Oota et al. (2025) and Timkey & van Schijndel (2021)

We agree that layer-wise VLM–brain comparison, and the fact that rogue dimensions distort similarity, are not new. We have rewritten the contribution paragraph (Introduction) as findings that these designs do not test:

  • Bavaresco et al. run RSA on the hidden states of concept-word text tokens (180 Pereira words) in the language network and high-level visual regions, and summarize each model by its best layer. They do not read image-token positions, include early visual cortex, analyze depth trends, or test the final layer or feature scaling.
  • Oota et al. fit voxel-wise encoding models to NSD from averaged hidden states of generated text-response tokens. In all three of their models, late layers predict early visual regions best. (Our submission said "two of three"; this is corrected on p. 2 and in the Discussion.) Our new generation-position analysis reproduces their pattern inside our models, while image positions of the same forward passes show the opposite late trend. The two results are compatible, and where the readout is taken decides which one a study sees. This is a new result, not a re-verification.
  • Timkey & van Schijndel show that a few dimensions dominate similarity within language models; our standardization control follows their remedy, and we cite them in Sec. 4.4. What is new is the consequence for model–brain comparisons:
    • (i) At image positions, the final layer that layer-wise studies score is a state no later computation reads. Its alignment jump is mostly scaling: three channels carry a median of 83% of the mean token's energy at L−1L-1, and the terminal lateral gain shrinks from +0.030+0.030 to +0.005+0.005 under standardization.
    • (ii) Scaling decides which checkpoints look brain-like: the early→higher-order pattern holds in 6/13 checkpoints with raw features and in 11/13 with standardized features.

W2 / Q2. The depth decomposition is post hoc. What does it show beyond verifying prior work?

On being post hoc. The L−1L-1 / LL split is fixed by the computational graph: no block reads image positions after the last one. Only the 0.75 boundary was chosen after inspection, and both patterns hold for every boundary from 0.50 to 0.90 (Table 10). The decomposition stays labeled exploratory; the frozen endpoint remains the primary estimand.

What it shows that an endpoint or best-layer score cannot:

  1. It separates the read state from the unread one. Under the raw metric, the NSD panel's lateral gain measured at L−1L-1 is −0.001-0.001 [−0.016,+0.014-0.016, +0.014]. The entire endpoint gain sits in the unread state, and standardization removes most of it. A study that scores the last layer, or picks a best layer that includes it, inherits this artifact.
  2. It finds a decline the endpoint hides. Early-cortex alignment falls over the last quarter in 13/13 checkpoints, although the endpoint is negative in only 9/13. In the SmolVLM checkpoints, for example, an earlier rise and the terminal rebound mask it. 89% of the panel's early decline accumulates after 0.75 depth.
  3. It resolves an apparent conflict with prior work. Applied at the generation position, it reproduces Oota et al.'s late early-cortex alignment; at image positions it shows the opposite (Q1-d).
  4. It locates where alignment is gained and lost. The decoder's peak lateral alignment exceeds the best vision-encoder layer before the projector in 9/11 checkpoints (+0.045 of the ceiling). Early-cortex alignment peaks inside the encoder and is lost in its final layers, not at the projector (Sec. 4.5, Table 13).
  5. It shows that both patterns are learned. Depth-matched untrained decoders show neither the rise (lateral −0.029-0.029 vs +0.045+0.045 trained, raw) nor the late decline.

Formatting

The title is now set in the unmodified ICLR 2027 template style (we had wrapped it in \textbf).

We hope these analyses and the narrowed claims address the reviewer's concerns, and we would be glad to discuss any remaining point.

Reviewer_UCKDOpenReview ↗
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Paper summary

This paper investigates how the similarity between visual token representations in the VLM decoder and human visual cortical representations changes across decoder depth. The authors analyze 13 VLM checkpoints and use fMRI data from the NSD and NOD datasets. They apply global mean pooling to the hidden states of visual tokens at each decoder layer to obtain image representations, construct representational dissimilarity matrices (RDMs), and compare them with seven visual cortical regions using representational similarity analysis (RSA).

