acceptodds
Under review as a conference paper at ICLR 2027

One Model, Many Minds: Strategy-Diversified Reasoning Is a Cross-Model Ensemble in Disguise

Abstract

The dominant recipe for test-time scaling is to sample more: draw many reasoning chains from one model and aggregate them. Yet chains from the same model under the same prompt share the same failure modes, so their errors are correlated and accuracy saturates well before the compute budget does. Cross-model ensembles break this correlation, since different architectures fail differently, but at the price of running several large models. We ask whether that diversity is genuinely architectural, or merely structural and reproducible within a single model. By forcing one model through deliberately distinct reasoning strategies (algebraic, geometric, backward, inductive, analogical), we decorrelate its errors most of the way toward switching models. Across four diversity sources, the mean pairwise error correlation follows a clean hierarchy: temperature () and prompt rephrasing () keep errors tightly coupled, whereas strategy diversification drops them to , a third of the way to a five-model ensemble (), without lowering per-attempt accuracy, and so attains the highest answer coverage of any source. At matched compute, the resulting single-model ensemble, One Model, Many Minds (OMMM), matches or beats the compute-matched baselines and rivals far costlier methods such as multi-agent debate. The decorrelation also buys calibration: because the strategies fail independently, the rate at which they agree is a free, well-calibrated confidence signal, and answering only when the strategies agree raises accuracy on the answered AIME problems from 37% to 100% (a selective-prediction gain, at reduced coverage). What decorrelates a model's errors is not how many times it answers but how differently it reasons.

Primary area:
foundation or frontier models, including LLMs
Keywords:
test-time scaling, self-consistency, ensemble diversity, error correlation, chain-of-thought, calibration

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_LvWdOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This work proposes One Model, Many Minds(OMMM) where test-time compute is spent on different reasoning strategies instead of repeatedly sampling the same reasoning mode. Basically the idea is ordinary self-consistency produces highly correlated errors while forcing different strategies can reduce this correlation, improve coverage and provide a useful agreement-based confidence signal. Overall I like the main idea of the paper but the paper still needs stronger theoretical justification for connecting error decorrelation to ensemble performance and clearer evidence that the gains translate to final prediction accuracy rather than mainly coverage.

Critical strengths
  1. The main idea is simple and the paper focuses on error correlation and tries to explain why repeated sampling can saturate instead of only reporting accuracy gains. I think this gives the work a clearer and more useful motivation.

  2. The experimental analysis is fairly thorough. The appendix includes useful checks on strategy compliance, alternative strategy sets, model-size effects, cross-model comparisons etc. I actually liked their cross-strategy agreement idea. The paper does not only use diversity to improve accuracy but also shows that agreement between different strategies can give a meaningful signal of confidence.

Critical weaknesses
  1. The way the paper connects pairwise error correlation to coverage (lines 193–204) is not convincing to me. The paper reduces the whole error structure to one number, the average pairwise correlation �0��0� and then uses that to estimate an effective ensemble size. But Coverage@K depends on how all strategies fail together not just on pairwise relationships, right? IMO two ensembles could have the same average accuracy and the same �1��1� but very different patterns of joint failure and therefore different coverage.

  2. OMMM often finds the correct answer with at least one strategy but the vote does not always recover it. For example, on Sonnet AIME-24, Coverage@5 is 96.7% while majority-vote accuracy is only 86.7% and on GPQA it is 47.0% vs 35.9% (Table 2). So the strategies contain substantially more correct solutions than the final vote captures. It seems like the strategies are finding useful additional solutions but somehow the current aggregation step is not able to make full use of them. Also Table 2 does not report Coverage@5. Could the authors clarify where the 96.7% and 47.0% values come from?

  3. D-FUSEr [1] already studies the problem of concentrated errors in test-time aggregation and they also argue that diverse failures can improve majority voting. Even though OMMM uses a different mechanism forcing different reasoning strategies at inference time but the broader motivation is somewhat similar to me. I think the paper should be clearer that the main novelty is the strategy-forcing mechanism rather than the general idea that error diversity matters for aggregation.

