- Rating
- 1
- Confidence
- 4
- Informativeness
- 1
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This paper compares layer-wise visual-textual fusion in two MLLM families: concatenation models (LLaVA-NeXT Vicuna/Mistral, Cambrian) and native models (SOLO, EVE, SAIL). The authors analyze cross-modal and intra-modal CKA, attention routing and entropy, and intrinsic dimensionality. Two interventions (i.e., masking text tokens on POPE and injecting layer-specific noise on MMBench) further validate their findings. They conclude that concatenation models follow a text-first, vision-later pathway, whereas native models exhibit earlier cross-modal co-adaptation. Cross-model visual CKA is also examined in relation to the Platonic Representation Hypothesis.
Critical strengths
-
[S1] The research question is clear and relevant. Most work on MLLM internals focuses on concatenation architectures, and comparing native, encoder-free models against them within a single layer-wise framework is a less explored and worthwhile direction.
-
[S2] The analysis design is methodologically reasonable in principle. The paper combines representation similarity, attention statistics, and intrinsic dimensionality rather than relying on a single score, is explicit about what each measure can and cannot reveal, and attempts to move from representational observations to interventions, which is appropriate for a mechanistic claim.
-
[S3] The paper includes robustness checks that are often omitted: bootstrap resampling with standard errors and relative bias (Appendix A.6), intrinsic-dimensionality results under multiple variance thresholds (Appendix A.4), and a Mutual KNN analysis as a local-structure complement to CKA (Appendix A.1). The writing is clear, and the authors are candid about the limits of their comparison and about SAIL as an exception.
Critical weaknesses
[W1] The evidence for the central claim is confounded and lacks controls.
-
(a) Asymmetric reference representations. The conclusion that native models “change their visual representations earlier” (Figures 3 and 5) rests on comparisons against the layer-0 representation. For concatenation models, layer 0 already contains semantic features produced by CLIP (or CLIP+DINO) and the projector, whereas for encoder-free native models it is close to a raw patch embedding. Figure 5 makes this explicit: the visual intrinsic dimension starts at 6 for EVE and at 30 for Cambrian. The early change observed in native models may therefore reflect the construction, inside the LLM, of visual features that CLIP already provides, rather than a difference in fusion pathway. The paper does not rule out this simpler explanation. One way to address it would be to re-align native models to the layer at which their visual representations reach a CLIP-level semantic structure and compare from there.
-
(b) No control for the POPE masking experiment. In Table 1, masked F1 scores fall to 36.3 to 53.8%, which is at or below chance for a binary task. This suggests that the question inputs themselves are damaged. Without a control that masks the same number of randomly chosen text tokens, the observed drop cannot be attributed to the functional importance of “concentrated textual anchors” rather than to input corruption in general.
-
(c) Imbalanced perturbation ranges. In Table 2, the early range covers layers 0 to 7 (8 layers) and the late range covers layers 16 to 32 (17 layers), so the total perturbation differs by more than a factor of two. The noise magnitude and the injection protocol (independent injection at each layer, or a single injection propagated forward) are not specified. Directly comparing early and late drops under these conditions is not well founded.
-
(d) Architecture is confounded with other factors. Each family contains three models, and LLM backbone, training data, resolution, and the number of visual tokens all vary with the family. The authors acknowledge in Section 3.1 that a controlled comparison is infeasible, but in that case the causal framing of the title (“Architecture-Dependent”) and of the conclusions goes beyond what the evidence supports.
[W2] The attention analysis and the causal experiment are not distinguished from attention sinks.
In Figure 9(e), SAIL’s normalized V→T entropy is exactly 0 at every layer while its V→T routing ratio is 0.4 to 0.7. By definition, this means every visual query attends to exactly one text key, and that single token absorbs more than half of the visual attention mass. If visual tokens could not see any text token at all, the routing ratio would be 0, so this token must be a text token positioned before the image in the sequence, most plausibly BOS or a prompt token. Viewed in the same way, the V→T entropies of 0.03 to 0.05 for Cambrian and LLaVA-Mistral also indicate mass concentrated on one or two tokens. This is the characteristic signature of attention sinks, which are well documented in LLMs.
If this possibility is not excluded, the Section 3.3 finding that concatenation models “attend to a small set of textual keys” becomes a rediscovery of the sink phenomenon rather than evidence of cross-modal information flow, and the Section 3.5 POPE experiment, which masks the tokens receiving concentrated attention, becomes an experiment that removes sink tokens, which would naturally explain the collapse in performance. I ask the authors to report (i) which text tokens, by sequence position and content, actually receive the visual attention mass, (ii) whether BOS is among the special tokens masked according to Section 3.1, (iii) whether system-prompt or question-template tokens are counted as “textual tokens,” and (iv) the identity of the anchor tokens masked in Table 1. Two controls would resolve this concern: masking only BOS, and masking randomly selected text tokens.
