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Under review as a conference paper at ICLR 2027

Mathematical Transfer in LLMs Follows Reasoning Approach More Than Topic

Abstract

When selecting mathematical training data for LLMs, a natural organizing principle is topic: probability examples for probability targets. An alternative is reasoning approach: worked solutions that share a solution method with the target, even when the mathematical domain differs. We ask which relation produces greater transfer after fine-tuning. We evaluate two counterbalanced designs: probability and combinatorics crossed with invariant reasoning and double counting (2,000 problems), and number theory and geometry crossed with complement and pigeonhole reasoning (800 problems). In each design, every cell serves as the held-out target in turn: same-approach (SA) sources share the target's method but change the topic, while same-topic (ST) sources share the topic but change the method. Every source appears once in each role, so additive source-quality effects cancel from the equally weighted aggregate contrast. Across five base models and three training seeds per design, SA outperforms ST in all 40 seed-pooled model–target comparisons. Model-level advantages range from 8.2 to 16.2 percentage points in the primary design (mean: 10.8) and from 12.0 to 16.0 in the second design (mean: 14.3); all ten model-level 95% confidence intervals exclude zero. In both designs, ST sources are more similar to targets under embedding and lexical measures, so the SA advantage runs opposite to the measured ordering of statement-level resemblance. These findings identify reasoning approach as a more effective matching criterion than topic for mathematical transfer across the evaluated topic–approach combinations.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
Large Language Models, Mathematical Reasoning, Reasoning Transfer, Mathematical Generalization, Reasoning Strategies, Cross-Topic Generalization

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Reviewer_mnNZOpenReview ↗
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2(+1)
Confidence
2
Informativeness
2
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3
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Paper summary

This paper investigates whether mathematical fine-tuning transfers more effectively when training examples share the target's reasoning approach rather than its mathematical topic. It proposes a counterbalanced 2×22 \times 2 experimental design comparing same-approach/different-topic (SA) supervision against same-topic/different-approach (ST) supervision.

The authors evaluate two synthetic mathematical datasets, five pretrained language models, and three training seeds. They report average SA-ST advantages of 10.8 and 14.3 percentage points, respectively, with positive seed-pooled contrasts across all 40 model-target comparisons. Additional analyses examine full fine-tuning, training-set size, absolute transfer, and statement similarity.

The central contribution is an empirical comparison of two criteria for selecting mathematical fine-tuning data. However, the experimental design identifies a performance contrast for specific source-target pairs rather than establishing that transfer of the intended reasoning mechanism explains the observed advantage.

Critical strengths

1. Structured experimental comparison.

The rotational design is a meaningful improvement over comparing independently selected datasets. Each source appears once under each matching relationship, so additive source-quality effects cancel from the equally weighted aggregate contrast. The paper also appropriately acknowledges that source-target interactions remain.

2. Consistent reported empirical ordering.

The SA-ST advantage is positive across all reported seed-pooled model-target comparisons in both synthetic designs. The authors additionally examine transfer relative to the base models, full-parameter fine-tuning, and different training sizes. Reporting per-seed results and acknowledging that bootstrap confidence intervals exclude training-seed uncertainty are positive aspects of the analysis.

Critical weaknesses

1. Fundamental identification limitations undermine the central mathematical interpretation.

The principal theoretical justification in Section 3.3 establishes only the cancellation of additive source and target effects. Under Equation (4),

