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Under review as a conference paper at ICLR 2027

Where Binding Begins: Atomic Feature Maps in Vision-Language Models

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Abstract

Vision-language models (VLMs) describe complex scenes fluently, yet they fail at conjunctive search, where the target is defined by a combination of features, such as a particular color and shape, and each distractor shares one of them. This failure is a signature of the binding problem: keeping track of which features belong to which object. Humans show the same failure when they must respond before attention can select objects one at a time. Recent mechanistic interpretability work suggests that VLMs bind features through content-independent spatial retrieval mechanisms, but it remains unclear how the feature representations supplied to these mechanisms are themselves constructed. By intervening on the internal activations of Qwen2.5-VL-7B, we find that the searched-for features are gathered while the model reads the question (e.g., “Is there a green letter L?”) by attention heads at the color word and at the shape word that build maps of where each feature appears in the image. Patching these maps between displays makes the model attach a feature to the wrong object and report an absent target. These illusory conjunctions grow as objects get closer together, as in human crowding, and this proximity effect is carried by shape heads, not color heads. Supplying a clean shape map raises search accuracy from 32% to 94%, whereas a clean color map has little effect. Ablating the maps impairs counting but spares spatial-relation judgments, consistent with a separate indexing mechanism. These results suggest that, within a single forward pass, the model implements a parallel, feature-based stage of search but lacks the serial, object-by-object selection that reliable binding requires.

Primary area:
interpretability and explainable AI
Keywords:
mechanistic interpretability, vision-language models, binding problem, visual search, attention heads, activation patching, feature integration, multimodal models, symbolic mechanisms, illusory conjunctions

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_9vFzOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper locates the feature representations for color × letter conjunctive search in Qwen2.5-VL-7B to a small set of attention heads at the query's color word and shape word. They argue these heads gather "atomic" spatial feature maps from the image tokens.

The supporting evidence includes: (1) patching heads induces illusory conjunctions, (2) patching shape heads raises accuracy on conjunctive trials, (3) the dependence of illusory conjunctions on object separation transfers when patching heads at the shape token, and (4) ablating the heads impairs counting but not spatial-relation questions.

The authors conclude that the shape map is responsible for binding failures in cluttered scenes, arguing that this mechanism lies upstream of Assouel et al. (2026). Finally, they argue VLMs implement the parallel but not the serial stage of human attention.

Critical strengths

1. The motivating tension

The introduction says location-based binding (Assouel et al.) "sits uneasily" with pre-attentive search behavior (Campbell et al.), and positions the paper as resolving this. I don't understand why the two findings conflict.

In human vision, location-based indexing is itself limited in capacity and resolution. For example, FINST indices and object files can only individuate a handful of objects at once (Pylyshyn & Storm, 1988; Pylyshyn, 1989; Kahneman, Treisman & Gibbs, 1992). The inefficiency of conjunction search is usually explained as a limited binding operation applied to too many candidate stimuli. So, for example, an indexing mechanism with similar limits would bind successfully in sparse displays and fail in crowded ones. I'm not sure the paper currently justifies its implication of a puzzle whose answer is that the failure lies "upstream of indexing."

I think the more productive question is: given that both feature maps and indices exist, where is the capacity limit? Answering this question would require measuring both mechanisms in the same displays.

"Upstream of indexing" is therefore an untested claim, in that:

  • There is no evidence that the feature-map heads write into the index or retrieval mechanism.
  • There is no measurement of whether the indices themselves degrade with set size (as the authors concede). That said, Assouel et al. already find that ID retrieval becomes less accurate when objects share features, and that patching in position IDs from displays with distinct features partly rescues these errors. This seems like the closest existing evidence on where the capacity limit lies, and it points at the index stage, so it should be discussed.

It's also not obvious to me that the feature maps are separate from the indexing mechanism. Assouel et al. report ID retrieval, ID selection and feature retrieval heads for this same model. Their ID retrieval heads act at the prompt tokens naming an object, in middle layers (12–16 in Qwen2-VL), and are localized by swapping object positions in the image and patching at those prompt tokens, which closely parallels the minimal-pair swap in Section 4.1. The feature-map heads here also sit at the prompt tokens naming the target's features, and stop at layers 16–17. If the two sets overlap substantially, the feature maps may be a per-word decomposition of ID retrieval rather than a stage upstream of it. That would still be a nice result, but it would change the framing.

In humans, the question of whether binding failures were due to degraded ventral feature representations or failed parietal object individuation was addressed with dissociation studies. For example, a patient with bilateral parietal lesions made illusory conjunctions despite having intact feature perception (Friedman-Hill, Robertson & Treisman, 1995; Robertson, 2003). Additionally, object individuation and identification dissociate across cortical regions (Xu & Chun, 2009).

