Decision and Meta-Review
rejected
Decision note: Not accepted: its area chair recommended rejection.
Curricula and self-play proposers in RL with verifiable rewards pick tasks by pass rate, reading the variance of success as what a task teaches. Under a stochastic verifier such as a sampled LLM judge, that variance sums a learnable signal, the spread of the verifier's mean across responses, and per-call coin noise. We prove that every score built only from single-call verdicts sees a task only through its pass rate, so it cannot tell a pure-noise task from a learnable one, while one re-verification identifies the signal: for conditionally independent calls, the covariance of two calls per response, test-retest learnability, is unbiased for it. Retests are simulated from our judges' exposed verdict means; hidden-mean judges, the intended use, are not run. On a Qwen2.5-0.5B policy's answers, reference-free and 0.5B judges are near-coins, while a reference-guided 1.5B judge has median reliability 0.744 falling with task level. In tabular GRPO curricula over that pool (no language model is trained), re-verified selection beats LILO's by +0.030 [0.024, 0.036] in true accuracy, +0.007 at matched divergence from the initial policy; it is zero when half the candidates are trained on and near zero on a 1.5B policy's pool. Averaging the two calls ties the covariance, as does answer clustering at equal calls where answers can be matched: the evidence supports reading more than the pass rate for judges sampled at a positive temperature.
Introduction
Reinforcement learning with verifiable rewards (RLVR) trains a language model on tasks whose answers a program can check (Shao et al., 2024; Lambert et al., 2024; DeepSeek-AI et al., 2025). Training tasks are chosen by learnability: DAPO discards groups whose rewards are all equal (Yu et al., 2025), online difficulty filtering keeps tasks whose pass rate lies in a band (Bae et al., 2025), LILO samples tasks in proportion to the variance of success for PPO-style training (Foster et al., 2025; Schulman et al., 2017), and self-play proposers such as AZR (Zhao et al., 2025), R-Zero (Huang et al., 2025), Prism (Mishra, 2026) and AERO (Gao et al., 2026) are rewarded for tasks at the edge of the solver's ability. The RLVR scores among these (DAPO's filter, the ODF band, LILO, and the AZR and R-Zero rewards) read one number per task, the observed pass rate, and they rest on an argument that the variance of success is the size of the learning signal (Bae et al., 2025; Bay et al., 2026).
That argument assumes a deterministic verifier. However, verifiers in practice are increasingly stochastic: an LLM judge sampled at a positive temperature, a rubric judge, a reference-free self-judge (Yuan et al., 2024), or a test suite with flaky tests. Version-pinned judges at temperature zero still flip a share of their verdicts on re-runs (Ayyagari, 2026), an instability of serving non-determinism whose retests may be correlated, a regime this study does not measure. A stochastic verifier's verdict variance then mixes a part an update can act on with the coin noise of each call. Work on noisy rewards corrects the gradient under estimated flip rates (Mansouri et al., 2025) or finds a 10%-flip verifier nearly harmless to RL's attainable gain at the 1B scale (Hou, 2026), and RaRE masks rollouts on which several judges disagree (Liu et al., 2026). None of these asks whether a pass-rate score can tell the two parts apart when the noise differs from task to task.
We show that it cannot, and that one re-verification can. The law of total variance splits a verdict's variance into a signal and a noise , the reliability coefficient of classical test theory (Spearman, 1904). Every score built only from single-call verdicts, not from which responses are identical, has a law that depends on the task only through its pass rate, so it gives a pure-noise task and a fully learnable task at the same pass rate identical scores. Calling the verifier a second time on each response the loop already drew identifies , and the cross-call covariance, which we call test-retest learnability (TRL), estimates it without bias. Averaging the two calls instead keeps half the noise. The derivations are short. The contribution is that the blindness is exact for every score that reads only single-call rewards (DAPO, ODF, LILO, AZR, R-Zero), and that the remedy costs one extra verifier call and no extra rollout.
We test the theory by exact enumeration and then measure real sampled judges. Qwen2.5 judges of 0.5B and 1.5B parameters (Qwen et al., 2024) score 23040 real answers, 16 from each of two policies, to 720 arithmetic and program-output tasks. Reference-free and 0.5B judges are near-coins on almost every task, and on the 0.5B policy's answers the reference-guided 1.5B judge has median reliability 0.744 that falls with task level (table 1). At the same rollouts, re-verified scores select tasks with more signal than every single-call score. In tabular GRPO curricula over the 0.5B policy's answer pool, re-verified selection reaches 0.701 true accuracy against LILO's 0.671, a margin of +0.030 [0.024, 0.036] over 6 paired runs, of which +0.007 survives matching the arms' reverse KL from the initial policy (table 3); on the 1.5B policy's pool the margin is near zero. Several pre-registered expectations fail, and the appendix lists them all. The main ones: TRL is not separated from averaging the two calls, its accuracy gain per verifier call is below LILO's at default budgets, LILO's and R-Zero's selections are more reliable than chance under the informative judge rather than less, and the self-play solver never learned its task. Our key contribution is an exact account of what pass-rate curricula measure under a stochastic verifier and a two-call estimator that removes the blind spot. The scope: no language model is trained, the judges are sampled at a positive temperature, and they expose their verdict mean, so every retest is simulated as an independent draw from it; judges whose mean is hidden, where TRL would be needed, are not run.
Related Work
Learnability scores for curricula and self-play. Curricula for reinforcement learning prefer tasks with uncertain outcomes, ranked by value loss (Jiang et al., 2020) or regret (Dennis et al., 2020); in RLVR the preference is written on the pass rate. DAPO keeps groups with mixed rewards (Yu et al., 2025). Online difficulty filtering proves that the improvement of group relative policy optimisation (GRPO) (Shao et al., 2024) is lower-bounded by the variance of task success and keeps a pass-rate band (Bae et al., 2025). LILO samples tasks by (Foster et al., 2025), and the group-standard-deviation identity shows that a group's disagreement equals the size of its update (Bay et al., 2026). Self-play proposers reward learnability on tasks with and zero otherwise (AZR (Zhao et al., 2025)), solver uncertainty (R-Zero (Huang et al., 2025)), an edge-of-solvability gate (Prism (Mishra, 2026)), answer entropy in a solvability gap (AERO (Gao et al., 2026)), or disagreement across several solvers (Selvendran et al., 2026), and Self-Challenging agents filter generated tasks with their own tests (Zhou et al., 2025). Each of these bounds and identities reads the variance of success as learning signal, which is exact only when the verifier is a deterministic function of the response. AZR comes closest to our concern, since it drops programs that are nondeterministic on re-execution, but it re-runs the program rather than the verifier on each response. We keep these methods' goal and show that under a stochastic verifier the scores among them that read only single-call verdicts (DAPO, ODF, LILO, AZR, R-Zero) cannot see the learnable part of the variance; entropy and multi-solver scores that read answer identity are outside that result.
