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Under review as a conference paper at ICLR 2027

Probing Perceptual Priors of MLLMs via Gibbs Sampling with Interpretable Generative Controls

Abstract

A model's behavior on a task is jointly determined by the input it receives and the prior it brings in, i.e. the distribution over stimuli it implicitly expects. Interpretability research has traditionally studied models by holding inputs fixed and examining model responses either mechanistically, probing how internal structure represents inputs, or behaviorally, measuring how variation in inputs leads to variation in outputs. Neither reconstructs the prior distribution itself, since internal structure shows what a model can represent, not what it expects, and any fixed stimulus set leaves most of the possible input space unseen. In particular, such an input space in real-world settings, such as images seen by VLMs, is extremely high-dimensional and diverse. These priors thus remain a poorly understood component of models that nonetheless influence real-world behavior. We propose a method to sample from models' perceptual prior distributions directly, by steering a generative model to produce stimuli along controllable axes and running Gibbs sampling over that space with the model under study as the judge. We apply this to a variety of categories and target variables (such as trustworthiness in faces and cheapness in art images) and recover both canonical biases and surprising novel priors invisible to direct prompting, warranting further investigation of their downstream effects.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Interpretability, Controllability, Priors, Biases, MLLMs, Gibbs Sampling, Markov Chain Monte Carlo

Reviews

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1234this paper, Top 49%
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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3(+1)
Confidence
2
Informativeness
2
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1
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Paper summary

The paper proposes a sampling-based method to recover the implicit visual priors of multimodal large language models. By combining controllable image generation with pairwise comparisons, it estimates joint distributions over visual attributes and analyzes how these preferences vary across concepts and models.

Critical strengths
  1. The paper introduces a cognitively inspired framework for quantitatively estimating the implicit visual priors of multimodal large language models (MLLMs).

  2. By combining interpretable slider spaces with FLUX-based image generation and adaptive sampling, the proposed method moves beyond fixed stimulus sets and extends prior work by Zhu et al. on implicit prior elicitation from LLMs to the multimodal setting.

  3. The method represents implicit priors as interpretable joint distributions over visual attributes, enabling systematic comparisons across models and concepts while capturing dependencies between attributes.

Critical weaknesses
  1. Convergence and reliability of recovered priors. Appendix E reports substantial convergence issues. For example, in Aesthetics, 50% of parameters for Qwen3-VL and 58% for Gemini 3 Flash have split-R-hat > 1.5 with median acceptance rates below 10%. Although the authors acknowledge these limitations, it remains unclear how they affect the reliability of the recovered distributions. Further convergence analysis and stability checks would strengthen the results.

  2. Insufficient comparison with explicit baselines. The explicit baselines in Appendix C rely on one-dimensional slider sweeps and do not adequately model inter-slider dependencies. Thus, it remains unclear whether IMH's advantage comes from implicit sampling or simply from capturing interactions neglected by the baselines. Moreover, sharper distributions are not necessarily more accurate. An interaction-aware explicit baseline with a comparable query budget and additional independent validation would help establish the proposed method's advantages.

  3. Potential biases in slider selection and labeling. The authors manually select 10 out of 64 candidate axes, potentially introducing subjective biases into the recovered priors. I would encourage a human-subject evaluation involving multiple independent participants to establish group-level consensus and assess selection reliability. Additionally, the automatic semantic labeling pipeline would benefit from quantitative validation against human judgments.

  4. Limited surprise of the recovered priors. Although the authors claim to uncover "surprising novel priors," several reported associations involving facial appearance, personality, and demographic attributes resemble biases documented in previous studies [1, 2, 3]. The authors could better distinguish genuinely novel findings from previously documented biases.

  5. Limited cross-modal validation. Although the framework is described as modality-agnostic, all experiments focus on images. Evaluating another modality would provide stronger empirical support for its generality.

  6. Limited quantitative evidence regarding direct slider manipulation. The authors discuss practical difficulties with direct slider manipulation, including oscillation and inefficient exploration. While these observations provide useful motivation, a quantitative comparison would help clarify the practical advantages of the proposed sampling approach.

[1] Howard, P., Fraser, K. C., Bhiwandiwalla, A., & Kiritchenko, S. (2025). Uncovering Bias in Large Vision-Language Models at Scale with Counterfactuals. Proceedings of the 2025 Conference of the Nations of the Americas Chapter of the Association for Computational Linguistics: Human Language Technologies (NAACL 2025), 5946–5991. https://doi.org/10.18653/v1/2025.naacl-long.305

[2] Gulati, A., D’Incà, M., Sebe, N., Lepri, B., & Oliver, N. (2025). Beauty and the Bias: Exploring the Impact of Attractiveness on Multimodal Large Language Models. Proceedings of the AAAI/ACM Conference on AI, Ethics, and Society (AIES), 8(2), 1154–1168. https://doi.org/10.1609/aies.v8i2.36619

[3] Lehr, S. A., Lothe, Y., & Banaji, M. R. (2026). Like Humans, Language Models Demonstrate Face-to-Character Biases. PNAS Nexus, 5(8), pgag247. https://doi.org/10.1093/pnasnexus/pgag247

Questions for authors
  1. How do the convergence issues reported in Appendix E affect the reliability of the recovered priors? Are the main findings stable across independent chains or longer sampling runs?