Section 5 provides half of such a design. I'd suggest:

  • Report how much the color and shape heads overlap with Assouel et al.'s ID retrieval heads in Qwen2.5-VL-7B. This should be cheap, since their head maps for this model are already published.
  • If the two sets are distinct, use path patching (Wang et al., 2023; Goldowsky-Dill et al., 2023) to check whether the map heads' outputs actually feed into the ID retrieval or selection heads. That would justify "upstream."
  • Measure the fidelity of both representations as a function of set size and spacing, in the same displays. For example, probe feature locations from the map heads and position IDs from the ID retrieval/selection heads.

Of course, the interp for localizing and testing feature maps still functions in the absence of these controls. But I think that the above would be the proper dissociative experiment to test the motivation stated in the Introduction.

2. The recovery result (32% → 94%)

Target-absent trials appear to be missing. Fig. 5 and Section 4.2 report target-present accuracy only. The unpatched rate is 32%. Combined with overall 15-distractor accuracy of about 0.6 (Fig. 1c), that implies correct rejections around 0.9, i.e. a strong "False" bias. Any intervention that pushes responses toward "True" would raise the rate.

To control for this effect, I would recommend applying the same patching to target-absent conjunctive trials. For example, you could place the source singleton at a location that, in the target scene, holds one of:

  • (a) a same-color/different-shape distractor. Then integration would predict an illusory "True."
  • (b) a different-color/same-shape distractor. The answer should stay "False."
  • (c) nothing.

If the model says "True" in all three cases, the patched map is acting as a generic "target present" signal rather than being bound with color.

Even with this control, I'm not sure the result shows the shape map is degraded in clutter. The source map isn't a cleaned-up version of the conjunctive shape map: in the conjunctive scene the correct shape map has many peaks (the target plus every same-shape distractor), while the pop-out source has one. So patching it effectively turns conjunction search into feature search. To show the shape map itself becomes unreliable, I think you'd need to measure its fidelity directly, e.g. by decoding the set of same-shape locations from the shape-head outputs as N grows.

Relatedly, the color null is an interesting result. By the same logic, a single-peaked color map should make the conjunction just as easy to resolve, so it's not intuitive to me why color wouldn't also restore performance. Possibilities include the word-order and head-budget issues in W3, or later positions re-reading color directly from the image tokens rather than relying on the color word. It would be great to see this discussed.

3. The color/shape asymmetry

I believe there are a few confounds in this experiment.

(a) Word order. The query reads "Is there a {color} letter {shape}…". Under causal attention, the shape token can attend to the color word, but the color token cannot see the shape word. Shape-token states can therefore be partly conjunctive ("green L") but color-token states cannot.

Fig. A5 fits this, as I read it:

  • Patching all heads at the color token from the swapped counterfactual gives ~100% false positives.
  • Patching all heads at the shape token gives roughly 0%.
  • The shape effect peaks at 1% of heads and declines as more are added.

The authors attribute the decline to "interference." A simpler interpretation is that most shape-token heads carry conjunctive information, which tells the model there is no green L in the counterfactual, and only a small selected subset is atomic. That would undercut both the atomicity claim at the shape position and the color/shape interpretation of the asymmetry, so it's important to rule out as an alternative hypothesis.

The test would be easy, just reverse the word order ("Is there an L that is green?") and check whether the bottleneck follows the feature dimension or the later token.

(b) Unequal, post hoc head budgets. If the percentages are taken over all 784 heads, the shape set is about 8 heads and the color set about 78. The two sets also differ in two further ways:

  • The fractions were chosen using the very effect being reported (A.3: shape peaks at 1%).
  • The two sets were localized with different source contrasts (Sec. 3.3 vs. A.2).

Please report:

  • absolute head counts and identities;
  • the overlap between the two sets. If the same heads act as "color heads" at one position and "shape heads" at the other, the selectivity lives in the query token, not the head. That would conflict with Sec. 2.2's claim that the heads are "selective for a feature dimension."

I appreciate that the sweeps are already in the appendix. Still, it seems like the main-text numbers should come from a budget fixed in advance (e.g. chosen on held-out trials), rather than the budget that maximizes the reported effect.

4. The tokenization argument

The Discussion rules out tokenization because accuracy changes smoothly over increments smaller than a token. My intuition would be that averaging over random positions and axes smooths a step function, so smooth curves are expected even if the mechanism is purely token-level. For example, given the architecture:

  • After 2×2 patch merging, each LLM visual token covers 28×28 px.
  • Most ViT layers attend only within 112×112 px windows.
  • So the 30–70 px range spans roughly one to three tokens.

There would be two easy controls here:

  • (i) Plot accuracy against separation in token-grid units, with grid phase controlled.
  • (ii) Use Qwen's native-resolution input to upsample the same images. This leaves the scene unchanged but increases tokens per object. If the critical spacing shrinks in scene units, the effect comes from tokenization or pooling.