= \mu + u_\sigma + v_\tau + w_{\sigma,\tau},$$ the aggregate SA-ST contrast eliminates the additive terms but leaves differences between unrestricted source-target interactions. Consequently, the measured advantage cannot distinguish genuine transfer of the intended reasoning approach from other pair-specific interactions, including recurring solution templates, problem-generation regularities, latent structural similarities, or differences in mathematical difficulty. This limitation is especially consequential because each $2 \times 2$ design contains only two undirected source-target pairs per matching relationship, evaluated in both directions. Repeating these comparisons across models and seeds does not generate independent evidence across a broad population of mathematical topic-approach relationships. The reported positive contrasts therefore demonstrate an empirical ordering for the selected cells, not a general mathematical principle governing transfer. Moreover, the approach categories are not necessarily disjoint. Invariant arguments can overlap with counting identities, while complement and pigeonhole reasoning can coexist within the same solution. The paper does not establish that its approach labels uniquely characterize the mathematical problems or their valid solution methods. Agreement among LLM judges is not an independent mathematical validation of the classification. Since evaluation checks final-answer correctness without requiring the intended approach, the experiments also do not directly demonstrate that the models transferred or used the claimed reasoning method. The rotational cancellation argument is correct, but it does not resolve these identification problems. The interpretation of the observed accuracy difference as evidence for a particular reasoning-transfer mechanism is therefore substantially underdetermined. **2. Statistical inference, effect heterogeneity, and evaluation reliability are insufficiently established.** The bootstrap procedure in Appendix F resamples individual evaluation problems conditional on the trained checkpoints. Although the authors correctly acknowledge that the resulting intervals exclude training-seed uncertainty, the analysis also does not account for the selection of topic-approach combinations or potential dependencies among synthetically generated problems. If the generator produces related templates or problem families, independent problem-level resampling may underestimate uncertainty. The 40 reported positive model-target contrasts should not be treated as 40 independent confirmations because they reuse related evaluation sets, source checkpoints, and a common construction pipeline. The second-design replication exhibits substantial heterogeneity that is obscured by the aggregate mean. From Table 7, the average SA-ST advantage is approximately 24.7 percentage points for pigeonhole targets but only 3.7 points for complement targets. Some individual effects are very small, including +0.8 points for Mistral on number-theory/complement. No target-level confidence intervals are provided for the second design. Consequently, the replication does not establish comparably strong effects across both reasoning categories. The mathematical correctness and classification validation are also insufficient. The final synthetic dataset relies heavily on LLM-generated problems, LLM answer agreement, and LLM approach judgments, with only 50 manually reviewed problems in the primary dataset. The manuscript does not quantify residual classification errors or independently establish the reliability of its approach assignments. The precise answer-extraction and mathematical-equivalence procedures are also unspecified, making it difficult to assess whether accuracy differences reflect mathematical reasoning improvements or evaluation-format effects. The statement-similarity analysis does not eliminate alternative explanations. Average lexical and embedding similarity favoring ST does not imply that approach matching is responsible for higher accuracy at the individual-problem level. Indeed, Table 13 reports that combinatorics/invariant targets have their nearest out-of-cell embedding neighbor in the SA cell more frequently than in the ST cell (52.8% versus 47.0%). This does not establish a similarity-based explanation, but it illustrates why aggregate similarity statistics alone cannot exclude one. Finally, the training-budget ablation changes both the number of training examples and the number of optimization steps, preventing separate identification of their effects. Taken together, these concerns affect the central scientific interpretation, statistical reliability, and reproducibility of the results. Addressing them convincingly would require independent validation of the approach taxonomy, stronger controls for synthetic-data dependencies, more complete statistical analysis, and experiments capable of distinguishing the proposed mechanism from alternative source-target interactions.
Questions for authors

1. Mathematical identification

Equation (4) leaves unrestricted source-target interactions after additive-effect cancellation. What evidence establishes that the remaining SA-ST contrast specifically reflects transfer of the intended reasoning approach rather than other source-target interactions? Can the authors provide an experimental control that distinguishes these explanations?

2. Approach classification and mathematical validity

How are approach labels validated independently of the generator and LLM judges? How are problems with multiple valid solution methods handled? What fraction of problems admits solutions using approaches other than their assigned labels, and how does this affect the interpretation?

3. Statistical inference and replication

How would the confidence intervals change under template- or problem-family-aware resampling, if the generated data contain dependent examples? Can the authors provide target-level confidence intervals for the second design and explain why the reported advantage is much larger for pigeonhole than for complement targets?

4. Evaluation reliability

What exact answer-extraction and mathematical-equivalence rules determine strict correctness? What independent evidence establishes the reliability of these decisions, particularly for models with near-zero base accuracy? Could grading or output-format differences account for part of the measured transfer advantage?

5. Similarity and optimization confounds

Does the SA advantage remain after controlling for individual-problem similarity and recurring solution templates? In the training-size ablation, can the authors separate the effect of increasing the number of examples from the effect of increasing optimization steps?

8 comments
AuthorsOpenReview ↗

Response to Weakness 1: Fundamental Identification Limitations

We strongly disagree that the stated concerns undermine our central finding.