  2. Have the authors considered an explicit baseline that directly evaluates multidimensional slider combinations? How can we distinguish the benefits of implicit sampling from those of modeling inter-slider interactions?

  3. How were the 10 axes selected from the 64 candidates? Was the selection based on judgments from multiple independent participants? How sensitive are the recovered priors to different axis selections?

  4. Has the automatic semantic labeling pipeline been validated against human judgments? To what extent do the assigned labels reflect human interpretations of the visual attributes?

  5. Which of the recovered priors do the authors consider genuinely novel compared with previously documented MLLM biases? What additional insights does the proposed method reveal beyond existing findings?

9 comments

We respectfully disagree with this review, and we discuss below in detail why. To summarize the main points:

  1. You express concern about high $\hat{R}$ scores. We use predictive checks in which we can predict held-out model decisions above chance across all models and domains. Also, $\hat{R}$ is one diagnostic and even here our values are similar to those from GSP [1] (we recomputed from their faces data). We discuss below how our HSL experiments also add internal validity. We report $\hat{R}$s for transparency
  2. You argue that our explicit baselines are insufficient. The inability of independent, one-dimensional elicitation procedures—the ones used in our baselines—to capture joint dependencies is precisely one of the motivations for our method. The other approaches you suggest are computationally infeasible, which is why MCMC methods exist in the first place.
  3. You question the slider selection and labeling. The sliders are the experimenters’ degrees of freedom, with a subset needed to make the computation tractable. The sliders and their labels are independent of the validity of the method, and should be selected carefully by experimenters to answer specific questions regarding the perceptual priors of MLLMs.
  4. You argue some recovered priors have been previously reported. This is a strength of the method! It shows the method’s reliability, while it also provides a joint distribution not available in other methods (in addition to new priors, of which we give a case study below)
  5. You argue our cross-modal validation is limited. We do not claim cross-modal validation. The method itself is modality-agnostic, i.e. it does not depend on a specific generative model or controlling method, and is fairly straightforward to expand to other modalities. We prioritize depth of investigation in the visual modality here
  6. You suggest a direct slider manipulation comparison. If direct manipulation had worked, the resulting method would be equivalent to the one described in the paper. That means it’d still be an MCMC method with a generative model, interpretable controls, etc. Thus, comparing them would be redundant; this is simply a more reliable way to obtain similar results

(W1 and Q1) Convergence and reliability of recovered priors

Our predictive checks show that these chains do meaningfully capture models' preferences. Within chains, we predict held-out accept and reject decisions with median accuracies of $\approx$ 0.70--0.83 across all models and domains (Figure 15). This includes conditions with the highest $\hat{R}$. Then, across chains, we fit densities on all chains but one and predict decisions from the held-out chain. We again predict above chance for every model and domain, with medians of $\approx$ 0.55--0.70 (Figure 16). 26/32 of tests against random chance are significant at $p < .05$

Our $\hat{R}$ values are similar to those of GSP [1]. In GSP study 4a, median $\hat{R}$ across sliders (per our reanalysis from their data) ranges from 1.07--1.23 across targets, and the max $\hat{R}$ is 2.41. Between 4 and 8 of their 10 sliders exceed 1.10 per target. Across their other face studies, $\hat{R}$ goes up to 5.78. On our face domain, median $\hat{R}$ ranges from 1.11--1.33 across models, and worst $\hat{R}$ ranges from 1.42--2.79 (as per Table 2)

Our HSL experiment shows how chains can recover correct distributions even under suboptimal $\hat{R}$. In this experiment, we know the correct answer for every target and we clearly recover the correct color for all 8 targets (Figure 17). Yet on saturation and lightness, which are bounded and non-circular like our sliders, $\hat{R}$ goes up to 1.70 for lavender, 1.80 for eggshell, etc. These values cover most of the range we report in our main experiments, where median $\hat{R}$ goes from 1.02--1.60 (as per Table 2)

Importantly, convergence issues appear in only some conditions. We acknowledge it lowers precision there, and include these values precisely for this reason (i.e. transparency). GPT-5.4 and Claude Sonnet 4.6 have median split $\hat{R}$ of 1.02--1.20 across all 4 domains, and at most 1% of their parameters exceed 1.5. We therefore draw our main conclusions from effects that replicate across independent chains and models. We would thus argue that it is misleading to interpret the least converged conditions as being representative of our full evaluation

(W2 and Q2) Insufficient comparison with explicit baselines.

The inability of independent, one-dimensional elicitation procedures to capture joint dependencies is precisely one of the motivations for our method, as detailed in Appendix C.

