acceptodds
Under review as a conference paper at ICLR 2027

Epistemic Context Learning: Building Trust the Right Way in LLM Multi-Agent Systems

Abstract

Individual agents in multi-agent (MA) systems often lack robustness, tending to blindly conform to misleading peers. We show this weakness stems from both sycophancy and inadequate ability to evaluate peer reliability. To address this, we first formalize the learning problem of history-aware reference, introducing the historical interactions of peers as additional input, so that agents can estimate peer reliability and learn from trustworthy peers when uncertain. This shifts the task from evaluating peer reasoning quality to estimating peer reliability based on interaction history. We then develop Epistemic Context Learning (ECL): a reasoning framework that conditions predictions on explicitly-built peer profiles from history. We further optimize ECL by reinforcement learning using auxiliary rewards. Our experiments reveal that our ECL enables small models like Qwen 3-4B to outperform a history-agnostic baseline 8x its size (Qwen 3-30B) by accurately identifying reliable peers. ECL also boosts frontier models to near-perfect (100%) performance. We show that ECL generalizes well to various MA configurations and we find that trust is modeled well by LLMs, revealing a strong correlation in trust modeling accuracy and final answer quality.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Large Language Model, Multi-Agent System, Reinforcement Learning, Social Awareness

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_Jb5tOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper introduces Epistemic Context Learning (ECL), a two-stage framework that enables individual LLM agents to assess peer reliability from historical interactions and use this information in subsequent reasoning. The authors introduce a Peer Recognition Reward (PRR) to supervise trust estimation and present experimental results on MMLU-Pro and GPQA across eight models under natural and adversarial peer settings.

Overall, the paper addresses an important problem in LLM-based multi-agent reasoning. The motivation is clear, and the diagnostic experiments provide useful insights into how agents assess and use peer information.

However, the experimental evaluation is not sufficiently comprehensive, and several methodological details need further clarification.

Critical strengths
  1. Addresses an important and relatively underexplored problem: how an individual LLM agent should assess peer reliability and selectively incorporate peer information.

  2. The diagnostic experiments identify meaningful failure modes, including limited use of historical reliability signals and over-reliance on incorrect peer consensus.

  3. The evaluation covers multiple model families, natural and adversarial settings, and analyses of peer counts, history lengths, and inference overhead.

Critical weaknesses
  1. It is not explicitly clear whether the two stages use the same LLM with shared parameters or separate models. Although the appendix provides prompts, the main text gives limited explanation of how historical interactions are transformed into trust representations and how the resulting representation is used by Stage 2.

  2. The paper emphasizes the selective utilization of peer information. However, the training objective of Stage 1 only rewards identifying the single most reliable peer. This reward design is overly simplistic and does not adequately capture the varying reliability of different peers or how their information should be selectively utilized.

  3. The authors claim that ECL can be applied on top of any existing multi-agent protocol. However, the experiments are limited to aggregation-based settings, without evaluating ECL in combination with existing multi-agent frameworks or topology optimization methods such as G-Designer.

  4. The authors only report the additional inference time overhead of ECL compared to conventional methods, without providing a comparison of inference-time token consumption token consumption, which is important for evaluating the computational efficiency of the proposed framework.

Questions for authors
  1. Are Stage 1 and Stage 2 implemented using the same LLM with shared parameters, or are they two separately trained models? How are the two stages optimized using their respective rewards?

  2. Could the authors provide additional experimental results to demonstrate whether ECL remains effective when integrated with existing multi-agent frameworks or topology optimization methods?

  3. Could the authors provide a comparison of inference-time token consumption, including both input and output tokens, between ECL and existing methods to better evaluate its computational efficiency?

6 comments
AuthorsOpenReview ↗

Rebuttal to Reviewer Jb5t (1/2)

Thank you for your helpful review and for recognizing the importance of our problem formulation, the diagnostic failure modes we identify, and our comprehensive evaluation across model families and configurations. We address your concerns and questions one by one as follows:

W1 & Q1: Are Stage 1 and Stage 2 implemented using the same LLM with shared parameters, or are they two separately trained models? How are the two stages optimized using their respective rewards?

A1: Thank you for raising your question and we apologize for your confusion. Stage 1 and Stage 2 are implemented using the same LLM with shared parameters. Regarding RL optimization:

  • ECL (I): A shared model serves as the policy for both stage 1 and 2, where both stage 1 and stage 2 responses receive the final OR as their reward.
  • ECL (E): A shared model serves as the policy for both stage 1 and 2, where the stage 1 response receives PRR as its reward and stage 2 receives the final OR as its reward.

On large models that are not trained with RL, the difference between ECL (I) and ECL (E) is only the different requirement of stage 1 summary (and correspondingly, stage 2 input) in prompts.

How historical interactions are transformed into trust representations and how the resulting representation is used by Stage 2

The generated contents outside the reasoning block will replace {output_stage1} in the stage 2 prompt, i.e., the free-form summary in ECL (I) and the conclusion in ECL (E).

We have added this explicit description of parameter sharing and inter-stage representation passing to the revised manuscript.

W2: PRR is overly simplistic and does not adequately capture the varying reliability of different peers or how their information should be selectively utilized.

A2: Thank you for this comment. We agree that identifying the single most reliable peer does not fully capture the complexity of trust modeling. However, PRR is intentionally designed as a minimal proof-of-concept for explicitly supervising trust estimation, rather than a comprehensive solution to modeling peer reliability.

