acceptodds
Under review as a conference paper at ICLR 2027

Who Gets Blamed? Attribution Under Interference in Multi-Agent LLM Markets

Abstract

An audit of interacting LLM agents needs to distinguish the effect of changing an agent's own deployment from the effects of changing its peers. Market-level comparisons can combine these effects and give a different answer from an agent-level evaluation. We study this problem across eight open-weight models in a repeated Bertrand pricing market, using a profit-based collusion index as the outcome. A two-stage design varies the treated share and randomly selects recipients, separating own effects from spillovers. Estimated own effects have significantly different values between no-peer-exposure and all-peer-exposure settings. High self-play collusion scores also coexist with low win rates against other models. To assess a query-based audit, we obtain agents' reaction functions at fixed market states and compose the maps. The stochastic composition recovers the spillover direction in seven of eight tested model-identity cells, but performs poorly for prompt-level spillovers and own effects. These findings motivate deployment-specific safety evaluation: specify whose outcome is measured, report peer exposure, and check which effects a query-based audit can recover before relying on it.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI safety, AI governance, accountability, trustworthy AI, evaluation validity, multi-agent system

Reviews

Among:
Shape:
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.
Reviewer_8nhFOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
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2
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Paper summary

This paper studies attribution under interference in multi-agent LLM markets, distinguishing the effect of changing an agent’s own deployment from spillovers caused by changes to its peers. Using eight open-weight models in repeated Bertrand pricing markets, the authors apply a two-stage design to estimate direct, indirect, and overall effects on a profit-based collusion index. They report that estimated own effects vary with peer exposure and that self-play collusion rankings do not necessarily predict mixed-market performance. The paper also evaluates a query-based composition surrogate built from elicited reaction functions, finding better agreement with model-identity spillover directions than with prompt-level spillovers or own effects.

Critical strengths
  1. Interference-aware causal evaluation. The paper provides a well-motivated application of causal inference under interference to multi-agent LLM evaluation. More importantly, its experiments demonstrate that aggregate deployment comparisons can yield conclusions that differ substantially, sometimes even in sign, from the agent-level effects of interest. This raises a meaningful concern about the interpretation of existing multi-agent evaluation results.

  2. Informative validation of query-based auditing. The paper evaluates reaction-function composition against randomized experimental estimates rather than relying solely on theoretical motivation or qualitative examples. The contrasting results for model-identity spillovers, prompt-level spillovers, and own effects provide useful evidence about both the potential and the limitations of this lower-cost auditing approach.

Critical weaknesses
  1. Missing direct inference for effect heterogeneity: The abstract claims significantly different own effects across peer-exposure settings, but Table 5 reports tests of individual effects rather than the contrast DE(1) − DE(0). Separate significance tests and sign differences between point estimates do not establish the significance of this contrast, leaving the stronger claim insufficiently supported.

  2. Limited predictive reliability of the composition surrogate. The surrogate substantially underestimates own effects and correctly predicts prompt-level spillover directions in only 6 of 11 cases. Although the authors acknowledge these limitations, they do not systematically investigate the sources of these errors or clarify under what conditions the surrogate can reliably support causal attribution. This weakens the practical value of the proposed query-based auditing approach.

Questions for authors
  1. Can the authors directly estimate DE(1) − DE(0) and report confidence intervals and tests that account for dependence between the estimates? Beyond the existing correction for the 66 main-effect tests, please clarify how multiplicity would be handled for these interaction contrasts.

  2. Understanding the surrogate's prediction failures. Could the authors investigate why the surrogate substantially underestimates own effects and performs poorly on prompt-level spillovers? In particular, an ablation examining history dependence, stochastic approximation, and mean-price scoring would help clarify the sources of these errors and the surrogate's reliability.

4 comments

Thank you sincerely for the constructive questions about inference and the surrogate. They motivated direct interaction tests and matched-history ablations. In the revised PDF, purple marks changes addressing your review and red marks shared changes. Footnotes identify the relevant reviewer IDs.