Appendix C compares our method against two widely used explicit elicitation strategies: (1) scalar ratings and (2) fixed pairwise comparisons. These test whether simpler, nonadaptive evaluations of individual sliders recover similar structure as adaptively sampling joint preferences. We show that this is not true, which motivates a method like ours.

Consider alternate ways of approximating a posterior over $d=10$ sliders (this is the number of generations/queries). #1 and #2 would be interaction-aware in the sense that you suggest:

MethodComplexityEvaluations per model–target
10-level factorial$O(10^d)$$10^{10}$ = 10 Billion
5-level factorial$O(5^d)$$5^{10}$ = 9.8 Million
Uniform random sampling$O(N)$$N$
Independent slider sweeps$O(dm)$$10 \times 10 = 100$
Ours: MH-within-Gibbs$O(T)$$10 \times 2,000 = 20,000$

Factorial approaches preserve interactions but scale exponentially, and independent sweeps are cheap but discard interactions. Random sampling is flexible depending on budget $N$, and thus is equivalent to (joint) IMH-without-Gibbs and less efficient unless the posteriors are near-uniform. Our method preserves interactions while making the cost linear in the number of sampling iterations.

Furthermore, Appendix C compares much more than distribution sharpness. It measures magnitude and ranking disagreements between methods, investigates relationships with inter-slider dependencies, and reports association between interaction strength and baseline disagreement

RE: sharper distributions are not necessarily more accurate; We explicitly make this point ourselves in Appendix C, where we caution that posterior concentration can be misleading when an elicitation procedure is biased or misspecified, and we do not claim ground-truth accuracy.

(W3 and Q3 and Q4) Potential biases in slider selection and labeling.

Neither of these points establishes a failure of our method.

Slider selection. In Section 3.2, we mention that these 10 sliders are selected from 64 candidates. These are the interpreters' degrees of freedom. Selecting a tractable, interpretable subset is also necessary for the experimental protocol, since sampling all 64 dimensions for every model and target is computationally unfeasible.

Crucially, this selection occurs before the downstream target concepts are evaluated and is independent of their labels and resulting preferences. We claim nowhere to have exhaustive coverage of visual features or invariance to arbitrary slider subsets. The fact that alternative subsets might reveal additional associations or alter inferred distributions is in fact a desirable feature of our method, since it supports diverse analysis goals without methodological alterations.

RE: automatic labeling: A slider being mislabeled would require correcting the semantic interpretation of its results, but would not retrospectively change anything in the sampling procedure (e.g. models’ preferences, etc.). Therefore, validating (or not) the auto-interpreted labels does not affect the underlying correctness of our method. Validating against human judgements could make the labels more reliable, but it’s not strictly necessary.

Importantly, the semantic labels are post-hoc interpretations of the learned coordinates and not inputs to the MLLM acceptance decisions.

### (W4 and Q5) Limited surprise of the recovered priors

While we agree that some of these facial associations have been reported previously, a new method recovering familiar associations is in fact strong validation (rather than a weakness). If our method could not recover such established effects, this would conceivably raise questions about construct validity. Even so, the methodological contribution does not require that all priors be unprecedented.

We will update the manuscript to cite the papers you listed as evidence that our method recovers known priors. Even in cases where we recover known priors, our method also provides joint distributions over multiple visual features, which conventional bias evaluations do not.

However, we do show new and surprising associations which invite further investigation. For example, in Criminal, “Receding Hairline” is robustly the leading slider. In humans, criminal stereotypes traditionally involve long, dark, shaggy hair [2]. Human studies of male pattern baldness that we can find appear to disagree, e.g. balding men rated as less aggressive [3]. “Receding Hairline” also is in the bottom three for Trustworthy, Hardworking, and Fun. Humans do traditionally penalize balding men on attractiveness [per 3] though, and our results reproduce this effect.

### (W5) Limited cross-modal validation

Our proposed method requires two components:

  1. A controllable generator with interpretable sliders
  2. A judge capable of providing binary comparisons between generated stimuli.

Nothing depends on the stimuli being images, and multimodal judges are widely available. So, using this method with a different modality just requires a controllable generator with interpretable sliders. For example, we could replace SliderSpace with an equivalent controllable method (e.g., AudioGen as an audio model, with SAEs as controls).

We do not claim to have empirically demonstrated this method across audio and other modalities. We invite the community to explore applications of our method in other modalities and problems leveraging their domain expertise.

### (W6) Limited quantitative evidence regarding direct slider manipulation

The direct slider manipulation (if it worked) would be equivalent to our method, and thus, the quantitative comparison you suggest would have no effect on the method proposed in this paper. If direct slider manipulation had worked, it would still be an MCMC sampling method using a generative model, MLLM judge, and interpretable controls. The only difference would be that we could avoid sampling over the slider via MH, since the judge would be doing that part as well. We had to work around that issue to make a method like this one possible.

Reviewer_GrmpOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This paper proposes a Metropolis-Hastings within Gibbs sampling framework to recover the implicit preference priors of MLLMs. By using binary MLLM comparisons as Barker acceptance decisions, the method samples from the models' implicit preference priors by a trained controllable generative model. The recovered distributions are then analyzed to reveal potential biases associated with specific concepts.