This design is motivated by two observations in our diagnostic experiments (Section 4):

  1. LLMs struggle to establish and utilize trust beliefs
  2. Outcome rewards provide only indirect supervision for trust estimation

More importantly, ECL does not restrict trust modeling or information utilization to a single peer, as our ECL (I) variant allows free-form reliability profiles capturing the varying reliability of different peers. We therefore view PRR as a minimal but effective implementation that establishes the value of explicit trust supervision. Designing richer rewards for more fine-grained trust modeling is a promising extension, but is not necessary for validating our central hypothesis.

AuthorsOpenReview ↗

Rebuttal to Reviewer Jb5t (2/2)

W3 & Q2: Could the authors provide additional experimental results to demonstrate whether ECL remains effective when integrated with existing multi-agent frameworks or topology optimization methods?

A3: Thank you for pointing out this ambiguity. When stating that ECL can be applied on top of existing multi-agent protocols, our intended meaning was architectural orthogonality: because topology design and communication protocols govern who communicates with whom at the system level, whereas ECL governs how an individual receiving agent processes incoming peer responses at the local level, ECL is interface-compatible with any protocol that supplies peer outputs, without implying that empirical gains have already been established across all dynamic topologies.

We agree that our current experiments focus on single-round aggregation rather than end-to-end multi-round graph topologies (such as G-Designer), which would require reconstructing multi-round interaction histories for each dynamic graph structure. Within our aggregation setting, we have already investigated its robustness across different multi-agent configurations in Section 6.3:

  • Number of peers (Table 11): ∣P∣∈{2,3,4}|\mathcal{P}| \in \{2,3,4\}
  • History length (Table 12): ∣H∣∈{2,5,8}|\mathcal{H}| \in \{2,5,8\}

ECL shows consistent gains over AG across all these structural variations. To prevent any over-interpretation of our claims, we have revised Section 1 to explicitly distinguish architectural orthogonality from our current empirical scope (single-round aggregation), and highlighted end-to-end integration with dynamic topology optimization as an important direction for future work in Section 7.

W4 & Q3: Could the authors provide a comparison of inference-time token consumption, including both input and output tokens, between ECL and existing methods to better evaluate its computational efficiency?

A4: Thank you for your interest in the token efficiency of our method. We compare the inference-time input, output, and total token consumption of ECL against AG and 1S below.

Mean input tokens

MethodGPQA (Nat.)GPQA (Adv.)MMLU-Pro (Nat.)MMLU-Pro (Adv.)Avg.
AG3914.61855.22227.71306.12325.9
1S5319.53312.53756.22775.43790.9
ECL (E)5528.33572.53901.83021.04005.9

Mean output tokens (including reasoning)

MethodGPQA (Nat.)GPQA (Adv.)MMLU-Pro (Nat.)MMLU-Pro (Adv.)Avg.
AG3349.16257.21466.51855.93232.2
1S4320.67179.02044.81605.93787.6
ECL (E)11292.015786.44310.15241.99157.6

Mean total tokens

MethodGPQA (Nat.)GPQA (Adv.)MMLU-Pro (Nat.)MMLU-Pro (Adv.)Avg.
AG7263.68112.33694.33161.95558.0
1S9640.110491.65801.04381.37578.5
ECL (E)16820.319358.98211.98262.913163.5

Analysis of Token Overhead: Compared to the history-aware 1S baseline, ECL increases input tokens by only 5.7%, because the distilled trust summary passed from Stage 1 to Stage 2 is highly compact (consistent with Appendix A.7). The 2.42$\times$ increase in output tokens (resulting in 1.74$\times$ total tokens) stems primarily from the internal CoT generated during Stage 1 to verify historical peer accuracy without ground-truth labels, alongside Stage 2's final reasoning.

Notably, this extra test-time compute is substantially more effective than alternative inference-scaling strategies: as shown in Table 10 (formerly Table 9), 3-round self-reflection incurs roughly 3$\times$ the compute of single-pass inference yet yields markedly smaller accuracy gains than ECL (e.g., 86.7% vs. 98.9% for Gemini 3 Flash on MMLU-Pro). Meanwhile, ECL incurs only 1.40$\times$ wall-clock latency over AG (Appendix A.7), representing a favorable efficiency-effectiveness trade-off. We have incorporated this token consumption analysis into Appendix A.7 (Tables 20–22) in the revised manuscript.

AuthorsOpenReview ↗

Sincerely Looking Forward to Your Further Feedback

Dear Reviewer Jb5t,

Thanks again for your insightful and helpful comments! We have submitted our response and we hope it has addressed all your concerns and questions. Since the end of discussion period is coming soon, we sincerely look forward to your further suggestions to our response, and we are open to any discussion to improve our paper.

Best regards,

Authors

Reviewer_m8FyOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper considers the problem of trust in LLM-based multi-agent setups. While multi-agent LLM setups have shown benefits over single-agent counterparts, the paper argues that LLMs tend to be sycophantic and cannot assess the reliability of other agents. The paper first presents some experiments to evidence that these issues exist, first by flipping the reliability of peers at test time, and secondly by rendering all peer agents unreliable. An explicit two-stage approach is then proposed, which first estimates the reliability of peers from historical information, then conditions outputs on these estimates. The authors study the approach comprehensively, investigating the benefits of trust mechanisms across training regimes and model sizes, whether peer information can be replaced with more reasoning, and what the impact on inference time is.

