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Under review as a conference paper at ICLR 2027

On Compositional Learning Behaviours in Formal Mathematics

Abstract

Language model-based AI agents capable of conquering the Olympiad-level tail of formal mathematics require Compositional Learning Behaviours (CLBs): the capacity to ground and recombine novel symbolic structures in context, beyond mere recombination of prelearned atoms. We propose **S2B-LM**, an adaptation of the CLB-evaluating Symbolic Behaviour Benchmark that removes numerical processing as a confound and adds chain-of-thought scaffolding to elicit rather than merely probe latent CLB competency. Cross-evaluating ten Lean 4 theorem provers on CLB competency in S2B-LM and miniF2F whole-proof performance, we find correlational and causal evidence of our claim: First, a necessary-condition analysis via quadrant test yields , with model scale being ruled out as a confound. Second, extracting a CLB-encoding activation direction from *DeepSeek-Prover-V2-7B* using S2B-LM traces via Contrastive Activation Addition and applying it during miniF2F whole-proof generation on the AIME subset, CLB suppression collapses solve rate from % to %, without loss of coherence, while suppressing a random activation direction of equal magnitude leaves it at %. Together, these results show that CLB competency is **necessary but not sufficient** for the hard tail of formal mathematical verification.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Compositional Learning Behaviours, Compositional Behaviours, Formal Theorem Proving, Lean 4, miniF2F, Symbolic Behaviour, Language Models, In-Context Learning, Chain-of-Thought Reasoning, Compositional Generalisation, Exact Permutation Testing, Self-Evolving Agents, Competence–Performance Distinction, Mathematical Reasoning

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_q4zSOpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
1
Soundness
2
Read review
Paper summary

The paper discussed CLB is a necessary but a bottleneck to solve Lean 4 questions. Therefore, based on CLB, they propose S2B-LM, removing numerical processing and adding chain-of-thought scaffolding. This is used for adj-ZSCT scoring. Then via experiments on minif2f, it gives a claim that CLB is a necessary but insufficient condition for formalizing difficult mathematics, and there is causal evidence for this.

Critical strengths
  1. the method is interesting that the paper clearly states the motivation of the two changes based on CLB, and the two changes are clearly targeting the motivation.
  2. experiments are a lot
  3. the findings are interesting and method provides insights
Critical weaknesses
  1. High score model such as Goedel-V2、DeepSeek-V2、Kimina have been trained via CoT while S2B-LM is prompted via CoT. I am concerned that adj-ZSCT is measuring the effectiveness of CoT or the ability that the model could use CoT. - maybe just try another model is not trained extensively via CoT?
  2. Actually the 10 models the paper assessed are from 3 families. Between the models stemming from the same family, I am not sure why the permutation test is valid.
  3. 600B+ model is MoE model - so I am concerned that the claim of model size is ruled out as a confound
  4. casual and effects tests are too narrowed: you only have 15 AIME tests, which reduced the persuasiveness of the experiments
  5. I suppose another experiments are worth investigating: for the lower difficulty level questions, whether the score still holds. I understand this is not the core investigation of the paper - as you are investigating the high-difficulty questions, but it will give us a confirmation whether the decrease from 32.3% to 2.9% is really due to CLB suppresion.
  6. p=0.004 is from the overall mark, but try to only use 80 difficulty questions and see whether the results changed?
  7. The language is too complicated so I mark the presentation is difficult to follow. There are even sentences longer than 5 row. And there are places such as [y] in line 48.

I am happy to reconsider the overall evaluation if the author addressed my concerns.

Questions for authors

see above

16 comments
AuthorsOpenReview ↗

Rebuttal (1/4)

We thank reviewer q4zS for a detailed review, and for noting that (S1) the two changes of S2B-LM are clearly motivated by CLBs and clearly target that motivation, (S2) the experiments are extensive, and (S3) the findings are interesting and the method provides insights. We also thank the reviewer for offering to reconsider their evaluation, and we address the weaknesses in order of their bearing on the paper's claims.