Noisy verifiers and judge variance. A second line treats verifier noise in RLVR as a property of the gradient. Noise-corrected GRPO models reward corruption as Bernoulli flips with estimated rates and debiases the update (Mansouri et al., 2025). Ablations at the 1B scale find a 10%-flip verifier nearly harmless to RL's attainable gain (Hou, 2026), and Dr. GRPO removes normalisation biases from the group estimator (Liu et al., 2025). Rubric judges extend such rewards beyond checkable domains (Gunjal et al., 2025), RaRE ensembles rubric judges and masks rollouts on which they disagree (Liu et al., 2026), TTRL rewards agreement with a majority vote (Zuo et al., 2025), and RLVR can raise some models' accuracy even with rewards nearly uncorrelated with correctness (Shao et al., 2025), so a curriculum's gain alone does not show that its reward carried signal. LLM judges are themselves measured as noisy instruments: even strong judges that match human agreement levels show position, verbosity and self-enhancement biases (Zheng et al., 2023), pinned judges flip verdicts on re-runs (Ayyagari, 2026), and repeated runs of code benchmarks split score variance into within- and between-problem parts (Zhou et al., 2026). Learning-progress exploration avoids noisy TVs (Hou et al., 2025), and RLVR difficulty labels estimated from few rollouts reproduce poorly across seeds (Chakma et al., 2026), a finite-sample instability whose evaluation budget that work quantifies; more rollouts sharpen but cannot separate verifier coin noise from signal. These works correct the update, mask rollouts, or bound evaluation precision. We use the same retest variance for a different decision, which tasks to train on, when the noise differs from task to task, and the classical tool for that is the reliability coefficient of test theory (Spearman, 1904; SPEARMAN, 1910).
Method
Figure 1. Re-verify, then select. A single verifier call per response cannot tell signal from coin noise; a second call on the same responses can.
Given a pool of tasks , a policy over responses , and a stochastic verifier that answers each call on with a verdict , the goal is to rank the tasks by how much a policy update on them can raise the verifier's mean, using only the verdicts a training loop already collects. The key challenge is that the variance every pass-rate score reads mixes two quantities, the spread of across the policy's responses and the coin noise of each call, and a single call per response cannot separate them. To this end, we decompose the verdict variance and show what one and two calls identify, link the learnable part to the policy update, and then define the two-call estimator TRL, its minimum-variance version, and what it cannot see.
Figure 1 sketches the procedure.
What a verdict's variance contains
Fix a task and drop from the notation. A response is drawn, and the verifier is called times on it, returning that are independent given with . The pass rate is , the variance of one verdict is , and an exact checker, where one exists, gives the true correctness . Two quantities split . The signal is how much the verifier's mean differs between the policy's responses, and the noise is the average coin variance of one call on a fixed response. By the law of total variance and the law of total covariance,
where are two calls on the same response . By equation 1, one verdict's variance is and cannot be split, while the covariance of a second call with the first equals whenever the calls are conditionally uncorrelated. The ratio is the test-retest reliability of classical test theory (Spearman, 1904; SPEARMAN, 1910), and it is the quantity table 1 measures for real judges.
Draw a group of responses iid from and call the verifier times on each. Marginalising each ,
where is the probability that one response receives verdicts on its two calls. The first line gives the blindness result.
Theorem 1 (single-call scores are blind to the signal). If the responses are drawn iid from and each receives one call, the law of every statistic of depends on only through . Each is a function of an independent pair of a response and a coin with , which proves it. A score that also reads which responses are identical, such as answer clustering, is not covered. The DAPO filter (Yu et al., 2025), the ODF band (Bae et al., 2025), the LILO weight (Foster et al., 2025), and the proposer-reward formulas of AZR (Zhao et al., 2025) and R-Zero (Huang et al., 2025), evaluated on the verifier's pass rate, are all such statistics (R-Zero itself computes as agreement with a majority-vote pseudo-label), so each gives a pure-noise task (, ) and a fully learnable task (, ) at the same identically distributed scores. A pure-noise task at attains the largest expected LILO and R-Zero score of any task. With two calls the law depends on and on nothing else, so , and become identifiable, and no higher moment of does. Theorem 1 states blindness, not anti-correlation: whether pass-rate scores pick unreliable tasks depends on how varies with across a pool, which is an empirical question that the selection experiment answers for one judge.
Why the signal is the quantity a curriculum wants
The first-order gain. Practitioner scores are justified by the claim that a task's pass-rate variance measures how much training on it helps (Bae et al., 2025; Bay et al., 2026). With a deterministic verifier that claim and equation 1 agree, because . With a stochastic verifier only part of the variance moves the policy. For a tabular softmax and the objective , one natural-policy-gradient (NPG) step of size changes, to first order in ,
where is true accuracy and the bound is the Cauchy–Schwarz inequality. The reward a policy is trained on improves by the signal, and the noise does not appear. The true accuracy improves by the covariance of correctness with the verifier mean, which vanishes whenever , so positive signal is necessary for a first-order gain in true accuracy but not sufficient: a verifier that is reliably wrong has large and negative . Equation 3 is exact only for one NPG step on a tabular softmax. The trained curricula of the experiments use Adam and std-normalised GRPO (Shao et al., 2024), so there it motivates ranking by and does not predict the size of the gain.
Size is not direction. The group-standard-deviation identity (Bay et al., 2026) shows that for binary rewards a group's disagreement equals the size of its GRPO update. On a pure-noise task the update keeps that size and loses its direction. With advantages and , a task with gives
where is the population standard deviation of the group's rewards and when it is zero. The cross terms vanish because, when , the are iid, independent of the verdicts, and , and whenever the group is split. Equation 4 is why a pass-rate curriculum can look busy and learn nothing: the tasks it favours on a noisy judge produce full-size updates with zero mean. For the unnormalised Dr. GRPO estimator (Liu et al., 2025), on every task, which vanishes when .
Test-retest learnability
The estimator. Equation 1 suggests the score directly. Call the verifier twice on each of the responses the loop already drew, and score the task by the across-group covariance of the two verdicts:
where is the mean of the -th call over the group and the second equality uses conditionally independent calls. TRL is ; it draws no extra rollout and doubles the verifier calls. It is the unbiased sample covariance of iid pairs, a U-statistic (Hoeffding, 1948), and its variance depends on only (appendix). We use it in three ways: curriculum selection (train on the top- tasks by ), a proposer reward , which is unclipped so that is maximised, at 1, by a clean task at and is zero on every pure-noise task, and a reliability filter , where is the sample variance of call . When a verifier exposes itself, as a judge's verdict probability does, the group variance of estimates with no second call. TRL is for verifiers whose is hidden: API judges without log-probabilities, judges that reason before their verdict, and flaky tests. Our judges expose , which is what lets us compute the oracle rankings; it also means the experiments test TRL on simulated independent retests drawn from ( in equation 8), not on a judge whose is hidden. The oracle- rows bound the signal that reading directly would select (table 2), though not trained accuracy (table 3).
The same-budget alternative. The obvious way to spend two calls is to average them and use the averaged reward's sample variance as a LILO-style score; we call that score Avg-2. For every realisation of the verdicts,
where and are the single-call sample variances. Avg-2 is the midpoint between the target of single-call scores () and the signal, so it keeps half the noise bias. It orders the tasks' expectations as does whenever rises with across the pool. The positive correlation between reliability and pass-rate variance measured in the experiments is consistent with this regime, and there the two scores tie.
The minimum-variance two-call estimator. Swapping the two calls of any response leaves the pair law of equation 2 unchanged, so the counts of responses with two passes and with disagreeing verdicts are sufficient. Averaging over the swaps gives
where the subtracted sum removes the within-response disagreement. is unbiased and a function of a complete sufficient statistic, so by the Lehmann–Scheffé theorem it is the minimum-variance unbiased estimator of from two calls; we report it as TRL-dc. TRL remains the pre-registered score, and the two are reported side by side.