Post-rebuttal update

I raised my score to a 3 after the discussion.

Critical strengths

S1. The key idea behind the paper is timely and provides a very sensible path towards improving the performance of multi-agent LLM setups beyond other techniques currently being investigated (e.g., topology design).

Critical weaknesses

W1. Limited novelty and lack of acknowledgment of multi-agent systems literature

The topic of trust has been investigated extensively in the "traditional" multi-agent systems literature going back many years; see for example [1] for a survey dating back 22 years, or [2] for a more recent example with a learned trust mechanism for multi-agent reinforcement learning. As such, while the application of trust mechanisms in the context of multi-agent LLM systems may be novel, their benefits have long been established. The paper would therefore benefit from engaging with this literature by contrasting with existing trust mechanisms. In addition, the paper should specifically discuss what is different or particularly challenging when agents are LLMs rather than traditional agents.

W2. Experimental evidence is somewhat weak

Only 5 seeds are used. This is insufficient to draw statistically robust conclusions, despite the manuscript reporting p-values in places. Confidence intervals or error bars should be provided in all analyses -- the ones in the main text omit them. Reporting mean +- sd (e.g. as in Table 15) is inappropriate; confidence intervals should be computed, which at 95% confidence level corresponds to approximately 1.97 standard deviations. This makes the results artificially appear more robust than they are.

Furthermore, and perhaps more importantly, the scope of experiments is limited. The paper tests the approach on question-answering benchmarks, but the claims being made are more general. To support such general claims, experiments should be extended to other tasks such as mathematical reasoning or coding.

References

[1] Ramchurn, S. D., Huynh, D., & Jennings, N. R. (2004). Trust in multi-agent systems. The Knowledge Engineering Review, 19(1), 1-25.

[2] Fung, H. L., Darvariu, V. A., Hailes, S., & Musolesi, M. Trust-based Consensus in Multi-Agent Reinforcement Learning Systems. RLJ 2: 714-732 (2024)

Questions for authors

Please address W1 and W2. I am also listing some further queries and suggestions for improving the work below.

C1. Why was SA excluded from Table 1?

C2. Can you explain why the OR reward can cause instability?

C3. L248, re. reward hacking: this appears unsupported. The degradation in performance is indeed shown -- but why is it attributed to reward hacking?

C4. The inference time cost is covered and shown to be modest. But what about training time? Is it substantially different between the 1-stage approach and the two-stage model that involves first estimating trust?

8 comments
AuthorsOpenReview ↗

Rebuttal to Reviewer m8Fy (1/2)

Thank you for your valuable feedback and for recognizing the timeliness and potential of trust mechanisms in improving multi-agent LLM setups. We address your concerns and questions one by one as follows:

W1: Comparison with traditional MA literature and the special challenge when LLMs are used as agents.

A1: Thank you for pointing out these relevant studies from traditional multi-agent systems literature. We agree that trust modeling has been extensively studied in MAS, and these references provide valuable context for our work.

We would first like to clarify that our novelty claims have always been scoped to LLM-based MAS, as reflected in our title, problem formulation (Section 3), and throughout the manuscript. We do not claim that trust modeling or its benefits in multi-agent collaboration are new concepts.

Specifically, Ramchurn et al. [1] provide a comprehensive survey of trust mechanisms in traditional MAS, while Fung et al. [2] propose an RL-based mechanism for learning which agents to trust in distributed consensus. Our work builds on the same general motivation but focuses on two challenges specific to LLM-based reasoning:

  • Trust estimation: LLM agents must infer peer reliability from natural-language interaction histories, rather than relying on predefined trust signals or structured interaction outcomes.
  • Trust utilization: Unlike traditional mechanisms that primarily use trust to guide interactions or filter messages, LLM agents must incorporate trust into their reasoning over rich, potentially misleading peer-generated content.

As demonstrated in Section 4, existing LLMs struggle with both challenges, often ignoring historical reliability and blindly conforming to peer responses. ECL addresses these failure modes through a two-stage framework that decouples trust estimation from final reasoning, together with auxiliary RL supervision for explicit trust modeling.

We appreciate the reviewer's suggestion and have expanded our Related Work (see Appendix B) to acknowledge these foundational studies and clarify the distinctions between traditional trust mechanisms and our LLM-specific setting.

W2: Weak experimental evidence.

A2: Thank you for raising your concerns about our experiments. Two aspects are mentioned: statistical significance and the scope of experiments. We respond to them one by one.

W2.1 Statistical significance:

We respectfully disagree that using 5 random seeds renders our results statistically unreliable. Statistical significance depends on the observed effect sizes relative to variance, rather than an arbitrary minimum number of seeds. As reported in Appendix A.4 (Table 16, formerly Table 15), we evaluate representative models across 5 random seeds, report their standard deviations, and conduct statistical significance tests. The improvements are statistically significant (p<0.05p < 0.05) in the reported comparisons, providing rigorous quantitative evidence beyond differences in mean accuracy alone. We also evaluate three representative models on an enlarged GPQA test set (90 samples instead of 40; Appendix A.5, Table 17), where the improvements remain consistent.