We start with the two points on the scope of the causal experiment, W4 (the narrow AIME set) and W5 (the lower-difficulty problems), which we answer with new experiments. We then turn to the three points on the correlational test: for W2 (model families), we clarify the unit of analysis; for W3 (the MoE model), we correct our scale claim; and for W6 (the 80 hard problems), we explain our threshold and state a limitation. We then address W1 (the chain-of-thought confound), and finally W7 (the readability of the paper).

W4: "casual and effects tests are too narrowed: you only have 15 AIME tests, which reduced the persuasiveness of the experiments"

This concern is shared with reviewer P3sz (Q1), and we address the underlying concerns with the same changes to the paper in Section 4.2.

We understand that the reviewer raises threats to the external validity (narrow sample) and statistical validity (power) of the causal intervention experiment of the paper (Section 4.2). We raise both validities in two ways:

  1. in comparison to only using the AIME subset, we extend to using both AIME and AMC 12 (+39 problems) subsets, which together cover about two thirds of the Olympiad-level problems of miniF2F;
  2. in comparison to checking that standard-error ranges do not overlap, we now apply a one-sided sign test over problems, which counts the problems where a control arm solves more often than the CLB suppression arm.

We test on the problems where the unsteered model (α=0\alpha=0) solves at least once, because a problem the model never solves cannot show a drop under suppression. This rule is applied to the unsteered run alone, before any steered arm is generated, so the selection cannot favour our hypothesis. As a result, it keeps 10 of the 15 AIME problems (32 samples each) and 15 of the 39 AMC problems (8 samples each), giving a total of 25 informative problems. We also add an orthogonal control: a random direction orthogonal to the CLB direction, with the same norm.

Pooled over the 25 informative problems, CLB suppression lowers the solve rate from 0.629 to 0.107, while the random and orthogonal controls leave it at 0.595 and 0.586. Per problem, CLB suppression solves less often than random on 21 of 25 problems and more often on none (one-sided sign test, p = 4.8e-7), and less often than orthogonal on 20 and more often on none (p = 9.5e-7). The conclusion therefore does not depend on the 15 AIME problems alone. In the revised paper, Figure 6 now shows the per-problem and pooled solve rates on the 25 informative problems, and Figure 7 shows the pooled output coherence. The sign-test results are reported in the main text at lines 456–459. The full tables are in our answer to reviewer P3sz (Q1).

In light of this addition that extends both the external and statistical validity of the paper, we hope that you can update your appreciation of the paper and possibly update your scores, or point out how we could improve the paper further.

AuthorsOpenReview ↗

Rebuttal (2/4)

W5: "for the lower difficulty level questions, whether the score still holds [...] confirmation whether the decrease from 32.3% to 2.9% is really due to CLB suppresion."

We thank the reviewer for this suggestion, which we understand as a check of the construct validity of the causal result (is the drop due to CLB suppression, or to generic damage?). We ran the same experiment on 24 lower-difficulty number-theory problems from the MATH subset of miniF2F (19 problems turned out informative), with 8 samples per problem. The drop holds and is direction-specific: CLB suppression lowers the solve rate from 80.3%80.3\% to 3.9%3.9\%, while the random direction leaves it at 77.6%77.6\%, which confirms that the decrease is due to CLB suppression.

The drop is, however, not larger on harder problems: the relative drop (the fall in solve rate as a fraction of the unsteered rate) is 0.793 on AMC and 0.951 on MATH-NT, so our pre-registered one-sided contrast (larger drop on harder problems) is not supported (difference −0.158, p = 0.993). This is not a ceiling effect, since no difficulty gradient appears at any dose, including α=−1.5\alpha = -1.5, where neither set saturates (relative drops of 0.405 on AMC and 0.387 on MATH-NT). It is also consistent with necessary but not sufficient: suppressing a necessary competency hurts at every difficulty level, while what sets hard problems apart lies in the competencies beyond CLB. If anything, this result extends our causal claim: the CLB direction is needed for formal proving at both difficulty levels we tested, not only at the Olympiad level.

