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Paper summary
This paper proposes Shared-Future Polar Sampling (SFPS), a training-free decoding method for reasoning. At each step, it samples several candidate segments and generates a few short continuations shared across them. An importance-weighted candidate–continuation matrix estimates how well each candidate is supported by its future, and continuation tokens are drawn with a "polar" proposal. The authors prove consistency for a finite candidate pool and horizon, and compare SFPS with base sampling, low-temperature decoding, MCMC Power, and public GRPO checkpoints on math, science QA, and code tasks.
Critical strengths
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The paper expresses local candidate likelihoods and the conditional probabilities of short continuations within a single importance-weighted comparison matrix, and analyzes the estimation properties of the polar proposal. Compared with a purely heuristic sampling rule, this makes the objective, sources of approximation, and scope of applicability clearer.
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On the reported model–task pairs, SFPS outperforms MCMC Power while using substantially fewer generated tokens and less wall-clock time. The appendix also provides useful mechanism analyses of the matrix readout and the proposal.
Critical weaknesses
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End-to-end accuracy supports the empirical effectiveness of the method, but does not verify the mechanistic claim that future evidence identifies better reasoning candidates. The paper describes SFPS as using evidence from future reasoning to revise local preferences. However, by definition, its future evidence is the sum of the base model's powered probabilities over future continuations; it measures the model's confidence in a continuation rather than correctness. Thus, at an individual decision point, this signal can shift probability mass toward a more confident but incorrect candidate. The final accuracies in Table 1 show that the method is effective overall in the evaluated settings, but this end-to-end metric also conflates candidate generation, repeated block commitments, test-time computation, and a preference for low-entropy continuations. It therefore cannot identify whether the gain is caused by future evidence promoting more correct candidates. The observation in the appendix that responses concentrate in high-likelihood, low-entropy regions is also consistent with the alternative explanation that the main benefit comes from a stronger confidence preference. Consequently, the paper's account of “future reasoning support” is currently better viewed as an explanatory hypothesis than as a directly supported conclusion.
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The experiments are insufficient to support the claim that SFPS is efficient and superior to existing training-free methods. Scalable Power Sampling and Power-SMC are efficient power-based samplers cited in Appendix A, but the main table compares only with MCMC Power. The computational costs of SFPS and MCMC Power differ substantially, yet the paper reports only one operating point and does not show performance under comparable compute budgets. Moreover, shared continuations require repeated scoring in multiple candidate contexts, but the actual computational cost is not fully characterized. The main table also lacks confidence intervals or significance tests; some gaps are small, while several tasks, especially AI-MO and GPQA, have limited sample sizes, making the stability of the results difficult to assess. Finally, the GRPO checkpoints are trained on mathematics data but are also evaluated on GPQA and HumanEval, and the paper does not fully specify prompt formats and tuning procedures for the baselines. Taken together, the relative performance across methods and tasks remains difficult to interpret reliably.
Questions for authors
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Could the paper more directly test whether a position shift improves correctness? For example, across tasks, what is the final accuracy of candidates for which SFPS changes the choice away from the initial leader, relative to the original leader? This would help distinguish beneficial future comparison from merely preferring low-entropy continuations.
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Could the authors compare with Scalable Power Sampling and Power-SMC? If reproduction is not feasible, please explain why. For MCMC Power, could the paper report performance-versus-budget curves under comparable generated-token counts, actual scoring cost, or wall-clock time, rather than only one configuration point?
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Please provide the prompt formats, answer extraction procedures, MCMC hyperparameters, and tuning procedures for all baselines, and report confidence intervals for the main results.
We now test final correctness after changing only the opening. The future score is likelihood-based; its usefulness is evaluated through a controlled outcome comparison. At the first shift in 267 MATH500 problems, both branches use the same saved state and Base continuation policy (Table 4(b); Appendix J.4):
The +3.0 pp gain measures the effect of choosing a different opening under a fixed downstream policy. Full-decoder ablations provide complementary evidence: removing future aggregation or column weighting reduces accuracy from 77.6% to 74.0% or 74.2%, with paired SFPS gains of +3.6 pp [1.2, 6.0] and +3.4 pp [1.2, 5.6] (Table 5).
We added efficient baselines, SFPS–SPS compute comparisons, and an MCMC step sweep. The four-task results and MATH500 costs are:
Qwen2.5-Math-7B scores (%) and MATH500 costs are from Tables 1–2; HumanEval uses pass@1. Parentheses normalize to Base: 8.25 s and 672.6 tokens.
SPS: L=K=M=8 (HF adaptation); Power-SMC: 64 particles (paper-based HF reference), as specified in Appendix J.2. Tokens include all candidates, particles, and futures.
At similar latency, SFPS improves accuracy by 5.8 pp near 17 s (about 2× Base time) and 3.4 pp near 27 s (about 3.3× Base time) over SPS (Figure 5). The new MCMC sweep (Table 17) gives:
Its best tested accuracy is 73.4%, versus SFPS's 77.6%. Figure 5 reports measured time/token budgets; Table 17 varies MCMC steps.
Shared-future scoring is included in the measured runtime. A full default round samples KL+nH=640 tokens and requires up to mnH=3,072 candidate–future token evaluations for eight live candidates (Appendix H.2). These evaluations are batched and build the comparison matrix during generation; selecting from the completed matrix requires no additional model pass (Section 4.4).
All methods use Power Sampling's task templates, answer extraction, and grading, with inference on H100 GPUs (Appendix H.3). Table 7 and Appendix J document configurations and sensitivity tests; Table 17 reports the MCMC step sweep. Primary comparisons retain the original SFPS default. For all main comparisons, we use the original default configurations of SFPS and each baseline, without additional hyperparameter tuning.
Table 14 gives the following SFPS-minus-baseline MATH500 differences, with paired question-level 95% intervals:
Tables 5 and 15 also report paired intervals for readout and sensitivity comparisons. Table 9 lists benchmark sizes; the GRPO rows measure transfer of the specific math-trained checkpoints identified in Table 8. We will release all experimental code, baseline configurations, and evaluation scripts.