Critical strengths
  1. The paper extends human perceptual prior elicitation methods to MLLMs, with theoretical grounding in Gibbs sampling and Barker acceptance.

  2. Extensive experiments across multiple models, domains, and concepts enable a systematic investigation of MLLM perceptual biases.

Critical weaknesses
  1. The paper lacks comparisons with existing approaches for probing visual preferences and detecting biases, such as Visual Persuasion [1] and DEXTER [2]. It remains unclear whether the observed biases are intrinsic to the MLLMs or influenced by the probing method and generative model, and whether these findings generalize across different approaches.

  2. The method relies on only 10 manually selected PCA-based sliders, which limits its ability to explore biases associated with other visual features. As a result, potentially important biases outside the predefined slider space may be overlooked, limiting its applicability to open bias discovery.

  3. Appendix C reports a p-value of 0.02, whereas Figure 13 reports 0.002 for the same correlation (ρ=0.63\rho=0.63).

[1] Cherep et al. (2026). Visual Persuasion: What Influences Decisions of Vision-Language Models?. ICML 2026.

[2] Carnemolla et al. (2025). DEXTER: Diffusion-Guided EXplanations with TExtual Reasoning for Vision Models. NeurIPS 2025.

Questions for authors
  1. The proposed method relies on binary choices from MLLMs to implement Barker acceptance in the Metropolis–Hastings sampler. However, binary responses may discard useful information about the model's preference strength. For models with accessible logits, such as Qwen3-VL, the authors could directly estimate the preference probability from the logits of the two candidate answers (A and B). For example, the model could be prompted with "Image A: [image 1], Image B: [image 2]. Which person looks more intelligent? Answer: _" Instead of sampling a single binary response, the logits corresponding to A and B could be normalized to obtain a continuous preference probability. Under the Bradley–Terry assumption, this probability could serve as a direct estimate of Barker acceptance, potentially providing richer information about the model's preference strength. Could the authors clarify why they use binary choices instead of logit-based preference probabilities? Could these richer preference signals improve the efficiency or reliability of prior estimation?

  2. The authors use an automatic interpretability pipeline to assign semantic labels to the learned sliders based on image–text similarities and LLM refinement. However, it remains unclear whether these labels accurately reflect the visual changes induced by the sliders. I would be interested in seeing whether the autoInterp results remain consistent when different MLLMs are used as the backbone of the interpretation pipeline. Additionally, the authors could consider conducting a small human study to validate the accuracy of the assigned labels.

  3. The paper assumes that MLLM preferences can be represented by a consistent latent utility function under the Bradley–Terry model. However, it remains unclear whether the models' pairwise preferences actually follow a consistent ordering. For example, could cyclic preferences arise, such as A > B, B > C, but C > A, when comparing different visual stimuli? Such inconsistencies would challenge the underlying Bradley–Terry assumption.

If a consistent preference ordering exists, it would also be interesting to investigate whether this ordering generalizes across different MLLMs. Do different models exhibit similar preference structures over the same visual stimuli, or do their rankings differ substantially? This could be investigated by constructing directed preference graphs, examining the presence of cycles, and comparing graph structures across models.

  1. Several recent works have investigated visual preferences and biases in vision models, such as Visual Persuasion [1] and DEXTER [2]. However, it remains unclear whether different approaches reveal consistent perceptual biases. Do these methods identify similar biases, or could they lead to substantially different, even contradictory, conclusions?

Moreover, I wonder whether perceptual biases could also be revealed through activation maximization. For example, given the prompt "[image] The person in this image looks intelligent.", one could maximize the logit of "intelligent" using methods such as DiffExplainer [2] or EnergyDPS [4], followed by caption-based interpretation as in DEXTER [3]. Would this approach reveal similar perceptual biases to those recovered through Gibbs sampling?

[1] Cherep et al. (2026). Visual Persuasion: What Influences Decisions of Vision-Language Models?. ICML 2026.

[2] Pennisi et al. (2025). DiffExplainer: Towards Cross-modal Global Explanations with Diffusion Models. Computer Vision and Image Understanding.

[3] Carnemolla et al. (2025). DEXTER: Diffusion-Guided EXplanations with TExtual Reasoning for Vision Models. NeurIPS 2025.

[4] Zhou et al. (2026). A Distributional View for Visual Mechanistic Interpretability: KL-Minimal Soft-Constraint Principle. ICML 2026.

4 comments

Thank you for your feedback! We have run an extra experiment, fixed a typo, and addressed concerns/misunderstandings. Let us know if anything needs further clarification. Otherwise, we would be grateful if you reconsidered increasing your score to reflect this new evidence.

The paper lacks comparisons with existing approaches for probing visual preferences and detecting biases, such as Visual Persuasion [1] and DEXTER [2]. It remains unclear whether the observed biases are intrinsic to the MLLMs or influenced by the probing method and generative model, and whether these findings generalize across different approaches.