Critical strengths
  1. This paper extends previous layer-wise brain alignment analyses, which mainly focused on the vision encoder, to the VLM decoder. It investigates how the similarity between visual representations and different human visual cortical regions changes across decoder depth, providing a new perspective.
  2. The experiments cover 13 VLM checkpoints with different model architectures and parameter sizes. The authors also use two human fMRI datasets, NSD and NOD, providing a broad experimental evaluation.
Critical weaknesses
  1. Limited novelty. Previous works, such as Bavaresco et al. (2026), have already investigated RSA alignment between VLM and human brain representations. Oota et al. (2025) also analyzed the alignment between different VLM layers and human visual cortical regions. Building on these studies, this paper further analyzes how the similarity between visual token representations in the decoder and human brain representations changes across depth. I think the overall novelty of this work is relatively limited.
  2. The effectiveness of visual token mean pooling needs further validation. This paper uses mean pooling to aggregate the visual token hidden states at each layer as the image representation. This approach assigns equal weight to all visual tokens. However, as far as I understand, models may selectively attend to different visual regions depending on the specific task. Therefore, it is unclear whether simply averaging all visual tokens can effectively represent visual information in the decoder. Although the authors conduct robustness experiments using trimmed-mean pooling and other pooling methods, these methods still do not fully account for the differences in importance among visual tokens.
Questions for authors
  1. Could the authors further clarify the main differences between this work and previous studies, such as Bavaresco et al. (2026) and Oota et al. (2025)?
  2. Could the authors further explain why global mean pooling is used to represent visual information at each decoder layer?
1 comment
AuthorsOpenReview ↗

Response to Reviewer UCKD

We thank the reviewer for the positive assessment and for two questions that pointed to what most needed sharpening. The revised PDF marks changes in red (new Sec. 4.5 and Appendix B).


W1 / Q1. Differences from Bavaresco et al. (2026) and Oota et al. (2025)

We agree that layer-wise VLM–brain comparison is not new and that our contribution paragraph read as a list of components; the revised Introduction states it as findings. The designs differ:

Bavaresco et al.Oota et al.ours
stimuli180 concept words (Pereira et al.)NSD imagesNSD + NOD images
model readoutconcept-word text tokensgenerated text-response tokensimage-token positions after every decoder block
cortexlanguage network, high-level visualearly and category-selective7 visual streams, incl. early
depthbest layer per modellayer-wise encodingfull trajectory, read vs unread states

The findings these designs do not test:

  1. The final layer measures an unread state. At image positions the returned state LL feeds no later computation, and its alignment jump is mostly scaling. Three channels carry a median of 83% of the mean token's energy at L−1L-1; standardizing features shrinks the terminal lateral gain from +0.030+0.030 to +0.005+0.005. A study that scores the last layer, or picks a best layer that includes it, inherits this effect.
  2. Feature scaling decides which models look brain-like. The early→higher-order pattern holds in 6/13 checkpoints with raw features but 11/13 with standardized ones.
  3. Two learned depth patterns. Alignment with higher-order occipitotemporal cortex rises over the first three quarters of the decoder. Alignment specific to early cortex (it survives partialling out all six other streams) falls in the last quarter. Neither appears in untrained depth-matched decoders.
  4. The readout position decides the late early-cortex trend (new). Oota et al. find that late layers best predict early visual regions in all three of their models; our submission misreported this as "two of three", which is now corrected. At the generation position, where the first answer token is decoded, we reproduce their pattern; image positions of the same forward passes show the opposite (8 checkpoints; Sec. 4.5, Tables 15–16):
early cortex, 0.75 → L−1L-1image-token meangeneration position
raw−0.027-0.027 (8/8 participants fall)+0.013+0.013 (8/8 rise)
standardized−0.041-0.041 (8/8 fall)+0.019+0.019 (8/8 rise)

The results are compatible (Oota et al. average generated tokens; ours is the step before the first).

  1. Where alignment comes from (new). The decoder's peak lateral alignment exceeds the best vision-encoder layer before the projector in 9/11 checkpoints. Early-cortex alignment is highest in intermediate encoder layers and is lost in the encoder's final layers (Table 13).

W2 / Q2. Why mean pooling, and token importance

Why the mean.

  • Comparability. Token grids differ across the 13 checkpoints (fixed grids, pixel-shuffle, dynamic resolution), so no spatially indexed readout is comparable across all of them. The mean is invariant to token count and matches the image-level brain RDMs.
  • Cost. Spatial layout is lost, so early-cortex scores concern image-level geometry, not retinotopy; Sec. 3.2 and the Limitations now say so.

Task-dependent selection. We agree that models weight visual regions by task, but in our setting that weighting cannot occur in the image-token states. The primary condition uses an empty prompt. In the usual layout (image, then question), causal attention prevents image tokens from attending to the question, so their states are identical for any task; we verified that they are bitwise identical across prompts. Task-dependent selection happens at the text positions that read the image. PaliGemma2, a prefix language model, is the exception.