We would also like to clarify the relationship between standard deviation and confidence intervals. Reporting mean±SD\text{mean} \pm \text{SD} is a standard and valid way to describe experimental variability; it is not intended to represent a 95% confidence interval. Moreover, the suggested factor of 1.97×SD1.97 \times \text{SD} does not apply to the confidence interval of the mean. For n=5n = 5 independent runs, the 95% confidence interval under the standard Student's tt-distribution is:

xˉ±t0.975,4s5≈xˉ±1.24s,\bar{x}\pm t_{0.975,4}\frac{s}{\sqrt{5}}\approx\bar{x}\pm1.24s,

where ss is the sample standard deviation (whereas ≈1.96\approx 1.96 applies to the standard error sn\frac{s}{\sqrt{n}} under a large-sample normal approximation, not directly to ss). Therefore, the absence of confidence intervals from the main tables does not invalidate our reported statistical tests or imply that our results are artificially made more robust. The existing evidence firmly supports our conclusions.

AuthorsOpenReview ↗

Rebuttal to Reviewer m8Fy (2/2)

W2.2 Scope of experiments:

We would first like to clarify that our manuscript already includes experiments on both mathematical reasoning and coding tasks (Math500 and LiveCode) in Sections 4-5. Across Tables 1-3 (and Table 13 in Appendix A.1), these controlled experiments systematically trace the full progression from Standalone Single-Agent (SA, Base/RL) and history-aware Single-Stage (1S, Base/RL) to two-stage ECL (I) and ECL (E) on Qwen 2.5-3B and Llama 3.2-3B, directly establishing the trust failure modes and validating our two-stage design and PRR supervision.

For our main multi-scale evaluation across 8 models of widely varying capacities (Section 6), we deliberately selected knowledge-intensive reasoning benchmarks (MMLU-Pro and GPQA) to avoid ceiling and floor effects: on standard math or coding benchmarks, frontier models can approach saturation under SA alone, whereas much smaller models may lack the foundational capability to leverage peer solutions. Knowledge-intensive benchmarks place all evaluated model scales in a non-trivial accuracy regime, enabling a well-calibrated comparison of how each model utilizes historical peer reliability. To ensure our conclusions remain strictly aligned with our empirical scope, we have also narrowed the framing of our claims in Sections 1 and 7 to focus specifically on verifiable reasoning and QA tasks, leaving open-ended collaborative tasks for future work.

C1: Why was SA excluded from Table 1?

A1: Thank you for pointing this out and we apologize for your confusion. SA results comparable with Table 1 are listed in Table 13 (formerly Table 12, Appendix A.1), and we have merged them into Table 1 as well for easier understanding.

C2: Can you explain why the OR reward can cause instability?

A2: Thank you for your interest in this phenomenon. The reason that OR reward can cause instability is that when we optimize both stages with OR, the supervision signal for stage 1 depends on an evolving stage-2 policy, making the optimization object non-stationary for stage 1.

C3: L248, re. reward hacking: this appears unsupported. The degradation in performance is indeed shown -- but why is it attributed to reward hacking?

A3: Thank you for pointing this out and we apologize for your confusion. This is summarized through our qualitative observation over model reasoning traces. Specifically, we see that when combining OR+PRR in 1S, the trained models tend to first answer the current question and then compare current-round answers to determine the reliable peer, without examining the history interactions. This violates the purpose of PRR on motivating trust establishment so we call it reward hacking. We have modified our statements in Section 5 and Appendix A.2 (Table 14) in the revised manuscript to make this clear.

C4: Comparison of training time over 1-stage and 2-stage.

A4: Thank you for your interest in the training cost of our method. Under the MA-Reasoning (Adversarial) setting on 8$\times$NVIDIA H200 GPUs (excluding validation), the mean training time per batch is 19.8 s for the 1S baseline and 39.8 s for ECL (E). This **2.0$\times$ training time is an expected and proportional consequence of generating two sequential rollouts (Stage 1 trust estimation followed by Stage 2 reasoning) per step. Since RL fine-tuning is a one-time offline cost and full training takes under an hour on our setup, this modest overhead is well justified by the substantial performance gains over 1S (e.g., +5.4% to +13.5% in Table 3).

AuthorsOpenReview ↗

Sincerely Looking Forward to Your Further Feedback

Dear Reviewer m8Fy,

Thanks again for your insightful and helpful comments! We have submitted our response and we hope it has addressed all your concerns and questions. Since the end of discussion period is coming soon, we sincerely look forward to your further suggestions to our response, and we are open to any discussion to improve our paper.

Best regards,

Authors

Reviewer_Pb57OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies how a single LLM agent in a multi-agent system should use peer responses when it can see the peers’ answers to earlier questions. Diagnostic probes (swapping which peer is reliable at test time, making all peers wrong) suggest that RL-trained models ignore this history and conform to their peers. The proposed Epistemic Context Learning (ECL) splits inference into two stages: Stage 1 sees only the history and produces a trust summary and Stage 2 answers the current question given that summary and the current peer responses. An auxiliary Peer Recognition Reward (PRR) trains Stage 1 to name the reliable peer, the authors show that this reward causes reward hacking without the two-stage split. Experiments on MMLU-Pro and GPQA with eight models (RL-tuned Qwen 3-4B/8B and six inference-only models) report gains over history-agnostic aggregation, particularly with adversarial peers.