In light of this result, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

W2: "Actually the 10 models the paper assessed are from 3 families. Between the models stemming from the same family, I am not sure why the permutation test is valid."

We understand this point as a threat to the statistical validity of the permutation test, which assumes that the units it permutes are exchangeable. We agree that the paper should have stated its unit of analysis explicitly: it is the training recipe, not the base weights. Indeed, each model stands for the recipe (data and training procedure) that turned a base model into a formal theorem prover, and the question we test is whether any recipe that reaches the Olympiad tier of miniF2F does so without CLB competency. Under this reading, models sharing a base are not repeated measurements of one unit but distinct treatments applied to a common starting point.

In more detail, Table 2 shows that the base weights do not determine CLB competency, while the recipes do: five recipes applied to the same base, DeepSeek-Prover-V1.5-Base, yield adj-ZSCT of 10.6 (Goedel-Prover-DPO), 12.0 (DeepSeek-Prover-V1.5-SFT), 13.8 (DeepSeek-Prover-V1.5-RL), 16.3 (Goedel-Prover-SFT) and 79.6 (DeepSeek-Prover-V2-7B). A shared base would induce dependence between the scores of models sharing it, but this spread shows that such dependence is weak compared with the effect of the recipes.

We have revised the paper accordingly, with all changes highlighted in blue: Section 4.1 now states the training recipe as the unit of analysis; Appendix D states it where the exchangeability assumption of the permutation tests is introduced, with the evidence above; and the introduction and discussion now phrase the main finding per training recipe ("no training recipe reaches the Olympiad-level tier without measurable CLB competency"). In light of this clarification, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

AuthorsOpenReview ↗

Rebuttal (3/4)

W3: "600B+ model is MoE model - so I am concerned that the claim of model size is ruled out as a confound"

We thank the reviewer for this point, which concerns the internal validity of our scale argument, and which is correct. Counting DeepSeek-Prover-V2-671B by its active parameters (about 37B) instead of its total, scale correlates significantly with miniF2F (exact permutation test: r = 0.61, p = 0.018; r = 0.70, p = 0.010 on a log scale), whereas the paper reported r = 0.36, p = 0.18 with total parameters. The statement that scale is "ruled out" as a confound is therefore too strong, and we have removed it.

Our claim, however, is one of necessity, and necessity separates the two variables. No training recipe reaches the Olympiad tier without CLB competency (the forbidden cell of our quadrant test remains empty, p = 0.004), and this still holds without the MoE model (N = 9, p = 0.0079). By contrast, training recipes do reach the Olympiad tier without scale: DeepSeek-Prover-V2-7B (75.6%) and Goedel-Prover-V2-8B (84.6%) are among the smallest models of the pool. Scale therefore correlates with miniF2F performance but is not necessary for it, while CLB competency is; the revised paper states it this way and reports the scale tests with both total and active parameters.

In light of this correction, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

W6: "p=0.004 is from the overall mark, but try to only use 80 difficulty questions and see whether the results changed?"

We understand this point as a threat to the construct validity of our outcome measure: the claim concerns reaching the Olympiad tier, but the quadrant test uses the overall miniF2F Pass@32 over all 244 test problems, which also reflects the 164 easier ones. The reviewer is right that the test uses the overall score. Our tail-partition test (Appendix D), which also gives p=0.004p = 0.004, splits models at 67.2% by design: this is the share of non-Olympiad problems in the test split (164 of 244), so a model can only score above it by solving Olympiad-level problems (AMC, AIME and IMO). In our pool, the median split of the quadrant test (67.95%) happens to give the same partition, and the models above it score between 75.6% and 88.1%.