1. Directly testing DE(1) - DE(0).

Your point about the missing comparison is well noted and taken. We now compute H = DE(1) - DE(0) within each seed block before estimating its mean and uncertainty. This retains dependence between the effects and their shared mixed-market outcomes.

With 32 new seed blocks per condition, mean H is -0.345 (95% CI [-0.531, -0.159]) for Qwen3-8B reasoning and -1.265 [-1.571, -0.960] for replacement by Mistral-24B. Holm-adjusted p-values are 0.000675 and 3.12e-9. Student-ized bootstrap and leave-one-seed-out checks support both contrasts (Appendix L, Tables 13 and 14). The claim rests on these direct differences, rather than separate main-effect significance or point-estimate sign changes.

2. Accounting for multiplicity.

The original 22 interaction contrasts receive Holm correction separately from the original 66 main-effect tests. Independent replication has a two-contrast Holm family; Cournot and five-agent H tests form another two-test family; four paired history contrasts receive Holm-4 correction. Table 11 lists these families. This provides error control within each family, not jointly across all analyses. Please note that surrogate-error comparisons below (point 3) are exploratory.

3. What explains the surrogate error?

We ran matched Qwen3-8B markets for reasoning and ICL with visible histories of 1, 5, and 10 rounds, using 16 fresh seed blocks. Maps cross transient/persistent elicitation, residual noise OFF/ON, and profit at mean prices versus mean per-round profit. Each prediction is compared with its matched-history market target.

For reasoning, switching to mean per-round profit changes average own-effect MAE by -0.0054 (exploratory 95% CI [-0.0109, -0.0014]). Adding noise changes it by +0.0029 [-0.0146, 0.0245]; persistent versus transient elicitation changes it by -0.0258 [-0.0458, 0.0051]. Scoring explains a modest part of the error. Noise and persistent elicitation, however, do not establish a general remedy.

Shortening history from 10 previous rounds to 1 reduces reasoning own-effect MAE by 0.2969 [0.1561, 0.3546]. The ICL reduction is 0.0142 [-0.1576, 0.1597]. There is a catch: history also changes the target. For ICL, H at one round minus H at ten rounds is -0.505 [-0.752, -0.259], with Holm-adjusted p = 0.0022. Cumulative profit remains visible, so one-round history does not remove all memory.

Appendix N, Tables 18 through 22, reports the market effects, map configurations, and average error changes. Error intervals jointly resample 20 snapshot clusters and 16 seed blocks while preserving shared controls.

These checks identify conditions where the approximation improves without isolating a single failure mechanism. A cheaper audit still needs validation for the intervention and history regime being assessed. Your suggestions helped us turn that very crucial caution into a concrete observation of (i) when the surrogate succeeds and (ii) where it falls short if it does.

Thank you again for your suggestions. We added direct interaction tests with dependence-aware inference and multiplicity correction, supported by 32 fresh seeds per condition, alongside matched-history ablations examining history, noise, and scoring.

With the November 18 (AoE) discussion deadline approaching, we would very much appreciate your thoughts on these results. If they address your concerns, we would be grateful if you could reconsider your assessment.

Thank you for the detailed response and additional experiments. The paired interaction tests and multiplicity corrections adequately address my main statistical concern, so I maintain my positive assessment of the paper.

Thank you for your engagement and positive assessment of our paper.

Reviewer_Xt3AOpenReview ↗
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3
Informativeness
1
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2
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Paper summary

The authors propose the use of randomized ‘treatments’, per-agent changes in a multi-agent experiment or deployment setting, during evaluation to use the contrast across markets (with different percentage of treatments applied to participating agents) to separate the effect on (i) treated agents and (ii) spillover on untreated agents. They show this using pricing market simulations with LLM agents running separate firms. The treatment dimensions are: reasoning, model identity, and prompts (in-context and via commentary). The main novel contribution of the study appears to be the treatment study of the effect across each of the above dimensions.

