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Under review as a conference paper at ICLR 2027

When Does Multi-Agent Debate Backfire? A Predictable and Preventable Failure Mode of Heterogeneous LLM Debate

Abstract

Multi-agent debate (MAD) is widely believed to improve the factuality and reasoning of large language models (LLMs). We show that in heterogeneous debate, the realistic setting where a strong agent debates weaker ones, debate can systematically destroy correct answers. Across three strong models (Claude-Opus, GPT-5.2, and Gemini-3; four model configurations over 4,554 calibrated BBH tasks), we find that on questions the strong agent initially answers correctly, debate flips 11.6% of them to wrong (a harmful-debate event), with rates as high as 23.6%. Crucially, this failure is not random but predictable before any debate round is spent: whether the strong and weak agents agree in round 0 almost perfectly separates safe from harmful debate. The harmful rate is 0.2% under round-0 consensus versus 26.4% under round-0 disagreement (a 129-fold gap, p < 10^-125 when merged; significant for every strong model individually). A single zero-cost observable feature, round-0 disagreement, recovers harmful debate with approximately 100% recall. We further show the failure is preventable: a simple training-free rule, PROTECT, that defers to the strong agent's initial answer whenever agents disagree, recovers accuracy on the at-risk subset to approximately 100% while skipping approximately 50% of debate compute; several variants even exceed the strong-solo baseline. We release the benchmark, predictability protocol, and PROTECT baselines as a testbed for when to trust debate.

Primary area:
foundation or frontier models, including LLMs
Keywords:
multi-agent debate, heterogeneous LLM agents, debate failures, selective debate, LLM safety

Reviews

Among:
Shape:
1234this paper, Bottom 9%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.50 over 4 reviews, above 9% of the others.
Reviewer_d81DOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies heterogeneous debate, where one strong model debates two weaker ones. The strong models are Claude-Opus, GPT-5.2, and Gemini-3. The experiments use 4,554 BBH instances pooled over four configurations. On the 3,475 instances the strong agent gets right at round 0, debate turns 11.6% into wrong answers. Nearly all of these harmful flips happen when the agents disagree at round 0. The harmful rate is 26.4% under disagreement and 0.2% under consensus. In 93.3% of harmful flips, the final wrong answer matches one that a weak peer gave at round 0. The paper proposes PROTECT, which keeps the strong agent's round-0 answer when the agents disagree. It also tests two variants. PROTECT and its variants are evaluated by offline replay of the logged debate transcripts.

Critical strengths
  1. The strong-plus-weak setting is realistic, and looking at item-level outcomes is the right way to study it. Table 2 splits outcomes into harmful, helpful, and neutral. It shows nicely how a near-zero net change can hide large movements in both directions.

  2. Table 3, on where harmful flips end up, is informative. In most harmful flips, the final wrong answer matches a weak peer's round-0 answer.

  3. The per-task-family breakdown in Fig. 5 shows a lot of heterogeneity. The authors are also upfront about the null merged net effect.

Critical weaknesses
  1. No cost comparison with the strong model alone. WEIGHTED gives the strong agent "a double vote on disagreement" (§6). The paper says it "beats both blind debate and the strong-solo baseline" and calls this "a usable gain". This comparison is made on accuracy alone. The strong-solo baseline is a single round-0 answer from the strong agent (App. A). WEIGHTED is triggered by round-0 disagreement. So in deployment it needs round-0 answers from all three agents, and possibly the debate rounds as well. The paper reports that PROTECT skips about half of the debate calls. For WEIGHTED, it reports no calls, tokens, or prices. The number of debate rounds is not given either. So it is unclear whether a gain of +1.3 to +5.7 points (Table 5) is worth the extra calls.

  2. The weak peers' own accuracy is not reported. The paper's story is that a capable model is "talked out of correct answers" by weaker peers (§4). The peers are described as "smaller" and "cheaper" models (§3, App. A). The task filter is described only in terms of the strong agent (§3). The peers' round-0 answers are logged (App. A), yet their accuracy on these tasks is never reported. So the paper does not show how much weaker the peers actually are on these tasks. This matters for reading the results. The two Claude configs use the same strong model with different weak peers. Their net effects in Table 2 are −9.0% and +2.0%. §4 refers to the config with the higher harmful rate as Claude-Opus's "more adversarial weak-peer config". Without the peers' accuracy, this difference is hard to interpret.