Critical strengths
  1. A clean, reusable design insight. Withholding the current question from Stage 1 blocks the shortcut of inferring peer reliability from current-round content. The single-stage OR+PRR result (App. A.2) and the Copy-Reliable-Peer ablation (Table 8) support that both the decoupling and the second-stage reasoning matter. This is the contribution I would most want the community to see.
  2. Informative probes and broad coverage. The Flip and All-Wrong settings make the mechanism directly testable, results span eight models from four families with and without RL training, and the authors provide code and data.
Critical weaknesses
  1. Evaluation design and reporting. The adversarial setting, used for all analyses, pairs one always-correct peer with always-wrong peers, so the task largely reduces to finding an oracle. Histories carry no correctness labels, so Stage 1 relies on the agent solving the history questions itself. Training and test histories are drawn from the same small question pool (Sec. 6.1, App. F.1), so the RL-trained models may have memorized them. In the Natural setting, gains are small and within noise on the 40–90-question test sets; larger test sets and a peer pool whose best peer is stronger than the receiving agent would make this setting more informative. Several reported numbers are inconsistent across Tables 5, 6, 7 and 15, and the Table 5 values do not look like 5-seed means. Finally, the main results omit the single-stage history baseline and Copy-Reliable-Peer, so the benefit of the two-stage design over simply adding history is not isolated.

  2. The central claim is only partly supported. ECL is presented as fixing both ignored history and blind conformity, but the Flip and All-Wrong results (App. A.6, E) show that it mostly shifts conformity to the historically trusted peer, often falling well below history-agnostic aggregation. This leaves the agent open to a peer that builds trust and then deceives, which is the very threat the method targets; only the appendix-only DB variant partly helps. The related-work claim that prior fixes are limited to the current round also overlooks KAIROS (Song et al., ICLR 2026), which studies historical peer rapport with GRPO.

Questions for authors

Questions

  1. How does ECL compare with the single-stage history baseline and Copy-Reliable-Peer in the adversarial setting? How much of the gain remains over simply copying the identified peer?
  2. Do the gains of the RL-trained models hold when training and test histories come from disjoint question pools?
  3. How are the Table 5 results aggregated across seeds? Also reconcile Tables 5, 6, 7 and 15.

Clarification (Will not affect scoring) 4. How does ECL behave with several moderately reliable peers, or with a peer that is reliable in the history but deceives at test time? Can ECL+DB be evaluated in the main setting?

4 comments
AuthorsOpenReview ↗

Rebuttal to Reviewer Pb57 (1/3)

Thank you for your thoughtful review and for recognizing the design insight of our two-stage decoupling, the clarity of our diagnostic probes, and our broad evaluation. We address your concerns and questions one by one as follows:

W1: Evaluation design and reporting.

A1: Thanks for raising your concerns regarding our evaluation. We respond to them as follows:

The adversarial setting largely reduces to finding an oracle.

We clarify that this setting is intentionally designed as a controlled diagnosis with two objectives: testing (1) whether LLMs can identify a reliable peer from the interaction history, and (2) whether Stage 2 reasoning properly leverages this trust together with its own epistemic autonomy. Crucially, even in the adversarial setting, the task does not reduce to merely copying an oracle: when Stage 1 misidentifies the reliable peer (rPRR=0r_{\text{PRR}}=0), the CRP strategy will drop to 0% accuracy, whereas in Table 7 ECL retains 55.0%-100.0% accuracy through Stage 2 reasoning. Furthermore, to evaluate regimes including no oracle peer, we pair this probe with our Natural setting, where the strongest peer (Gemini 3 Flash) still makes frequent errors.

Training and test histories are drawn from the same question pool.

We kindly refer you to our response to Q2.

A peer pool whose best peer is stronger than the receiving agent would be informative.

Thank you for highlighting this distinction. We agree that this evaluation is particularly informative. This regime is already covered in our Natural setting results (Table 5) for smaller receiving agents such as Qwen 3-4B, Qwen 3-8B, and Qwen 3-30B (all weaker than the strongest peer, Gemini 3 Flash), where ECL achieves substantial gains over AG. At the same time, we included frontier receiving agents (similar to or stronger than Gemini 3 Flash) to verify that ECL does not degrade performance when peers offer less additional information. We have added a dedicated discussion on relative peer strength in Section 6.2 of the revised manuscript.

Inconsistent numbers across Tables 5, 6, 7 and 15, and Table 5 does not look like 5-seed means.

We kindly refer you to our response to Q3.

The main results omit the single-stage history baseline and CRP, so the benefit of 2-stage design over simply adding history is not isolated.

We have reported the comparison between 1S (RL) and ECL in our analyses (Table 3), which shows that simply adding history does not inspire LLMs to learn and utilize trust. To further address your concerns in comparison with 1S and CRP, we conduct additional experiments, provide additional explanations, and kindly refer you to our response to Q1.

W2: Instability in peer reliability and comparison with KAIROS.

A2: Thank you for raising these concerns. We would like to clarify the scope of our work and its differences from KAIROS.

Instability in peer reliability.

Our work aims to investigate how LLMs can build and utilize epistemic trust from historical interactions, rather than how to handle arbitrary changes in peer reliability. To isolate this problem, we adopt an approximately stationary trust assumption, which is explicitly stated in Section 7.

Under this formulation, the Flip and All-Wrong experiments serve as stress tests examining how models utilize historical trust and what happens when the reliability assumptions are violated.

We agree that ECL remains vulnerable to sudden trust reversals. However, robustness against non-stationary or compromised peers is a distinct research problem, rather than the central claim of this work. We have explicitly acknowledged this limitation in Section 7 and explored a complementary solution through Decoupled Belief (DB) in Appendix E.

