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Under review as a conference paper at ICLR 2027

Belief Without Behavior: Evaluating Social Reasoning-to-Action in Multimodal LLM Agents

Abstract

Effective social interaction requires agents to translate mental state inferences into coordinated behavioral signals across verbal and nonverbal channels simultaneously. Yet existing benchmarks evaluate theory of mind (ToM) reasoning and embodied behavior in isolation, leaving unmeasured the gap between social inference and social action. We introduce MOSAIC (Multimodal Orchestration of Social Action, Inference, and Communication), a controlled benchmark in which two embodied agents interact across cooperative and competitive scenarios requiring integration of verbal statements, spatial trajectories, gaze direction, and facial expression under varied ToM constraints. Evaluating 16 models, including 14 VLMs, across 200 trials per model, we find that VLMs fail to produce behaviors consistent with the expected outcomes under ToM-order constraints, and that imposing explicit ToM-order constraints produces no reliable behavioral change aligned with the specified reasoning level. Signal-level diagnostics identify two recurring bottlenecks: weak directional signal production, and limited correspondence between available signals and receiver choices. PCM-LLM, included as a structured architectural reference point with an explicit ToM module, is the only evaluated system that clears both bottlenecks under the canonical experimental geometry, but its deceptive strategy collapses under non-canonical spatial layouts, indicating that explicit belief-action coupling is a promising, though not on its own sufficient or robust, architectural ingredient for this class of tasks.

Primary area:
datasets and benchmarks
Keywords:
theory of mind, embodied social intelligence, vision-language models, social reasoning and deception

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

This paper proposes MOSAIC, a benchmark for evaluating whether multimodal models can act on social inferences rather than only report them. Most theory-of-mind benchmarks ask a model questions about someone else's mental state. Here, two embodied agents share a virtual room, and one of them is responsible for changing what the other believes. The informed agent knows which of two boxes hides a reward. It must help its partner in cooperative mode and work against it in competitive mode, where actively misleading the partner is expected only under the deeper-reasoning condition. The uninformed agent has to work out where the reward is from the informed agent's behavior and words. Signals travel through several channels at once. These are where the informed agent walks, where it looks, its facial and physiological expression, and three short spoken exchanges. The outcome is decided by which box the uninformed agent ends up closest to. The authors cross the cooperative/competitive framing with how deeply the informed agent is asked to reason, either acting on its own preferences (ToM-0), or deliberately modeling and steering its partner's beliefs (ToM-1). This gives four conditions, labeled Cooperative-ToM0 through Competitive-ToM1. They evaluate a range of small open vision-language models (1B–14B), a text-only model, and PCM-LLM that serves as a reference point.

The most notable aspect is how the evaluation separates outcome from mechanism. The primary score, TOCS, measures how often a trial's outcome matches what its condition predicts. It is read alongside two checks on whether apparent success is real. One is positional bias, a fixed habit of picking the same box. The other is an uncertainty rate, the share of trials where the agent ends equidistant from both boxes, which the authors read as a failure to move. The separate signal scores ask whether the informed agent produced a usable signal. They cover how often it shows facial expression and whether its gaze and trajectory point toward the reward. A final score asks whether the partner's choice followed that signal. This shifts the question from whether a model can win the game to where it breaks along the chain from inference to signal, to response. The central claim comes out of this framing. No vision-language model's outcome differs significantly from chance after multiple-comparison correction, and telling the informed agent to reason more deeply does not reliably change its behavior. Most models fail to produce coherent nonverbal signals in the first place, and when signals are present, the partner does not act on them. Only PCM-LLM gets through both steps in the original layout, and even its deception falls apart when the room layout changes. The authors also report that removing the rendered image does not hurt the two models it was tested on, and that imitation fine-tuning on PCM-LLM's behavior does not close the gap.

Critical strengths

Critical Strengths

  1. Social reasoning is tested through action, not question answering.
    • The informed agent must change its partner's belief through movement, gaze, expression and speech, and the score depends on hat the partner finally does. Most ToM benchmarks only ask about mental states, and most multi-agent ones stay in language.
    • The 2×2 design gives each condition a clear expected outcome. The task is solvable, since the reference architecture succeeds in most conditions, yet no VLM differs from chance.
    • This is the paper's main contribution.
  2. Diagnostics that catch shortcuts and show where a model fails.
    • Positional bias and uncertainty rate reveal when apparent success comes from a fixed habit or a failure to move.
    • Separate scores for the sender's signals and the receiver's response show which side of the exchange breaks.
  3. Changing the room layout breaks the reference architecture's deception, and the authors trace this to a specific flaw in how it models visibility.
Critical weaknesses
  1. Using one model for both agents prevents a clean separation of signal production and signal decoding.

    • The same model checkpoint plays both the subject and the participant in every run (Sec. 3). FES, GAS and TAS measure subject-side signal production, but SSS and TOCS depend on both agents together. Participant-side decoding is therefore observable only when the same model also produces clear subject-side signals, which the paper reports for very few models. A model that produces clear signals but decodes poorly can also obtain the same TOCS as a model that fails at both.
    • Evaluating each model against a fixed reference agent in the other role would separate subject-side and participant-side performance and make both comparable across models.
    • The title claim, that models form correct beliefs but fail to act on them, has no corresponding metric. Sec. 4 describes its evidence as an exploratory analysis of one hand-picked case per failure type, with no frequency estimates, although the logged reasoning traces would allow a trial-level count. A benchmark's value rests on scores that can be attributed to the capability it claims to measure.
  2. The task design confounds social reasoning with other factors.