  4. �2��2� formula is heuristic rather than theoretically justified for coverage. If I understand correctly the expression �3��3� comes from variance reduction for equicorrelated variables. But the paper then plugs this effective sample size into the independent-coverage formula �4��4�. I dont see a derivation showing that this should hold for binary success/failure events with correlated strategies. Appendix J shows that the approximation fits the experiments well but I think it should be presented as an empirical approximation rather than a general theoretical result.

Inconsistencies:

  1. The main text (296–297) says strategy forcing “decorrelates significantly more than prompt variation” but Appendix D shows this is not true for every reasoner. For Qwen3-235B, difference is not significant �5��5�. The wording should be more qualified.

  2. Table 3 caption says the high-agreement AIME slices are small �6��6� but this does not match all rows. For Sonnet, 60% of 30 AIME problems is about 18 problems and for DeepSeek, 50% is about 15. Also Table 8 caption says that "the ensemble benefit is larger for more capable models" but the GPQA results do not really follow that pattern. OMMM improves over self-consistency by +5.6 points for Qwen3-32B and +2.5 for Qwen3-Next-80B but drops by 3.5 points for Qwen3-235B. The paragraph below the table gives a more nuanced explanation so I think the caption should be revised to avoid suggesting a general trend that is not consistent across benchmarks.

  3. Table 7 text says agreement is better calibrated on every hard-benchmark cell but Sonnet AIME-24 is clearly worse for agreement 0.230 vs 0.113 and DeepSeek AIME-24 is a tie 0.107 vs 0.107.

[1] https://proceedings.mlr.press/v306/baek26a.html

Questions for authors
  1. Authors need to clarify the theoretical motivation behind �0��0�. In particular why should the usual effective-sample-size expression based on pairwise correlation be expected to predict Coverage@K for correlated binary outcomes?

I am not asking the authors to run more experiments, I think the paper already includes a fairly substantial empirical evaluation. My hesitation is mainly on the theoretical side+some inconsistencies i mentioned. Particularly I am not fully convinced by the way the paper connects pairwise error correlation, effective ensemble size, coverage and final majority-vote accuracy. So I am currently leaning slightly negative.

5 comments
AuthorsOpenReview ↗

Gentle reminder: author–reviewer discussion period ending in a few days

Dear Reviewer LvWd,

We wanted to send a brief reminder that the author–reviewer discussion period concludes in a few days.

In our responses, we measured coverage, majority voting and adjudication on the same candidates (with the same adjudication, OMMM improves over self-consistency by 2.6 points [+0.7, +4.7]); presented K_eff as a descriptive summary only; and, in the follow-up, described D-FUSEr in full, explained how OMMM targets a different quantity (which problems each candidate solves, rather than which wrong answers a sampler produces), and replaced the "strictly improves the ensemble" statement in §3.2 with a precise coverage guarantee and the additional condition majority voting requires.

If these updates address your concerns, we would be glad to hear it, and we would be grateful if you would consider reassessing your rating accordingly. If there are any remaining questions or concerns, we would be happy to address them during the remaining discussion period.

Thank you again for the time and effort you put into reviewing our work.

Best regards,

Authors

I went through the revised paper and rebuttal. Paper seems much better now but I still have a few reservations, so I am not really able to increase my rating.

Again on novelty I understand the distinction pretty much now. But the AM-GM argument still feels quite general and not specific to reasoning strategies. So while I do see novelty in the strategy forcing mechanism itself.. I think the broader conceptual or theoretical framing is overstated. But tbh I am not opposed to acceptance on this point alone.