Critical strengths

None

Critical weaknesses
  • W1. The paper seems to add little to the body of work in this area. The treatments are an additional interesting way to formalize experimentation in multi-agent auction/pricing market experiments. Other works already apply and measure per-agent differences during experimentation, for instance Keppo et al 2026 that you already cite, or others like Agrawal et al 2025 https://arxiv.org/abs/2507.01413
  • W2. The abstract is very hard to read with many terms that require context from the main body to understand it. In the abstract the reader is expected to understand the following terms with little to no context: agent-level evaluation, treated share, no-peer-exposure, all-peer-exposure, stochastic composition, spillover (direction), model-identity cells, prompt-level spillovers, query-based audit. Most of the paper reads the same way, sentences are packed with terms and are difficult to understand.
  • W3. The p values for most of the cells in fig 1 are not significant (as per table 5).
Questions for authors
  • Q1. Is your main (novel) contribution the randomization of the per-agent applied changes (treatments) and the application itself of the interference/treatment framework?
  • Q2. How is your proposition in 3.2 about the homogeneity of multi-agent market systems different from previous literature? e.g. Keppo et al 2026 or Lee and Park 2026.
  • Q3. Can you comment on why you call it ‘deployment’ as opposed to ‘set up’ or ‘configuration’ throughout the paper? When talking about LLMs, ‘deployment’ carries a lot of meaning and considerations, that I do not think apply anywhere in this paper (being serviced as a product, and/or geared towards real users, etc)
4 comments

Thank you for asking us to sharpen the contribution and strengthen its statistical support. In the revised PDF, dark green marks changes addressing your review and red marks shared changes. Footnotes identify the relevant reviewer IDs.

1. What does the paper add to prior market experiments? (W1/Q1)

Individual-agent interventions and heterogeneous markets have been studied before. Keppo et al. (2026) examine heterogeneity and collusion, while Agrawal et al. (2025) study communication, model choice, and environmental pressures in double auctions.

Our question targets (i) who experiences the effect of a configuration change, and (ii) how that effect changes when peers receive it too. We use established interference methods to separate the changed agent's own effect, the spillover onto an unchanged peer, and the difference in own effects across peer configurations. We test these quantities and compare a cheaper query-based audit with randomized market outcomes.

The contribution lies in this empirical attribution audit. It reveals discrepancies between evaluation targets and shows where exactly the surrogate compresses own effects. We do not claim a new randomization method. The Introduction and Section 2 clarify this distinction.

2. What work does Proposition 1 do? (Q2)

Observing all-control and all-treated markets identifies OE(1) = DE(1) + IE(1), but leaves the mixed-assignment means unobserved. Those means are needed to separate the components. Put simply, knowing that heterogeneous agents behave differently does NOT tell us who bears the effect of a particular change.

Lee and Park (2026) show that information manipulation can propagate through competitors. Proposition 1 explains which additional assignments are needed to distinguish our attribution quantities from theirs. Section 3.2 presents it as a standard ID implication motivating the decided experimental design.

3. Are the key differences statistically significant? (W3)

We now test H = DE(1) - DE(0) directly, preserving dependence across assignments. Appendix L reports the original interaction contrasts with Holm correction over 22 tests. Replication uses 32 new seed blocks per condition, not including the original eight.

Mean H is -0.345 (95% CI [-0.531, -0.159]) for Qwen3-8B reasoning and -1.265 [-1.571, -0.960] for model replacement by Mistral-24B. Both survive Holm correction over the two replication contrasts (p = 0.000675 and even closer to zero (3.12e-9); Table 13). The average own effect hence differs across peer configurations. This conclusion rests on a direct comparison, rather than separate main-effect significance tests or a requirement for sign reversal.

4. Terminology and "deployment." (W2/Q3)

The abstract now explains changing an agent versus changing its peers before abruptly introducing further terms. The Introduction defines "deployment" as the model, prompt, and generation configuration in our simulated markets, not a live service. We use "configuration" in the revised overview and clarify the estimands in Section 3.1.