    • Movement actions are specified in egocentric directions, while positions are given in world-frame coordinates (App. B). The paper's own cases show the reasoning trace naming the correct box, followed by movement toward the wrong one because world-frame coordinates are mapped onto egocentric directions incorrectly (Sec. 4, App. E). TOCS, therefore, mixes social reasoning failures with spatial grounding failures, and no ablation with object-targeted movement separates the two.
    • The ToM conditions are set only through prompt text, with no check that models follow them. The subject is told its strategy "should match" its ToM order and that it "may" mislead, and the prompt defines ToM order 0 only by how much an agent trusts others, not by how the subject should act. The authors note that this does not establish that models follow the specified reasoning (Sec. 3.2). The null effect of ToM order therefore cannot distinguish an inability to reason at ToM-1 from not following the instruction.
    • The benchmark is framed as multimodal, but positions, orientations and preferences are also provided in the structured belief-and-observation state. The text-only Llama-8B reaches comparable TOCS and higher TAS than most VLMs (Table 4, Fig. 3), and removing the rendered image does not degrade either model tested. The necessity of the visual channel is not established.
    • The subject-side metrics do not distinguish deceptive from honest signaling. Under Competitive-ToM1, PCM-LLM obtains TAS 1.00 and GAS 0.74, the same sign as a subject the paper describes as following an honest strategy (App. I.2), whereas Table 1 defines misdirection as a negative score. SSS is also affected by fixed spatial biases of both agents in the canonical layout (App. D.1), contrary to the statement in Sec. 4.3.1 that this layout largely avoids the problem. - TOCS places every VLM at chance, so differences between models appear only in the signal-level metrics (App. D.2.5).
  3. Several reported results are inconsistent with the paper's own tables and figures.

    • PCM-LLM's Competitive-ToM1 result in that the canonical layout is not significant in Table 4 (p_adj = 0.136) but is significant in Table 7 (p_adj = 0.046), likely because the two tables apply Holm correction over different sets of tests. The chi-square tests diverge in the same way (Tables 5 and 8). The paper does not state which correction applies.
  4. Several values reported in the text differ from the corresponding figures and tables.

Questions for authors
  1. In the participant's belief states shown in App. E.2, fields such as "Marie | felt emotion valence" and "Marie | preference towards Dark brown box" appear. Are these the participants' own estimates or the subject's true values?
  2. After each verbal exchange, the subject's preference-updating module can change its preference toward the participant and toward the boxes. Both the interaction mode and the subject's belief about where the reward is are encoded as these preferences. How often does either one change during a trial, and how are such trials handled in the analysis? Are there any statistics present on this? If not, can the authors provide?
  3. App. C.3 defines GAS using a gaze certainty for each box and a threshold θ_g. How is this certainty computed from the subject's behavior, and what value of θ_g is used?
  4. App. B.1 says reward locations were assigned without a fixed seed, while App. F.2 says identical seeds were used across models. Which is correct? Since each cell appears to have been run once at temperature 0.7, could you report confidence intervals for the signal-level metrics as well as for TOCS?
  5. App. F.3.2 reports InternVL-14B SSS values from −0.227 to −0.731 in the aligned layout, and App. F.3.3 describes its TAS and GAS as showing strongly negative correlations in the orthogonal layout. Neither matches the per-condition values in Fig. 6. Are these values computed separately by reward location?
  6. The Discussion mentions a study with 35 human participants under a related nine-round protocol. Could you report its methods, ethics approval, and results, and explain how its protocol differs from MOSAIC?
  7. For the two fine-tuned InternVL models (App. H), how many demonstrations were used, which agent role was trained, and what training settings were used?
  8. Using the logged reasoning traces, please report per model and condition how often the box named in the reasoning differs from the box the agent then moves toward.
  9. Please report SSS only for the trials in which the subject produced a clear directional signal, so that participant-side decoding is measured only where a signal exists.
  10. Why are the evaluations not presented against a fixed reference agent in the subject role?
  11. Please see the Weaknesses section. I have mentioned some issues there.
10 comments
AuthorsOpenReview ↗

Response to Weakness 1

Response to W1.1 and 1.2:

We thank the reviewer for the careful reading of our signal-level metrics. We agree that even role-specific metrics cannot cleanly separate the two roles, so we ran the suggested cross-play. The fixed reference agent is PCM-LLM, the only system that both produces and reads signals in self-play. It was paired with Internvl-4B, -8B, -14B, Minicpm-8B, and Qwen3.5-9B in both directions, with 50 trials per cell, otherwise as in the main experiment. We chose these five because their self-play subjects represent different channel profiles under cooperation: Internvl-14B gives clear trajectory and gaze signals (TAS 0.76–0.86, GAS 0.88–0.90), Qwen3.5-9B mainly gaze (GAS 0.52–0.58), Minicpm-8B gaze only in Coop-ToM1 (GAS 0.50, TAS ≤ 0.08), and Internvl-8B and Internvl-4B weak signals on both channels (TAS ≤ 0.26, GAS ≤ 0.42).

PairingVLMCoop-ToM0Coop-ToM1Comp-ToM0Comp-ToM1
VLM subject, PCM-LLM participantInternvl-14B0.78 (0.45)0.66 (0.47)0.44 (0.42)0.36 (0.43)
Internvl-8B0.94 (0.48)0.80 (0.48)0.60 (0.47)0.34 (0.42)
Internvl-4B0.88 (0.48)0.68 (0.44)0.74 (0.44)0.14↓ (0.44)
Minicpm-8B0.64 (0.47)0.80 (0.47)0.54 (0.45)0.50 (0.44)
Qwen3.5-9B0.62 (0.47)0.48 (0.45)0.48 (0.45)0.40 (0.47)
PCM-LLM subject, VLM participantInternvl-14B0.34 (0.37)0.46 (0.33)0.40 (0.38)0.38 (0.37)
Internvl-8B0.28 (0.35)0.40 (0.34)0.30 (0.34)0.44 (0.38)
Internvl-4B0.14↓ (0.34)0.28 (0.35)0.24↓ (0.41)0.50 (0.40)
Minicpm-8B0.32 (0.39)0.38 (0.43)0.40 (0.38)0.52 (0.44)
Qwen3.5-9B0.34 (0.33)0.30 (0.38)0.26 (0.32)0.40 (0.35)

TOCS with the chance level in parentheses. Bold: above chance. ↓: below chance (Holm within each model's four conditions, p_adj < 0.05).