Comparison with KAIROS.

Thank you for raising these points. These are important considerations that we also discussed in our original submission (Section 7 and Appendix E) and have further clarified in our revision.

KAIROS and ECL investigate fundamentally different historical signals and learning objectives. KAIROS constructs historical rapport based on how frequently peers agree with the target agent, primarily studying how social familiarity influences conformity. Its history construction collectively manipulates peer agreement, rather than establishing differentiated epistemic reliability profiles.

Consequently, while KAIROS evaluates GRPO with historical interactions and reports performance improvements under certain configurations, its training does not explicitly optimize the identification and utilization of historically reliable peers.

In contrast, ECL specifically studies how agents distinguish peers with different reliability and selectively incorporate their information. Our two-stage framework and PRR directly address this objective, which is not investigated by KAIROS. We have added this explicit comparison with KAIROS directly to Section 2 (Related Work) in the revised manuscript.

AuthorsOpenReview ↗

Rebuttal to Reviewer Pb57 (2/3)

Q1: How does ECL compare with the single-stage history baseline and Copy-Reliable-Peer in the adversarial setting? How much of the gain remains over simply copying the identified peer?

A1: Thank you for your question. We clarify the two comparisons below.

Comparison with 1S: Beyond the RL comparisons in Tables 2-3, we additionally evaluate the history-aware 1S baseline on the main adversarial setting (MA-Reasoning) across frontier models:

ModelMMLU-Pro 1SMMLU-Pro ECL (E)GPQA 1SGPQA ECL (E)
DeepSeek V3.290.091.177.585.0
GPT-5-mini82.290.080.085.0
Gemini 3 Flash96.798.990.095.0

ECL consistently outperforms 1S across all six comparisons by 1.1-7.8 percentage points, confirming that decoupling trust estimation from final reasoning provides consistent benefits beyond simply concatenating history into the prompt.

Comparison with CRP: In the adversarial setting, CRP accuracy is mathematically identical to the Stage 1 Peer Recognition Rate (Table 6), because the single reliable peer is always correct (100%100\%) and all other peers are always wrong (0%0\%). While Stage 2 reasoning can occasionally introduce errors when overriding a correctly identified peer, its primary advantage in the adversarial setting lies in fault tolerance when Stage 1 fails (rPRR=0r_{\text{PRR}}=0): whereas CRP suffers 0% accuracy upon misidentification, ECL recovers 55.0%-100.0% accuracy via independent Stage 2 reasoning (Table 7). Moreover, in the more realistic Natural setting where no peer is infallible, ECL consistently outperforms CRP by 2.5-12.5 percentage points (Table 8), demonstrating the clear benefit of trust-conditioned reasoning over simply copying the selected peer.

Comparison with CRP: In the adversarial setting, CRP accuracy is mathematically identical to the Stage 1 Peer Recognition Rate (Table 6), because the single reliable peer is always correct (100%100\%) and all other peers are always wrong (0%0\%). While Stage 2 reasoning can occasionally introduce errors when overriding a correctly identified peer, its primary advantage in the adversarial setting lies in fault tolerance when Stage 1 fails (rPRR=0r_{\text{PRR}}=0): whereas CRP suffers 0% accuracy upon misidentification, ECL recovers 55.0%-100.0% accuracy via independent Stage 2 reasoning (Table 7). Moreover, in the more realistic Natural setting where no peer is infallible, ECL consistently outperforms CRP by 2.5-12.5 percentage points (Table 8), demonstrating the clear benefit of trust-conditioned reasoning over simply copying the selected peer.

Q2: Do the gains of the RL-trained models hold when training and test histories come from disjoint question pools?

A2: Thank you for pointing this out. To address your question, we conduct additional experiments with Qwen 3-4B on MMLU-Pro, where we split the history set into two independent subsets (of the same size) for training and testing respectively. The results are shown as follows.

SettingContextAGECL(I)ECL (I) in Table 5ECL(E)ECL (E) in Table 5
MA-OutcomeAdversarial70.080.085.682.282.2
MA-OutcomeNatural67.873.372.271.171.1
MA-ReasoningAdversarial78.990.090.090.090.0
MA-ReasoningNatural78.981.185.681.184.4

We find that RL-trained models still outperform AG baselines with independent history sets, showing that the benefit does not come from pure memorization in peer identification. These results are included in Appendix A.9 (Table 24) of the revised manuscript.

Q3: How are the Table 5 results aggregated across seeds? Also reconcile Tables 5, 6, 7 and 15.

A3: Thank you for pointing this out and we apologize for the confusion caused by our imprecise description in Section 6.1 and the Table 5 caption. Due to API cost constraints, the results in Tables 5, 6, and 7 are evaluated with a fixed random seed by default, except for the representative model-setting combinations covered in Table 16 (formerly Table 15), whose values in Table 5 are the exact 5-seed means matching Table 16.

In addition, we identified a typo in Table 16 (formerly Table 15) for GPT-5-mini on MMLU-Pro, where the SA and AG means should be 80.0% and 84.4%, respectively (matching Table 5). We have corrected these typos in Table 16 and clarified the seed aggregation protocol in Section 6.1 and the Table 5 caption in the revised manuscript.