What re-verification cannot see. A judge whose errors persist on a response is indistinguishable from signal. If the second call copies the first with probability and is otherwise a fresh draw, then and
where is the retest copula parameter. Re-verification removes only the noise that is fresh on every call. For our single-token judges at the verdicts are deterministic, , and TRL ranks exactly as LILO does, so equation 8 scopes every claim here to sampled judges and stochastic execution; reward hacking by a reliably wrong verifier is a separate problem. Every identity in this section was checked by exact enumeration and every implemented gradient by finite differences (appendix).
Experiments
Experimental Setup
Implementation Details. Two procedurally generated, exactly checkable task families are used whole: F1, chained integer arithmetic word problems, and F2, predicting a short Python program's output (AZR's deduction format (Zhao et al., 2025)), each at four levels of length. Each (family, level) cell has 30 tasks for each of three instance seeds, which redraw the tasks, so the study holds 720 tasks. Qwen2.5-0.5B- and Qwen2.5-1.5B-Instruct (Qwen et al., 2024) each give 16 sampled answers per task at temperature 1, none truncated at a 2,048-token cap, and the answers of one policy form its answer pool (accuracies in table 7; on F2 neither policy exceeds a question-only answer rule, and the 0.5B policy falls below it). Qwen2.5 judges of both sizes see each distinct answer either reference-free, as in self-rewarding judging (Yuan et al., 2024) (there the policy judges itself), or with the gold answer, the reference-guided grading of (Zheng et al., 2023) on which rubric-based RL rewards also build (Gunjal et al., 2025). A judge emits one Yes/No token, so is read exactly from one forward pass at every temperature and a retest is an exact draw from the judge's verdict distribution, so retests are simulated, independent given by construction, and is computed from , not measured from re-run calls. The exact checker gives . Seed 0 was the only tuning seed, every setting was fixed in the experiment plan, and seeds 1–3 were run once. Intervals are 95% (Wilson for proportions (Wilson, 1927), bootstrap (Efron, 1979) or Student- otherwise), and a matched-divergence contrast is a mean accuracy difference over a grid of divergence from ; the appendix gives both procedures. Everything ran on one 14-core laptop CPU without a GPU (the appendix lists the protocol and where each result lives).
Compared configurations. The scores are those of section 3: uniform selection, DAPO's filter (), an ODF-style band (, our thresholds), LILO, R-Zero and AZR, three scores that use more than single-call rewards (identical-answer clustering, RaRE-style drop-on-disagree (Liu et al., 2026) and Avg-2; defined in the appendix), and oracle rankings by the true and by . TRL and TRL-dc are this paper's arms. The primary judge is 1.5B-ref at , and a task with is called low-reliability.
Real judges are uneven retest instruments
Table 1 measures reliability on the 0.5B-policy pool. The reference-free and 0.5B judges are near-coins, with a pool-level median (table 5) of at most 0.021. The reference-guided 1.5B-ref judge is heterogeneous: its median is 0.744 [0.703, 0.780], about a quarter of its tasks lie below and another quarter above , and its reliability falls with level in both families (table 5). A paraphrased second prompt gives a similar profile, and as the second call it leaves the signal unchanged: averages 0.098 [0.093, 0.104] against 0.098 for a same-prompt retest (Spearman 0.980 over tasks). On the 1.5B-policy pool the same judge's median is 0.007 and its reliability rises with level; that policy gives a single answer on 21% of tasks, where by the policy and not by the judge. We pre-registered that Spearman for some judge in each family. It holds by its letter only for the near-coin 0.5B-ref judge; the informative 1.5B-ref judge has the opposite sign on both families, with intervals excluding zero. Under this judge reliability rises with the pass-rate variance across tasks, a marginal correlation that table 5 reports per family.
Table 1. Test-retest reliability () of four sampled judges and a paraphrased retest, per family and level. Median over the 90 tasks of each cell of , the share of a task's verdict variance that a second call reproduces, computed from the judge's exposed verdict probability (an independent retest by construction, not re-run calls); 0.5B-policy answer pool, . Ref.: the judge is shown the gold answer. Brackets: 95% percentile bootstrap over tasks. Red: lower than the primary judge in the same cell. Pool-level medians are in table 5.
| Family | Judge | \rotatebox{90}{Ref.} | \rotatebox{90}{Level 1} | \rotatebox{90}{Level 2} | \rotatebox{90}{Level 3} | \rotatebox{90}{Level 4} |
|---|---|---|---|---|---|---|
| F1 arithmetic | 0.5B-free | ✗ | 0.003 [0.002, 0.004] | 0.003 [0.003, 0.004] | 0.003 [0.003, 0.004] | 0.003 [0.003, 0.004] |
| F1 arithmetic | 0.5B-ref | ✓ | 0.018 [0.013, 0.022] | 0.021 [0.016, 0.028] | 0.020 [0.016, 0.023] | 0.021 [0.016, 0.027] |
| F1 arithmetic | 1.5B-free | ✗ | 0.067 [0.054, 0.081] | 0.038 [0.032, 0.049] | 0.025 [0.021, 0.031] | 0.015 [0.012, 0.018] |
| F1 arithmetic | 1.5B-ref, paraphrased retest | ✓ | 0.912 [0.901, 0.924] | 0.842 [0.801, 0.891] | 0.858 [0.832, 0.890] | 0.837 [0.791, 0.867] |
| F1 arithmetic | 1.5B-ref (primary) | ✓ | 0.972 [0.967, 0.978] | 0.938 [0.908, 0.947] | 0.869 [0.835, 0.889] | 0.814 [0.783, 0.843] |
| F2 program output | 0.5B-free | ✗ | 0.013 [0.009, 0.020] | 0.006 [0.004, 0.008] | 0.011 [0.009, 0.015] | 0.012 [0.010, 0.014] |
| F2 program output | 0.5B-ref | ✓ | 0.037 [0.028, 0.051] | 0.021 [0.018, 0.025] | 0.015 [0.012, 0.018] | 0.017 [0.015, 0.023] |
| F2 program output | 1.5B-free | ✗ | 0.036 [0.022, 0.087] | 0.012 [0.010, 0.016] | 0.010 [0.009, 0.012] | 0.008 [0.007, 0.010] |
| F2 program output | 1.5B-ref, paraphrased retest | ✓ | 0.677 [0.635, 0.766] | 0.574 [0.502, 0.650] | 0.180 [0.043, 0.464] | 0.086 [0.033, 0.315] |
| F2 program output | 1.5B-ref (primary) | ✓ | 0.691 [0.631, 0.759] | 0.466 [0.379, 0.552] | 0.147 [0.094, 0.277] | 0.110 [0.082, 0.185] |
Selection results: re-verified scores pick more signal
Each score ranks the 720 tasks of a pool from simulated groups of real answers with real-judge verdicts, 1,000 replicate groups per task, and keeps the top 10% (table 2). At the same rollouts, TRL's set has more signal than every single-call score's on both pools; the smallest margin is over LILO on the 0.5B pool, +0.0161 [0.0131, 0.0186]. LILO given twice the rollouts (, the same verifier calls) reaches 0.198 on the 0.5B pool, with overlapping intervals, so at matched calls the two tie, and identical-answer clustering at is above TRL with overlapping intervals (appendix). The pre-registered test that TRL selects more signal than Avg-2 fails: the differences on both pools have intervals that contain zero, so the bias of equation 6 does not change the top- set at this judge. The prediction that pass-rate scores select less reliable tasks than chance is refuted in the opposite direction for LILO and R-Zero, which rank identically: LILO's set has higher mean than uniform selection by +0.236 [0.211, 0.262] on the 0.5B pool; there AZR's set is lower than uniform's with overlapping intervals. Theorem 1 predicts blindness, and here blindness costs signal without selecting noise.