  • VLM as subject: some signals are usable. The three Internvl models in both cooperative conditions and Minicpm-8B in Coop-ToM1 are above chance. PCM-LLM also follows the VLM subject's gaze above the baseline (Minicpm-8B and Qwen3.5-9B in all conditions, the Internvl models in the cooperative ones). The strongest sender is the smallest model, Internvl-4B, whose Coop-ToM0 TOCS rises from 0.26 in self-play to 0.88.
  • VLM as participant: the failure is on the receiver side. PCM-LLM's signals are clear (TAS 0.72–1.00, cooperative GAS 0.76–1.00), yet no VLM participant is above chance (p_adj ≥ 0.14), and only 1 of 40 per-channel follow scores is above the baseline. The Internvl-4B participant even turns away from the signals (Coop-ToM0 0.14 and Comp-ToM0 0.24, both below chance).
  • Competition. Misleading signals could lead PCM-LLM's ToM-0 participant to the empty box, but no VLM subject shows reliable Comp-ToM1 outcome conformance. Internvl-4B reveals the reward box honestly under both ToM orders. This meets the ToM-0 prediction in Comp-ToM0 (0.74, above chance) and lowers Comp-ToM1 TOCS to 0.14 (below chance). With VLM participants, no competitive pairing is above chance.

Therefore, the sender side and the receiver side can therefore be clearly distinguished.

Response to W1.3:

We accept this point and used all logs to add frequency statistics at two levels, now reported in Appendices E.4 and E.5.

  • Trial level. We take the participant's preferred box at the last timestep as its belief and compare how often the final choice differs from it with a within-cell permutation baseline. PCM-LLM's rate is 0.02–0.15, below the baseline of about 0.5 in all four conditions. No VLM is below the baseline in self-play. Internvl-14B sits at the baseline (0.46–0.61 vs. 0.48–0.51), and Internvl-4B and Qwenvl-4B in Comp-ToM1 and Qwen3.5-9B in Coop-ToM1 are even above it. Yet the final beliefs of the Internvl-4B, Qwenvl-8B, and Qwenvl-4B participants point to the reward box in three or four conditions. This is a correct belief that action does not follow.
  • Call level. The share of moves away from the box named in the reasoning is mostly at most 0.28 for subjects, but at least 0.50 for both boxes in 6 models' participants, up to 0.86 (Q8).

Belief-to-action conversion is therefore a measurable bottleneck, concentrated on the participant side. It is, however, only part of the failure. For the other VLMs, the chain breaks earlier: the subject sends no directional signal, or the participant forms no correct belief. We therefore changed the title to a neutral one that covers every break point: "MOSAIC: Tracing Social Reasoning from Belief to Behavior in Embodied Multimodal Agents".

AuthorsOpenReview ↗

Response to Q1-Q4

Response to Q1:

Thanks for this question. We clarify that they are the participant's own estimates, not the subject's true values, so there is no information leakage that would undermine attributing the participant's success to social reasoning. Each agent receives only its own belief state. Felt emotion and preference are the participant's estimates of the subject, updated by its own belief module from observations (or dialogue), never copied from the subject's state. "Marie | felt emotion valence" makes this clearest: felt emotion is internal, so others can only infer it from facial and physiological cues.

PCM-LLM's successful deception also requires these fields to be estimates. In Comp-ToM1, the subject shows a negative expression while gazing at the reward box, the participant's estimate of "the subject prefers the reward box" drops to −0.49-0.49, and 70% of trials end at the empty box. A participant reading true values could not be misled.

Response to Q2:

We thank the reviewer for this question and provide the statistics below.

Frequency. Each trial has three verbal exchanges, each followed by one output of the preference-updating module. Per trial, the module requests a change in the subject's preference toward the participant 0.58 times and toward the boxes 1.65 times on average. These requests reverse the interaction mode 0.17 times and the reward belief 0.21 times per trial.

Handling. The original analysis kept all trials and did not treat trials with reversal requests separately, because verbal updates are a small share of the subject's preference updates. At each of the 10 timesteps, the subject re-outputs its preferences in action prediction from the nonverbal interaction, whereas verbal updates occur only 3 times (rounds 3, 6, and 9) and reverse the mode or reward belief less than once per trial. Verbally induced changes are therefore likely to be overwritten or diluted by the many nonverbal updates that follow. They may matter in individual trials, but we suppose that their effect on the overall statistics is limited.

Response to Q3:

We thank the reviewer for pointing out this missing piece of the GAS definition. With this addition, GAS is fully reproducible. Gaze certainty reuses the sensory-certainty function of the Projective Consciousness Model (Rudrauf et al., 2022, J. Theor. Biol., Section 4.2.2). It is visual acuity, which decays exponentially as the box moves away from the center of gaze, divided by a distance term. With ϕ\phi the angle between the gaze direction and the direction to the box, and dd the box distance projected onto the gaze direction:

gi,tb=2exp⁡(−κ(1−cos⁡ϕ)/2)1+max⁡(1,λd),κ=10, λ=0.01.g^b_{i,t}=\frac{2\exp\big(-\kappa(1-\cos\phi)/2\big)}{1+\max(1,\lambda d)},\quad \kappa=10,\ \lambda=0.01.

Values lie in (0, 1]. There is no gaze command. The subject controls its gaze by moving and turning, so GAS measures the gaze signal it produces with its body.

θg\theta_g is fixed at 0.3 in all experiments, chosen from how certainty varies with pose.

  • Initial pose. Facing the participant, subject has initial certainty about 0.28 towards both boxes.
  • Turning toward a box in place raises that box's certainty to about 0.44.

0.3 lies in between. The default pose counts as gazing at no box, and turning toward a box counts as gazing at it even without approaching it. Appendix C.3 now gives the formula, source, parameters, and this rationale.

Response to Q4:

Random seeds. Appendix B.1 is correct. The "identical seeds" statement in F.2 was wrong and has been removed. No experiment used a fixed seed. The reward location is drawn independently in each trial, so reward sequences differ across models. We checked balance after the experiments. In the main experiment, the reward is at b1b_1 in 465, 447, 449, and 460 of the 900 trials per condition (p ⩾\geqslant 0.33, Appendix D.2). In the layout experiment, it is at b1b_1 in 20–32 of the 50 trials per cell, and no cell deviates from 0.5 (uncorrected p⩾0.065p \geqslant 0.065, Appendix F.3). In F.1, "counterbalanced" now reads "drawn at random in each trial and checked for balance after the experiment".