  3. Only one panel size and one vote weight are tested. Every debate in the paper uses one strong agent and two weak agents. The paper motivates this by realistic deployments (§3) and by not relying on a single weak model (App. A). §7 leaves "larger debates" to future work, but no smaller panel is tested either. A one-strong-one-weak panel is the natural, cheaper point of comparison. It matters because 51.0% of harmful flips end on an answer that both weak peers gave at round 0 (Table 3). With one peer, this two-against-one case cannot occur. The weight in WEIGHTED is fixed at a double vote without explanation, and no other weight is tried. With two weak peers of one vote each, a double vote ties whenever both peers agree against the strong agent. The paper does not say how such ties are broken, or which round's answers enter the vote.

Questions for authors
  1. (W1) Could you add the cost of each policy to Table 5, in model calls and tokens, or in price? Please also give the number of debate rounds. How does WEIGHTED compare with the strong model alone at a similar cost? One option is a majority vote over several samples from the strong model.

  2. (W2) Could you report each weak peer's round-0 accuracy for every config, overall and per task family? This should be computable from the existing logs. It would also help explain the gap between the two Claude configs.

  3. (W3) Could you add a one-strong-one-weak configuration for at least one strong model? For WEIGHTED, why a double vote, and how are ties broken? Suppose each weak peer's answer counts once and the strong agent's answer counts w times. If the answer with the largest total wins, the decision changes only at w = 1 and w = 2. Besides the reported w = 2, it would help to report one value between 1 and 2 and one above 2. Together these cover every case in which the strong agent counts more than a peer.

Reviewer_CvciOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

The paper studies heterogeneous multi-agent debate, in which one strong LLM debates two weaker LLMs on BBH tasks. The strong models are Claude-Opus, GPT-5.2 and Gemini-3.

Critical strengths
  1. The setting is common in practice, since a strong model is often paired with cheaper helpers. Showing that item-level harm can sit under an aggregate null effect (Table 2) is a useful observation.

  2. Table 3 is clean and informative. In 93% of harmful flips, the strong agent adopts an answer a weak peer already gave at round 0. All routing variants are scored by offline replay on the same transcripts, so the comparisons are matched per item, and the authors report the non-significant merged net effect.

Critical weaknesses

1. The predictability result is close to true by construction. A harmful event needs the strong agent to move from a correct answer to a wrong one, and Table 3 shows that 93% of the time the wrong answer came from a weak peer at round 0. If all three agents agree at round 0 on this subset, they are all correct, so there is no wrong answer to adopt. Near-zero harm under consensus is expected almost by definition, and only the 4 of 1,958 residual events are informative. To show predictability, the paper would need to predict harm within the disagreement bucket, that is, to say which disagreements end in capitulation. There the best training-free rule reaches 26% to 39% precision (Table 7). The z-test with p < 10^-125 compares a bucket where harm is nearly impossible with one where it is possible, so it says little about the quality of a predictor.

2. PROTECT is the strong-solo baseline, so the 100% recovery is tautological. On disagreement, PROTECT returns the strong agent's round-0 answer. On consensus all agents already share one answer, which debate almost never changes. Table 5 confirms this. PROTECT equals the baseline exactly, at +0.0 on all three models. On the base_ok=1 subset the strong agent's round-0 answer is correct by definition, so "recovers the at-risk subset to ≈100%" only says that skipping debate leaves the round-0 answer unchanged. PROTECT also discards all 382 helpful fixes. Section 6 also contradicts itself on compute: the definition runs debate on consensus and skips it on disagreement, yet the text says PROTECT skips "the ∼50% of items that are round-0-agreement (safe) and thus not worth debating".

Other issues that also affect my assessment.