1. The four positive directional contrasts provide evidence against a purely additive explanation.

Both conditions are evaluated on identical target problems, canceling additive target-difficulty effects. Each source appears equally as SA and ST, canceling additive source effects in the aggregate.

More importantly, under an additive-only model, the contrasts must satisfy Δ(PI) = −Δ(CD) and Δ(CI) = −Δ(PD). Thus, both members of either pair cannot be positive in expectation. Yet all four observed contrasts favor SA across all five models in both designs.

This provides evidence of systematic source–target interactions aligned with approach matching, rather than differences in intrinsic source quality or target difficulty. An alternative explanation must account for why these interactions consistently favor same-approach supervision across different mathematical topics and in both transfer directions.

2. Approach overlap can favor ST rather than SA.

The criticism concerning overlapping approaches overlooks an important implication of our design. The SA source already shares the target's designated approach, whereas ST uses a different designated approach. If these approaches overlap, ST may also provide supervision relevant to the target's approach, potentially narrowing the observed SA−ST advantage. Such overlap cannot simply be assumed to inflate the SA effect.

Moreover, Section 3.1 explicitly defines approach labels according to reference solutions, not as exclusive classifications of all valid methods. Evaluation accepts any mathematically correct solution, as required by our accuracy-based transfer comparison.

3. The reviewer challenges a claim our paper does not make and overlooks the evidence from independent experimental designs.

The reviewer concludes that "the interpretation of the observed accuracy difference as evidence for a particular reasoning-transfer mechanism is therefore substantially underdetermined" and uses this to argue that our central finding is undermined.

However, our study does not claim to identify a particular internal reasoning-transfer mechanism. It directly compares the effectiveness of approach-matched versus topic-matched supervision for mathematical fine-tuning. Sections 3.3 and 7 explicitly acknowledge the limitations of mechanistic identification.

The reviewer also understates the generalizability evidence provided by our second experimental design. We do not merely repeat the same source–target relationships across models and seeds. We conduct a second factorial experiment using entirely different mathematical topics and reasoning approaches, yet observe the same positive SA−ST ordering across all model–target comparisons. This replication demonstrates that the finding is not confined to the particular topic–approach relationships of the primary design.

Identifying the internal mechanism responsible for transfer is a fundamentally different research question, requiring a different experimental design that investigates additional factors, including fine-tuning objectives and methods, training dynamics, solution representations, and model-internal computations.

Our experiment deliberately controls the fine-tuning procedure to isolate the comparison between supervision-selection criteria. Requiring identification of internal mechanisms would therefore impose an entirely different research objective rather than evaluate the validity of the experiment we conducted. The inability to uniquely identify an internal mechanism does not invalidate our empirical comparison.

AuthorsOpenReview ↗

Response to Weakness 2: Statistical Inference, Effect Heterogeneity, and Evaluation Reliability

1. Statistical inference and effect heterogeneity are being interpreted against an incorrect standard.

The manuscript explicitly defines the uncertainty quantified by the reported confidence intervals (Section 4.3 and Appendix F) and separately reports training-seed results. Our evidence spans five models, three seeds, four target rotations, and two distinct experimental designs; we do not treat the resulting 40 model–target comparisons as statistically independent replications.

More importantly, our hypothesis concerns whether approach-matched supervision yields greater transfer than topic-matched supervision, not whether the effect must have identical magnitude across reasoning categories. The reviewer emphasizes the smaller advantages on complement targets, but differences in effect magnitude do not contradict the primary, equally weighted SA−ST comparison defined in Section 3.2.

The second design reports positive SA−ST point estimates for every model–target combination, despite changing both mathematical topics and reasoning approaches. The reviewer identifies heterogeneity in these estimates, but heterogeneity alone does not establish that the aggregate comparative finding is unreliable. The requested dependence-aware and target-level uncertainty analyses are provided in our response to Question 3.

2. The mathematical-validation criticism does not establish that the reported results are unreliable.

Section 4.1 documents a multistage verification process. Each candidate undergoes eight unconstrained re-solutions, followed by approach classification requiring unanimous agreement among three LLM judges. Two of these models also independently solve the problems without access to the reference solutions, with answer agreement required for retention. The process also includes the rejection and replacement of problems with inconsistent answers. Separately, 50 randomly selected problems per cell underwent manual review, and all 50 were verified as correct.