Table 2. What each score selects: mean signal and reliability of its top 10% (). Judge 1.5B-ref, , , top 72 of 720 tasks per answer pool. , : brackets are the 95% interval over 1,000 replicate draws of the groups and verdicts (fixed pool). = TRL minus the row, brackets a paired bootstrap over tasks; R-Zero ranks exactly as LILO and is omitted; the oracle ranks by the true and makes no call. Best per column underlined.
| 0.5B-policy pool | 1.5B-policy pool | ||||||
|---|---|---|---|---|---|---|---|
| Score | Calls | ||||||
| Uniform | 1 | 0.098 [0.082, 0.115] | +0.0966 [+0.0907, +0.1022] | 0.597 [0.516, 0.677] | 0.029 [0.018, 0.042] | +0.1032 [+0.0910, +0.1168] | 0.232 [0.155, 0.317] |
| DAPO filter | 1 | 0.123 [0.107, 0.139] | +0.0716 [+0.0662, +0.0771] | 0.690 [0.621, 0.755] | 0.065 [0.051, 0.079] | +0.0673 [+0.0582, +0.0777] | 0.450 [0.367, 0.529] |
| ODF band | 1 | 0.151 [0.137, 0.164] | +0.0442 [+0.0397, +0.0485] | 0.769 [0.716, 0.822] | 0.102 [0.089, 0.116] | +0.0301 [+0.0241, +0.0382] | 0.593 [0.525, 0.659] |
| AZR score | 1 | 0.075 [0.062, 0.089] | +0.1202 [+0.1123, +0.1251] | 0.538 [0.467, 0.615] | 0.035 [0.025, 0.045] | +0.0973 [+0.0830, +0.1125] | 0.325 [0.251, 0.403] |
| LILO | 1 | 0.179 [0.168, 0.190] | +0.0161 [+0.0131, +0.0186] | 0.832 [0.795, 0.867] | 0.111 [0.098, 0.123] | +0.0214 [+0.0175, +0.0253] | 0.619 [0.557, 0.681] |
| Answer clustering | 1 | 0.186 [0.175, 0.195] | +0.0094 [+0.0074, +0.0109] | 0.865 [0.833, 0.893] | 0.124 [0.112, 0.135] | +0.0084 [+0.0067, +0.0117] | 0.715 [0.654, 0.769] |
| Drop-on-disagree | 2 | 0.186 [0.176, 0.195] | +0.0088 [+0.0063, +0.0108] | 0.854 [0.823, 0.882] | 0.130 [0.119, 0.139] | +0.0027 [+0.0004, +0.0055] | 0.731 [0.676, 0.781] |
| Avg-2 | 2 | 0.195 [0.186, 0.203] | 0.0000 [-0.0001, +0.0000] | 0.905 [0.884, 0.924] | 0.131 [0.120, 0.140] | +0.0014 [-0.0007, +0.0040] | 0.744 [0.689, 0.790] |
| Oracle | – | 0.228 [0.228, 0.228] | – | 0.953 [0.953, 0.953] | 0.162 [0.162, 0.162] | – | 0.857 [0.857, 0.857] |
| TRL-dc | 2 | 0.195 [0.186, 0.203] | +0.0000 [+0.0000, +0.0000] | 0.905 [0.884, 0.924] | 0.133 [0.123, 0.141] | -0.0005 [-0.0010, -0.0001] | 0.792 [0.754, 0.825] |
| TRL | 2 | 0.195 [0.186, 0.203] | – | 0.905 [0.884, 0.924] | 0.132 [0.123, 0.141] | – | 0.794 [0.756, 0.825] |
Trained curricula on the real answer pools
Each task's policy is a softmax over its own 16 real answers, initialised at their frequencies. Each step scores 64 candidate tasks with responses, trains on the top 16 with one std-normalised GRPO step under Adam, and rewards the update with the first judge call for every arm, so arms differ only in what they select. The true accuracy comes from the exact checker, which no arm sees.
Table 3 reads in three steps. First, every arm ends far above the initial policy (0.198), and TRL gains +0.030 over LILO, a margin that keeps its sign at matched reverse KL, matched forward KL and matched Jensen–Shannon divergence, as do the margins over R-Zero and AZR. Against LILO the gain is only partly a better direction: at matched reverse KL +0.007 remains (+0.015 at the top of the grid), and the rest is distance from . Second, the margins over uniform selection and DAPO are mostly distance: their matched-forward-KL contrasts are negative. Third, information beyond the pass rate carries the gain, not the unbiased estimator: TRL's final margins over Avg-2 and drop-on-disagree contain zero, TRL-dc ends level with TRL, and answer clustering, which needs exact answer identity rather than a second call, closes the gap at matched calls and is ahead at matched forward KL. Per verifier call TRL gains less than LILO (0.0012 against 0.0023 per thousand calls), failing that pre-registered test, but against LILO with 128 candidates, at matched calls, its margin is +0.037. The exact-checker control behaves as predicted: with TRL and LILO coincide (table 6). With the near-coin 0.5B-free judge as reward (last column of table 3) every arm stays near : TRL moves true accuracy by -0.019 and AZR at 128 candidates by +0.009. Selecting by the oracle ends below TRL at the final step, which equation 3 does not predict, though the oracle is ahead at the largest common divergence (appendix). Across one-at-a-time changes (table 6) the margin over LILO stays positive under correlated retests and with Dr. GRPO, but it falls to +0.008 at , its size depends on the step size, it vanishes when 32 of 64 candidates are trained on, and it is +0.0005 on the 1.5B-policy pool.