Pass@32 restricted to the 80 Olympiad problems is, however, not available for all ten models, since published results report the overall score and we would need each model's per-problem outputs. We therefore cannot run the quadrant test on that subset now, and we report it as a limitation.

In light of this clarification, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

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

This work proposes S2B-LM, which is an adaptation of the CLE-evaluating Symbolic Behaviour Benchmark that removes the numerical processing as a confound and adds chain-of-thought scaffolding to elicit rather than merely probe latent CLB competency. This work also claim that the CLB is necessary but not sufficient for hard formal mathematical verification.

Critical strengths
  1. This work use experiment to support that CLB competency is necessary but not sufficient for the hard tail of formal mathematical verification.
  2. This work propose S2B-LM, an adaptation of the CLB-evaluating Symbolic Behaviour Benchmark that removes numerical processing as a confound and adds chain-of-thought scaffolding to elicit rather than merely probe latent CLB competency.
  3. This work use different datasets, such as miniF2F and AIME.
  4. This work add sufficient appendix to explain this work, and also the code
Critical weaknesses
  1. The work use experiment to support "CLB competency is necessary but not sufficient", which it seems that the theorical analysis is missing.
  2. This work mainly use DeepSeek model, so that it is not sure whether the conclusion is still the same for other models.
  3. Whether the S2B-LM has the human validaton to check the dataset?
Questions for authors

NA

5 comments
AuthorsOpenReview ↗

Rebuttal (1/n)

We thank reviewer XASj for the review, and for noting that (S1) the experiments support that CLB competency is necessary but not sufficient for the hard tail of formal mathematics, (S2) S2B-LM removes numerical processing as a confound and adds CoT scaffolding to elicit latent CLB competency, and (S3) the appendix and code are sufficient to explain the work.

The review highlights three weaknesses that concern different parts of the paper, and we answer them in order of their bearing on the paper's claims. We first address W2 (other models), which raises an external validity concern, with a new experiment: the causal intervention replicates on Goedel-Prover-V2-8B, a second model with a different base and training recipe than DeepSeek-Prover-V2-7B (one-sided sign test, p = 0.002). Then, for W3 (human validation), which raises a construct validity concern, we separate the validation that S2B-LM requires (that its labels are correct and recoverable from the information given to the tested agents) from the one it does not (human solvability), and add a reference solver entry to Table 2 that addresses the former. Finally, for W1 (missing theory), we explain why our main claim is empirical by design, and add, as a complement, a formal account of what adj-ZSCT measures.

W2: "This work mainly use DeepSeek model, so that it is not sure whether the conclusion is still the same for other models."

We understand this point as a threat to the external validity of the causal intervention experiment. We agree in part: the correlational analysis already covers ten models from three families (Table 2), but the causal intervention in the paper is on DeepSeek-Prover-V2-7B only.

We have therefore replicated the causal intervention on Goedel-Prover-V2-8B, a model built on a different base (Qwen3) and with different training recipes than DeepSeek-Prover-V2-7B, in order to increase the external validity of the causal intervention experiment.

Matching the perturbation size. The steering strength α\alpha multiplies the CAA direction vector, so the same α\alpha yields a different perturbation in different models. We therefore matched the ratio of the steering norm to the residual-stream norm: DeepSeek-Prover-V2-7B's α=−3\alpha = -3 corresponds to α=−4.77\alpha = -4.77 on Goedel-Prover-V2-8B. These norms were measured from the steering vectors before any Goedel-Prover-V2-8B experiment, and the matching matters: at the unmatched values α=−3\alpha = -3 and −4-4, the perturbation is too small to meaningfully separate the CLB and random directions on S2B-LM (ZSCT 68.3% against 68.7%, and 71.4% against 78.4%).

On S2B-LM. At this matched strength (α=−4.77\alpha = -4.77), suppressing the CLB direction lowers ZSCT to 53.3%, against 94.8% for a random direction of the same norm (vs unsteered: 75.2%; 3 seeds per steered arm, 8 for unsteered). The effect is therefore found to be direction-specific on a second model. It remains to verify whether the effect transfers from S2B-LM to miniF2F proof generation, which we test below.