The reviewer questions the sufficiency of this procedure without identifying a concrete mathematical error or demonstrating a systematic validation bias favoring SA. The use of synthetic data and LLM-assisted verification does not itself establish that the resulting empirical comparison is unsound.

Furthermore, Section 3.1 explicitly acknowledges boundary cases between mathematical approaches and defines labels according to reference solutions rather than requiring unique valid methods. The classification and alternative-method questions are examined further in our response to Question 2.

3. The evaluation-reliability criticism must be distinguished from the actual comparative estimand.

The primary outcome is the difference in final-answer accuracy between SA and ST on identical held-out target problems (Section 3.2). Both conditions are evaluated under the same protocol, and neither receives a different correctness criterion.

The reviewer raises evaluation-format differences as a possible explanation but provides no evidence of a systematic grading effect favoring SA. Moreover, the concern about near-zero base accuracy does not directly challenge the primary SA−ST estimand, which compares two fine-tuned conditions rather than relying on their absolute accuracy relative to the base model.

The exact extraction and equivalence rules, together with independent evidence of grading reliability, are provided in our response to Question 4.

4. The similarity criticism does not establish an alternative explanation for the observed ordering.

The reviewer highlights combinatorics/invariant, where the nearest out-of-cell embedding neighbor belongs to SA more frequently than ST (52.8% versus 47.0%). However, this is the only target among the four primary-design cells with that ordering. The other three favor ST, as do the aggregate lexical and embedding similarity measures reported in Section 6.

Our similarity analysis is a diagnostic showing that greater measured statement resemblance does not generally correspond to greater transfer. It is not presented as proof that every possible source–target interaction has been eliminated. The cited individual exception does not establish that similarity explains the observed advantage. We address individual-problem similarity and recurring solution templates directly in our response to Question 5.

AuthorsOpenReview ↗

Q1, Q2, Q3

Note on numerical results. The original run artifacts became unavailable under the university's storage-retention policy. We therefore reran the experiments using the same datasets, models, seeds, training configurations, and evaluation pipeline. The numerical results below come from these reruns; the SA−ST ordering remains positive across all 40 model–target comparisons. Additional analyses and controlled experiments are identified below.

1. Mathematical identification

We report the different-on-both (DH) control, whose training source shares neither topic nor designated approach with the target. Because each source serves once as SA, ST, and DH across the rotations, aggregate contrasts retain the cancellation of additive source effects. SA−DH compares sources differing in approach match while both differ in topic; ST−DH compares sources differing in topic match while both differ in approach.

  • SA−DH: +9.2 to +15.4 percentage points (pp) in Design 1 and +12.0 to +15.2 pp in Design 2; all ten model-level 95% CIs exclude zero.
  • ST−DH: −1.6 to +0.8 pp across the ten model-level comparisons.

Thus, the SA advantage is not merely a disadvantage of the particular ST source: approach-matched training also consistently outperforms a source matching neither attribute, whereas topic matching adds little relative to DH. The similarity and recurring-template alternatives raised in the question are directly tested in Q5.

2. Approach classification and mathematical validity

We added a deterministic, non-LLM approach-vocabulary check, separate from the generator and LLM judges. Using fixed, approach-specific cues in reference solutions, it finds the assigned approach's vocabulary in 95–98% of Design 1 solutions and 100% of Design 2 solutions. This checks expressed approach markers without an additional LLM judgment. Multi-method problems are retained: training uses the labeled reference solution, while grading accepts any correct method.

To examine alternative valid methods, we identify targets that at least one untuned base model answers correctly without using vocabulary associated with the assigned approach. This applies to 11–22% of Design 1 targets and 13–34% of Design 2 targets. These are measurable proxy rates, not an exhaustive enumeration of every mathematically possible solution method.

On this proxy-defined subset, SA−ST remains positive in all 40 model–target comparisons. The result therefore persists for targets where base-model behavior supplies evidence of alternative solution routes.

3. Statistical inference and replication

We recomputed confidence intervals by resampling entire similarity-defined problem families, including families spanning target cells. Families are constructed by average-linkage clustering of statement and reference-solution embeddings using Qwen3-Embedding-0.6B; we test multiple similarity thresholds.

The intervals widen as expected, yet all ten model-level SA−ST CIs remain above zero, even under the coarsest clustering (20 families in Design 1; eight in Design 2). Using the rerun outputs, Qwen's Design 1 CI widens from [15.3, 18.9] under problem-level resampling to [9.6, 21.8] under family-aware resampling; in Design 2, it widens from [13.4, 18.6] to [7.4, 18.7].