While it is difficult to mount a direct comparison to Visual Persuasion [1] because of the many differences (no sliders to compare, etc.), we conducted a small-scale replication on two held-out datasets using a subset of sliders and targets:

  • Counterfactual edits: we sampled 10 real faces from the Face Research Lab London Set [2] and used Gemini 2.5 Flash Image (i.e. "Nano Banana") to produce high- and low-slider edits (100 edited images total) while instructing the model to preserve identity and unrelated visual properties. This approach is inspired by [1]
  • Natural faces: we selected high–low pairs per slider (100 images total) from MAAD-annotated [3] VGGFace2 [4] images (naturally occurring instances only). This is an even more extreme case with no edits

As seen below, the recovered estimated marginal means correlate significantly with the experiment posterior medians:

DatasetPearsonSpearman
Counterfactual edits$0.698,\ p = .001$$0.596,\ p = .009$
Natural faces$0.773,\ p < .001$$0.676,\ p = .002$

These results (which total over 4,000 VLM judgements) provide corroborating evidence, suggesting that a substantial part of the recovered structure transfers beyond the original FLUX–SliderSpace manifold. When we repeat this exercise with the confidence intervals from these new experiments vs. the credible intervals from the prior distributions, we see Pearson from $0.518$–$0.717$ ($p < 0.03$ for all).

[1] Cherep, M., Maes, P., & Singh, N. (2026). Visual Persuasion: What Influences Decisions of Vision-Language Models?.

[2] DeBruine, Lisa Marie and Benedict C. Jones. “Face Research Lab London Set.” (2017).

[3] Terhörst, P., Fährmann, D., Kolf, J. N., Damer, N., Kirchbuchner, F., & Kuijper, A. (2021). Maad-face: A massively annotated attribute dataset for face images.

[4] Cao, Q., Shen, L., Xie, W., Parkhi, O. M., & Zisserman, A. Vggface2: A dataset for recognising faces across pose and age. (2018)

The method relies on only 10 manually selected PCA-based sliders, which limits its ability to explore biases associated with other visual features.

Allow us to clarify. Our method is agnostic to the number of sliders and their semantic interpretation. These sliders are an experimenter’s degree of freedom, so anyone can study a different question with more or fewer sliders, having the same or different interpretations. To demonstrate the utility of our method, we rely on 10 sliders per domain, but this is not a limitation.

Appendix C reports a p-value of 0.02, whereas Figure 13 reports 0.002 for the same correlation

Thank you for catching this typo. The correct value is indeed $p = 0.002$ as in Figure 13.

Could the authors clarify why they use binary choices instead of logit-based preference probabilities? Could these richer preference signals improve the efficiency or reliability of prior estimation?

There are several reasons behind our choice:

  • This is more general, as it allows using the method on arbitrary proprietary models via black-box queries only
  • The binary choice paradigm has a precise interpretation due to decades of work in behavioral and cognitive science [1,2,3]
  • Logit-based probabilities can be miscalibrated in post-trained models [4]
  • This allows future comparisons with humans, from whom logits cannot be directly obtained
  • Using logits would require additional assumptions about how token probabilities relate to subjective preferences
  • Users interact with models through their outputs, and so this approach captures behaviors which users normally see

[1] Thurstone, L. L. (2017). A law of comparative judgment. In Scaling (pp. 81-92). Routledge.

[2] Bradley, R. A., & Terry, M. E. (1952). Rank analysis of incomplete block designs: I. the method of paired comparisons. Biometrika, 39(3/4), 324-345.

[3] Sanborn, A., & Griffiths, T. (2007). Markov chain Monte Carlo with people. Advances in neural information processing systems, 20.

[4] Xie, J., Chen, A. S., Lee, Y., Mitchell, E., & Finn, C. (2024, November). Calibrating language models with adaptive temperature scaling. In Proceedings of the 2024 Conference on Empirical Methods in Natural Language Processing (pp. 18128-18138).

The authors use an automatic interpretability pipeline to assign semantic labels to the learned sliders based on image–text similarities and LLM refinement. However, it remains unclear whether these labels accurately reflect the visual changes induced by the sliders. I would be interested in seeing whether the autoInterp results remain consistent when different MLLMs are used as the backbone of the interpretation pipeline. Additionally, the authors could consider conducting a small human study to validate the accuracy of the assigned labels.

We agree that the interpretability of the controls is important. However, it’s worth noting that the semantic labels are post-hoc interpretations of the learned coordinates and not inputs to the MLLM acceptance decisions.

A slider being mislabeled would require correcting the semantic interpretation of its results, but would not retrospectively change anything in the sampling procedure (e.g. models’ preferences, etc.). Therefore, validating (or not) the auto-interpreted labels would not affect the underlying correctness of our method.

A human validation study or interpretability with different MLLMs would assess the reliability of the semantic interpretation, rather than the validity of the method itself.

### [...] it remains unclear whether the models' pairwise preferences actually follow a consistent ordering. For example, could cyclic preferences arise, such as A > B, B > C, but C > A, when comparing different visual stimuli? Such inconsistencies would challenge the underlying Bradley–Terry assumption.