  • WEIGHTED and CONF-GATED are chosen and scored on the same logged transcripts, with no held-out split. The best policy changes by model, from +5.4% on GPT-5.2 to −4.1% on Claude, and the WEIGHTED rule (which round is voted, how ties are broken) is not specified well enough to reproduce.
  • There is no no-peer control. Part of the 11.6% may be sampling instability that would appear if the strong agent re-answered alone for the same number of rounds, especially on low-confidence items where Fig. 6 reports harm as high as 39%.
  • The "4,554 calibrated BBH tasks" appear to be task × config instances. The Table 1 counts are multiples of BBH subtask sizes (salient translation 1000 = 4 × 250, causal judgement 561 = 3 × 187, disambiguation 500 = 2 × 250), yet the merged tests treat instances as independent. Subtask coverage also differs across configs, which confounds per-model comparisons with task mix.
  • Figure values disagree with the text. Fig. 2 shows 17.6, 14.7, 11.8, 9.8 and 4.3% with "4 strong models" and merged n=434, versus 23.6, 13.1, 7.4 and 2.1% and n=3,475 in the text. Fig. 3's title says 0.4% vs 27.3% (p<1e-17) versus 0.2% vs 26.4% in the text. Fig. 6 shows 39.3, 11.2 and 3.6% versus 29.8, 14.6 and 4.5%. Fig. 4 bars sit at about 90% to 96% versus 81.7, 92.6 and 97.9%. Sec. 7 says every harmful event follows a disagreement, which conflicts with the 4 events under consensus.
  • Sec. 2 says BBH is complemented with GSM8K and MATH, but no such results appear. The debate protocol (rounds, prompts, temperature, confidence elicitation) is not given. There is no comparison with DOWN (Eo et al., 2025) or with majority vote or self-consistency at matched compute.
Questions for authors
  1. How many unique BBH items are there, and how was the mid-difficulty filter applied? Did it use the strong model's own correctness?
  2. On base_ok=1, what is the flip rate when the strong agent revises alone for the same number of rounds?
  3. What is the exact WEIGHTED rule (which rounds are voted, how ties are broken), and how were the CONF-GATED thresholds chosen? Can you report results on a held-out split?
  4. For the final testbed, are the figure values (Figs. 2, 3, 4 and 6) or the text values correct?
  5. How do PROTECT and WEIGHTED compare with DOWN and with majority vote or self-consistency at matched compute?
  6. Within the disagreement bucket, which features predict capitulation better than chance?
Reviewer_6WNKOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies debate between one strong LLM and two weaker ones, scoring the strong agent's final answer. On 4,554 BBH runs across four configs (Claude twice, GPT-5.2, Gemini), debate turns 11.6% of the strong agent's initially correct answers wrong, while the net accuracy change is about zero when merged. Almost all of these flips happen when agents disagree at round 0 (26.4% vs 0.2%), and 93.3% land on an answer a weak peer already gave, which the authors read as sycophancy. They then propose PROTECT, which keeps the strong agent's round 0 answer on disagreement, and report that it brings the initially correct subset back to about 100% while skipping about half of the debate. A weighted vote variant beats the strong agent alone on all three models.

Critical strengths

The decomposition in Table 2 is useful. Splitting debate into broken answers and fixed answers per config shows something a mean accuracy number hides, and the authors do report that the merged effect is null (404 broken vs 382 fixed). This is the most valuable part of the paper and I would like to see it kept.

The Claude pair A vs pair B comparison is also interesting. The same strong model loses 23.6% or 13.1% of its correct answers depending on the weak peers, so who you debate with matters a lot. The paper mentions this only in passing.

Critical weaknesses

Weakness 1. Predictable and preventable are close to true by construction.

Prevention first. On items the strong agent got right at round 0, keeping the round 0 answer gives 100% by definition, so "recovers accuracy to about 100%" is not a result. The fair number is global accuracy, and there Table 5 shows PROTECT at +0.0 on all three models. It is the strong agent alone, except that you also paid for two weak agents at round 0. So it saves debate calls compared to full debate, but it is dominated by simply not debating. It is also worse than full debate on GPT-5.2 (79.4 vs 83.4) and Gemini (81.6 vs 82.9). The claim that a false positive "costs nothing" only holds inside the subset selected with gold labels, which you do not have at deployment. Outside that subset a flag can cancel a fix, and debate fixes 382 of the 1,079 wrong answers. That cost is never shown.

Prediction has the same problem. If everyone already agrees there is nothing to flip to, so disagreement predicts that the answer can change, not that the change is bad. The paper only reports harm conditioned on initially correct answers. It never reports fixes split by agreement, and I would expect most of the 382 fixes to sit in the same disagreement bucket. If so, the bit does not tell you harm from help, and the merged counts suggest roughly a coin flip on the items where debate matters. The p value of 10^-125 is measuring something that is almost structural. Precision also looks better than it is, since the 26% is computed after removing the items the strong agent got wrong.

The rule itself is not consistent. Section 6 defines PROTECT as skipping debate on disagreement, but then says it skips the round 0 agreement items as not worth debating. If both hold, no debate is ever run. Under the stated definition GPT-5.2 keeps its 4 harmful events under consensus, so 100% on all models cannot be right, and Figure 4 itself shows 99. I also could not tell what WEIGHTED does. If a double vote is cast on round 0 answers it is hard to see how it gains over the strong agent, and if it is cast on post debate answers then debate was run and no compute was saved. Its gains come from replay on the same data as the other variants, with no held out split and no intervals, so "beats both blind debate and the strong solo baseline" is not established.

Weakness 2. The causal story has no control, and the reported evidence has been patched together.