On miniF2F (AIME). Goedel-Prover-V2-8B is trained to reason in CoT before writing Lean proof, and without CoT it solves only 8.8% of the AIME samples, so we used its CoT mode to replicate the causal intervention experiment. The CoT mode gave a valid prefix for 14 of the 15 AIME problems (valid meaning that the unsteered completion contains a Lean 4 code block; the prefix stops at its opening, so it contains the reasoning and proof plan but not the proof). However, switching to CoT mode raises the confound that miniF2F performance suppression might be caused by damage to the CoT reasoning prior to the Lean 4 proof generation. Thus, to exclude this confound, we collected each unsteered CoT reasoning prior to Lean proof generation, and generated the Lean proof from the steered LMs conditioned on that identical prefix, thus containing both problem statement and unsteered CoT reasoning. We condition with that same prefix both steered LMs, in the CLB suppression arm and the random direction arm.

On the 14 AIME problems with valid prefixes (up to k=4k = 4 samples each), the mean per-problem solve rate falls from 23.2% (unsteered) to 5.4% under CLB suppression, while the random direction leaves it at 33.9%. Critically, the CLB suppression arm solves less often than the random arm on 9 problems and more often on none (one-sided sign test, p = 0.002). The drop in performance is therefore direction-specific, and it occurs even when the CoT that precedes the Lean 4 proof is held fixed.

AuthorsOpenReview ↗

Rebuttal (2/n)

This replication has one limitation: with k=4k = 4 samples per problem on AIME, and 3 seeds per steered arm on S2B-LM, the estimates are coarse. This may also explain why the random arm comes out above the unsteered one in both settings; on AIME, the difference is not significant (random solves at least once 8 of the 10 problems with complete samples, against 6 for unsteered).

We have not extended the replication to AMC yet due to high computational complexity of Goedel-Prover-V2-8B in CoT mode on our hardware (8192 tokens max cap, versus 1024 in the non-CoT mode of DeepSeek-Prover-V2-7B). We will extend it to AMC for the camera-ready version.

In the revised paper, we add this replication as Appendix G (with Table 3), and point to it from the end of Section 4.2; all changes are red-lined in blue. In light of this replication, which is significant even at k=4k = 4 samples per problem (p = 0.002) and extends the causal claim of the paper to a second model, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

W3: "Whether the S2B-LM has the human validaton to check the dataset?"

We understand this point as a threat to the construct validity of the benchmark, asking about the following: are the benchmark labels correct, and is the task well posed? However, the term "human validation" can mean two things, which carry different weight here, so we answer each separately below:

  1. Label validation (are the correct answers recoverable from the stimuli and consistent?). S2B-LM is generated procedurally, so every label follows from the generating rules rather than from annotation. To check that the labels are recoverable, we ran a rule-based reference listener that tracks hypotheses about token meanings, based solely on the same information that the tested LMs are provided. It reaches 100% ZSCT under vocabulary permutation over 8 seeds (same setting as in other entries in Table 2). The labels are therefore valid and recoverable from the episode alone.

  2. Human solvability (can human beings do the task?). S2B-LM is a synthetic diagnostic of a model-side competency, so human performance is not the criterion of its validity, as for other synthetic diagnostics such as needle-in-a-haystack tests, for instance the RULER benchmark (Hsieh et al., COLM 2024).

Could the reviewer clarify which meaning they have in mind?

In light of this clarification, we hope that you can update your appreciation of the paper and possibly your score, or point out how we could improve it further.

AuthorsOpenReview ↗

Rebuttal (3/n)

W1: "[...] the theorical analysis is missing."

This concern is related to reviewer q4zS (W1, whether adj-ZSCT measures the effectiveness of chain-of-thought), and the formal account below, which we promised in our answer to that reviewer, addresses both.

