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Paper summary
This paper addresses the challenge of allocating a limited computational budget across multiple incomplete reasoning trajectories during test-time reasoning, with the goal of avoiding the repeated generation of identical answers or evidence. The core tension lies in the trade-off that while inspecting early previews of trajectories helps identify complementary paths, the previews themselves consume tokens and may encroach upon the budget reserved for completing the reasoning. Specifically, the study investigates three key aspects: the amount of early information required to select complementary rather than redundant trajectories; the conditions under which the informational value of a preview justifies its computational cost; and how to employ inexpensive checks to filter out duplicate candidates as more answers are discovered, thereby ensuring that costly reasoning is completed only for candidates that provide novel information.
Critical strengths
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The paper gives a clear definition of semantic coverage. Equation (2) separates changes in individual value from gains from fewer repeats. Theorems 1–3 study learning enough to coordinate, exact diagnostic profitability, and discovery with two operation costs.
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The experiments separate two settings clearly. One uses the same shared previews and candidate pool for different selection rules. The other compares complete procedures under a shared token ceiling and charges all online work. The paper reports both gains from product-union selection and cases where agreement-filtered lists have higher target F1 at lower cost.
Critical weaknesses
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The link between Theorem 1 and the experiments is not strong enough. The theorem requires complete contributor observations and a common circular order that makes an arc. However, SCPS uses entity previews and product-union selection. The paper does not show how these previews provide complete contributor observations or a consistent order.
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The empirical evidence is limited, and the theory alone does not establish practical usefulness. More importantly, several assumptions of the diagnostic theory are hard to verify at deployment. Theorems 2–3 assume known conditional diagnostic laws, persistent candidate labels, fresh independent reports, and, in the discovery model, uniform hidden classes. Appendix C.5 requires calibration on deployment conditional laws of novel and duplicate examples, and states that fitting and calibration costs must be charged or amortized. However, the empirical predictors are fitted using gold reference matches. The paper does not report calibration cost or calibration sample size, and it does not test distribution shift. Therefore, it remains unclear whether the required information is available in practice and whether the diagnostic provides a net benefit.
Questions for authors
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How are the conditional diagnostic laws estimated at deployment?
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How many deployment-matched labeled examples are needed to calibrate the diagnostic, and does the Eq. (5) threshold correctly predict realized cost savings after charging calibration and acquisition costs?
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Please add more experiments.
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Could the authors clarify the practical use cases of the proposed framework? In which real tasks is it necessary to acquire early information and select among unfinished attempts according to semantic coverage, rather than use direct generation or agreement-filtered lists? Please provide a concrete example in which this choice improves final utility under a shared token ceiling, and explain what the useful contribution, diagnostic, and completion correspond to in that task.
5 comments
Response to Reviewer vhdF (2/3): deployment requirements and labeled sample size
W2 and Q1. Can the requirements be met at deployment, and how are the laws estimated? We agree the submission should have discussed this. The decision needs the fraction of useful candidates and how often the diagnostic (an early look at an unfinished candidate, such as a preview) flags useful () and other candidates ().
How the two flag rates are measured.
- Run the diagnostic on a sample of candidates from the task.
- Complete every candidate, including those the diagnostic would reject.
- Record which were useful, and the flag rates among useful and among other candidates.
- Buy the diagnostic only if , less a confidence margin for examples of each kind, exceeds , the boundary of Theorem 2 (: the diagnostic's price; : a completion's cost); otherwise complete directly.
Of the assumptions you list, measured rates replace known laws; each candidate is completed once and labeled by that completion, so its label is fixed by construction. Fresh repeated reports and uniform classes are needed only for the results on repeated diagnostics and on discovery, as Sec. 3.2 now says.
Gold references, calibration cost and shift. Step 3 needs a verifier of usefulness: execution where the task has one (tests), or labeled development questions (question answering). New App. G.1.1 reports what you asked for on our question-answering predictors: sample size (91–96 questions per fit), held-out calibration (ECE 0.02–0.06), and the one-time cost of the fitting data (1.29M and 7.04M tokens, two backbones). Without refitting, on a separate 160-question population, the Qwen3.5-9B predictor’s ECE goes from 0.058 to 0.088 with retrieved evidence.
Changes in the paper. Sec. 3.2 (new paragraph "Using the boundary") gives the measurement procedure for the rule and the assumptions it needs; App. C.5 the sample sizes and repayment; new App. G.1.1 the predictors’ calibration, cost and transfer.
Q2. How many labeled examples, and does the threshold predict realized savings? We agree that the threshold should be checked against realized outcomes. The revision applies it in two settings, and in both the boundary’s verdict matches the realized comparison.