Confidence intervals. Each cell was not run only once. It contains 50 independent trials, each sampled at temperature 0.7. We added 95% intervals for TOCS (exact Clopper-Pearson) and for TAS, GAS, FES, and SSS (10,000 bootstrap resamples) in every cell. The median half-widths are 0.14 for TOCS, 0.22 for TAS, 0.24 for GAS, 0.17 for SSS, and 0.04 for FES. The full table for all 18 systems and four conditions is added to Appendix D.2, and the intervals for the layout experiment to Appendix F.3.

AuthorsOpenReview ↗

Response to Q5-Q7

Response to Q5:

  • F.3.2. (aligned layout, Internvl-14B). These values were not computed by reward location. They are a typo: the text was not updated to match the figure. The per-condition SSS shown in Fig. 6 is −0.52-0.52 to −0.23-0.23, and the revision now reports these values.
  • F.3.3 (orthogonal layout, Internvl-14B). "Both TAS and GAS show strongly negative correlations" was ambiguous. It meant that the subject's trajectory and gaze signals correlate strongly negatively with the participant's choice, that is, a strongly negative SSS, not that TAS and GAS are negative. The participant picks the dark box in 44–49 of the 50 trials per condition, while the subject's signals lean toward the light box. The two fixed preferences point to opposite boxes, so SSS is strongly negative. The sentence now reports TAS, GAS, and SSS directly.

Response to Q6:

This is a human-participant experiment we ran under a related protocol, and its full results are not in this paper. The main difference from MOSAIC is the number of rounds per trial.

Methods. Participants wore a VR headset (Meta Quest Pro) and replaced the participant agent in the competitive task against the subject agent, Marie. As in MOSAIC, Marie knows where the reward is, the participant infers it from Marie's verbal and nonverbal behavior, and the choice is the box the participant ends closer to. MOSAIC trials have 10 rounds, with verbal rounds at R3, R6, and R9. Human trials have 9 rounds, 7 nonverbal and 2 verbal (R3, R6), because each round gives both sides a fixed 10-second thinking period and 10 rounds would keep participants in VR too long. The design was 2×22\times 2 within-subject, crossing Marie's architecture (PCM-LLM vs. Llama3.1-8B-Instruct) with ToM order (ToM-0 vs. ToM-1). Position, gaze target, and facial action units were recorded at every step, and participants answered a questionnaire in VR after each trial. As a reference, we ran 280 agent-agent simulations (70 per condition) under the same 9-round protocol.

Ethics and participants. The study was approved by the institutional ethics review board (institution and approval number withheld for anonymous review), and all participants gave written informed consent. Of 38 recruited participants, 3 were excluded because VR discomfort prevented them from completing all trials, leaving 35 (19 female, 16 male, age 22.37±4.3322.37 \pm 4.33 years).

Results. Task success was compared with a binomial GEE clustered on participant, and seven-round trajectories and gaze sequences with clustered bootstrap tests, with Bonferroni correction within each family. Task success did not differ between human and simulated participants in any condition (padj⩾0.12p_{\text{adj}} \geqslant 0.12). Human/simulated TOCS: PCM-LLM ToM-0 0.67/0.64, PCM-LLM ToM-1 0.47/0.63, LLM ToM-0 0.49/0.44, LLM ToM-1 0.54/0.61. Behavior nonetheless differed: 9 of 12 continuous trajectory comparisons and all 4 gaze-sequence comparisons were significant.

Role in the paper. Because the round schedule differs and only the competitive condition was tested, the study cannot serve as a human baseline for MOSAIC, and the Discussion uses it only as human-level support. It shows that equal task success can coexist with different receiver behavior, in line with MOSAIC's point that outcome metrics are not self-validating and must be reported with signal production and receiver behavior.

Response to Q7:

The full setup is in the table in our response to Reviewer 2, W2, and is added to Appendix H.

Reviewer_Vw9GOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper studies whether VLM agents can turn social reasoning into useful behavior during an interaction. MOSAIC places two agents in a Unity environment where an informed agent must help or mislead a partner searching for a hidden reward. The agents communicate through speech, movement, gaze, and facial expression. The experiment crosses cooperation/competition with prompted ToM order and evaluates 16 base systems over 200 trials each. The paper contributes a controlled testbed for active social interaction and a useful set of diagnostics for checking whether apparent task success reflects meaningful communication. The analysis of positional bias is particularly helpful, as are the cases where an agent produces clear directional cues but its partner's choices show little correspondence with them. The image ablations and additional spatial layouts give the study more depth than a single benchmark comparison. The outcome tests in Table 4 do not establish VLM/LLM performance above the neutral-adjusted chance level after Holm correction, although Table 6 does detect condition-dependent changes in several VLM signal metrics. PCM-LLM has the strongest outcome results in the canonical layout, but its deceptive behavior deteriorates in the other layouts.

Critical strengths
  1. I like the focus on what agents actually do during an interaction. The combination of cooperative and competitive conditions with several communication channels makes MOSAIC a useful setting for studying the connection between social reasoning and action. Reporting positional bias and neutral outcomes alongside TOCS helps avoid rewarding agents that simply keep choosing the same box.
  2. The paper gives concrete examples of behavior that an aggregate score would miss. InternVL-14B's cooperative signals are fairly well directed toward the reward, yet the participant's choices correspond poorly with those signals (Figure 3). The additional layouts expose failures in PCM-LLM as well (Appendix F). I appreciate that the authors examine the limitations of their strongest reference system and acknowledge that the image ablation retains structured spatial information.
Critical weaknesses
  1. (Major) The receiver-side failure analysis needs a more direct control. Appendix E already shows cases where an agent names the intended box but moves in the wrong direction. The paper identifies this problem qualitatively, but it remains unclear how much of the aggregate receiver failure it explains. SSS also measures correspondence between signals and choices, which the authors correctly acknowledge in Section 5. Averaging gaze and trajectory responses can obscure which signal the receiver used. A control that keeps the model's box decision but executes the movement correctly, together with a scripted sender, would make the proposed failure decomposition much more convincing.
  2. (Minor) The fine-tuning discussion is harder to assess than the main evaluation. Appendix H does not give the dataset size, data split, or optimization settings needed to interpret the negative result. It also describes the InternVL-8B Comp-ToM1 improvement as roughly 0.4 to 0.7, while Table 4 gives 0.30 to 0.52. I would correct this discrepancy and keep the conclusion about action-level imitation specific to the tested setup until the training details are clearer.
Questions for authors
  1. How much of the receiver's failure remains if the model selects a box and an oracle controller handles movement toward it? This would help separate difficulty using social information from the coordinate-conversion errors illustrated in Appendix E.
  2. Could you clarify the interpretation of negative SSS in Comp-ToM1? Under Eq. (12), following a misleading cue to the empty box gives positive correspondence for that channel. Reporting gaze and trajectory correspondence separately, with a scripted signal follower as a check, would help explain what the negative score captures in the PCM-LLM trials.
  3. Would speech-only and nonverbal-only controls change the main findings? The current image ablation retains structured spatial information, as the paper notes. These additional controls would help establish which communication channels are needed to solve the task.
  4. Could you provide the fine-tuning dataset size, split, and training settings, and reconcile the Comp-ToM1 improvement in Appendix H with Table 4? These details would help judge whether the result points to a limitation of action-level imitation or of this particular training setup.
4 comments
AuthorsOpenReview ↗