5. The "maps," and their atomicity, are never shown

There is no visualization or quantification of where these heads attend. Fig. 1's maps are schematic, which the caption should state. The following would be cheap to report:

  • the shape heads' attention over image tokens (ideally weighted by value-vector norms, since raw attention weights can be misleading; Kobayashi et al., 2020);
  • the fraction of attention on matching-shape objects vs. other objects vs. background or sink tokens;
  • how that fraction changes with N.

This would turn the Discussion's softmax-normalization hypothesis into a potential result. It would also be cool to see!

Atomicity is currently only tested through the swap. A direct test would be to patch shape heads from sources where the L at the critical location has different colors (green, red, blue). An atomic shape map should give the same effect in every case.

6. The parallel-vs-serial conclusion is not tested

The abstract and Discussion conclude that the model "lacks serial, object-by-object selection." But none of the experiments manipulate or measure seriality, so I'd suggest presenting this as consistent with, rather than evidence for, the absence of serial selection. Two reasons for caution:

  • Set-size effects on conjunction accuracy don't by themselves require a missing serial stage. Parallel models with noisy feature representations predict them too, since more distractors sharing a target feature means more chances for a false alarm (Eckstein et al., 2000; Palmer, Verghese & Pavel, 2000).
  • Twenty-eight layers could in principle implement some iterative selection within a single forward pass.

A positive test of the claim would be: does chain-of-thought or pointing (as in Haputhanthri et al., 2026) rescue the 35-distractor condition? And do the map heads behave differently when the model selects objects one at a time?

7. The Section 5 dissociation

For spatial relations, the reference object is always the top-left letter (A.1.6). In a 2×2 grid, "the letter to the right of X" can only refer to a left-column object, and "below X" only to a top-row object. The model is therefore choosing between two candidates, and a reading-order prior could account for much of the 0.89 baseline. If the task can be solved without locating the reference by its conjunction, the spared accuracy after ablation doesn't tell us whether the maps are needed for binding. Please:

  • randomize the reference position;
  • report accuracy on the subset where binding is required, i.e. where an object sharing a feature with the reference sits in the competing position.

This also matters for W1. Assouel et al. show that position IDs are reused in spatial-relation questions, so if the map heads were ID retrieval heads, ablating them at the reference's words should hurt relation accuracy. With the confound fixed, this experiment could help tell the two mechanisms apart.

8. Scope (lower priority)

The paper uses one model and synthetic displays. I'm less concerned about this than about the points above. Still, generality matters here, because several effects plausibly depend on Qwen2.5-VL's visual tokenization. A second model with a different visual tokenizer would show whether the proximity and color/shape effects are architectural. Rendered 3D objects (CLEVR-style) with color × shape conjunctions would be a reasonable step before natural images.

To be constructive, the most pertinent weaknesses I would like to see addressed are (1), (2), and (3). I additionally think (5) would be useful and should be relatively easy to add. I'm certainly open to raising my score if you can implement some of these controls or explain why they aren't needed.

Presentation (doesn't affect my decision, just a heads up)

  • Duplication: The last paragraph of the Introduction appears twice in near-identical form ("Together, these results help reconcile…" / "These results help reconcile…"), including the sentence about whether indices degrade with set size.
  • Repetition: The "parallel, feature-based stage but not the serial, object-by-object stage" formulation appears in the abstract, twice in the Introduction and in the Discussion. Once is enough.
  • Typos and rendering: The Fig. 6 title reads "leter."
  • Speculation: The A.6 "functional hierarchy / priority signal" paragraph is speculative and should be shortened or flagged as such.
  • Fig. A7: As I read it, ablating a random 10% of color heads reduces conjunctive accuracy noticeably (about 0.81 -> 0.68). That isn't quite "little effect."
Critical weaknesses

1. The motivating tension

The introduction says location-based binding (Assouel et al.) "sits uneasily" with pre-attentive search behavior (Campbell et al.), and positions the paper as resolving this. I don't understand why the two findings conflict.

In human vision, location-based indexing is itself limited in capacity and resolution. For example, FINST indices and object files can only individuate a handful of objects at once (Pylyshyn & Storm, 1988; Pylyshyn, 1989; Kahneman, Treisman & Gibbs, 1992). The inefficiency of conjunction search is usually explained as a limited binding operation applied to too many candidate stimuli. So, for example, an indexing mechanism with similar limits would bind successfully in sparse displays and fail in crowded ones. I'm not sure the paper currently justifies its implication of a puzzle whose answer is that the failure lies "upstream of indexing."

I think the more productive question is: given that both feature maps and indices exist, where is the capacity limit? Answering this question would require measuring both mechanisms in the same displays.

"Upstream of indexing" is therefore an untested claim, in that:

  • There is no evidence that the feature-map heads write into the index or retrieval mechanism.
  • There is no measurement of whether the indices themselves degrade with set size (as the authors concede). That said, Assouel et al. already find that ID retrieval becomes less accurate when objects share features, and that patching in position IDs from displays with distinct features partly rescues these errors. This seems like the closest existing evidence on where the capacity limit lies, and it points at the index stage, so it should be discussed.