My remaining reservation is more about what is left after your correlation clarification. For K>2K>2 pairwise correlation is mainly an empirical diagnostic rather than a theoretical guarantee for coverage or majority vote acc. And since plain OMMM is mostly comparable to self-consistency while the clearer gain appears with adjudication, I see the practical contribution more as producing a better candidate pool for a stronger aggregator to exploit. Its useful but it is a narrower story than your original decorrelation/ensemble framing.

One other thing I am still unsure about is that a lot of the new evidence is now at the 30K tok cap while the main experiments were at 4096 tok. The correlation ordering also changes for some models at the larger cap. So I am not fully sure how robust the main story is to the reasoning budget or how much of the new result depends on this much larger inference regime.

Again I really appreciate the authors effort and dedication in addressing the comments. I hope my rating does not discourage you in any way. I still have the concerns mentioned above but if the other reviewers are convinced and support acceptance, I have no objection from my side. Wishing you all the best with the submission.

We thank the reviewer for reading the revision carefully and for the encouraging and constructive feedback. We agree that the paper should make a narrower claim than our original ensemble framing, and the revision does so; we address the three remaining points below.

Generality of the coverage bound. We agree with the reviewer that the AM–GM bound is general, and we do not view the bound itself as OMMM's conceptual novelty. It is a general condition, not an explanation of why reasoning strategies produce complementary candidates: for a given problem, candidates with different success probabilities reach higher coverage than i.i.d. candidates with the same mean success probability. Whether a particular diversity source produces such profiles is an empirical question, and our contribution is to study reasoning strategies as a controllable source of this diversity within one model. The answer depends on the model and the source. At the 30K cap, strategy forcing lowers Sonnet's mean pairwise error correlation from 0.62 (temperature sweep) to 0.51, against 0.46 for the five-model reference, and gives the highest Coverage@5 among Sonnet's single-model sources (95.9%, vs. 94.6% for the temperature sweep), whereas prompt rephrasing, another way to condition generations differently, raises the correlation to 0.68. The bound therefore gives a general perspective on coverage, while our experiments test whether strategy forcing produces complementary candidates; §3.2 presents the bound in this role, and the revised appendix makes explicit that the effect of a diversity source must be established empirically.

What remains after the correlation clarification. We agree with the reviewer that, for K > 2, pairwise correlation is an empirical diagnostic rather than a guarantee of coverage or majority-vote accuracy, and we have narrowed the practical claim to the one the reviewer describes: the revised conclusion presents OMMM as a way to build a complementary candidate pool from one model, and our experiments show that two different aggregators can exploit this pool to improve accuracy. With the same adjudication applied to both methods, OMMM's candidates gain 3.1–6.2 points from adjudication, against 0–2.1 for self-consistency at comparable coverage, a pooled advantage of +2.6 points (95% CI [+0.7, +4.7]) on 290 competition-math problems over three models, at 1.03–1.28× the tokens. The benefit is not limited to adjudication. A second training-free aggregator, cross-model agreement selection, uses three jurors from model families that never generate in OMMM (Kimi-K2.5, gpt-oss-120b and GLM-5.3-Flash, one answer each) and returns the pool answer most jurors agree with, breaking ties by pool frequency and falling back to the most frequent pool answer when no juror's answer is in the pool. Applied identically to both pools at the original 4,096-token cap, it gives OMMM +4.9 points (95% CI [+2.7, +7.0]) over self-consistency on AIME-24, AIME-25 and OlympiadBench.