Response to W1 and W2

Response to W1:

We thank the reviewer for the careful review and the concrete controls proposed. We ran both: an oracle controller that keeps the model's box decision and executes the movement correctly, and PCM-LLM as a fixed sender. We also split SSS by channel and counted execution errors. The receiver-side failure falls into two kinds. Internvl-4B, -8B, and -14B fail at execution: once execution errors are removed, their cooperative TOCS is above chance. Minicpm-8B and Qwen3.5-9B fail at reading the signal: with execution errors removed, their TOCS is still not detectably above chance.

1. Frequency of execution errors. Across all reasoning logs, the share of moves away from the box named in the reasoning is at most 0.28 for subjects in 8 of 11 models, but at least 0.50 for participants in 6 models whichever box is named, up to 0.86 (per-model table in Reviewer 3, Q8). The cause is the reference frame. The agents face each other, and 67% of the participants' first-person box locations are wrong (197/292), versus 15% for subjects (19/128).

2. SSS by channel. We compute conditional SSS separately for gaze and trajectory, on trials where the subject's signal in that channel is clear and the participant makes a choice, and compare it with a permutation baseline produced only by fixed preferences (method in Reviewer 3, Q9). In self-play, only the PCM-LLM participant is above the baseline on both channels, and no VLM cell is.

3. Fixed sender. We used PCM-LLM as the fixed subject (Reviewer 3, W1.2). It plays the role of a scripted sender: its signals are clear and honest (TAS 0.72–1.00, cooperative GAS 0.76–1.00), and its own participant reads them. Unlike a rule-based script, it also speaks and shows facial expressions, so the VLM participant faces the same channels as in self-play. Facing it, no VLM participant is above chance, and only 1 of 40 per-channel follow scores is above the baseline. The participant's final belief, its preferred box at the last step, points significantly to the reward box for Internvl-4B, -14B, and -8B in four, three, and three conditions, but stays at chance for Minicpm-8B and Qwen3.5-9B in every condition.

4. Oracle controller. With the controller, the Internvl models' choices follow their beliefs and cooperative TOCS rises from chance to significantly above chance (0.64–0.80). Minicpm-8B and Qwen3.5-9B keep chance-level beliefs, and their TOCS is still not detectably above chance, so we cannot yet confirm whether the oracle changed it. No model recovers under competition (details in Q1).

5. How much execution errors explain. It depends on the model. For the three Internvl models, execution errors caused by the reference frame decide the cooperative outcome, although their repaired scores stay below PCM-LLM's (0.84–0.90). For Minicpm-8B and Qwen3.5-9B, execution errors do not explain the failure, because their final explicit preferences show no reliable reward-location information.

In summary, the Internvl models form the correct belief but break between belief and action, at execution, while Minicpm-8B and Qwen3.5-9B break earlier, between signal and belief.

Response to W2:

"0.4 to 0.7" in Appendix H is a typo, and Table 4 is correct: Internvl-trained-8B rises from 0.30 to 0.52 under Comp-ToM1, and the 14B variant from 0.44 to 0.46. The full training details are below.

ItemSetting
Demonstrations400 extra PCM-LLM trials in the canonical layout (100 per condition), disjoint from the evaluated trials. The 323 trials whose outcome matches the condition's prediction are kept.
Samples (train / val)7,106 (6,395 / 711)
RolesSubject and participant, equal sample counts
Input and targetAction-prediction prompt plus belief and observation state as text, no image. Target: PCM-LLM's action JSON without reasoning.
ModuleAction prediction only. At inference the adapter is active only for action prediction.
LoRAr=16r = 16, α=32\alpha = 32. Vision encoder and projector frozen.
OptimizationAdamW, lr 2×10−42\times10^{-4}, cosine, 5% warmup, weight decay 0.01, effective batch 16, bf16, max length 2,048, 3 epochs, 1,200 steps

Data are split 90/10 with seed 42, and the validation set is used only to monitor the loss. Results come from fresh rollouts with resampled reward locations. In the revision and appendix, we tighten the conclusion to: timestep-level action imitation on these two InternVL variants did not break through either bottleneck.

AuthorsOpenReview ↗

Response to Q1

We ran this supplementary simulation with an oracle controller on five models, chosen to match those used in cross-play. For InternVL-4B, -8B, and -14B, the controller removes the reference-frame conversion gap, and cooperative TOCS rises from chance to significantly above chance (0.64–0.80). For MiniCPM-8B and Qwen3.5-9B, beliefs stay at chance and TOCS is still not detectably above chance.

Setup. The 8 egocentric directions are replaced by object-targeted actions: walk to the dark or light box, look at a box or the partner, or stay. When the model walks to a box, the controller reads the agent's position and orientation and executes the correct step, which removes coordinate-conversion errors entirely. The controller acts on both agents. Each model ran self-play with 50 trials per condition, otherwise as in the main experiment.