It's also not obvious to me that the feature maps are separate from the indexing mechanism. Assouel et al. report ID retrieval, ID selection and feature retrieval heads for this same model. Their ID retrieval heads act at the prompt tokens naming an object, in middle layers (12–16 in Qwen2-VL), and are localized by swapping object positions in the image and patching at those prompt tokens, which closely parallels the minimal-pair swap in Section 4.1. The feature-map heads here also sit at the prompt tokens naming the target's features, and stop at layers 16–17. If the two sets overlap substantially, the feature maps may be a per-word decomposition of ID retrieval rather than a stage upstream of it. That would still be a nice result, but it would change the framing.

In humans, the question of whether binding failures were due to degraded ventral feature representations or failed parietal object individuation was addressed with dissociation studies. For example, a patient with bilateral parietal lesions made illusory conjunctions despite having intact feature perception (Friedman-Hill, Robertson & Treisman, 1995; Robertson, 2003). Additionally, object individuation and identification dissociate across cortical regions (Xu & Chun, 2009).

Section 5 provides half of such a design. I'd suggest:

  • Report how much the color and shape heads overlap with Assouel et al.'s ID retrieval heads in Qwen2.5-VL-7B. This should be cheap, since their head maps for this model are already published.
  • If the two sets are distinct, use path patching (Wang et al., 2023; Goldowsky-Dill et al., 2023) to check whether the map heads' outputs actually feed into the ID retrieval or selection heads. That would justify "upstream."
  • Measure the fidelity of both representations as a function of set size and spacing, in the same displays. For example, probe feature locations from the map heads and position IDs from the ID retrieval/selection heads.

Of course, the interp for localizing and testing feature maps still functions in the absence of these controls. But I think that the above would be the proper dissociative experiment to test the motivation stated in the Introduction.

2. The recovery result (32% → 94%)

Target-absent trials appear to be missing. Fig. 5 and Section 4.2 report target-present accuracy only. The unpatched rate is 32%. Combined with overall 15-distractor accuracy of about 0.6 (Fig. 1c), that implies correct rejections around 0.9, i.e. a strong "False" bias. Any intervention that pushes responses toward "True" would raise the rate.

To control for this effect, I would recommend applying the same patching to target-absent conjunctive trials. For example, you could place the source singleton at a location that, in the target scene, holds one of:

  • (a) a same-color/different-shape distractor. Then integration would predict an illusory "True."
  • (b) a different-color/same-shape distractor. The answer should stay "False."
  • (c) nothing.

If the model says "True" in all three cases, the patched map is acting as a generic "target present" signal rather than being bound with color.

Even with this control, I'm not sure the result shows the shape map is degraded in clutter. The source map isn't a cleaned-up version of the conjunctive shape map: in the conjunctive scene the correct shape map has many peaks (the target plus every same-shape distractor), while the pop-out source has one. So patching it effectively turns conjunction search into feature search. To show the shape map itself becomes unreliable, I think you'd need to measure its fidelity directly, e.g. by decoding the set of same-shape locations from the shape-head outputs as N grows.

Relatedly, the color null is an interesting result. By the same logic, a single-peaked color map should make the conjunction just as easy to resolve, so it's not intuitive to me why color wouldn't also restore performance. Possibilities include the word-order and head-budget issues in W3, or later positions re-reading color directly from the image tokens rather than relying on the color word. It would be great to see this discussed.

3. The color/shape asymmetry

I believe there are a few confounds in this experiment.

(a) Word order. The query reads "Is there a {color} letter {shape}…". Under causal attention, the shape token can attend to the color word, but the color token cannot see the shape word. Shape-token states can therefore be partly conjunctive ("green L") but color-token states cannot.

Fig. A5 fits this, as I read it:

  • Patching all heads at the color token from the swapped counterfactual gives ~100% false positives.
  • Patching all heads at the shape token gives roughly 0%.
  • The shape effect peaks at 1% of heads and declines as more are added.

The authors attribute the decline to "interference." A simpler interpretation is that most shape-token heads carry conjunctive information, which tells the model there is no green L in the counterfactual, and only a small selected subset is atomic. That would undercut both the atomicity claim at the shape position and the color/shape interpretation of the asymmetry, so it's important to rule out as an alternative hypothesis.

The test would be easy, just reverse the word order ("Is there an L that is green?") and check whether the bottleneck follows the feature dimension or the later token.

(b) Unequal, post hoc head budgets. If the percentages are taken over all 784 heads, the shape set is about 8 heads and the color set about 78. The two sets also differ in two further ways:

  • The fractions were chosen using the very effect being reported (A.3: shape peaks at 1%).
  • The two sets were localized with different source contrasts (Sec. 3.3 vs. A.2).

Please report:

  • absolute head counts and identities;
  • the overlap between the two sets. If the same heads act as "color heads" at one position and "shape heads" at the other, the selectivity lives in the query token, not the head. That would conflict with Sec. 2.2's claim that the heads are "selective for a feature dimension."