Robustness to the reasoning budget. We agree with the reviewer that the 30K results should not be treated as interchangeable with the original 4,096-token experiments. The two settings differ mainly in how often generations reach the cap: on the same 290 competition-math problems, the total (input plus output) token count reaches the 4,096-token cap for 11% (Sonnet), 30% (DeepSeek) and 62% (Qwen) of strategy generations, against at most 1.2% at 30K; these are upper bounds on output-cap hits rather than confirmed truncations. The revised paper reports the two settings separately and labels each result with its cap. OMMM helps in both regimes, through different measurements. At 4K, its Coverage@5 exceeds self-consistency's by +7.0 points (95% CI [+4.7, +9.2]) pooled over the three models (+16.2 for Qwen), and the cross-model aggregator turns this into the +4.9-point accuracy gain above; at 30K, where both pools reach about 88% coverage, the gain appears through adjudication (+2.6). The correlation result depends on the model and the budget, and we report it that way: strategy forcing has the lowest mean pairwise error correlation (point estimate) among single-model sources for all four reasoners at 4K and for Sonnet and Qwen at 30K, six of the seven model–budget combinations, but not for DeepSeek at 30K; the five-model reference stays lower throughout, except for Kimi-K2-Thinking at 4K, where the two are statistically indistinguishable. The revised §5.1 states this ordering per model and cap rather than as a general claim.

We appreciate the reviewer's point that these results support a more focused contribution than our original framing. The revision presents OMMM as a strategy-conditioned method for generating candidates, evaluates their coverage and error dependence across budgets, and measures how stronger aggregators exploit the pool. We are grateful for the reviewer's engagement throughout the discussion.

Reviewer_1orDOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates how different sources of diversity affect error correlation in LLM reasoning and proposes OMMM. The method uses strictly constrained prompts to guide the same model to reason using different strategies, then aggregates the answers through majority voting, yielding some improvements in task accuracy.

Critical strengths
  1. The paper raises an interesting question: does the diversity obtained through cross-model reasoning arise from differences between heterogeneous architectures, or can it be reproduced by guiding a single model to reason differently?
  2. The method is simple and intuitive, and the overall pipeline is presented relatively clearly. In addition to reporting accuracy, the experiments examine metrics such as error correlation, ensemble accuracy, and Coverage@5, which help analyze the method from different perspectives.
Critical weaknesses
  1. The proposed method offers insufficient novelty and incremental contributions. The paper does not adequately explain what substantive changes the explicit MUST/MUST NOT constraints introduce to the reasoning strategies compared with existing methods such as Self-Contrast. The current description primarily emphasizes prompt constraints.
  2. Some experimental results are inconsistent with the mechanistic explanation. Table 9 shows that although strong constraints reduce Agreement, their Coverage@5 is lower than under the no-constraint condition. This contradicts the paper’s statement that strong constraints maintain or improve coverage and indicates that more diverse answers do not necessarily yield more correct answers. Furthermore, the experiments have not resolved whether reasoning diversity arises from model architectures or the structure of the reasoning process, nor have they established that single-model strategy diversity is equivalent to cross-model diversity.
Questions for authors
  1. Compared to existing methods such as Self-Contrast, what substantive improvements and contributions does this approach based on strict prompt constraints offer?
1 comment
AuthorsOpenReview ↗

Gentle reminder: author–reviewer discussion period ending in a few days

Dear Reviewer 1orD,

We wanted to send a brief reminder that the author–reviewer discussion period concludes in a few days.

In our response, we clarified what OMMM adds over Self-Contrast and DIV-SE (a fixed strategy set with explicit constraints in independent generations, and a study of the resulting error dependence, coverage and aggregation); compared with Self-Contrast at a 30K cap with measured tokens; revised the Table 9 text on constraint strength and coverage; and stated the model dependence of the single- vs. cross-model comparison explicitly. Under the same adjudication step, OMMM also improves over self-consistency by 2.6 points [+0.7, +4.7].

If these updates address your concerns, we would be glad to hear it, and we would be grateful if you would consider reassessing your rating accordingly. If there are any remaining questions or concerns, we would be happy to address them during the remaining discussion period.

Thank you again for the time and effort you put into reviewing our work.