Intransitivity in individual stochastic comparisons does not, by itself, violate Bradley-Terry. Under a probabilistic preference model, it is entirely possible to observe A > B, B > C, and C > A in three individual trials, even when all comparison probabilities are generated by a globally consistent utility function.

In fact, the intransitivity of preferences is a well-known result in studies with people, as described by Amos Tversky in Intransitivity of preferences (1969).

It’s also important to note that in high-dimensional manifolds (generative models such as FLUX) with continuous sliders, these transitive cycles are extremely unlikely to occur.

Do different models exhibit similar preference structures over the same visual stimuli, or do their rankings differ substantially? This could be investigated by constructing directed preference graphs, examining the presence of cycles, and comparing graph structures across models.

We already analyze cross-model agreement in Section 4.3, and Figure 3 reports pairwise Spearman rank correlations between model-specific slider rankings across all four domains. The results show that agreement varies substantially by domain.

Constructing directed preference graphs is out of scope—it is unclear how we could make a graph out of 10d continuous parameters—but the general question of cross-model consistency is already investigated.

Moreover, I wonder whether perceptual biases could also be revealed through activation maximization. [...] Would this approach reveal similar perceptual biases to those recovered through Gibbs sampling?

This would be a completely different method that differs in the object it estimates (e.g., no preference distribution over interpretable controls), and is thus beyond the scope of this paper. It’s also worth reiterating the limitations of using logits, as we described in detail above (e.g. restriction to open-source models).

I thank the authors for their responses and the effort devoted to the additional experiments. I appreciate the clarifications and would like to share two final thoughts.

First, regarding binary choices, I appreciate their value in enabling comparisons between MLLMs and humans. However, while MLLMs share certain behavioral similarities with humans, they also possess unique properties, such as steerability and access to internal signals like logits. I believe that both adapting established cognitive science methods and developing model-native probing approaches are valuable directions. Exploring the connections and differences between the perceptual priors recovered by these approaches could also be an interesting avenue for future research.

Second, regarding the Bradley-Terry assumption, my concern is not about stochastic cycles arising from individual random comparisons, but rather systematic intransitivity in the underlying preference probabilities. In fact, Tversky (1969) explicitly investigates violations of weak stochastic transitivity, which would be incompatible with the BT assumption. Such violations could be examined through repeated comparisons of fixed stimuli, even along a single slider dimension. I believe this distinction deserves further consideration.

I will therefore maintain my original rating.

Thank you for engaging with us in the discussion! We have now updated the paper (with all changes highlighted in blue) to (1) include a discussion regarding access to internal signals, like logits, in Appendix Q, and (2) include new experiments across 13,824 judgments showing NO systematic intransitivity in the MLLM preferences in Appendix R.

We’ve also fixed the typo you mentioned in Appendix C and included your suggested experiments comparing to Visual Persuasion in Appendix O.

We believe we have gone above and beyond to improve our paper following your feedback, and would appreciate it if you could consider raising your score.

Reviewer_VwqqOpenReview ↗
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1
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2
Informativeness
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1
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Paper summary

This paper proposes a method to probe the implicit perceptual preferences of multimodal language models (MLLMs) using Metropolis–Hastings-within-Gibbs sampling. The authors use FLUX with SliderSpace to generate images controlled by interpretable visual features, such as smiling, eyeglasses, and gender presentation. At each iteration, one slider is randomly modified, and an MLLM is asked to choose which image better matches a target concept (e.g., intelligence or trustworthiness). The authors interpret these choices as Barker acceptance decisions, allowing them to sample a distribution over visual features conditioned on the target concept. They apply the framework to four MLLMs across 23 target concepts and report visual associations and demographic biases.

Critical strengths
  1. Interesting application of established psychophysical methods. Adapting Gibbs Sampling with People to MLLMs provides a potentially useful framework for behavioral evaluation.

  2. Interpretable experimental controls. Using learned semantic directions in a diffusion model enables relatively systematic manipulation of visual features, which is useful for studying MLLM judgments.

  3. Broad empirical evaluation. The experiments cover multiple models and perceptual domains, and include comparisons with direct rating and pairwise-preference baselines.

Critical weaknesses
  1. The central MCMC assumption is not adequately validated. The method assumes that MLLM pairwise choices follow a Bradley–Terry model corresponding to a consistent global utility function. However, the authors do not directly establish this assumption. Coordinate-wise comparisons are not sufficient unless they are compatible with the same joint distribution. Orthogonality of the CLIP directions does not guarantee consistency of MLLM preferences. Without this assumption, the proposed transition kernel is not guaranteed to sample the claimed target distribution.

  2. Insufficient justification for the generative control mechanism. The authors rely on training LoRA adapters to manipulate PCA directions in CLIP space. It is unclear why this comparatively complicated mechanism is necessary. Simpler alternatives, including direct text conditioning or learned conditioning embeddings (e.g., textual inversion), could potentially provide comparable semantic controls. These alternatives should be evaluated experimentally, particularly given the additional training and computational costs.