How many labeled examples? The number of labeled candidates in step 3 depends on how far the diagnostic clears its price. At 95% confidence, a diagnostic whose estimated exceeds by 0.20 needs 220 independent examples of each kind; one that clears it by 0.10 needs 877. If labeling, fitting and calibration cost , they are repaid over uses only when , being the saving per use; if , nothing repays them (App. C.5).
Executable tests (new experiment). Can a look at a test’s first 128 tokens tell whether the test is worth finishing and running?
- Sample. On 16 TestGenEvalLite tasks, we finished and executed every candidate: 240 labeled tests, 20 of them useful.
- Measured rates. A screen on the first 128 tokens (fitted on other tasks) flags 30% of the useful tests and 24% of the others.
- What the rule says. Do not buy the screen. With 20 useful tests, a 6-point gap cannot be distinguished from zero (95% interval: −20 to +28 points), and the rule buys only on a reliable gap. Even at face value, the prefix costs at least 14.3% of the rest of the test, nearly twice the 7.7% that such a gap could repay (App. H.4).
The whole experiment took 1.40M tokens of generation. So a sample labeled by execution alone was enough to decide against this screen before deployment, and to show what would change the decision: a cheaper prefix or a sharper screen.
Question answering. Could SCPS’s previews pay?
- Measured price. A prefix and two previews cost 0.97–1.45 times a completion (App. G.1).
- What the rule says. The loop finishes one candidate in four. At this price, previews save compute only if that quarter holds more than all of the useful candidates on the two Qwen models (109% and 104%), which is impossible, or 86% of them on Gemma-4-12B (App. G.3.3).
- What happened. Under the same token ceiling, the same loop without previews finishes about twice as many traces and recovers 0.29–0.84 more distinct correct answers. It uses 4–17% more tokens and has slightly lower F1 on two models (Tab. G3).
Changes in the paper. Both analyses are now in Sec. 4.3; details are in new App. G.3.3 (Tab. G8) and new App. H.4.
Response to Reviewer vhdF (3/3): further experiments and practical use
Q3 (and the limited evidence noted in W2). More experiments. After the submission, we added the following experiments and connections between the experiments and our theory, which should address your concern:
- Table 1 at the start of Sec. 4, pairing Theorems 1–2 and Eq. (2) with the experiments that test or illustrate them;
- two checks of Theorem 1's condition, one with an independent-sampling baseline, and how far coordination is from the theorem's ceiling (App. E.1);
- a new experiment applying the purchasing rule to executable tests, with 240 labeled candidates (Sec. 4.3, App. H.4);
- the price analysis of previews (Sec. 4.3, App. G.3.3, Tab. G8);
- sample sizes, held-out calibration, fitting costs and a separate question population for the predictors (App. G.1.1);
- further test-generation experiments on 32 Django and SymPy components, scored by TestGenEval execution (App. H.5–H.6).
Q4. Practical use cases. We agree the submission should have made this concrete. In short: choosing by coverage pays whenever information about overlap is cheap enough, and the paper gives a general rule to decide, from measured prices and rates, whether acquiring early information pays in a given task.
Which real tasks, and what the contribution, diagnostic and completion are in each. The setting arises wherever a set of attempts is valued for what it supplies together.
- Questions with many answers (QAMPARI; also retrieving all relevant evidence, or proposing candidate hypotheses). In our experiment, the contribution is a distinct correct answer, the diagnostic is a short preview (at most 24 tokens) that forecasts an unfinished trace's answer, and completion is the rest of the trace.
- Test generation. The contribution is a newly covered line from a test that passes and preserves the suite, the diagnostic scores a candidate test's first 128 tokens, and completion writes up to 896 more tokens and runs the test.
- Tasks with a verifier, such as code generation or theorem proving scored by pass@k. The contribution is the first output that gets verified.
When acquiring early information is the right choice. Theorem 2 gives the condition: the diagnostic’s price must be below , a fraction of a completion. This is the regime of long completions and cheap, discriminating diagnostics: in the worked example of Sec. 3.2, a diagnostic priced at a fifth of a completion lowers the cost of a useful result from to . A labeled sample shows which side of the boundary a task is on (Q2). In our runs, the two measured diagnostics do not clear it: one because a forecast, bought with its prefix, costs about as much as a completion even with prompt caching, and the other because its screen separates candidates weakly; there, direct generation or agreement filtering is the better choice. The same calculation shows what would change this: if a preview cost only its output tokens, the share of useful candidates that the loop's completions must contain would fall from 86–109% to at most 56–65% (App. G.3.3). Where overlap information is free, as with the decoding order in Part 1, answer-first coordination adds 0.04–0.20 distinct correct answers per four outputs (9–20%) at no extra generation.