As firms delegate more decisions to LLMs, who gains and who bears the cost cannot be read off an aggregate market outcome alone. And we strongly believe introduction of rigorous audits on agentic systems must follow the ever-so-fast-moving market conditions. Your detailed comments helped us clarify this question and strengthen its evidence.

Thank you again for your feedback. We clarified the contribution relative to prior work, simplified the presentation, and added direct interaction tests with 32 fresh seeds per condition; both replication contrasts remain significant after Holm correction.

As the discussion closes on November 18 (AoE), we would appreciate your feedback and (if these revisions address your concerns) reconsideration of your assessment.

Thank you for your rebuttal.

1. I understand that the main contribution is the empirical attribution audit, I still think this adds little to the body of work in the area. Fundamentally most LLM market experiments deal with (i) and (ii) (though not in as much as this paper, where it is the central question). There is also a question of applicability where in real markets the configuration change would not be known (and so consequent effect cannot be tracked).

2 and 4. Thank you for the explanations and updates to the manuscript. I do not find the definition of deployment the authors use to be standard, is this not just your experimental set up?

3. I would recommend updating Figure 1 accordingly (which displays a subset of table 5 values as far as I understand). I find it bizarre that instead of explaining the original p-value that was not significant you chose to run more seeds (I had no issue with the previous number of seeds n=8). I remain concerned about replication and generalization.

I think the idea behind the paper is interesting but I disagree with the novelty, presentation and validity of the results.

I will keep my score.

Thank you for the engagement--and for the follow-up! We would like to further clarify the statistical evidence and scope.

We have revised Figure 1’s caption and the Results text to explicitly identify the original 8 seed estimates and note that the positive DE(0) is not significant at p = 0.07. The original nonsignificant estimates remain nonsignificant; the new experiments are not meant to (and really shouldn't) change those. Table 5 tests individual effects, whereas our central claim concerns the contrast between effects across peer configurations, also presented as H = DE(1) − DE(0). We added direct tests of this contrast and independent replications using 32 fresh seed blocks per condition, excluding the original eight. Both replication contrasts survive Holm correction. This supports peer dependence for the tested interventions.

Regarding applicability, our setting is a controlled evaluation where configuration changes are known and assigned exogenously. We do not claim to identify unobserved changes in real markets; the term "configuration" describes this scope more precisely.

We partly do recognize the remaining concern about novelty. Our contribution is an empirical attribution audit that goes strictly beyond documenting heterogeneous agent behavior: we (i) causally separate effects on changed agents from spillovers onto unchanged rivals, (ii) directly establish peer-dependent own effects in independent replications, and (iii) empirically test which attribution quantities a cheaper surrogate can recover. The results show how the choice of evaluation target changes the conclusion an audit supports.

Reviewer_HM19OpenReview ↗
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2
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Paper summary

The authors pursue a key causal question about characterizing the influences of changing a single agent in a multi-agent environment: How does changing one agent’s behavior depend on the other agents that it interacts with and how does the complexity of dependencies on other agents’ behaviors make it difficult to characterize the influence of making a single change per the view of the change to the agent. When an agent's capabilities are changed (e.g., when reasoning is turned on or intensified), the changes seen in the agent and its behavior can be functions of ripples extending from the change and leading to behaviors on other agents, coming back around to the behavior of the agent. This is a challenge of understanding causal influences under the general condition of interference.

The authors argue that trying to understand the influence of changes in an agent's behavior in an ecosystem with multiple agents bundles together multiple changes: the agent changes, its competitors change in response, and their responses feed back into the first agent's behavior. The authors seek to bring in the broader considerations into evaluations of interacting LLM agents.

The authors deployed 8 open-weight models in a repeated pricing game. Each sets a price, sees recent history of the larger market, and tries to maximize cumulative profit. Markets are run for 100 rounds, with the final 30 used for the principal outcome. The authors vary four aspects in tests: model identity, reasoning enabled versus not, two examples in the prompt, and a sentence describing weakening market demand.