AuthorsOpenReview ↗

Rebuttal to Reviewer Pb57 (3/3)

Q4: How does ECL behave with several moderately reliable peers, or with a peer that is reliable in the history but deceives at test time? Can ECL+DB be evaluated in the main setting?*

A4: Thank you for raising these important edge cases—as noted in our discussion of limitations (Section 7 and Appendix E), dynamic or homogeneous peer reliability is a critical consideration for multi-agent deployment. We address each scenario below:

With several moderately reliable peers: ECL will perform similarly to AG, analogous to humans weighing peer voices equally when peers are similarly reliable, which we believe is appropriate. This has also been studied in KAIROS, which found homogeneous peers do not provide useful signals, yet our contribution is showing that heterogeneous peers can help.

ECL+DB evaluation in the main setting: In Table 25 (formerly Table 20, Appendix E), we have evaluated ECL+DB on GPQA under both standard and All-Wrong settings, showing that incorporating DB generally maintains or improves standard accuracy while boosting robustness when all peers are wrong.

To further test robustness against trust reversal, we evaluate ECL+DB under the Flip setting on GPQA (Adversarial, 40 test questions) across both MA-Outcome and MA-Reasoning. In the table below, Normal accuracies are from Table 25 (formerly Table 20), non-DB Flip accuracies are from Table 18 (formerly Table 17), and DB Flip cells are our newly added evaluations (— indicates AG Flip is the same with Normal since AG does not use history):

ModelMethodMA-Outcome NormalMA-Outcome FlipMA-Reasoning NormalMA-Reasoning Flip
GPT-5 miniAG87.5—75.0—
GPT-5 miniECL(I)87.580.082.580.0
GPT-5 miniECL(I)+DB82.585.085.087.5
GPT-5 miniECL(E)85.075.085.082.5
GPT-5 miniECL(E)+DB85.085.085.082.5
Gemini 3 FlashAG87.5—87.5—
Gemini 3 FlashECL(I)95.050.092.555.0
Gemini 3 FlashECL(I)+DB97.562.597.562.5
Gemini 3 FlashECL(E)97.535.095.065.0
Gemini 3 FlashECL(E)+DB100.062.592.567.5
DeepSeek V3.2AG77.5—80.0—
DeepSeek V3.2ECL(I)80.072.582.565.0
DeepSeek V3.2ECL(I)+DB87.582.587.577.5
DeepSeek V3.2ECL(E)82.562.585.062.5
DeepSeek V3.2ECL(E)+DB87.557.595.065.0

These additional results show that DB can substantially mitigate the performance degradation caused by trust reversal, e.g., improving Gemini 3 Flash from 35.0% to 62.5% under MA-Outcome with ECL (E). Together, these findings suggest that independent reasoning complements historical trust estimation, enhancing robustness against unreliable peers without sacrificing standard performance. These new DB Flip results have been incorporated into Table 25 in the revised manuscript.

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Sincerely Looking Forward to Your Further Feedback

Dear Reviewer Pb57,

Thanks again for your insightful and helpful comments! We have submitted our response and we hope it has addressed all your concerns and questions. Since the end of discussion period is coming soon, we sincerely look forward to your further suggestions to our response, and we are open to any discussion to improve our paper.

Best regards,

Authors

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of Revisions in the Updated Manuscript

We thank all reviewers for their constructive feedback. We have uploaded a revised version of our manuscript with the following key updates (all revised contents highlighted in blue fonts):

  • Clarified Scope & Orthogonality (Sections 1 & 7): Explicitly distinguished architectural orthogonality (interface compatibility with multi-agent communication protocols) from our empirical scope (single-round aggregation), and scoped our claims and conclusions specifically to verifiable reasoning and question-answering tasks.
  • Expanded Literature Comparison (Section 2 & Appendix B): Added an explicit comparison with KAIROS (Song et al., 2026) in Section 2 to contrast social rapport with individual epistemic reliability, and expanded Appendix B to engage with foundational trust mechanisms in traditional multi-agent systems (Ramchurn et al., 2004; Fung et al., 2024).
  • Completed Diagnostic Baselines (Section 4, Table 1): Included standalone Single-Agent (SA) RL baseline accuracies directly inside Table 1 alongside the Flip and All-Wrong probing results for immediate comparison.
  • Clarified Methodological & Optimization Details (Section 5): Added an explicit explanation of shared-parameter execution across Stage 1 and Stage 2, how the distilled external trust representation (BjB_j) replaces {output_stage1} in Stage 2 prompts (excluding internal <think> traces), why direct outcome reward (OR) propagation to Stage 1 causes non-stationary instability, and how single-stage OR+PRR leads to current-round reward hacking.
  • Reconciled Seed Aggregation & Fixed Typos (Section 6.1, Table 5, & Appendix A.4 Table 16): Clarified the random seed aggregation protocol (single fixed seed by default vs. 5-seed means with standard deviations for representative model-setting combinations) and corrected the GPT-5-mini SA/AG mean typos on MMLU-Pro in Table 16 (formerly Table 15).
  • Added Analysis of Relative Peer Strength (Section 6.2): Added a dedicated paragraph discussing why ECL yields larger gains when the receiving agent is weaker than the strongest peer, while maintaining standalone performance without harmful conformity when the receiving agent matches or exceeds peer capability.
  • Added Main-Setting Single-Stage History Baseline (Section 6.3, Table 9): Evaluated the history-aware single-stage (1S) baseline against ECL (E) across frontier models in the 4-peer adversarial setting (MA-Reasoning), isolating the benefit of two-stage decoupling.
  • Expanded Efficiency & Training Cost Analysis (Section 6.3 RQ 3.2 & Appendix A.7, Tables 20–22): Added inference-time input, output, and total token consumption comparisons across AG, 1S, and ECL (E), alongside per-batch RL training time comparisons (1S vs. ECL (E)).
  • Added Disjoint History Pool Generalization Study (Appendix A.9, Table 24): Evaluated RL-trained ECL when training and test histories are drawn from completely non-overlapping question pools, confirming that gains do not rely on question memorization.
  • Extended Decoupled Belief (DB) Evaluation to Trust Reversal (Section 6.3 & Appendix E, Table 25): Added Flip setting results for ECL+DB across frontier models in Table 25 (formerly Table 20) and linked this analysis from the main text.
AuthorsOpenReview ↗