There is no arm where the strong model simply answers again, alone or after seeing peers with random answers. Conditioning on one correct sample already selects some answers that were lucky, so some of the 11.6% is likely instability that has nothing to do with debate. Item difficulty is a confound too, because hard items produce both disagreement and flips. The 93.3% "adopted from a weak peer" figure does not show capitulation either. On a correct item with disagreement a wrong answer is already on the table, and with few options, or yes/no in causal judgement, a flip has few places to land. A chance baseline is needed before calling it sycophancy. The debate prompt, the number of rounds and the temperature are not given, and these may drive the effect.

The merged 11.6% also hides a lot. Claude gives 315 of the 404 harmful events and pair A alone gives 203. Table 2 shows pair A is the only config where debate is net harmful, and GPT-5.2 is significantly helped (p=4.7e-4). This contradicts the text saying the harmful direction is highly significant per model. The 5.8e-10 quoted for Claude-Opus matches neither pair A (8.8e-10) nor my calculation for merged Claude (about 4e-4). Strong model and weak pair are also not crossed, and the Gemini config uses a flash tier model as the "strong" agent.

Figures 2, 3, 4 and 6 come from a different and much smaller run than the text. Figure 2 says n=434 with 17.6, 14.7, 9.8, 4.3 and 11.8, against 23.6, 13.1, 7.4, 2.1 and 11.6 in the text. Figure 3 has 0.4% vs 27.3%, p<1e-17 in its title. Figure 6 has 39.3, 11.2 and 3.6 against 29.8, 14.6 and 4.5. Figure 4 omits Claude completely and shows 90 and 96 instead of 92.6 and 97.9. The captions were updated but not the plots. So I have no way of telling which analysis the numbers come from.

Questions for authors
  1. How do fixes split by round 0 agreement, per config? If disagreement also holds most of the fixes, what is left of the predictability claim on the full task population?

  2. What happens when the strong agent answers the same question again with no peers, on the same temperature and prompt? What flip rate does that give, and how much of the 11.6% survives after subtracting it?

  3. What is the chance rate of landing on a peer answer given the number of options per family?

Reviewer_fyWjOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies cases where heterogeneous multi-agent debate changes a strong model’s initially correct answer into an incorrect one. It evaluates three strong models across four debate configurations on selected BBH tasks and reports that harmful changes are concentrated in cases with round-0 disagreement. Based on this observation, it introduces PROTECT, which keeps the strong model’s initial answer when agents disagree, and evaluates weighted and confidence-gated variants.

Critical strengths

1.Separating harmful and helpful answer changes is useful. Aggregate accuracy alone does not show which initially correct answers are lost. I appreciate that the paper also reports helpful changes and the small merged net effect, rather than presenting the harmful cases alone.

2.The comparisons across strong models and weak-peer configurations are a strength. Round-0 agreement is also a simple, interpretable signal that is available once the initial answers have been collected and does not require training a separate predictor.

Critical weaknesses
  1. I find the diagnostic results more convincing than the claim about prevention. The paper presents PROTECT as a diagnostic baseline, which is reasonable. Still, the near-100% accuracy on initially correct items is somewhat expected when the rule keeps the initial answer. On initially incorrect items, the same decision may lose an opportunity for correction. Table 5 is helpful here: plain PROTECT matches strong-solo, while the weighted variant provides gains. A clearer account of the helpful corrections lost would make it easier to judge when protection is preferable to either full debate or strong-solo.
  2. A few reporting differences made the results harder to follow. Figure 2 labels the merged sample as n=434 and gives a GPT-5.2 harmful rate of 9.8%, whereas the caption and Section 4 report n=3,475 and 7.4%. Section 6 also switches between describing agreement and disagreement cases as the ones skipped. These may be editing issues, but the numbers and routing description should be made consistent so that the reported accuracy and compute savings can be interpreted together.
  3. The explanation in terms of peer pressure could be more cautious. Table 3 shows that 93.3% of harmful final answers match an answer proposed by a weak peer. This is consistent with peer influence, but answer overlap alone does not tell us whether the strong model followed the peer or was persuaded by an incorrect argument. I would be more comfortable treating sycophancy as a possible explanation, unless there is further evidence from the exchanges themselves. This would not diminish the value of the observed failure pattern.
Questions for authors

For the items flagged by PROTECT, how many harmful changes are prevented and how many helpful corrections are missed? Could the authors also confirm the intended sample sizes and routing rule? Finally, is the peer-pressure interpretation based on evidence from the debate exchanges beyond the final-answer overlap?

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

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