We understand this point as a question about the construct validity of the paper: does adj-ZSCT measure CLB competency, and is the necessity claim supported without a theory? We first explain why our main claim is empirical by design, and then add, as a complement, a formal account of what adj-ZSCT measures.

CLB competency is necessary but not sufficient is a falsifiable claim about trained models and their training recipes, not about an idealised/formal learner. Thus, proving it theoretically would require a formal model of what a given pre-training corpus and training recipe produce, which no existing theory provides for LMs. The appropriate tests are therefore empirical: a necessary-condition test (quadrant test, p = 0.004) and a causal intervention with relevant controls, which we have now replicated on a second model (see our W2 answer in the previous message) and extended to the AMC 12 subset of miniF2F (cf. our answer to reviewer q4zS's W4). The reviewer's own first strength notes that the experiments proposed in the paper do already support the claim.

Nonetheless, the reviewer's question prompted us to make precise what these experiments measure, which we recognise to be address-able by theory. To do so, we derive below that above-chance accuracy requires the tested model to use information about the episode's encoding that only the episode provides, that it cannot come from looking up whole stimuli seen earlier in the episode, and that adj-ZSCT increases with a lower bound on the information that the model's answers carry.

Intuition. In one S2B-LM episode, the speaker may encode piano as symbol 8 and swimming as symbol 5 (Appendix C); in the next episode, the vocabulary is permuted again, so symbol 8 may encode golf. A tested model as listener player therefore cannot know what the speaker's message [8, 5, 6] denotes from its training data: it can only infer it from the games played earlier in the same episode. If, moreover, the episode never showed the stimulus [piano, swimming, eggplant] as a whole, the model must also recombine the meanings it inferred for each separate symbol.

Setup. We need three definitions: what an episode is, what the paper's score measures on it, and what competency the score is meant to reveal.

Definition 1 (episode and game). Following the Meta-Referential Games framework, an S2B-LM episode ee is a sequence of referential games drawn from a distribution D\mathcal{D} over meta-referential games. At the start of ee, the episode's encoding σe\sigma_e fixes which symbol encodes which attribute value in this episode. Intuitively, σe\sigma_e is a fresh permutation of the symbols over the attribute values, but formally we define it as a bijection from the attribute values used in episode ee to symbols.

Each referential game gg has a speaker stimulus sS(g)s^S(g), the speaker's message mg=σe(sS(g))m_g = \sigma_e(s^S(g)), and a listener stimulus sL(g)s^L(g); the listener sees (mg,sL(g))(m_g, s^L(g)), and the correct answer is Yg=1[sL(g)≠sS(g)]Y_g = \mathbb{1}[s^L(g) \neq s^S(g)] (0 for same, 1 for different). A stimulus is a tuple of attribute values, one per position, each position drawing from a different category, so the values of a stimulus are distinct; σe\sigma_e is applied to it position by position.

The episode has a supporting phase, then a querying phase whose games form the set QeQ_e. For a querying-phase referential game g∈Qeg \in Q_e, He,gH_{e,g} is the history of all games of ee before gg, with their feedback: after each game, the speaker's stimulus is revealed, so the history pairs earlier messages with the stimuli they encode.

Reviewer_P3szOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper proposes S2B-LM which extends previous work S2B on 2022 to evaluate LLM's ability of CLB. The major difference between this work and S2B is removing numerical components and adjusting the evaluation approach. The authors evaluate different models from Deepseek-Prover-V1 to Kimina-Prover. This paper is not well-written. Important concept is not well explained.

Critical strengths

None.

Critical weaknesses
  1. Not self-contained. This paper is an incremental work of S2B. However, according to the reference, the S2B paper is only published on arxiv. Therefore, related concepts and designs should be carefully explained.

  2. Not well-written. This paper use hard-to-read English and usually a concept is used or introduced without sufficient explanation.