Table 3. Trained curricula: final true accuracy () and TRL's margin over each arm. Tabular GRPO over each task's real answers, 400 steps, 240 tasks per run, 6 runs per arm (3 instance seeds 2 training seeds). Calls: verifier calls per run. : TRL minus the row at the final step, and at matched reverse KL and matched forward KL from (means over a 20-point divergence grid; appendix). Brackets: 95%, the wider of a hierarchical bootstrap and a interval over runs ( over runs for matched contrasts). Last column: the near-coin 0.5B-free judge as reward.
| Reward: 1.5B-ref judge | 0.5B-free | |||||
|---|---|---|---|---|---|---|
| Curriculum | Calls | Accuracy | final | KL-matched | fwd-KL-matched | Accuracy |
| Uniform | 51200 | 0.606 [0.580, 0.630] | +0.095 [+0.087, +0.104] | +0.006 [+0.004, +0.009] | -0.006 [-0.009, -0.004] | 0.180 [0.168, 0.192] |
| DAPO filter | 204800 | 0.667 [0.644, 0.690] | +0.034 [+0.030, +0.039] | +0.007 [+0.005, +0.009] | -0.007 [-0.010, -0.004] | 0.193 [0.180, 0.207] |
| ODF band | 204800 | 0.672 [0.648, 0.695] | +0.029 [+0.022, +0.036] | +0.005 [+0.004, +0.007] | -0.002 [-0.004, +0.001] | 0.185 [0.172, 0.198] |
| AZR score | 204800 | 0.588 [0.565, 0.612] | +0.112 [+0.107, +0.119] | +0.062 [+0.057, +0.067] | +0.020 [+0.016, +0.023] | 0.202 [0.188, 0.215] |
| LILO | 204800 | 0.671 [0.646, 0.694] | +0.030 [+0.024, +0.036] | +0.007 [+0.006, +0.009] | +0.006 [+0.004, +0.008] | 0.183 [0.171, 0.196] |
| R-Zero score | 204800 | 0.671 [0.646, 0.695] | +0.030 [+0.023, +0.038] | +0.007 [+0.005, +0.008] | +0.005 [+0.002, +0.009] | 0.189 [0.174, 0.203] |
| LILO, 128 candidates | 409600 | 0.664 [0.638, 0.689] | +0.037 [+0.029, +0.045] | +0.010 [+0.009, +0.012] | +0.013 [+0.011, +0.015] | 0.186 [0.174, 0.198] |
| Answer clustering | 204800 | 0.697 [0.671, 0.722] | +0.004 [+0.000, +0.007] | +0.000 [-0.001, +0.002] | -0.008 [-0.010, -0.006] | 0.189 [0.176, 0.201] |
| Clustering, 128 cand. | 409600 | 0.702 [0.678, 0.725] | -0.001 [-0.003, +0.001] | +0.002 [+0.001, +0.004] | -0.006 [-0.007, -0.004] | 0.187 [0.175, 0.200] |
| Drop-on-disagree | 409600 | 0.699 [0.673, 0.723] | +0.002 [-0.001, +0.005] | +0.002 [+0.000, +0.003] | +0.001 [-0.001, +0.002] | 0.185 [0.171, 0.199] |
| Avg-2 | 409600 | 0.698 [0.673, 0.722] | +0.002 [0.000, +0.005] | +0.001 [+0.000, +0.002] | +0.000 [-0.003, +0.003] | 0.184 [0.170, 0.198] |
| Oracle | 51200 | 0.687 [0.663, 0.711] | +0.014 [+0.010, +0.017] | +0.007 [+0.006, +0.008] | +0.013 [+0.010, +0.016] | 0.182 [0.168, 0.195] |
| Oracle | 51200 | 0.693 [0.669, 0.716] | +0.008 [+0.004, +0.013] | +0.004 [+0.001, +0.006] | +0.008 [+0.003, +0.013] | 0.172 [0.158, 0.186] |
| TRL-dc | 409600 | 0.701 [0.677, 0.725] | – | – | – | 0.183 [0.169, 0.197] |
| TRL | 409600 | 0.701 [0.676, 0.724] | – | – | – | 0.179 [0.166, 0.192] |
Self-play with a learned proposer
A two-layer character transformer solver is trained from scratch with GRPO on F2 programs, and a learned proposer, updated with REINFORCE (Williams, 1992), chooses among 16 generator arms: four levels crossed with four verification channels (the exact checker, and the 1.5B-ref, 1.5B-free and 0.5B-free judges, whose verifier mean on each response is resampled from the measured law of given correctness for that level). Table 4 shows that proposers rewarded by the AZR, R-Zero and LILO formulas end with almost all their mass on channels with , while the TRL proposer ends with 0.002, as pre-registered. The result holds without the exact channel and with an entropy bonus, and clipping the reward to breaks it, as the bias of a clipped predicts. No proposer, however, taught the solver the task: no arm's interval lies above the question-only modal-answer floor at any level, the TRL solver answers the modal string on every held-out program and scores the floor exactly, and the pass-rate solvers end on non-terminating strings in most runs. Once a solver emits a constant, on the exact channel, and the judge channels' remaining verdict variance is redrawn for each response independently of what the solver emits, so no update can exploit it; the mass result reflects training before that collapse. This experiment supports the claim about where proposers put their mass and says nothing about solver accuracy.
Table 4. Self-play: where each proposer reward puts its mass, and what the solver learned. 16 generator arms (4 levels 4 verification channels: exact, 1.5B-ref, 1.5B-free, 0.5B-free), 1,500 solver updates, 3 instance seeds. Mass: final proposer mass on arms with (). Accuracy: held-out greedy exact accuracy, mean of 4 levels; the question-only modal-answer floor is 0.218. Brackets: 95% interval over the 3 runs, which with 2 degrees of freedom can extend past . Exact: whether the exact channel is offered. Floor: levels (of 4) whose accuracy interval lies above that floor.
| Proposer reward | Exact | Calls | Mass on | Accuracy | Floor |
|---|---|---|---|---|---|
| Uniform proposer | ✓ | 1 | 0.438 [0.438, 0.438] | 0.077 [-0.253, 0.407] | 0 |
| AZR | ✓ | 1 | 0.999 [0.999, 1.000] | 0.059 [-0.195, 0.314] | 0 |
| R-Zero | ✓ | 1 | 1.000 [1.000, 1.000] | 0.000 [0.000, 0.000] | 0 |
| LILO | ✓ | 1 | 1.000 [1.000, 1.000] | 0.000 [0.000, 0.000] | 0 |
| Avg-2 variance | ✓ | 2 | 1.000 [1.000, 1.000] | 0.007 [-0.022, 0.035] | 0 |
| Clipped | ✓ | 2 | 0.999 [0.998, 1.000] | 0.000 [0.000, 0.000] | 0 |
| Oracle | ✓ | 1 | 0.000 [0.000, 0.001] | 0.163 [-0.043, 0.368] | 0 |
| TRL | ✓ | 2 | 0.002 [-0.001, 0.004] | 0.218 [0.151, 0.285] | 0 |
| AZR | ✗ | 1 | 1.000 [0.999, 1.000] | 0.000 [0.000, 0.000] | 0 |
| R-Zero | ✗ | 1 | 1.000 [1.000, 1.000] | 0.000 [0.000, 0.000] | 0 |
| TRL | ✗ | 2 | 0.001 [-0.001, 0.002] | 0.141 [-0.169, 0.451] | 0 |
| AZR + entropy bonus | ✓ | 1 | 0.997 [0.991, 1.003] | 0.030 [-0.099, 0.159] | 0 |
| TRL + entropy bonus | ✓ | 2 | 0.002 [-0.001, 0.006] | 0.156 [-0.180, 0.491] | 0 |
Conclusion
Under a stochastic verifier, the variance a pass-rate curriculum reads is the sum of a learnable signal and the verifier's coin noise, and every score built only from single-call verdicts depends on a task only through its pass rate, so none can separate the two. One re-verification per response identifies the signal, and the cross-call covariance TRL estimates it without bias. On arithmetic and program-output tasks answered by two small Qwen2.5 policies, reference-free and small judges were near-coins, and on the 0.5B policy's answers the reference-guided 1.5B judge's reliability fell with task level (table 1). At the same rollouts, re-verified scores selected more signal than every single-call score (table 2), and in tabular curricula over the 0.5B policy's answers they reached higher true accuracy than LILO, R-Zero and AZR, by a margin over LILO that shrinks to +0.007 at matched divergence from the initial policy (table 3). All of this used judges that expose their verdict mean, with retests simulated from it. Averaging the two calls was not separated from the unbiased covariance and single-call answer clustering tied it at equal verifier calls, so the evidence supports reading more than the pass rate, by re-verification where answers cannot be matched, rather than this particular estimator, and under this judge LILO's selections were more reliable than chance, not less. The limitations, including the scale of this CPU study, are stated in the appendix. The next tests are a judge whose verdict mean is hidden, called twice on a real answer pool to measure and , a trained language model under a sampled judge, and a self-play solver that leaves its answer floor, which ours did not.