The requested Design 2 target-level SA−ST estimates and 95% family-aware CIs are below (pp; mean statement/solution cosine threshold ≥0.6, 34 families):

TargetQwen3-4BLlama-3-8BDeepSeek-Math-7BMistral-7BGemma-3-4B
Number theory / complement+4.7 [2.1, 11.7]+4.7 [1.2, 7.2]+4.5 [1.2, 9.2]+1.5 [1.0, 3.0]+2.2 [0.1, 4.3]
Number theory / pigeonhole+22.3 [11.2, 26.7]+20.0 [15.4, 28.1]+17.7 [10.5, 25.6]+14.7 [6.8, 23.6]+19.8 [14.1, 30.5]
Geometry / complement+13.0 [7.7, 20.2]+2.5 [0.6, 4.4]+6.7 [3.4, 11.0]+2.0 [0.2, 3.5]+2.0 [0.5, 4.3]
Geometry / pigeonhole+26.0 [13.7, 36.6]+30.8 [9.8, 43.6]+27.3 [7.1, 39.2]+30.0 [8.8, 42.6]+23.7 [2.8, 35.4]

All 20 Design 2 point estimates favor SA; all 20 family-aware CIs exclude zero. Across both designs, all target-level family-aware CIs exclude zero at this threshold. As with the original analysis, these intervals are conditional on the trained checkpoints.

For the effect-size difference, complement performance is near floor for four models (SA accuracy only 2.5–10.0%). On pigeonhole targets, 12–34% of ST generations end without an answer at the shared token limit, versus 1–7% for SA. We also remove the 23% of pigeonhole targets for which the statement exposes a direct "bound plus one" shortcut. On the remaining 77%, SA−ST remains +5.8 to +29.7 pp, with all corresponding CIs above zero.

Reviewer_CEo3OpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper categorizes math fine-tuning data based on topic and reasoning approach, and compares their effectiveness using synthetically generated problem and reasoning sets. The authors show that fine-tuning on problems with the same reasoning approach (SA) leads to better performance on target problems than fine-tuning on problems from the same topic (ST).

Critical strengths

None

Critical weaknesses
  1. Motivation for comparing "topic" and "approach" for math data selection is unclear. When fine-tning LLMs, both coverage of mathematical knowledge and reasoning are important and complementary. The authors should clarify how this paper contributes to fine-tuning LLMs on math. Moreover, distinction between "topic" and "approach" is also unclear. The paper compares a few predefined subsets, but such simple distinction may not be applicable to complex mathematical reasoning, where multiple concepts and reasoning skills are combined.

  2. The paper claims its need as a "training data selection", but all experiments rely on fully llm-generated synthetic datasets, including the questions themselves. The quality and diversity of the problem generated by LLMs are not sufficiently validated, which can be a significant flaw, considering that the evaluation also relies on this synthetic data. Moreover, it is unclear whether their findings are useful for selecting from existing large-scale mathematical reasoning datasets.

Questions for authors

Do the authors validate the quality of the generated problems through human evaluation, including how diverse generated problems are within each topic, and whether the generated problems are solvable, and the selected answers are truly correct?

7 comments
AuthorsOpenReview ↗

# Response to Review CEo3 — Submission 55482

The review raises concerns about the paper’s motivation, experimental design, synthetic data, validation, and applicability. We address these against the research question and the evidence provided. The distinction throughout is between limitations on the scope of a finding and methodological problems that undermine the finding itself.

AuthorsOpenReview ↗

1. Complementarity does not answer the comparative research question

The review states:

Motivation for comparing "topic" and "approach" for math data selection is unclear. When fine-tning LLMs, both coverage of mathematical knowledge and reasoning are important and complementary. The authors should clarify how this paper contributes to fine-tuning LLMs on math.

The research question is concrete: when selecting mathematical fine-tuning supervision for a target, does matching the reasoning approach or matching the mathematical topic produce greater transfer? This is a comparison between selection criteria, measured through changes in performance after parameter updates.

The paper does not claim that knowledge and reasoning are mutually exclusive, that either is unnecessary, or that either should be removed from training. Their complementarity is compatible with either outcome of our experiment. It therefore does not resolve—or contradict—the comparative question.