Best regards,

Authors

Reviewer_BT56OpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

The paper asks whether the error decorrelation you get from cross-model ensembles really comes from using different models, or from making the model compute differently. OMMM prompts one model with 5 forced strategies (algebraic, geometric, backward, inductive, analogical for math), majority-votes the answers, and uses agreement between strategies as a confidence score. The main result is a correlation ordering at K = 5 on Sonnet 4.6: temperature 0.69, prompt rephrasing 0.71, strategies 0.60, five different models 0.43. The paper also compares accuracy against SC, prompt diversity, Self-Contrast, self-correction and debate on MATH-500, AIME, GPQA, HumanEval and ARC, and uses agreement for selective prediction and for routing hard problems to debate.

Critical strengths
  1. The question is a good one: is the benefit of cross-model ensembles about the models, or about computing differently? Comparing diversity sources at a fixed budget of 5 generations is a simple, clean setup, and the method is easy to use (training-free, prompts in the appendix).

  2. The appendices are honest about non-significant and negative results (Table 5, App. I), which made the paper easy to check.

Critical weaknesses
  1. The claims are much stronger than the results.

The title says strategy forcing is a cross-model ensemble in disguise, but it only moves ρ from 0.69 to 0.60, against 0.43 for five models (Sonnet). That is about a third of the way, as the abstract itself says, while the TL;DR says "most of the way". In Table 5 the gap to temperature is significant for only 1 of 4 models, and strategy forcing is still significantly above cross-model for 3 of 4.

The accuracy results are similar. In Table 6, OMMM beats the best compute-matched baseline (SC-5, DiVeRSe, Self-Contrast) in 3 of 18 cells and loses in 11, including 4 of the 6 AIME cells. For DeepSeek it is the worst compute-matched method on both AIME sets. The claim that debate costs 5–10x the tokens also doesn't match Sec. 5.4: escalating 10% of problems costs 56% of debate, which means debate costs only about 2x OMMM.

  1. DIV-SE already runs one call per reasoning approach (including "working backwards") and majority-votes. That is not just surface variation, as the paper describes it, and it should be a baseline.

  2. I'm not convinced the main measurement is about reasoning strategy.

Every generation is capped at 4096 tokens, and the paper doesn't say whether thinking is on. Qwen3-235B gets 33.3 on AIME-24 with SC-5 here, vs 85.7 in the Qwen3 report (thinking mode), but 83.3 with debate. That looks like truncation, with multi-round methods winning because they get more total tokens.

  1. The paper reads more like the output of an automated research pipeline than a focused study. The writing follows one template throughout. Most sections end in a confident one-line takeaway. The setup has the same feel. Instead of a few well-powered experiments on the core question, there is a wide sweep of models, benchmarks and baselines, plus about a dozen appendices of small ablations, mostly on a single model and often on the 30-problem AIME splits.
Questions for authors
  1. Was thinking on for each model, and how often did generations hit the 4096 cap in each condition? Does the ρ ordering hold with each model's normal budget?
  2. What is ρ with i.i.d. samples at T = 0.7 and T = 1.0? And how often do wrong answers collide, P(ai=aj∣both wrong)P(a_i = a_j \mid \text{both wrong}), for each source? That is what actually matters for voting.
3 comments
AuthorsOpenReview ↗

Gentle reminder: author–reviewer discussion period ending in a few days

Dear Reviewer BT56,

We wanted to send a brief reminder that the author–reviewer discussion period concludes in a few days.

In our response, we repeated the primary comparisons with a 30K-token cap and without thinking mode, with measured token usage; added i.i.d. sampling at T = 0.7 and 1.0, Coverage@5 and wrong-answer collision counts; added DIV-SE as a baseline and replaced the debate-cost estimate with measured tokens (2.1–2.2× OMMM); and showed that with the same adjudication step applied to both, OMMM improves over self-consistency by 2.6 points [+0.7, +4.7] on 290 competition-math problems. The revised introduction also states the title's phrase as the hypothesis we test.

If these updates address your concerns, we would be glad to hear it, and we would be grateful if you would consider reassessing your rating accordingly. If there are any remaining questions or concerns, we would be happy to address them during the remaining discussion period.