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Appendix
Additional Details
Exact checks of the theory
Every identity of section 3 was checked by exact enumeration over random pairs with
support up to 6 and (2256 pairs for Theorem 1), and
every implemented gradient (vanilla and natural policy gradient, GRPO, Dr. GRPO, the tabular update
of the trained curricula, the self-play solver loss and the proposer gradient) by central finite
differences. All 20 of 20 checks pass: every
enumeration error is below and every finite-difference relative error below
(runs/aggregate__e0_exact.json). On the enumeration grid, the variance of TRL-dc
relative to TRL has median 0.919,
as equation 7 predicts. The exact variance of TRL, used in the method section, is
which follows from the variance of an unbiased sample covariance of iid pairs and the identity under conditionally independent calls. It depends on only, as equation 2 requires. For equation 7, write , so that . Given , the swaps make a sum of independent signs, so , which proves the first equality, and . Since , , which gives the variance gap. The symmetric pair law is a full-rank family over a set of with non-empty interior, so is complete and the Lehmann–Scheffé theorem applies. At the law of is a coarse lattice, so no per-task interval is used, and every interval in the paper is over tasks, replicates or runs.
Protocol, choices and where each result lives
Data. All tasks are generated by the study's own generators: F1 combines 2 to 5 integers with , and F2 has 2, 4, 6 or 8 statements over integers and lists, with one loop from level 3. No sample was drawn from a fixed benchmark and no data were subsampled. The policy decodes by sampling, seeded per task, because the object of study is the answer distribution; under greedy decoding every task would have one answer and by construction. The spread reported comes from the instance seeds, never from decoding seeds. On F1, the answer is the last integer of the whole completion: a calibration pass on seed 0 found that many 0.5B answers derive the result over several lines, so scoring the first line would have scored a derivation's opening, and the rule was changed before any reported seed was run. The per-task oracle quantities are plug-ins on 16 answers, so as estimates of the model's own they are biased low by a factor .
Configurations and seeds. Every arm, step size, group size and selection size was fixed in
the experiment plan before the reported seeds ran; seed 0 alone was used for calibration, timing and
smoke runs, and seeds 1–3 were run once. The trained curricula comprise 77
configurations and 462 runs of 400 steps, and the self-play study
15 configurations and 45 runs of 1500
updates. The tables show the configurations the claims rest on; the result of every configuration,
including those not tabled here, is in its aggregate under runs/. Two changes were made after a result was seen, both on the theory side. The
first full run of the exact checks failed two finite-difference checks, one because a search
direction was not normalised and one from round-off at the smallest step; both were fixed and the
first outputs overwritten. The enumeration then showed that the disagreement-corrected estimator
dominates TRL, so TRL-dc was added as an extra score and an extra curriculum arm. The
self-play runs took 4.6 hours, far more than the timing pilot
predicted, because solvers that never terminate emit full-length outputs; no finished cell was
dropped. A probe re-ran the 18 main self-play runs with answer logging, reproduced every curve
exactly, and found that 14 of the 18 solvers end on one constant string, two on almost one, and two R-Zero solvers on many non-terminating strings, all wrong. The pre-registered test of
whether pass-rate scores pick unreliable tasks was specified on the selected set's median ;
only means and fractions were stored, and both lie far on the refuting side.
Beyond those named in the main text, these pre-registered expectations were not met. LILO given
twice the rollouts was expected to stay below TRL in selected signal and ties it. The
TRL margin over LILO was expected to shrink as retests become correlated and stays within
overlapping intervals at . Every arm was expected to match uniform
under the near-coin judge, and AZR at 128 candidates is separated above it. The margin was expected
to keep its sign at every step size and selection size, and is zero at 32 of 64. Pass-rate
selections on the 1.5B pool were expected to be at least 30% single-answer tasks, and LILO's are
2.8%. TRL's selected
was expected to exceed LILO's with separated intervals, and the intervals overlap. In
self-play, the solver comparisons at matched divergence could not be tested because no solver
learned, and the Avg-2 proposer's mass was expected to lie between AZR's and TRL's and
matches AZR's. Each pre-registered criterion was
read against its interval by the venue rule (an interval that contains the baseline does not
support the claim); an independent second reading of those verdicts was planned and could not be
run.
Baselines and statistics. Identical-answer clustering scores a group by the between-answer variance of the per-answer mean first-call verdict; drop-on-disagree applies LILO's to the responses whose two calls agree and needs at least two of them. Medians and Spearman correlations over tasks carry a percentile bootstrap over tasks; contrasts between curricula carry the wider of a bootstrap over runs and then tasks and a Student- interval over the 6 paired runs. The two training seeds that share an instance seed are treated as independent there, so only three task draws are independent. A matched-divergence contrast is the mean, over a 20-point grid of the divergence from running from zero to the smaller arm's final value, of the difference in accuracy interpolated against each run's running maximum divergence; its interval is a interval over the 6 paired runs. At the top of that grid alone the reading can differ: TRL minus the oracle- curriculum is -0.0027 [-0.0042, -0.0011] there, against the positive grid average of table 3. Fixed benchmarks (GSM8K-style sets (Cobbe et al., 2021), CRUXEval (Gu et al., 2024)) were considered and not used, because they cannot be redrawn per seed and have no controlled level.
Answer clustering at matched calls. With responses and one call each, the same verifier calls as TRL at , clustering's top 10% has mean 0.205 [0.198, 0.211] on the 0.5B pool, against TRL's 0.195. In the trained curricula, TRL minus clustering at matched forward KL is -0.008 [-0.010, -0.006]. Clustering needs answers that can be matched exactly, which holds for these integer and program-output tasks and not in general for free-form answers.
Where results live. Each number in this paper is printed from an aggregate under
runs/: the exact checks in aggregate__e0_exact.json, the answer pools in
aggregate__e1_policy_*.json, the judges in aggregate__e1_judge_*.json, selection
in aggregate__e1sel_*.json, the curricula and their contrasts in
aggregate__e2_*.json, and self-play in aggregate__e3_*.json. Each aggregate is
written by runs/aggregate.py from the experiments' declared outputs, and every experiment
was re-run from a clean copy and matched its recorded output.