I appreciate that the sweeps are already in the appendix. Still, it seems like the main-text numbers should come from a budget fixed in advance (e.g. chosen on held-out trials), rather than the budget that maximizes the reported effect.

Questions for authors
  1. What happens when the source singleton sits at a non-target location?
  2. Are the shape bottleneck and the Fig. A5 non-monotonicity results retained after reversing the order of the color and shape words?
  3. How much do the color and shape heads overlap with Assouel et al.'s ID retrieval heads in this model? Does patching or ablating those heads interact with the feature-map heads?
  4. Does chain-of-thought or pointing rescue the high-N condition? Does it change how the map heads are used?
5 comments
AuthorsOpenReview ↗

Regarding weaknesses 1 & 2

We sincerely thank reviewer 9vFz for the thoughtful and constructive review.

Regarding weakness 1:

We agree that a more productive question regards understanding the interaction and overlap between the retrieval heads and our identified feature-map heads, and have thus revised our phrasing in the introduction to reflect this. In Appendix A.8, we do a more robust analysis of their relation. We find that ID retrieval heads and feature-map heads have a significant overlap, resting slightly under 50% for the top 1%, 5%, and 10% of heads. Interestingly, we find that the disjoint set of feature-map heads tends to sit at earlier layers, whereas disjoint ID retrieval heads sit at later layers. We conduct the scene description experiment in Assouel et al. (2026), and find that patching 5% feature-map heads can induce a flipped answer 45.5% of the time, compared to a 92% rate for retrieval-ID heads. By not allowing the disjoint retrieval heads to be updated by feature-map patching, we find that this induced flip rate drops from 45.5% -> 1.5%. Implying that the overlapped heads are not sufficient alone for spatial indexing, but rather rely on sending signal to the downstream disjoint heads. Overall, we interpret this as feature-map heads and retrieval-ID heads being closely linked, and containing a blurry line of seperation (and have updated our writing to reflect this). We plan to run further analysis on the interaction and limitations of both, as we agree the two mechanisms are tightly linked and identifying the overlap and differences is interesting.

Regarding weakness 2:

As mentioned in our general post, we ran a series of further experiments to better understand how feature-map heads mediate performance in cluttered scenes. We found that the proposed target-absent experiments did not show the intended results in the 15-distractor setting. To address this, we designed an alternative attention intervention experiment in the 15-distractor setting and reran our experiment in the 5-distractor setting, as baseline “False” confidence tends to be higher, leading to a lower possibility for small “true” pushes to obscure results. We find that in the target-absent setting, placing a singleton on an opposite target feature successfully induces a swap to “True” 68% of the time for color heads, and 98% of the time for shape heads. When placing the singleton on the same feature, this rate appropriately drops to 9% for color heads, whereas for shape heads it drops to 61%. While we take this to imply that performance recovery for color heads can be trusted, shape-head recovery results should be interpreted cautiously.

To further understand how these heads can play a role in recovering behavior, we conduct a second attention reallocation experiment. Specifically, we reallocate attention from distractors to the target for these heads and find that this increases performance. As a control, we apply this reallocation experiment to random heads and reallocate top heads to a blank patch, and find that both of these conditions do not improve performance by nearly as much. Furthermore, we find that removing attention from feature-sharing distractors for each head recovers performance more than non-feature-sharing distractors. We thank the reviewer again for bringing up these concerns and believe these experiments give further insight into how feature-map heads are tied to performance in cluttered scenes.

AuthorsOpenReview ↗

Regarding weaknesses 3-6

Regarding weakness 3:

Notably, our 5-distractor patching experiment and attention reallocation experiments no longer display a stark asymmetry between color and shape heads, and thus we have updated our writing to no longer claim this. We do, however, agree that understanding the effects of token ordering is important and interesting. We have thus conducted both the 5-distractor and attention reallocation experiments using the reverse word order (Appendix A.10.1 and A.7.2). We observe that the asymmetries do not reverse for the attention reallocation experiment, implying that non-target distractors inherently take up a relatively larger proportion of attention for shape heads than color heads. A possible explanation could be that distinguishing between shape information requires contextualizing information across tokens whereas color information is stored within token. For the pop-out patching experiment we find that asymmetries tend to be inconclusive across models. However, we emphasize that interaction between the two tokens does not undercut atomicity claims, as the ability to intervene atomically on the first token inherently requires it to not be overwritten by the second token by reading the image. We included a distributed alignment search experiment (Figure 3) on the residual streams of these tokens to provide insight into the structure of the representation being written by the heads. We find a subspace in the first token that causally encodes the corresponding target feature of each object in the image. Furthermore, the second token encodes both of these features in separate subspaces. Together, this suggests a clearer picture of a successive build-up where features are read one at a time and consistent with successive atomic accumulation of feature information. DAS implementation details can be found in Appendix A.2

We appreciate the feedback on the unequal, post hoc head budgets, and have updated both color and shape heads to use a fixed budget of 5% (N=39) of heads throughout the paper, and have included the head counts.