[W3] Experimental details needed to interpret the results are missing.
The following are not specified anywhere in the main text or appendix, which makes the results difficult to reproduce or interpret. (i) The input template and token order (whether the image precedes the text). Under causal attention this determines which text tokens the visual tokens can see and is directly tied to W2. (ii) Whether the cross-modal CKA in Figure 1 uses the same sample-level mean pooling described in Section 3.2, and whether it uses 10,000 or 5,000 samples. (iii) Whether the matrix used for intrinsic dimensionality is token-level or sample-level pooled. If token-level, the differing numbers of visual tokens across models affect the estimates. (iv) The noise variance and injection protocol for Table 2. (v) What exactly the layer-0 visual representation of native models is in Section 3.2 (raw patch embedding, or the output of a first projection).
[W4] Sample-level and model-level uncertainty are not shown in the main figures.
Figures 1 and 3 report point estimates per layer with no indication of variability. Two kinds of uncertainty are needed.
-
(a) Sample-level. CKA yields a single value per layer over the whole sample set, so sample-level uncertainty must come from resampling. The authors already perform bootstrap resampling in Appendix A.6, but report it only for Cambrian at layers 1, 15, and 30 (Table 3), and it is not reflected in the main figures. Given that the appendix itself reports a relative bias of 12.6% at n=500, I ask the authors to extend the bootstrap to all layers and all models and to draw confidence bands around each curve. This is particularly important for judging whether the transition-range dip in Figure 1 (roughly 0.47 to 0.37) exceeds resampling variability.
-
(b) Model-level. The family averages are arithmetic means of three models, and the individual model curves are shown only as faint lines whose colors are hard to tell apart. In Figure 1, the early peak near layer 3 (about 0.67) and the sharp drop at the final layer (about 0.42) each appear to be produced by a single model, so it is not possible to tell whether the shape of the family average reflects a family-wide property or a single model. I ask the authors to add a band showing the across-model standard deviation or min-max range around each family average, and to state in the text at which layers the two families’ bands overlap and at which they separate. With only three models per family these bands are likely to be wide, and if so the strength of the “family-level difference” claim should be adjusted accordingly.
Figure 4 already reports medians with IQR and meets this standard, so applying the same treatment to Figures 1, 3, and 5 should be straightforward. Separately, the introduction states that CKA is robust to “common linear transformations.” Linear CKA is invariant only to orthogonal transformations and isotropic scaling, and this statement should be corrected.
[W5] Scope of the contribution and unvalidated practical implications.
-
(a) It is unclear whether the three analyses function as independent tests. When routing ratios fail to separate the families (Δr is 0.3 to 0.6 in both), the comparison shifts to entropy. SAIL is excluded from the attention analysis and treated as a “structural exception.” Intrinsic dimensionality is shown in the main text for only one pair of models. Because results that do not fit the narrative are handled as exceptions, it is not clear what outcome would have falsified the proposed two-pathway hypothesis.
-
(b) The core conclusion, namely that concatenation models preserve the visual encoder’s features in early layers while native models construct visual features from scratch, follows to a large extent from the definitions of the two architectures. The paper should state more clearly what it finds beyond this expectation.
-
(c) Section 5 proposes concrete practical implications, including transition-band layer-selective LoRA, anchor regularization, and earlier cross-modal feedback, but none is tested. Since the per-layer intervention infrastructure of Section 3.5 is already in place, an experiment comparing LoRA applied only to the transition band against uniform application across all layers would not have been difficult, and it would have directly demonstrated the practical value of the analysis.
-
(d) The Platonic Representation Hypothesis analysis in Section 4 is only loosely connected to the two-pathway claim. Moreover, most evaluated models share Vicuna, Mistral, or Llama backbones, so deep-layer convergence cannot be distinguished from shared structure in the LLM residual stream.
Due to the aforementioned weaknesses, my initial score is 1. However, I am willing to raise it to 2 if the authors can convincingly address at least three of these weaknesses.
Questions for authors
- How exactly is the cross-modal CKA in Figure 1 computed? The sample-level mean pooling is described only in Section 3.2 for the intra-modality CKA, and it is not stated whether the same procedure applies to Figure 1. Please specify the two matrices being compared at each layer, including their dimensions and the number of samples used.
- Is there a formal definition of the transition layers? The ranges early (0 to 7), transition (8 to 15), and late (16 to 32) appear only as labels in Figure 1, and the caption’s reference to Section 3.1 concerns the model classification rather than the layer ranges. Please state the criterion used to define these ranges and whether they were fixed a priori or chosen after observing Figure 1.