The authors assert that a randomized design separates an agent's own effects from spillovers, whose estimates can differ in both sign and magnitude. They conclude that in self-play and mixed markets scores an agent’s audit must account for the company that it keeps around it.

Critical strengths

The authors explore important ideas and results on attribution of changes in agent's behaviors in a larger ecosystem of agents that will only grow in importance with growing use and reliance on agent-centric systems.

Clear definitions and formalism. The causal question is well-specified.

Set of interesting experiments and results.

The scope of the studies and the implications of the results is stated carefully.

Critical weaknesses

Statistical support for the key reversals could be stronger. Eight markets per treatment share is a small experimental sample, Some five-agent conditions have only three.

Questions for authors

Can the authors demonstrate the same evaluation problem in a second interactive task? Cross-game one-step elicitation does not establish generalization?

2 comments

Thank you sincerely for the constructive questions and for recognizing the importance of attribution in interacting agent systems. Your comments prompted independent replication and a second repeated game. In the revised PDF, blue marks changes addressing your review and red marks shared changes. Footnotes identify the relevant reviewer IDs.

1. Do the key differences hold across independent seeds?

We went back to this question with 32 new seed blocks for each condition: Qwen3-8B reasoning and replacement by Mistral-24B. These exclude the original eight seeds, and each block covers every treatment share. We directly test H = DE(1) - DE(0), the change in an agent's own effect when its rival also receives the intervention.

Mean H is -0.345 (95% CI [-0.531, -0.159]) for reasoning and -1.265 [-1.571, -0.960] for replacement. Both survive Holm correction over the two contrasts (p = 0.000675 and 3.12e-9). Seeds are the independent units; inference retains dependence across assignments. Student-ized bootstrap and leave-one-seed-out checks support both findings (depicted in detail through Appendix L, Tables 13 and 14).

There is a distinction that worth noting here. Reasoning does not reproduce a positive unilateral own effect: DE(0) is -0.047 [-0.179, 0.085], versus DE(1) of -0.391 [-0.476, -0.307]. What persists is the discrepancy across peer configurations. An exploratory paired comparison also finds a larger loss for the unchanged rival than for the changed agent: IE(1) - DE(0) = -0.256 [-0.320, -0.192]. This recipient asymmetry is distinct from H.

2. What happens in a larger market?

We expanded the five-agent experiment to 16 fresh seed blocks at every treated share. Mean H is -0.059 [-0.253, 0.136], while the spillover onto an untreated firm with all four peers treated is -0.419 [-0.548, -0.289].

The negative spillover is strongly supported but the endpoint own-effect contrast remains less significant. Explanation being: competition among more (five) firms may leave less room for individual profit gains, though we do not isolate that mechanism to test. Table 17 reports the full own-effect curve, so the larger-market evidence can be assessed on its own terms.

3. Does the attribution problem extend to another repeated game?

We added differentiated Cournot competition with 100 rounds, 16 fresh seed blocks, and final-30-round scoring. In raw-profit units, DE(0) = +0.0457 [0.0030, 0.0884], DE(1) = +0.2883 [0.1759, 0.4008], and H = +0.2426 [0.0971, 0.3881]. H survives Holm correction with the five-agent contrast (p = 0.0058).

The direction differs from logit pricing, but peer-dependent attribution remains. These games differ in strategic responses, feedback, and payoff calibration. Appendix M, Tables 15 and 16, reports the settings and raw and normalized coefficients; normalized magnitudes should not be compared directly across games.

These additions strengthen the central finding: the effect attributed to an agent depends on how its peers are configured. As firms delegate more economic decisions to LLMs, separating an agent's gains from the costs born by others matters for accountability and fair market competition. Your questions helped us a lot into putting that finding on much firmer empirical ground.

Thank you again for your feedback. In response, we added independent replications with 32 fresh seeds per condition and a second repeated game, differentiated Cournot competition, both supporting peer-dependent effects.

With the November 18 (AoE) discussion deadline approaching, we would appreciate your thoughts on these additions. If they address your concerns, we would be grateful if you could reconsider your assessment and rating.

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

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