An importance-weighted readout. The generation position is exactly such a reader: it aggregates the image tokens through the model's own learned, content-dependent attention. At that position:

  • the higher-order rise holds and is larger (lateral +0.19+0.19 vs +0.06+0.06 of the ceiling, raw; measured from llm.01, where that position first depends on the image);
  • the late early-cortex trend reverses.

Token weighting therefore matters for early cortex, and we now restrict the early-cortex claim to the mean over image positions.

Unweighted alternatives. Trimmed-mean pooling (the 1% highest-norm tokens removed, which excludes high-norm attention-sink tokens) and median pooling leave both patterns unchanged in both datasets and both metrics (Table 11). Spatially or task-indexed readouts need new forward passes; we will add them for fixed-grid checkpoints in the final version.

We thank the reviewer again and would be glad to clarify further.

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Summary of the revision (to all reviewers and ACs)

Summary of the revision

We thank all reviewers for careful and constructive reviews. We have uploaded a revised PDF in which every change is marked in red (hyperlinks stay blue). The main text remains within 10 pages. All new analyses use the released result artifacts and representation caches; no new extraction or model training was needed.

Main new results

  • NOD vs NSD. NOD's wider intervals are not explained by its image count. In 1,000 random 120-image NSD subsets the last-quarter early-cortex decline is negative in every subset and NSD's noise ceilings are unchanged; NOD's ceilings are 3–4× lower in every stream. On NOD the decline is negative in 8/9 participants under both metrics, but checkpoint signs agree with NSD in only 6/10 after standardization, which we now report as a genuine dataset difference (pxVk, nLyM).
  • Regional specificity. Partial correlations show that the rise is shared by the lateral and ventral streams, so we now call it higher-order occipitotemporal. The late decline is specific to early cortex (nLyM).
  • Readout position. At the generation position, early-cortex alignment rises late, reproducing Oota et al. (2025), whereas at image positions of the same forward passes it falls. The early-cortex claim is now restricted to image-token positions (UCKD, pxVk).
  • Vision-encoder baseline. The decoder's peak lateral alignment exceeds the best encoder layer before the projector in 9/11 checkpoints (nLyM).
  • Checkpoint-level inference. The variance-corrected bootstrap of Schütt et al. (2023) resolves checkpoint-level effects at n=8n=8. The early decline is never significant in the opposite direction (nLyM).

Changes to the main text

  • Title: set in the unmodified template style (pxVk).
  • Abstract, Introduction: contribution stated as findings, not components; "higher-order occipitotemporal" for the rise; early decline restricted to image positions (all reviewers).
  • Related work, Discussion: Oota et al. (2025) corrected from "two of three" to "all three" models; readouts of Bavaresco et al. (2026) and Oota et al. stated (UCKD, pxVk).
  • Sec. 3.2: why mean pooling; it discards retinotopy; trimmed mean removes high-norm sink tokens (nLyM, UCKD).
  • Secs. 3.4, 4.1: checkpoint-level tests descriptive, panel tests confirmatory; raw RSA scale and ceilings (nLyM).
  • Sec. 4.2: NOD uncertainty no longer attributed to image count (pxVk, nLyM).
  • Sec. 4.3: only the 0.75 boundary was chosen by inspection; results for boundaries 0.50–0.90 (pxVk).
  • Sec. 4.4:
    • the parietal stream groups with early cortex;
    • the remaining exceptions after standardization are named;
    • NOD does not replicate the checkpoint-level pattern.
  • New Sec. 4.5: regional specificity, readout position, vision encoder.
  • Discussion / Limitations: NOD is not a replication; retinotopy, no text-only baseline, and coverage of the new analyses.

Changes to the appendix

  • Existing appendix:
    • Table 1 caption names the bootstrap used for bold values;
    • A.2 now describes the regions;
    • A.10 now reports the outcomes of the listed controls.
  • New Appendix B (Tables 3–16):
    • B.1 raw RSA and noise ceilings, both datasets;
    • B.2 NSD–NOD per-step comparison, the 10 shared checkpoints, and 120-image NSD subsets;
    • B.3 boundary sweep;
    • B.4 token pooling;
    • B.5 partial correlations;
    • B.6 vision-encoder layers;
    • B.7 Schütt et al. bootstrap per checkpoint;
    • B.8 generation-position readout.

We are grateful for the reviewers' time; the requested analyses have made the claims narrower and better supported.

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

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