Regarding weakness 4:

In Figure A11, we report a more controlled tokenization experiment, where we fix the distance between the two objects and shift them to land within and outside the same token. We find that both conditions lead to a similar false positive rate (albeit with the within-token condition being slightly lower), further emphasizing that illusory conjunctions are likely not solely due to tokenization.

Regarding weakness 5:

We agree that the atomicity is not directly shown and have thus conducted a set of attention matrix analyses for these heads. Beyond the attention reallocation experiment mentioned earlier, we test the entropy of attention over visual tokens as the number of objects in the scene increases. In Appendix A.7, we find that as same-feature objects (aka green Ts, for “Green” in “Green L”) are introduced, entropy consistently increases, whereas alternate-feature objects (aka red Ls, for “Green” in “Green L”) result in significantly smaller increases. We also include a visualization of the attention pattern over objects as more distractors are in the scene. We thank the reviewer for the suggestion, as this nicely displays the softmax dilution hypothesis, where attention is reallocated to feature-sharing objects. A nice qualitative visualization is shown in Figure A12.

Regarding weakness 6:

We leave the direct evidence for parallel-vs-serial outside the scope of this project and have updated our phrasing to reflect this.

AuthorsOpenReview ↗

Regarding weaknesse 7 & 8

Regarding weakness 7:

We have updated the spatial reasoning and counting experiments to better distinguish between the role of stimuli and prompts. For both counting and scene description, we test them on a 2x2 and 3x3 grid that all have a binding demand. For the scene description experiment, we ask what object is to the {top, bottom, left, or right} of a randomly placed target conjunction (importantly, we fix one to exist in the scene only, and ensure the distractors share only the target color or shape). For the counting scene, target color, shapes, and their conjunctions are asked about with answers ranging from 0-2 for the 2x2 setting and 0-5 for the 3x3 setting (more details are in Appendix A.1.5). Under this setup, we continue to see ablating feature-map heads leading to degraded performance in counting for 2x2 and 3x3. Interestingly, we find that scene description performance now drops to baseline when ablating feature-map heads on the 3x3 scene, implying that more complex scenes require feature-map heads.

Regarding weakness 8:

In Appendix A.9 we have included results for internvl3.5-8b and gemma-3-12b. Intern and Qwen show very consistent results across all experiments. Gemma performs worse behaviorally than Qwen, and shows less conclusiveness result at the shape token in the minimal swap experiment. Furthermore, we are running an attention head ablation experiment on a CLVR-style dataset to understand whether they are used in more realistic scenes, and hope to have updated results as soon as the results become available.

We thank the reviewer again for their comprehensive review and believe that it significantly strengthened our work significantly.

Reviewer_yLYjOpenReview ↗
Rating
4
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

This paper provides a mechanistic account of where visual binding in VLMs (in the context of conjunctive search), and demonstrates results suggesting that VLMs actually do perform parallel feature based search but subsequently fail at reliably performing the serial object-object selection needed to reliably perform conjunctive search.

Critical strengths

The experiments in the paper are really nicely designed, and are set up in such a way that enables the authors to hone in on the claims made in the paper. Where a lot of papers settle on "just so stories" about plausible mechanisms or how to interpret mechanistic work, this paper has clearly spent time and effort designing a series of carefully crafted experiments designed to disentangle competing hypotheses.

The results found are also significant for understanding how VLMs process information, and the types of higher-order computations they are performing on visual data, and how these differ from e.g., the human visual system. While the existence of these differences was known from previous work, this paper brings together a compelling mechanistic account.

Critical weaknesses

The experiments and results are limited to a single model. While VLMs generally share a similar structure and training regime, results on a single model do not necessarily generalise to VLMs as a whole. It would improve the paper to see similar patterns across multiple VLMs. Currently the paper makes claims about VLMs, which I do not believe are sufficiently substantiated outside of Qwen.

Questions for authors

What drove the choice of the model to be Qwen? Why only a single model?

1 comment
AuthorsOpenReview ↗

Response to review

We thank reviewer yLYj for the positive review and for recognizing the carefully designed experiments.

Regarding Weakness 1:

We have conducted all the experiments in the main text on InternVL3.5-8B and Gemma-3-12B, and we see that InternVL shows very consistent results with Qwen on all the experiments. Gemma-3-12B shows very similar results to Qwen on every experiment except for the minimal-pair-swap. However, we find that this may be due to the scene containing only two distractors, as later experiments can successfully induce illusory-yeses in more cluttered scenes. These results can be seen in Appendix A.9.