Summary of the Rebuttal and Discussion

Dear Area Chair and Reviewers,

We sincerely thank all reviewers for their careful reading and constructive feedback. In the discussion, all three reviewers converged on positive assessments: Pb57 maintained a positive rating (3), m8Fy confirmed that our additional per-seed results and benchmark justifications resolved their concerns and raised their rating from 2 to 3, and Jb5t stated that our rebuttal "addressed most of my concerns" and indicated consideration of raising their rating to 3.

In their reviews, the reviewers highlighted the clean, reusable two-stage decoupling insight that blocks current-round shortcuts (Pb57), the importance and timeliness of individual-level peer trust modeling in LLM multi-agent systems (m8Fy, Jb5t), the informative Flip and All-Wrong diagnostic probes (Pb57, Jb5t), and the broad evaluation spanning 8 models from 4 families across natural and adversarial regimes (Pb57, Jb5t). We summarize the main points of the discussion below; the corresponding manuscript updates are detailed in a separate comment titled "Summary of Revisions in the Updated Manuscript".

Summary of the discussion

  1. Isolation of two-stage decoupling (1S and CRP baselines) (Pb57, Jb5t). We added a direct comparison against the history-aware single-stage (1S) baseline in the main 4-peer adversarial setting (Section 6.3, Table 9), where ECL (E) outperforms 1S across all frontier models by +1.1% to +7.8% confirming benefits beyond raw history concatenation. Compared with Copy-Reliable-Peer (CRP), ECL outperforms CRP by +2.5% to +12.5% in the Natural setting (Table 8) and retains 55.0%–100.0% accuracy via Stage 2 fault-tolerant reasoning when Stage 1 misidentifies the reliable peer (Table 7).
  2. Generalization to disjoint history pools (Pb57). To rule out memorization from sharing a history pool between training and testing, we evaluated RL-tuned Qwen 3-4B with completely non-overlapping train/test history pools on MMLU-Pro (Appendix A.9, Table 24), confirming consistent gains over AG across all settings.
  3. Per-seed distributions and statistical robustness (Pb57, m8Fy). We reconciled the seed aggregation protocol in Section 6.1 and Table 5, corrected the GPT-5-mini SA/AG mean typos in Table 16, and provided the complete sorted per-seed accuracy distributions across all 5 runs for Table 16 (to be added to Appendix A.4). On MMLU-Pro, ECL (E)'s worst single run strictly exceeds AG's best single run across every model (non-overlapping ranges), ruling out outlier distortion, alongside tightened standard deviations (0.7%–1.8%) on the enlarged 90-sample GPQA split (Table 17).
  4. Empirical justification for benchmark transition (m8Fy). We provided concrete preliminary data explaining the task–capability calibration between Sections 4–5 and Section 6 (to be added to Section 6.1): newer-generation Qwen 3-1.7B/4B/8B models already reach 95%–98%+ standalone accuracy on Math500/LiveCode (ceiling saturation), whereas earlier-generation 3B/7B/8B models remain below 30% on 4-option GPQA even after RL (near random-guessing floor). Evaluating Qwen 3 and frontier models on MMLU-Pro and GPQA places all 8 models in an informative 52.5%–90.0% regime.
  5. Non-stationary peers (ECL+DB) and relative peer strength (Pb57). We added new Flip trust-reversal evaluations for ECL+DB across frontier models in Appendix E (Table 25), showing substantial mitigation of reversal drops (e.g., improving Gemini 3 Flash from 35.0% to 62.5%), and added a dedicated discussion on relative peer strength in Section 6.2.
  6. Architectural clarity, compute overhead, and literature positioning (m8Fy, Jb5t). In Section 5 we clarifiy shared-parameter execution and inter-stage passing of the external trust representation BjB_j, while in Sections 1 and 7 we scope protocol orthogonality to single-round aggregation (Tables 11–12). In Section 2 and Appendix B we contrast ECL with KAIROS and traditional MAS trust literature. Finally, Section 6.3 (RQ 3.2) and Appendix A.7 (Tables 20–22) document efficiency: ECL (E) incurs 1.40× wall-clock latency over AG, +5.7% input tokens over 1S, and 39.8s vs. 19.8s (1S) per-batch RL training time on 8×H2008\times\text{H200} GPUs, outperforming 3-round self-reflection (~3× compute, Table 10).

Together with consistent gains across 8 models from 4 families, we believe these results further support ECL's effectiveness and generality.

We thank the reviewers again for their thoughtful comments, which have helped us improve the paper.

Best regards,

Authors

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