Thank you again for the time and effort you put into reviewing our work.

Best regards,

Authors

Thanks for the detailed response and the new experiments. They partially address my concerns, and I’ll raise my score for the effort. Two things still bother me. First, the 30K reruns weaken the main claim. The ordering only holds in point estimates for Sonnet and Qwen. It flips for DeepSeek, and majority-vote OMMM ends up about even with SC-5. Yet the main text still present mainly with the 4,096-token results, which were often truncated. Second, some overclaims are still in the revision, like “the ordering holds for all four reasoners” in Sec. 5.1.

AuthorsOpenReview ↗

Response to Reviewer BT56 (follow-up)

We sincerely thank the reviewer for reading the new experiments carefully and for raising the score. We address the two remaining points below and have revised the paper accordingly.

Presenting the 30K results in the main text. We agree with the reviewer that the 30K results should carry equal weight in the main text, given how often generations reach the 4,096-token cap (for Sonnet, DeepSeek and Qwen, the total input-plus-output token count reaches the cap for 11%, 30% and 62% of strategy generations at 4K, against 1.2%, 0.1% and 1.0% at 30K; these are upper bounds on output truncation). The revised Table 1 now reports both caps side by side. Its new 30K block gives the temperature sweep, prompt rephrasing and strategy forcing for Sonnet, Qwen3-235B and DeepSeek-V3.2. The abstract now gives the 30K values next to the 4K ones, and §5.1 states the ordering separately for each cap and model. At 30K, strategy forcing has the lowest single-model point estimate for Sonnet (0.51, against 0.62 for the temperature sweep and 0.46 for the five-model reference) and for Qwen3-235B (0.57 against 0.61–0.66 for the other single-model sources), but not for DeepSeek-V3.2 (0.61 against 0.56–0.58). We present these as point estimates, since the intervals overlap. For Sonnet, the 30K result is stronger than the 4K one: strategy forcing closes about two thirds of the gap between the temperature sweep and the five-model reference, against about a third at 4K. The revised paper therefore describes strategy forcing as a model-dependent source of within-model error diversity, not as a general substitute for cross-model diversity, and the introduction states that the results support the title's hypothesis only in part.

Accuracy at 30K. We agree with the reviewer that plain majority-vote OMMM is broadly comparable to SC-5 at 30K, and the revised §5.2 states this. The reason is measurable: wrong-answer collisions remain frequent for every single-model source (Appendix I), so counting votes cannot fully use the additional diversity. The accuracy benefit therefore appears when the aggregator evaluates the candidates rather than counting their answers. With the same adjudication step applied to both methods, OMMM's candidates gain 3.1–6.2 points from adjudication, against 0–2.1 for SC-5 at comparable coverage. This is a pooled advantage of +2.6 points (95% CI [+0.7, +4.7]) on 290 competition-math problems over three models, at 1.03–1.28× the tokens of SC-5. The revised paper presents OMMM's practical value in these terms: it builds a complementary candidate pool from one model, which aggregators that use more than the vote count convert into accuracy.

Remaining overclaims. We agree with the reviewer and have revised every statement of this kind that we found. In Table 1's caption, §5.1 and Appendix D, the ordering among single-model sources is now stated per cap and model: "the ordering holds for all four reasoners" now reads "in the point estimates, for all four reasoners at the 4,096-token cap, and for Sonnet and Qwen3-235B but not DeepSeek-V3.2 at the 30K cap." We removed "only forcing a new strategy changes how the model fails" and "most tellingly." The §5.2 heading "Decorrelation Buys Ensemble Accuracy at Matched Compute" is now "Ensemble Accuracy at Matched Compute." The reproducibility statement now says that the correlation and accuracy experiments include open-weight reasoners, rather than that the results "replicate" on them.

We thank the reviewer again for the careful and constructive feedback throughout the discussion, which has made the paper's claims considerably more precise.

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

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