Reviewer_hitHOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper analyzes the binding of multiple attributes in a VLM using a controlled setting and a simple task. The authors ask Qwen2.5-VL about the existence of a colored letter while adding distractors that either share the same letter but differ in color (disjunctive) or share either the target's color or shape (conjunctive). The VLM fails in the conjunctive case as the number of distractors increases, which the authors attribute to binding failures. Using causal tracing and activation patching, they identify attention heads at the attribute-word positions that appear to encode spatial information about individual features. They further investigate how object proximity influences binding errors and test the importance of the identified heads for counting and spatial-relation tasks through ablation experiments.

Critical strengths
  • The paper presents a mechanistic study of binding in VLMs, contributing to our understanding of how visual information is perceived and integrated by the LLM.
  • The experiments are well-designed, and several complementary experiments support the findings. The presentation is very clear, with well designed figures and precise explanations.
Critical weaknesses
  • The idea of feature maps that spatially encode a single attribute is very simplified and never directly proven. The experiments mainly show that patching moves the predication. The results are consistent with the interpretation the paper makes but a more systematic representation analysis would strengthen that contribution.
  • VLMs tend to prefer answering "yes" over "no," independent of the visual evidence (see, e.g., Chan et al. (2026)). In Figure 3, this would explain why removing the same head when the target is present increases the margin, while it decreases the margin when the target is absent. This is even more critical in Figure 5, where only target-present scenes are included, and due to a possible yes-bias, the experiment cannot distinguish successful binding from an increased tendency to predict the presence of the target.

  • Figure 7a shows big performance drops not only for conjunction counting but also for single-feature counting. This supports the importance of the identified heads for visual feature processing, but does not specifically establish their contribution to binding. The interpretation should distinguish general feature retrieval from the additional computation required to combine features.

Chan et al. (2026). System-Mediated Attention Imbalances Make Vision-Language Models Say Yes. Findings of ACL 2026.

Questions for authors

I have a few questions, ranked in descending order of priority:

  • Could the authors verify the yes-bias? A potential idea would be to run Figure 5 experiments on target-absent scenes, reporting true-positive and false-positive rates.
  • Could the small effect of ablating the binding heads in the spatial-relation experiment be explained by a positional shortcut, given that the scenes contain only four objects and the reference object is always in the same position?
  • The authors draw parallels to human visual attention and claim that VLMs implement parallel feature-based processing but lack serial object-by-object selection. How can this conclusion be supported without directly testing sequential object inspection, for example by comparing single-pass inference with explicit step-by-step processing?
  • Do the identified mechanisms generalize to more realistic visual reasoning tasks, such as multi-instance reasoning in natural images?
  • Do the findings generalize beyond Qwen2.5-VL-7B to other VLM architectures?
  • What motivates the choice of five consecutive attention blocks in Section 3.2, and how sensitive are the localization results to this choice?
2 comments
AuthorsOpenReview ↗

Response to weaknesses

We thank Reviewer hitH for their constructive review.

Regarding the first weakness:

We agree that our patching experiments alone do not directly demonstrate the encoding of a single attribute. To provide further evidence for this, we conduct a series of analyses on the attention matrix of our feature-map heads. We start by analyzing the entropy of attention over the visual tokens as more distractors are present in the scene. In Appendix A.7, we observe that for color heads, the entropy increases starkly as more same-color distractors are introduced, whereas the increase is much smaller for same-shape distractors. We see a consistent trend with the shape heads too, further implying that the heads query atomically. We also provide a visualization (Figure A12) that shows that attention to the target conjunction in increasingly cluttered scenes is reallocated to feature-sharing distractors.

Regarding the second weakness:

As specified in our general post, we have updated our experiments to address the potential True bias. We started by recomputing our feature-map head rankings using a split of data that should induce the model to answer “False” under the atomic hypothesis. We then provide multiple controls for the performance recovery experiment. First, we verified that swapping the pop-out feature maps did NOT recover performance for the alternate heads, ensuring no generic “yes push” under patching.

Next, we tested the effect of pop-out maps on the target-absent scenes for a 5-distractor setting. We find that for both color and shape heads, placing the target feature on the alternate feature causes a noticeably larger “inducing” rate than placing it on the same target feature. However, we note that for shape heads specifically, the false inducing rate is still noticeable, and therefore raises questions about the degree to which the target-present results can be trusted. To understand this better, we conduct a second attention-intervention experiment on the 15 distractor scenes. Specifically, we reallocate attention from distractors to the target for feature-map heads and find that performance increases, and that reallocating from same-feature distractors increases performance more than alternate features. As a control, we reallocate attention to a blank space and observe a much smaller recovery. We thank the reviewer again for these suggestions, and overall believe these experiments provide further insight into how feature-map heads mediate the drop in performance in cluttered scenes.

Regarding the third weakness:

While we observe that performance drops for single-feature tasks, we see this as a positive result, as our identified attention heads are viewed as a feature-aggregation stage which is necessary for binding. This experiment further emphasizes that these heads aggregate features atomically and are a required step across binding-required tasks. We have updated our text to make this point clearer.