Changes in the paper. The rewritten first paragraph of the introduction names tasks scored by what attempts supply together and reports that one answer list is not enough; Table 1 and Sec. 4.3 show where our measured diagnostics stand against the boundary; the rewritten Discussion states the practical conclusion and the limitation for reasoning-first traces.
Thank you again. Your questions on Theorem 1 and on what the rule needs in practice led to the new checks, the price analysis, and the test experiment, and we consider the paper stronger with them.
Response to Reviewer vhdF (1/3): Theorem 1 and the experiments
Thank you for the detailed, technical review; your questions helped make the paper more precise. You identified the two places where it needed to be more explicit: what Theorem 1 requires and what App. C.5 asks of deployment.
W1. The link between Theorem 1 and the experiments. We agree, and the revision now makes the link clearer. SCPS’s previews give neither complete contributor sets nor a consistent order, so SCPS does not test Theorem 1, but the coordinated-sampling experiment of Sec. 4.1 does, and coordination helps there under the output format that the theorem’s condition calls for. The experiment was in the original submission but did not state this link; the revision connects its sampler to Theorem 1 and checks the theorem’s condition:
1. The sampler is Theorem 1’s systematic sampler. In inverse-CDF decoding, one number u∈[0,1) selects one output, token by token. Each possible output i then owns an interval of length πi, its probability under decoding, and outputs that share an opening occupy one consecutive stretch. Independent sampling draws the k values of u independently. The lattice sampler used in Sec. 4.1 draws output j at uj=(j/k+Δ)mod1, with one shift Δ∼U[0,1) shared by the batch, so the k points are evenly spaced and each output keeps the model’s distribution. This is systematic sampling, with the outputs as actions, the decoding order as the circular order, and selection probabilities kπi.
2. What the theorem predicts. Let Be be the outputs that name answer e, with total probability π(Be). If the outputs in Be are adjacent, a batch never repeats e when kπ(Be)≤1 and never misses it when kπ(Be)≥1: it names e with probability min(1,kπ(Be)). No sampler with these output probabilities can do better. Independent sampling gives 1−(1−π(Be))k, which is lower because its draws can repeat e. Of course, the theorem does not say that every output format meets this condition, but it shows how much coordination can achieve with the appropriate information. If the model must state its answer first, all outputs that give the same answer begin with the same tokens, so they sit next to each other in the order (up to different names for one answer). If the model must reason first and answer last, outputs that give the same answer begin in many different ways and are scattered across the order, and the theorem then gives no guarantee.
3. What we observe. We crossed format with sampler for three models and two kinds of evidence (retrieved, and answer-bearing passages that contain the answers), six settings in all. With the answer first, coordination adds 0.04–0.20 distinct correct answers per four outputs (9–20% over independent sampling), every interval above zero; with the rationale first, no change is detected in any setting. The difference between the formats is significant in all six settings after Holm correction. Since each output keeps its distribution, the gain comes from repeats avoided (Eq. (2), Fig. 2).
We also added checks of the adjacency condition on generated outputs; the main one tests a consequence of it. If the outputs naming answer e occupy one interval of length π(Be), the k evenly spaced points land in it ⌊kπ(Be)⌋ or ⌈kπ(Be)⌉ times whatever the shift, so across batches the number of times e is named takes at most two adjacent values. If they are scattered, the count can vary by more. Over twelve batches per question (164 questions, two models), we looked at every answer named at least twice. With the answer first, the count takes at most two adjacent values for 92% of them, against 41% under independent sampling; the exceptions are consistent with different names for one answer. With the rationale first, it does so for 41%, about the same as under independent sampling (39%). Rare answers pass under any sampler, so we also looked at answers named at least eight times: 89% pass with the answer first, against 9–17% in the other three cases. The check is necessary for adjacency, not sufficient: it is consistent with adjacency for nearly all answers under the answer-first format, and rejects it for most under the other.
Where SCPS fits. Here the order comes from decoding, so nothing has to be learned, and no contributor observations are needed. SCPS is used for the other results: it illustrates Eq. (2) in Sec. 4.2, and Sec. 4.3 applies Theorem 2 to its measured prices.
Changes in the paper. This explanation is now in the paper: Sec. 4.1 gives the sampler’s link to Theorem 1, the role of output format and the count check; App. E.1 gives the formal argument, the full check with its independent-sampling baseline, and the distance from the ceiling; new Table 1 (Sec. 4) pairs each result with its experiment.