  3. Result not significant. The authors claims that they find CLB competency is necessary but not sufficient for good formal math performance. This is not surprising at all. It is obvious (at least to me) that generating good formal math proofs needs model competency of a lot of dimensions.

Questions for authors
  1. Why only consider the AIME subset of mini-F2F? Is there any experiment result on full mini-F2F?
  2. Currently, GPT and Claude can already generate good formal math proof, is there any experiment result on that?
2 comments
AuthorsOpenReview ↗

Rebuttal (1/2)

We thank reviewer P3sz for their time and review. We address below the points raised in the review. We start with weakness W3, which contains a major misunderstanding regarding the claim of the paper. We then address the two questions with some experimental evidence. Finally, we ask the reviewer for further details regarding weaknesses W1 and W2, revolving around the self-containment of the concepts discussed in the paper and its readability.

W3: "Result not significant. [...] CLB competency is necessary but not sufficient [...] not surprising at all. It is obvious [...] generating good formal math proofs needs model competency of a lot of dimensions."

While we agree with the reviewer that '[i]t is obvious [...] that generating good formal math proofs needs model competency of a lot of dimensions', this is not the claim of our paper. Indeed, our paper claims that CLB competency in particular is a necessary but not sufficient model competency for good formal math proofs. The value of our paper in terms of novelty and impact lies in the identification of CLB competency as being critical competency for the task. This is a novel result in itself (i.e. the literature on formal math proving does not discuss that concept at all, not even under another name), and it is impactful because it highlights to the community a formalised skill that formal theorem provers should control and optimise for, as we propose as future work.

In light of this critical clarification, we hope that you can update your appreciation of the paper and possibly update your scores, or point out how we could improve the paper to enable you to update your scores.

Q1: "Why only consider the AIME subset of mini-F2F? Is there any experiment result on full mini-F2F?"

This concern is shared with reviewer q4zS ("you only have 15 AIME tests"), and we address the underlying concerns with the same changes to the paper in Section 4.2.

We thank the reviewer for this 2-part question, which we understand as raising threats to the external validity (experiments over a narrow problem set) and statistical validity (test power under small-size problem subset) of the paper.

First, we clarify that the correlational experiment of Table 2 uses the full miniF2F test split Pass@32 (244 problems) for all ten models. Thus, to answer the second part of the question: yes, the correlational evidence is on full miniF2F, and the original paper details the reason why on lines 68–70: ``we focus on miniF2F whole-proof test-split pass@32 (Zheng et al., 2022) as it is the evaluation setting we found to be the most consistently reported across papers.''

Second, only the causal steering experiment used the AIME subset. This was motivated by the fact that proof generation and Lean compilation are expensive in time and resources, and we therefore chose to use only 1 of the 3 Olympiad-level subsets from miniF2F (AIME, AMC, and IMO) that qualifies to test our hypothesis, while providing sufficient power to show statistical significance. The original paper reports sample-level solve rate's error of the mean, and we targeted non-overlapping standard-error ranges as being sufficient to assert statistical significance of our results.

While this is argued as a sufficient setup, we propose to follow the direction set forth by the reviewer by raising further the external and statistical validity of our causal experiment in two ways:

  1. in comparison to only using the AIME subset, we extend to using both AIME and AMC (+39 problems) subsets;
  2. in comparison to checking that standard-error ranges do not overlap, we now apply a one-sided sign test over problems, which counts the problems where a control arm solves more often than the CLB suppression arm.

We test on the problems where the unsteered model (α=0\alpha=0) solves at least once, because a problem the model never solves cannot show a drop under suppression. This rule is applied to the unsteered run alone, before any steered arm is generated, so the selection cannot favour our hypothesis. As a result, it keeps 10 of the 15 AIME problems (32 samples each) and 15 of the 39 AMC problems (8 samples each), giving a total of 25 informative problems. We also add an orthogonal control: a random direction orthogonal to the CLB direction, with the same norm.