  3. The interpretation as a perceptual prior is questionable. The recovered distribution is conditioned on a textual criterion and restricted to images reachable through a small, selected set of FLUX sliders. It is therefore more accurately described as a task-conditioned preference distribution within a particular generative representation, rather than the MLLM's underlying perceptual prior.

  4. Convergence and reliability concerns. Some reported chains exhibit poor mixing, with substantial deviations of R-hat from 1. The paper's convergence and predictive diagnostics do not establish that the Bradley–Terry assumption holds. Consequently, the reliability of some reported posterior estimates remains uncertain.

Questions for authors
  1. How do the authors validate the Bradley–Terry assumption and ensure that the MCMC sampler targets a well-defined joint distribution?
  2. Why use LoRA-based sliders instead of simpler alternatives such as text conditioning or textual inversion?
  3. What does MCMC offer over direct pairwise preference evaluations?
  4. Why interpret the recovered task-conditioned preferences as perceptual priors?
6 comments

We respectfully disagree with this review. Your score depends on 4 premises, and below we explain why each is either inaccurate or already addressed in the paper. To summarize:

  1. You argue that our sampler is unsound because we do not validate Bradley–Terry (BT). BT is an assumption, as is standard in MCMCP/GSP [1, 2], RLHF/RLAIF [3,4], DPO [5], and Elo ratings. In fact, our assumption is weaker, as we explain below. You call our method an “application of established psychophysical methods" — we agree, and this is one such method
  2. You suggest text conditioning/inversion could match SliderSpace. Gibbs sampling requires separate, continuous dimensions which we can update one at a time. We cannot obtain these from text conditioning or textual inversion.
  3. You question our use of "perceptual prior." Here we follow prior work [e.g. 6]. Specifically, we seek to sample from subjective probability distributions which shape decisions. We sample from $\pi(z \mid C) \propto \exp(\ell_C(z))$, and obtain this distribution from the model's decisions, so your suggested "task-conditioned preference distribution" describes the same object
  4. You express concern about high $\hat{R}$ scores. We use predictive checks in which we can predict held-out model decisions above chance across all models and domains. Also, $\hat{R}$ is one diagnostic and even here our values are similar to those from GSP [2] (we recomputed from their faces data). We discuss below how our HSL experiments also add internal validity. We report $\hat{R}$s for transparency

How do the authors validate the Bradley-Terry assumption? (Q1 and W1)

This conflates the mathematical validity of our proposed sampling construction with the empirical question of how accurately Bradley-Terry approximates MLLM judgments.

BT is a standard assumption throughout preference modeling research [1–6] where MCMCP is perhaps the closest precedent [1]. Sanborn and Griffiths treat pairwise choices as Barker acceptances under a Luce/BT choice rule (without first proving that people follow BT). This is also applied to model judgments in RLAIF reward models [4].

Importantly, our assumption is also weaker than full BT. In Assumption 1, we require BT only for comparisons which change one slider. By contrast, it is standard to assume BT for all stimulus pairs in traditional RLHF, DPO, and Elo ratings.

Under Assumption 1, our sampler targets $\pi$. We posit one global utility $\ell(z)$ and so coordinate updates are compatible by construction. Using symmetric proposals and Barker acceptance, we obtain, for any two states that differ along one coordinate:

$$ \frac{\alpha(z,z')}{\alpha(z',z)} = \exp(\ell(z')-\ell(z)) = \frac{\pi(z')}{\pi(z)} $$

We do not require independence between sliders. In fact, recovering interactions between sliders is one of our main reasons for using this approach.

Note that we also check resulting behavior empirically. In our HSL experiment (see Appendix G), we know the correct answer for every target. Across 10 chains of 2,000 trials each, we recover the correct color region for all eight targets. Also, we use predictive checks (see Appendix E) wherein we use sampled densities to predict held-out accept and reject decisions. Under BT, models should accept proposals more often when $\pi(z') > \pi(z)$, and this predicts their decisions above chance across all models and domains

Why use LoRA-based sliders instead of simpler alternatives such as text conditioning or textual inversion? (W2 and Q2)

This goes directly against the purpose of the experimental design.

This Gibbs sampling based approach requires:

  1. Continuous control over visual attributes
  2. Reasonably consistent semantic meaning across slider values
  3. Composable interventions that permit coordinate-wise updates while other coordinates remain fixed.