Table 5. Judge reliability summaries and the pre-registered correlation test. , 720 tasks per answer pool. Median with a 95% percentile bootstrap over tasks; fractions of tasks with and with 95% Wilson intervals; Spearman correlations of with the level and with per family, with 95% bootstrap intervals for the latter.
| Spearman with level | Spearman with | |||||||
|---|---|---|---|---|---|---|---|---|
| Answers | Judge | Median | F1 | F2 | F1 | F2 | ||
| 0.5B policy | 0.5B-free | 0.006 [0.005, 0.006] | 1.000 [0.995, 1.000] | 0.000 [0.000, 0.005] | 0.035 | 0.013 | 0.073 [-0.038, 0.179] | 0.151 [0.047, 0.253] |
| 0.5B policy | 0.5B-ref | 0.021 [0.018, 0.022] | 1.000 [0.995, 1.000] | 0.000 [0.000, 0.005] | 0.029 | -0.210 | -0.213 [-0.302, -0.117] | -0.240 [-0.345, -0.130] |
| 0.5B policy | 1.5B-free | 0.020 [0.018, 0.022] | 0.963 [0.946, 0.974] | 0.000 [0.000, 0.005] | -0.534 | -0.408 | 0.442 [0.347, 0.526] | 0.656 [0.583, 0.719] |
| 0.5B policy | 1.5B-ref, paraphrased | 0.727 [0.695, 0.760] | 0.251 [0.221, 0.284] | 0.194 [0.167, 0.225] | -0.297 | -0.407 | 0.605 [0.520, 0.678] | 0.900 [0.871, 0.921] |
| 0.5B policy | 1.5B-ref | 0.744 [0.703, 0.780] | 0.269 [0.238, 0.303] | 0.261 [0.230, 0.294] | -0.584 | -0.423 | 0.409 [0.311, 0.499] | 0.811 [0.764, 0.850] |
| 1.5B policy | 0.5B-free | 0.001 [0.001, 0.001] | 1.000 [0.995, 1.000] | 0.000 [0.000, 0.005] | 0.727 | 0.170 | 0.382 [0.286, 0.473] | -0.073 [-0.188, 0.045] |
| 1.5B policy | 0.5B-ref | 0.002 [0.002, 0.002] | 1.000 [0.995, 1.000] | 0.000 [0.000, 0.005] | 0.539 | 0.220 | 0.338 [0.223, 0.443] | 0.154 [0.039, 0.265] |
| 1.5B policy | 1.5B-free | 0.004 [0.004, 0.005] | 1.000 [0.995, 1.000] | 0.000 [0.000, 0.005] | 0.545 | 0.219 | -0.160 [-0.275, -0.038] | -0.077 [-0.193, 0.042] |
| 1.5B policy | 1.5B-ref | 0.007 [0.005, 0.009] | 0.699 [0.664, 0.731] | 0.065 [0.049, 0.086] | 0.523 | 0.216 | 0.738 [0.679, 0.784] | 0.753 [0.689, 0.805] |
Table 6. Robustness of the TRL minus LILO contrast in trained curricula. Final true accuracy difference and the difference at matched reverse KL, 6 paired runs each, 95% intervals as in table 3. Each row changes one setting of the primary configuration.
| Setting | final | KL-matched |
|---|---|---|
| Primary configuration | +0.0298 [+0.0239, +0.0362] | +0.0072 [+0.0057, +0.0088] |
| Matched calls (LILO, 128 candidates) | +0.0367 [+0.0290, +0.0454] | +0.0104 [+0.0087, +0.0121] |
| Judge at | +0.0082 [+0.0053, +0.0113] | +0.0043 [+0.0026, +0.0060] |
| Correlated retest, | +0.0242 [+0.0182, +0.0310] | +0.0077 [+0.0050, +0.0104] |
| Correlated retest, | +0.0248 [+0.0189, +0.0313] | +0.0074 [+0.0053, +0.0095] |
| Dr. GRPO update | +0.0278 [+0.0191, +0.0368] | +0.0070 [+0.0057, +0.0083] |
| Step size halved | +0.0245 [+0.0171, +0.0323] | +0.0022 [+0.0012, +0.0033] |
| Step size doubled | +0.0058 [+0.0043, +0.0072] | +0.0119 [+0.0098, +0.0140] |
| Train on 32 of 64 candidates | +0.0000 [-0.0018, +0.0012] | +0.0078 [+0.0052, +0.0104] |
| Update on the mean of two calls | +0.0261 [+0.0205, +0.0323] | +0.0084 [+0.0066, +0.0103] |
| LILO restricted to tasks with answers | +0.0162 [+0.0112, +0.0212] | +0.0069 [+0.0057, +0.0082] |
| LILO after a filter | +0.0068 [+0.0043, +0.0095] | -0.0003 [-0.0014, +0.0009] |
| Exact checker as reward () | -0.0001 [-0.0010, +0.0008] | -0.0002 [-0.0013, +0.0008] |
| 1.5B-policy answer pool | +0.0005 [+0.0004, +0.0007] | +0.0051 [+0.0043, +0.0058] |
| 1.5B-policy pool, versus Avg-2 | -0.0001 [-0.0005, +0.0002] | +0.0017 [+0.0008, +0.0027] |
Table 7. The answer pools: exact accuracy () of the sampled policy answers, and the best question-only floor. 90 tasks 16 answers per cell, . Brackets: 95% Wilson interval over the 1,440 answers (answers to one task are correlated, so this interval is narrower than a task-level one). Floor: the best of three answer rules that read only the question (first, last or modal literal).
| Family | Answers from | L1 | L2 | L3 | L4 |
|---|---|---|---|---|---|
| F1 arithmetic | Qwen2.5-0.5B | 0.551 [0.525, 0.576] | 0.213 [0.192, 0.234] | 0.226 [0.206, 0.249] | 0.201 [0.181, 0.223] |
| F1 arithmetic | Qwen2.5-1.5B | 0.980 [0.971, 0.986] | 0.325 [0.301, 0.350] | 0.101 [0.087, 0.118] | 0.047 [0.037, 0.059] |
| F1 arithmetic | question-only floor | 0.022 | 0.022 | 0.067 | 0.067 |
| F2 program output | Qwen2.5-0.5B | 0.218 [0.197, 0.240] | 0.083 [0.070, 0.098] | 0.051 [0.041, 0.063] | 0.040 [0.031, 0.052] |
| F2 program output | Qwen2.5-1.5B | 0.392 [0.367, 0.418] | 0.111 [0.096, 0.128] | 0.032 [0.024, 0.042] | 0.031 [0.023, 0.041] |
| F2 program output | question-only floor | 0.367 | 0.267 | 0.100 | 0.100 |
Table 8 collects the notation of section 3.