AuthorsOpenReview ↗

Rebuttal (2/2)

Thus, we update the paper with the following extended results, presented here as tables:

armpooled meanAIMEAMC
no steering (α=0\alpha=0)0.6290.4840.725
CLB α=−3\alpha = -30.1070.0440.150
random α=−3\alpha = -30.5950.4630.683
orthogonal α=−3\alpha = -30.5860.4660.667
comparison (25 problems)mean difference in solve rate [95% CI]problems: control better / CLB better / tiedone-sided sign test p
random vs CLB+0.487 [+0.359, +0.619]21 / 0 / 44.8e-7
orthogonal vs CLB+0.479 [+0.349, +0.610]20 / 0 / 59.5e-7

The two matched controls are almost identical and both far above suppression, on both problem families. In the revised paper, Figure 6 now shows the per-problem and pooled solve rates on the 25 informative problems, and Figure 7 shows the pooled output coherence, which stays stable under all three steered arms. The sign-test results are reported in the main text at lines 456–459. All changes are highlighted in blue.

In light of this addition that extends both the external and statistical validity of the paper, we hope that you can update your appreciation of the paper and possibly update your scores, or point out how we could improve the paper further.

Q2: "Currently, GPT and Claude can already generate good formal math proof, is there any experiment result on that?"

We thank the reviewer for this question. To answer it, we measured two general-purpose models on S2B-LM and added the results to Table 2 of the paper: GPT-6.1-sol and Claude Opus 5.5 both reach 100.0 +/- 0.0 ZSCT (adj-ZSCT 100.0) over 8 seeds, with the same setup as the other models in Table 2. They are therefore evaluated as having high CLB competency.

As they are closed-source LMs that are very expensive to run through their API for any miniF2F evaluation, we do not have the budget to report miniF2F proof-generation results for them in our harness, and, to the best of our knowledge, there are no published numbers for them either. We therefore cannot include them in our correlational investigation, and because their weights are closed, we cannot include them in our causal intervention experiment either.

We hope this clarifies the scope of what can be measured for closed models, and we welcome suggestions for an affordable and relevant miniF2F protocol for them.

W1 & W2: "Not self-contained. This paper is an incremental work of S2B. [...] related concepts and designs should be carefully explained." / "Not well-written. [...] a concept is used or introduced without sufficient explanation."

Firstly, we respectfully disagree that the paper is incremental with respect to S2B. S2B-LM changes S2B in two ways, a categorical stimulus domain, and chain-of-thought scaffolding through a rule-based verbalizer, and the ablation of Table 1 shows that both are needed: ZSCT rises from 57.9% for the original S2B to 87.0% for S2B-LM. More importantly, the main contribution of the paper, the correlational and causal link between CLB competency and formal theorem proving, has no counterpart in the S2B paper.

Secondly, we agree that the paper bridges several subfields, so that readers from each side need background on the others, and we take the readability concern seriously. To address this concern, and that of W2 ("a concept is used or introduced without sufficient explanation"), we have added a glossary in Appendix F, and every use of its terms in the main text now links to the entry. Its entries are grouped by subfield:

  • Emergent Communication: Symbolic Behaviour Benchmark (S2B), Meta-Referential Game (Meta-RG), referential game, supporting and querying phases, sync round, S2B-LM, Compositional Learning Behaviour (CLB), receptivity, constructivity, Zero-Shot Compositional Test (ZSCT), and adjusted ZSCT (adj-ZSCT);
  • LLM evaluation: numerical understanding and processing ability (NUPA);
  • Interpretability: Contrastive Activation Addition (CAA);
  • AI4Math: miniF2F and Pass@32.

We would be grateful if the reviewer could point to concrete examples, either among these concepts where the explanation still falls short, or of other concepts that were particularly difficult to follow, so that we can extend the glossary and the main text accordingly.

If these changes address the reviewer's concern about presentation, we hope that they can be reflected in the reviewer's assessment of the paper.

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

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