Prompt edits are discrete and almost always change several attributes at once in an uncontrolled way. With textual inversion, we could perhaps learn embeddings for individual concepts but each embedding yields a point in token space (i.e. not an axis). Textual inversion would also require us to specify concepts in advance and collect example images for each one. With SliderSpace, we discover interpretable axes automatically (we additionally validate the resulting slider space in Appendix K). GSP [2], under the same requirement, controlled StyleGAN through PCA directions from GANSpace

Importantly, LoRA is not a requirement of our proposed sampling method. Section 2.3 explicitly discusses alternative controllable representations. Our contribution is the general sampling framework, realized here with LoRAs because they have these favorable properties. Training these is simple and takes only about 9 GPU hours per domain

As an extra generator-independence experiment, we validated a subset of recovered priors on two held-out datasets. In the first, we edited real faces from the Face Research Lab London Set with Gemini 2.5 Flash Image. In the second, we selected natural face pairs from VGGFace2 using MAAD attribute annotations. Across more than 4,000 MLLM judgments, our posterior medians correlate with held-out effects at Pearson $r = 0.698$ ($p = .001$) for edited faces and $r = 0.773$ ($p < .001$) for natural faces. Our credible intervals also correlate with the held-out confidence intervals ($r = 0.518$–$0.717$, $p < .03$).

The interpretation as a perceptual prior is questionable. (W3 and Q4)

We follow existing work. In MCMCP, Sanborn and Griffiths sample from subjective probability distributions over stimuli associated with categories, which formal models of cognition use to capture learners' assumptions [1]. Zhu and Griffiths [6] refer to these distributions as "priors" when eliciting them from LLMs. We sample from $\pi(z \mid C) \propto \exp(\ell_C(z))$, with textual criteria $C$ in place of categories, and we obtain this distribution from the model's decisions. Thus, the suggested term of "task-conditioned preference distribution" describes this same object already

You also note that we restrict sampling to stimuli the generator can reach. We state this explicitly ourselves in Sections 4/5, and in Appendix K we test regions these sliders can reach. GSP [2] indeed operated under much more restrictive constraints, since they used PCA on domain constrained StyleGAN. We also selected sliders before probing any targets, i.e. we could not tune them to produce particular associations

We will add an explicit definition of perceptual prior to Section 3.

Convergence and reliability concerns (W4)

Our predictive checks show that these chains do meaningfully capture models' preferences. Within chains, we predict held-out accept and reject decisions with median accuracies of $\approx$ 0.70--0.83 across all models and domains (Figure 15). This includes conditions with the highest $\hat{R}$. Then, across chains, we fit densities on all chains but one and predict decisions from the held-out chain. We again predict above chance for every model and domain, with medians of $\approx$ 0.55--0.70 (Figure 16). 26/32 of tests against random chance are significant at $p < .05$

Our $\hat{R}$ values are similar to those of GSP. In GSP study 4a, median $\hat{R}$ across sliders (per our reanalysis from their data) ranges from 1.07--1.23 across targets, and the max $\hat{R}$ is 2.41. Between 4 and 8 of their 10 sliders exceed 1.10 per target. Across their other face studies, $\hat{R}$ goes up to 5.78. On our face domain, median $\hat{R}$ ranges from 1.11--1.33 across models, and worst $\hat{R}$ ranges from 1.42--2.79 (as per Table 2)

Our HSL experiment shows how chains can recover correct distributions even under suboptimal $\hat{R}$. In this experiment, we know the correct answer for every target and we clearly recover the correct color for all 8 targets (Figure 17). Yet on saturation and lightness, which are bounded and non-circular like our sliders, $\hat{R}$ goes up to 1.70 for lavender, 1.80 for eggshell, etc. These values cover most of the range we report in our main experiments, where median $\hat{R}$ goes from 1.02--1.60 (as per Table 2)

Importantly, poor mixing appears in a few conditions. We acknowledge it lowers precision there, and include these values precisely for this reason (i.e. transparency). GPT-5.4 and Claude Sonnet 4.6 have median split $\hat{R}$ of 1.02--1.20 across all 4 domains, and at most 1% of their parameters exceed 1.5. We therefore draw our main conclusions from effects that replicate across independent chains and models. We would thus argue that it is misleading to interpret the least converged conditions as being representative of our full evaluation

What does MCMC offer over direct pairwise preference evaluations? (Q3)

This question is already addressed experimentally in Section 4.5 and Appendix C, in which we compare our method against both direct scalar ratings and pairwise Bradley–Terry evaluations.

Consider alternate ways of approximating a posterior over $d=10$ sliders (this is the number of generations/queries):

MethodComplexityEvaluations per model–target
10-level factorial$O(10^d)$$10^{10}$ = 10 Billion
5-level factorial$O(5^d)$$5^{10}$ = 9.8 Million
Uniform random sampling$O(N)$$N$
Independent slider sweeps$O(dm)$$10 \times 10 = 100$
Ours: MH-within-Gibbs$O(T)$$10 \times 2,000 = 20,000$

Factorial approaches preserve interactions but scale exponentially, and independent sweeps are cheap but discard interactions. Random sampling is flexible depending on budget $N$, and thus is equivalent to (joint) IMH-without-Gibbs and less efficient unless the posteriors are near-uniform. Our method preserves interactions while making the cost linear in the number of sampling iterations.

Therefore, our approach is not a replacement for pairwise evaluation; it is a way of turning pairwise evaluations into samples from a joint distribution. This is the central methodological contribution of the paper.

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

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