To address the shortcut point brought up, we have updated this experiment to systematically distinguish the effect of visual stimuli and task/prompting for this experiment. For both counting and scene description, we test them on a 2x2 and 3x3 grid that all have a binding demand. For the scene description experiment, we ask what object is to the {top, bottom, left, or right} of a randomly placed target conjunction (importantly, we fix one to exist in the scene only, and ensure the distractors share only the target color or shape). For the counting scene, target color, shapes, and their conjunctions are asked about with answers ranging from 0-2 for the 2x2 setting and 0-5 for the 3x3 setting (more details are in Appendix A.1.5). Under this setup, we continue to see ablating feature-map heads leading to degraded performance in counting for 2x2 and 3x3. Interestingly, we find that scene description performance now drops to baseline when ablating feature-map heads on 3x3 scenes, implying that more complex scenes require feature-map heads.

AuthorsOpenReview ↗

Response to Questions

Response to question: Parallels to human visual attention and claims that VLMs lack serial object-by-object selection.

We agree that our experiments do not directly test the parallel-vs-serial; therefore, we have rewritten our text to emphasize that our findings are consistent with past literature suggesting this absence, rather than evidence for.

Response to question: Generalization to realistic tasks and other models

We have conducted all the experiments in the main text on InternVL3.5-8B and Gemma-3-12B, and we see that InternVL shows very consistent results with Qwen on all experiments (Appendix A.9). Gemma-3-12B shows very similar results to Qwen on every experiment except for the minimal-pair-swap. However, we find that this may be due to the scene containing only two distractors, as later experiments can successfully induce illusory-yeses in more cluttered scenes. Furthermore, we are currently running a feature-map head ablation experiment on a replicated CLVR-style dataset to observe whether these heads support binding in more realistic scenes, we hope to update our draft with results as soon as the results become available.

We thank the reviewer again for the thoughtful review, we believe it has significantly strengthened our paper.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General-post to reviewers (True Bias When Patching)

We thank all the reviewers for their feedback on our paper; we have updated a couple of experiments to address concerns brought about by Reviewer hitH and 9vFz about a potential “True”-bias (yes-bias), which we have highlighted below.

Updated Head Rankings

In our original head ranking setup, our scoring condition always ranked heads by the logit difference towards answering “True”. To address this, we updated our head scoring to directly score logit shifts towards “True” and “False” for two separate templates under the atomic feature hypothesis. Details of the updated rankings are provided in Appendix A.3, and all experiments in the paper are ran and updated to reflect results using this updated ranking. Overall, the results tend to provide stronger evidence for atomic-features.

Target Absent Control

For the performance recovery experiment (Figure 5), we conducted a control on the target-absent split of the data. First, we patched the feature-map heads from a pop-out scene with one target feature onto a scene that had the alternate target feature (we term this “inducing”). Under this setting, we expect the illusory perception. We then patched attention heads from a scene where the single target feature lied on a matching single target feature (“we term this “matching”). Under this setup, we expect the model to NOT perceive the target. We found that the 15-distractor scene caused the model to perceive the target at a similar rate, bringing into question whether the recovery observed in the target-present case can be trusted. To address this, we conducted an attention intervention experiment on the 15-distractor scene and re-ran this experiment on the 5-distractor scene (both of these are summarized below)

In the 5-distractor setting, target-present performance remains degraded, while providing an environment where baseline illusions remain lower and logit confidence is higher. In this setting, we observe that patching is noticeably more consistent. Specifically, for color-heads, we see that the inducing case successfully induces illusions 68% of the time, and for the matching case, it appropriately remains low at 9%. For shape heads, inducing the illusion is once again high at 98%, whereas the matching case is noticeably lower at 61%. While the color-heads patching recovery observed in the target-present split (66% -> 86%) can be trusted, the shape-head results can only be partially trusted, as target-absent has a noticeable “False inducing” rate. Specific details of the experiment are in Appendix A.10.

To provide further evidence towards feature-map heads mediating performance drops in cluttered scenes, we provide a variety of attention analyses (Appendix A.7). Notably, we conduct a causal intervention on the attention matrices of the feature-map heads. We find that reallocating attention from the distractors to the target directly improves performance in the 15-distractor scene. 30% -> 83% for color heads, and 30% -> 63% for shape heads. We further observe that reallocating attention from same-feature distractors improves performance noticeably more for both types of feature heads, as expected for the atomic feature-map claim. Finally, it is worth noting that both the attention-reallocation and 5-distractor setting no longer suggest a strong color/shape asymmetry, and have therefore removed the claim from our manuscript.

We would like to thank the reviewers once again for identifying these important controls; we believe that, with these updated experiments, we continue to observe that feature-map heads mediate performance degradation in cluttered scenes, and the direct attention analyses and interventions highlight that degradation is likely due to softmax dilution in cluttered scenes, as we originally speculated in our discussion.

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

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