ModelCoop-ToM0Coop-ToM1Comp-ToM0Comp-ToM1
Internvl-4B0.26 →\rightarrow 0.800.36 →\rightarrow 0.680.30 →\rightarrow 0.620.40 →\rightarrow 0.24$\downarrow$
Internvl-8B0.40 →\rightarrow 0.660.46 →\rightarrow 0.740.34 →\rightarrow 0.440.30 →\rightarrow 0.36
Internvl-14B0.44 →\rightarrow 0.680.42 →\rightarrow 0.640.40 →\rightarrow 0.580.44 →\rightarrow 0.48
Minicpm-8B0.44 →\rightarrow 0.460.36 →\rightarrow 0.560.36 →\rightarrow 0.440.38 →\rightarrow 0.38
Qwen3.5-9B0.28 →\rightarrow 0.460.48 →\rightarrow 0.420.56 →\rightarrow 0.440.52 →\rightarrow 0.52

TOCS, original →\rightarrow oracle. Bold: above chance. ↓\downarrow: below chance (binomial test). No original cell is significant.

ModelFinal belief on the reward box (oracle)Choice ≠\neq belief (oracle) [baseline]
Internvl-4BSignificant in all four conditions (0.78–0.88)0.17–0.23 [0.49–0.50], below baseline in all four
Internvl-8BSignificant in both cooperative conditions (0.80, 0.90)0.17–0.33 [0.32–0.42], below baseline in three
Internvl-14BSignificant in all four conditions (0.66–0.84)0.17–0.33 [0.45–0.52], below baseline in all four
Minicpm-8BAt chance (0.42–0.65)0.15–0.27 [0.15–0.31], same as baseline
Qwen3.5-9BAt chance (0.43–0.63)0.15–0.27 [0.37–0.47], below baseline in all four

Final belief: the participant's preferred box at the last step. Baseline: mean disagreement after shuffling choices within the cell, reflecting fixed preferences only.

  • Internvl models: cooperation recovers. Their choices now follow their beliefs, whereas in self-play none was below the baseline and Internvl-4B was even above it in Comp-ToM1 (0.74 vs. 0.51). Their participants also follow the subject's gaze above the baseline (Internvl-14B in all four conditions, Internvl-4B in both cooperative ones, Internvl-8B in Coop-ToM1), and cooperative TOCS becomes significantly above chance. Internvl-4B changes most. Its participant turned away from PCM-LLM's signals in cross-play (Coop-ToM0 TOCS 0.14, below chance) and reaches 0.80 with the controller.
  • Minicpm-8B and Qwen3.5-9B: no change. Their participants show no above-baseline following in any condition or channel, and TOCS is not detectably above chance, so we cannot yet confirm whether the oracle changed their performance. The cause is upstream, as their beliefs stay at chance. They also make wrong-way errors, but with a wrong belief, correct execution still does not bring TOCS detectably above chance. Qwen3.5-9B's choice now follows its belief, but the belief carries no information about the reward.
  • Competition does not recover. No model is above chance in Comp-ToM1. Internvl-4B's subject still reveals the reward box honestly, which gives above-chance TOCS in Comp-ToM0 (0.62) and below-chance TOCS in Comp-ToM1 (0.24), as in cross-play.

What remains. Removing coordinate conversion leaves the other break points. The final explicit preferences of Minicpm-8B and Qwen3.5-9B show no reliable reward-location information, and no VLM shows reliable Comp-ToM1 outcome conformance. The new Appendix E.3 reports the setup, implementation check, and full results.

AuthorsOpenReview ↗

Response to Q2-Q4

The reviewer's reading is correct: according to our definition of TAS and GAS, choosing the box a channel indicates scores positively for that channel. PCM-LLM's negative SSS comes from how the metrics reduce a trial to one box. TAS, GAS, and SSS first find the box the signal points to at each timestep and then take a majority vote over the trial. The table splits the two competitive conditions by channel and adds the suggested scripted follower, a mechanical participant that picks the majority box of one channel and so reads signals exactly as SSS does.

ConditionChannelSignal toward reward (TAS / GAS)Timesteps toward empty boxScripted follower picks empty boxPCM-LLM participant: conditional SSSPCM-LLM participant picks empty box
Comp-ToM0Trajectory1.000%0/500.961/50
Comp-ToM0Gaze1.0010%0/500.961/50
Comp-ToM1Trajectory1.000%0/50−0.46-0.4635/50
Comp-ToM1Gaze0.7424%6/49−0.19-0.1935/50

Conditional SSS counts only trials where the subject's signal on that channel is clear and the participant makes a choice.

The trajectory never points to the empty box. The few timesteps that do are all in gaze, and their share rises from 10% to 24% in Comp-ToM1. They are outvoted, so the scripted follower almost never picks the empty box. PCM-LLM's participant, by contrast, picks the empty box in 35 of 50 Comp-ToM1 trials and turns significantly away from the trajectory.

The participant reads the negative expression as avoidance. Every Comp-ToM1 trial contains at least one step in which the subject gazes at the reward box with a negative expression (1.78 on average), and no Comp-ToM0 trial does. The participant's estimate of the subject's preference for the reward box falls to −0.49-0.49, versus −0.09-0.09 under Comp-ToM0 (Mann-Whitney p<10−13p < 10^{-13}). The more such steps a trial contains, the more often the participant picks the empty box (10 of 18 trials with one step, 25 of 30 with two or more; Fisher p=0.049p = 0.049).

Negative SSS under Comp-ToM1 therefore means that the participant responded to a few steps of negative expression and turned away from a trajectory that always pointed to the reward box. It does not mean that the participant followed a signal pointing to the empty box.

Response to Q3:

The reviewer is right that the visual ablation removes only the rendered image, so it shows only that the image is unnecessary, not which channel the task requires. Given the rebuttal time limit, we did not run speech-only or nonverbal-only controls, but existing data give two indirect answers.

Effect of speech on behavior. The action-prediction module receives only the image and the belief state, not the dialogue. Speech can therefore change an agent's movement only through the preferences that the preference-updating module writes after each of the few verbal exchanges, whereas both agents re-output their preferences from the nonverbal interaction at each of the 10 timesteps. Across all 18 systems, we counted how often per trial these post-verbal updates request a sign reversal, either of the preference toward the other agent (interaction mode) or of the preferred box (reward belief). The subject reverses its preference toward the participant 0.01–0.61 times per trial (highest: Minicpm-8B) and its reward belief 0.01–0.62 times (highest: Internvl-14B). The participant reverses its preference toward the subject 0.00–0.24 times (highest: Qwen3.5-2B) and its reward belief 0.01–0.42 times (highest: Internvl-14B).