The review itself identifies “training data selection” as the intended application. Recognizing that application does not preclude a request for clearer exposition, but it does establish what the comparison is intended to inform: the choice of mathematical supervision for fine-tuning. The contribution is the controlled measurement of the relative transfer associated with these two matching relationships.

The statement about complementarity does not identify a flaw in that motivation or in the reported comparison. It addresses a claim about the necessity of knowledge and reasoning that the paper does not dispute.

AuthorsOpenReview ↗

2. Complex, mixed-approach problems require a separate research question and experimental design

The review states:

The paper compares a few predefined subsets, but such simple distinction may not be applicable to complex mathematical reasoning, where multiple concepts and reasoning skills are combined.

The quoted concern addresses a different research question, outside the scope of the present study and requiring a different experimental setup. Our question is whether matching a designated reasoning approach or matching the mathematical topic produces greater transfer under controlled fine-tuning conditions. Answering it requires source–target relationships in which those two forms of alignment can be distinguished. The predefined subsets make that comparison possible, and the crossed design counterbalances additive source-cell effects.

For a target combining several reasoning methods, “matching the approach” could mean sharing one component, several components, or their joint use. Both source conditions could then share some components of the target’s reasoning. Simply substituting mixed-approach problems would therefore change the supervision conditions and the interpretation of the resulting transfer. Without redesigning the matching conditions, those problems would not answer the controlled SA–ST question tested here.

Studying mixed-approach reasoning requires distinguishing transfer associated with individual methods from transfer associated with their combination. That calls for explicit definitions of approach overlap, training conditions that separate component matching from joint use, and evaluation targets that test those distinctions. It is a separate investigation with its own controls, rather than simply a larger or harder evaluation set for the current experiment.

The manuscript already identifies applicability to mixed-approach problems as a limitation and a direction for future work. This boundary is part of the stated scope of the research. The paper does not present its controlled comparison as evidence that the result already extends to arbitrary combinations of reasoning methods.

The present finding is a critical empirical step toward studying that broader problem. A second design changes both the topics and the approaches, and the SA advantage remains positive across all 40 model–target comparisons. Establishing that matching advantage under defined conditions supplies a controlled basis for investigating how it changes when methods are combined, whether supervision should emphasize constituent methods or their joint use, and how mathematical datasets should represent those relationships. The present study establishes the comparison on which that subsequent investigation can build.

The review’s phrase “may not be applicable” identifies an acknowledged question for future work. It does not show that the present question is incorrectly posed or inadequately tested. The absence of a separate experiment on mixed-approach reasoning cannot, by itself, substantiate a fundamental soundness objection to the controlled study actually conducted.

Reviewer_DpXsOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper investigates mathematical capability transfer in LLMs via two different dimensions, topical (i.e., the model transfers the topic but the method is related; referred to as same-approach) and methodological (the topic stays the same but the method transfers; referred to as same-topic). The authors experiment with both approaches using a 2x2 design with the topics of probability and combinatorics, using invariant and double counting approaches.

The paper experiments with a dataset of 2000 problems (500 per cell), generated using GPT-OSS. GLM-5.3, DeepSeek-V4-Pro, and GPT-5.6-Terra are used as the judge models. The paper then experiments with five base models (Qwen3-4B-Base, Meta-Llama-3-8B, DeepSeek-Math-7B-Base, Mistral7B-v0.3, and Gemma-3-4B-pt), and runs LoRA in each of them for adaptation.

In terms of results, the paper shows that same-approach training outperforms same-topic training consistently across all models.

Critical strengths
  • The paper is overall well-written and technically sound. The experimental setup is thoroughly designed, to isolate the effects that are intended to be measured.
  • The experimental results are insightful and clearly demonstrate the benefit of same-approach training and topical transfer in the context of mathematical reasoning. The fact that the results hold consistently across five base models makes the implications of this work strong.
  • As such, the paper is likely interesting to the research community focussing on the topic of mathematical reasoning in LLMs.
Critical weaknesses
  • The paper's scope and experimental results are quite limited. The paper only investigates a small subset of mathematical reasoning tasks and their capability transfer. Since the experimental setup is relatively simple, the paper would benefit from greater exposure to additional topics and tasks, to make a better-supported case of capability transfer in LLMs.
Questions for authors

N/A

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