In every system, speech reverses an agent's mode or reward belief less than once per trial on average. Removing speech may therefore change behavior little, and the main findings may hold. This count does not capture updates that strengthen or weaken a preference without reversing it, so it remains an inference, and speech-only results still require controlled experiments.

Which channel carries the information. In PCM-LLM, the only system that solves the task, the Comp-ToM1 results are consistent with facial expression contributing to the misdirection, but the independent contribution of speech is not yet established. Without a verbal pointer, its participant still picks the empty box in 18 of 23 trials, with no detectable difference from trials with one (13 of 17; Fisher p=1p = 1). Under Comp-ToM0, with verbal pointers to the empty box but no negative expression, the participant picks it in only 1 of 9 trials (vs. 13 of 17 under Comp-ToM1, p=0.003p = 0.003). The full decomposition is in Appendix E.4.3.

Response to Q4:

Please see our response to W2.

Thanks for the replies and additional experiments. The authors have clarified some issues and some points are incisive. However, it does not fully resolve the major control and channel control issues. I would like to keep my original score.

Reviewer_6SxNOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This article discusses the ability of multimodal models to infer what others are thinking; the question then arises: can these models translate such inferences into actions that influence others? While this overlaps with existing research—such as studies on the persuasive capabilities of large language models (LLMs)—I find it particularly interesting to examine this through the lens of Theory of Mind (ToM).

Critical strengths

This paper approaches the topic through the lens of MLLMs—or, more broadly, multimodal embodied agents. This perspective closely mirrors that of a human, making it both highly challenging and deeply significant. While I personally find that approaching this via "coding agents" feels more "LLM-native," that does not diminish the fact that the perspective taken in this paper is a highly challenging one.

Critical weaknesses
  1. The choice of models limits the generalizability of the conclusions. At its core, "Theory of Mind" (ToM) in this benchmark pertains to an agent's interactive capabilities. Recent generations of models have shown significant improvements in interactive and multi-turn action-taking abilities—far surpassing the LLMs of the earlier "chatbot" era. However, most of the models evaluated in this paper are not "agentic models." For the Qwen 3.5 series, only the 2B, 4B, and 9B versions were assessed, and none of the Vision-Language Models (VLMs) evaluated exceed 14B parameters. Therefore, the paper should examine the performance of agentic models, rather than focusing solely on chatbot-level LLMs.

  2. Poor performance may stem from unfamiliarity with the task format rather than a genuine lack of "Theory of Mind" (ToM) capabilities. Furthermore, the Unity 3D environment may not be an appropriate proxy for evaluating contemporary LLM-based agents. Current development in LLM agents is primarily focused on areas such as coding and tool use. I suspect that in these types of scenarios, models may already demonstrate the "belief-to-action" link that the paper seeks to investigate—for instance, when a model infers the intentions of a collaborator or opponent through code, commits, or tool calls, and subsequently takes action to cooperate with them.

I suggest that the authors consider the appropriateness of using coding tasks to evaluate ToM in this context.

Questions for authors

Please refer to weakness section

4 comments
AuthorsOpenReview ↗

Response to W1

We thank the reviewer for the careful reading and constructive feedback. Given the time constraints, we do not add simulations with larger models. We follow the reviewer's second suggestion: every claim is now stated for the evaluated open-source VLMs, up to 15B parameters, acting through MOSAIC's embodied action interface, and none is extended to larger or frontier API models. We would like to clarify, however, that on this task and within the evaluated range, performance is not fully determined by model size or release date.

Within 1B–15B, neither performance nor the break point follows size or release date. The main results, cross-play, and the oracle controller give the clearest contrast (Please refer to Reviewer 3, W1.2; Reviewer 2, W1 and Q1).

  • Only the 1B–2B models fail systematically. The participants of Internvl-1B, Internvl-2B, and Qwen3.5-2B almost always choose the same box, and Qwenvl-2B rarely produces effective movement (Appendix F, Section 4.3). Above 4B, the differences between models are small, and within a family the 4B model can outperform the 8B one. Internvl-4B is the strongest sender in cross-play, and its participant forms a correct belief in all four conditions.
  • The newest family is no better. Apart from the older Llava models, the newest Qwen3.5 (2026) performs no better than Qwenvl (2025) or Internvl (2025). Internvl-14B and Qwenvl-4B at least produce clear trajectory signals, while Qwen3.5-9B's belief stays at chance in cross-play and under the oracle, so it breaks at the first receiver stage.

Revisions. For this comment, we made only the minimal change of narrowing the claims:

  • The Abstract now reads: "Evaluating 16 models, including 14 VLMs (up to 15B parameters), across 200 trials per model, we find that the evaluated open-source VLMs, acting through MOSAIC's embodied action interface, fail to produce behaviors consistent with the expected outcomes".
  • In the Conclusion, "Off-the-shelf VLMs fail at different transitions" now reads "The evaluated open-source VLMs fail at different transitions".
  • The sentence "indicating these failures reflect architectural constraints specific to the evaluated VLMs rather than the task itself" is deleted from the contributions.
AuthorsOpenReview ↗

Response to W2

We thank the reviewer for the constructive feedback. We agree that competence and performance must be distinguished and have added this to the Discussion. To test whether the failures come from interface unfamiliarity, we checked the diagnostic chain stage by stage with two new interventions: cross-play with PCM-LLM as a fixed partner, and an oracle controller. MOSAIC locates where each model is most likely limited, which helps separate interface failures from the others.

1. Do the failures come from the interface? Cross-play first shows which role fails (details in our response to Reviewer 3, W1.2).

  • VLM as subject. TOCS is significantly above chance for the three Internvl models in both cooperative conditions and for Minicpm-8B in Coop-ToM1. Except for Internvl-14B, their trajectories are weak (cooperative TAS 0.02–0.36), so PCM-LLM read the reward location from other channels such as gaze.
  • VLM as participant. PCM-LLM's trajectory honestly points to the reward box (TAS 0.72–1.00), yet no VLM participant is above chance, and Internvl-4B is significantly below chance in two conditions.

The cooperative failures thus lie mainly on the receiver side, while Qwen3.5-9B is at chance in both directions. Taking the participant's preferred box at the last step as its final belief, Minicpm-8B and Qwen3.5-9B stay at chance (0.44–0.67, 0.45–0.60) and break at reading the signal. The three Internvl models form correct beliefs in three or four conditions (0.72–0.90), yet their TOCS stays at chance, so they break after the belief.

A likely cause of the latter is a reference-frame error. The agents face each other, so left and right are mirrored, and 67% of the participants' first-person box locations are wrong (197/292, all judged in world coordinates), versus 15% for subjects (19/128). If so, executing the movement for them should help the Internvl models but not the two without a correct belief. The oracle controller tests this by replacing the 8 egocentric directions with object-targeted actions: the model picks a box and the controller executes the step, like a call to walk_to(dark_box). As predicted, the Internvl models' choices start to follow their beliefs and cooperative TOCS rises significantly above chance, while Minicpm-8B and Qwen3.5-9B stay at chance (Reviewer 2, Q1).

2. Tool calls and the modality ablation. The oracle is the tool-call format the reviewer has in mind, yet it only repairs cooperative execution for models with correct beliefs. Not switching strategy under competition and chance-level beliefs show no detectable recovery. The modality ablation (Section 4.4) agrees. Positions, orientations, preferences, and expressions are always given as text, and removing the image leaves Minicpm-8B unchanged, so its chance-level belief is not a failure to parse the 3D scene. The reference-frame error also arises in text, in converting world-coordinate positions into egocentric actions, which is exactly what the oracle removes.

AuthorsOpenReview ↗

Response to W2 (continued)

3. Where the failures occur.

Break pointEvidenceRelated to execution?
Sender, cooperation: weak trajectoryMinicpm-8B, Qwen3.5-9B: cooperative TAS 0.02–0.10 in cross-play. Only 13 and 23 calls target a box (Internvl-14B: 215), while subjects of 8/11 models move toward the box they name. They rarely decide to walk to a box.No, decision level
Sender, competition: no strategy switchNo VLM subject deceives, even a ToM-0 PCM-LLM. Internvl-4B stays honest in Comp-ToM1 (TOCS 0.14, below chance). Under the oracle, no model is above chance in Comp-ToM1.No, strategy level
Receiver: no beliefMinicpm-8B, Qwen3.5-9B: belief at chance in cross-play and under the oracle. The belief comes from the preference module, not the motor interface.No, signal reading
Receiver: belief not acted onThree Internvl models: under the oracle, choices follow beliefs and cooperative TOCS is above chance.Yes, reference frame

The results suggest that different models may be limited at different stages, execution being only one of them. Because the oracle changes both agents and the client still has its own execution noise, these factors cannot yet be fully separated.

4. The two suggestions.

(i) Competence versus performance. The new "Competence versus performance" paragraph in the Discussion states that MOSAIC measures acting on social inferences through the embodied interface, not competence in other formats, and shows where the belief–action gap opens, as in the table. The abstract now reads "the evaluated open-source VLMs, acting through MOSAIC's embodied action interface, fail to produce behaviors consistent with the expected outcomes". The contribution list is qualified the same way, and the sentence "indicating these failures reflect architectural constraints specific to the evaluated VLMs rather than the task itself" is deleted.

(ii) Why a 3D embodied setting. Intentions are also conveyed by movement, gaze, and expression. QA-style ToM benchmarks, multi-agent frameworks that compress signals into language or abstract actions, and text- or code-based settings all drop these channels, which are what MOSAIC tests. Not every channel must be perfect. The outcome depends only on the box the participant picks, so one or two informative channels suffice, and the participant only needs to walk to the box it believes in. Points 1–3 provide the basis for separating ToM failures from interface unfamiliarity.

AuthorsOpenReview ↗

Response to W1 (continued)

As proposed by the reviewer, we additionally ran Qwen3.5-27B in the self-play setting to test whether our findings hold at a larger scale. The protocol was identical to that of the main study, with 50 trials per condition. All metrics were computed with the same pipeline as in the paper.

Table Qwen3.5-27B self-play results. Mean with 95% CI (TOCS: Clopper–Pearson).

ConditionnnTOCSTASGASFESSSS
Coop-ToM0430.37 [0.23, 0.53]0.26 [0.14, 0.40]0.86 [0.70, 0.98]0.85 [0.82, 0.88]0.05 [−0.13-0.13, 0.22]
Coop-ToM1420.43 [0.28, 0.59]0.17 [0.05, 0.31]0.86 [0.71, 0.98]0.86 [0.84, 0.88]−0.08-0.08 [−0.26-0.26, 0.10]
Comp-ToM0490.49 [0.34, 0.64]0.04 [−0.06-0.06, 0.14]0.00 [−0.24-0.24, 0.24]0.68 [0.61, 0.75]0.00 [−0.11-0.11, 0.12]
Comp-ToM1450.40 [0.26, 0.56]0.00 [−0.09-0.09, 0.09]0.20 [−0.07-0.07, 0.47]0.69 [0.62, 0.76]0.01 [−0.12-0.12, 0.16]

TOCS (0.37–0.49) is unchanged at 27B and does not differ from the chance level in any condition (binomial test, Holm-corrected, all n.s.).

What changes with scale is signal production. In cooperation, the 27B sender's gaze points to the reward box far more consistently (GAS 0.86, vs 0.52–0.58 for 9B). In competition this cue falls to 0.00–0.20 and never turns negative: the model keeps a poker face rather than emitting misleading signals. The Mode effect is significant for GAS, FES and TAS (Scheirer–Ray–Hare, Holm-corrected: p<0.001p < 0.001, p<0.001p < 0.001 and p=0.024p = 0.024). No metric shows a ToM effect or a Mode ×\times ToM interaction. Thus, larger scale strengthens the production of non-verbal signals and their modulation by social context. The sender–receiver gap reported in the paper persists at 27B.

Due to time constraints, we could not extend the crossplay and oracle control simulations to this model. Since the results and the conclusion do not change the overall picture, we prefer not to add Qwen3.5-27B to the main text.

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

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