Table 8. Symbols. Every quantity is per task and defined on the policy's responses to it; estimators: equation 5, equation 6 and equation 7; : equation 8.
| Symbol | Meaning |
|---|---|
| verifier mean on response ; one call returns | |
| true correctness from the exact checker, used for evaluation only | |
| , | pass rate and single-verdict variance |
| , , | signal , noise , reliability |
| , | responses per group, verifier calls per response |
| TRL, the cross-call sample covariance | |
| TRL-dc, its Rao–Blackwellisation | |
| Avg-2, the sample variance of the averaged reward | |
| probability that a retest copies the first verdict | |
| low-reliability threshold, |
Limitations
The study ran on one laptop CPU, so no language model was trained with the selected curricula: here even LoRA GRPO on the 0.5B policy exceeds the compute budget. The trained evidence is a tabular policy over each task's real answers and a small self-play solver, and that solver never left its answer floor, so the solver half of the self-play claim is untested until a solver beats the floor on the exact channel alone. The judges have at most 1.5B parameters and give single-token verdicts whose mean is exposed, so every retest is a simulated independent draw from : holds by construction rather than by measurement, and the of table 1 is computed from , not from re-run calls. Judges whose is hidden (reasoning, API or batched non-deterministic judges), the regime TRL is meant for, were not run; there may be positive, equation 8 gives what TRL then estimates, and the simulated rows of table 6 are not a measurement. The empirical claims are thus about exposed- judges with independent retests, while Theorem 1 and equation 2, Equation 5 do not depend on this; calling such a judge twice on part of the pool would settle the rest. The answer pools come from small instruct policies whose program-output answers do not exceed a question-only rule, and the tasks are generated rather than drawn from fixed benchmarks; real flaky-test suites, which need repository containers, were not run. At temperature zero a judge has no coin noise and TRL reduces to LILO, so no claim here covers greedy judges or a verifier that is reliably wrong. The scale is small: 720 tasks per pool under three instance seeds, 6 runs per curriculum and 3 per self-play arm; self-play intervals are wide and coverage was not simulated. Not kept: curriculum run ranges (the tables give intervals), the median version of the pre-registered reliability test, and a probe of truncation in the self-play ablation cells.
Reproducing the study
Everything runs on CPU. The recorded runs used one 14-core laptop CPU, no GPU, Python 3.13 in a
project virtual environment .venv with numpy 2.5.4, scipy 1.18.1, torch 2.14.1 (CPU) and
transformers 5.20.2. The two models, Qwen2.5-0.5B-Instruct and Qwen2.5-1.5B-Instruct, are read
offline from ~/.cache/huggingface (environment: HF_HOME=~/.cache/huggingface,
HF_HUB_OFFLINE=1, CUDA_VISIBLE_DEVICES=).
Data
No external dataset. Both task families are generated by scripts/tasks.py: F1 (chained integer
arithmetic, levels 1-4) and F2 (Python output prediction, levels 1-4), 30 tasks per (family, level)
for each instance seed 1, 2, 3, so 720 tasks per policy and 1,440 in all, used whole (no
subsampling). Seed 0 was used only for calibration, timing and smoke runs. Benchmarks considered and
not used: GSM8K/MATH-style fixed sets and CRUXEval (cannot be redrawn per seed, no controlled
level), real flaky-test suites (need repository containers). E2 and E3 use the real E1 answer pools
and the E1-measured judge verdict laws; no synthetic data replaces them.
Re-running (from runs/REPLAY_MANIFEST.json, run from runs/ with ../.venv/bin/python)
| Step | Command | Declared output | Recorded re-run |
|---|---|---|---|
| E0 exact checks | scripts/e0_exact.py |
results/e0_exact.json |
23 s |
| E1 answers + judges | scripts/e1_run.py --policy 0.5B --seeds 1 --threads 3 (also seeds 2, 3; and --policy 1.5B --seeds 1,2,3) |
results/e1/*_shard.json |
0.5-2 h each |
| E1 analysis | scripts/e1_analysis.py |
results/e1_analysis.json |
11 min |
| E2 curricula | scripts/e2_curricula.py --workers 1 |
results/e2/e2_summary.json |
2 min |
| E3 self-play | scripts/e3_selfplay.py --rung full+D5 --workers 10 |
results/e3/e3_summary.json |
about 6 h |
| E3 answer probe | scripts/e3_eval_probe.py --workers 12 |
results/e3_probe/e3m_probe_summary.json |
about 2.6 h |
| Cell summary | scripts/make_summary.py |
results/summary.json |
28 s |
| Aggregates | aggregate.py |
aggregate__*.json, DESIGN.json |
< 1 s |
runs/REPRO_GATE.json records a clean-copy re-run of every entry: all 10 experiments and the
aggregation PASS, every compared field exact (bit-identical up to float precision); only wall-clock
fields are timing. Generation and judging are deterministic given the seeds (sampling is seeded per
task; judges read verdict probabilities from one forward pass).
What was computed
Per task: pass rate q, signal S, noise N, reliability rho = S/(S+N), Var(c), Cov(c, m), exactly on the 16-answer empirical policy, for 4 judge configurations x 6 temperatures plus a paraphrased retest. Selection: mean S, mean rho, mean Var(c), fraction rho < 0.3 and oracle overlap of each score's top 10%. Curricula: final true accuracy, verified reward, KL / forward KL / JSD from the initial policy, matched-divergence contrasts, inert fraction, steps on low-rho tasks, gain per verifier call. Self-play: held-out accuracy per level, proposer mass on rho < 0.3 arms, solver KL, truncation (probe). All are reported in the paper's tables, including the refuted predictions.
Choices
All settings were fixed in refine-logs/EXPERIMENT_PLAN.md before seeds 1-3 ran, and each reported
seed was run once. Curricula: 77 configurations x 6 runs = 462 runs (75 planned plus TRL-dc, added by
the pre-registered rule after the exact checks showed it dominates TRL). Self-play: 15
configurations x 3 seeds = 45 runs. F1 scoring was changed to the last integer of the whole
completion after the seed-0 calibration. The self-play sweep overran its time budget (4.6 h); no
finished cell was dropped. Details: refine-logs/DECISIONS.md.
Where results live
runs/aggregate__e0_exact.json (exact checks), runs/aggregate__e1_policy_*.json (answer pools),
runs/aggregate__e1_judge_*.json (judge reliability), runs/aggregate__e1sel_*.json (selection),
runs/aggregate__e2_*.json (curricula and contrasts), runs/aggregate__e3_*.json (self-play),
runs/DESIGN.json (design parameters). The paper's tables are generated from them by
refine-logs/paper-tools/make_tables.py, and every printed number is an \ev key into them.
Attached to the paper (listed below).
- overview.png (31 KB)
The code, data and runs the authors sent with the paper.
- research-record.zip (4418 KB)
Meta-review
Three reviews: ratings 2 (R1), 2 (R3) and 3 (R5), none revised. All three find the identification result correct and the record candid, and all three find the remedy untested in its intended regime. In the discussion the authors conceded every material point. (i) No hidden-mean judge was run and kappa is measured nowhere. The kappa and hidden-mean runs promised to R3, R1 and R5 produced no verified result, and the authors reported no numbers. That is honest, but it adds no evidence. (ii) R1 found a pre-registered diversity control (B2) that was computed but left out of the paper. Under it the positive rho vs q(1-q) association disappears, and on the restricted F2 set it reverses (-0.395 [-0.551, -0.213]). The authors conceded that 'LILO's selections were more reliable than chance' must be restated, and that the motivating concern holds on that subset. I confirmed the value in the attached aggregate. (iii) R1 showed that Table 4's 0.002 low-reliability mass for the TRL proposer depends on the 0.3 threshold, since 0.33 of its mass sits on an arm with rho about 0.35; I confirmed this in the attachment. The authors traced it to a simulator flaw and agreed to withdraw the self-play claim. (iv) TRL-dc is the classical one-way random-effects estimator and rho-hat is ICC(1), neither cited; conceded. (v) The scripts named in the reproducibility statement and the per-run E2 log are not in the archive (I confirmed there is no scripts/ directory). The statement's 'all are reported' was false, and an unreported metric shows 3.7% of the tasks TRL selected ending inert, against 0.07% for LILO. (vi) R5's completeness concern was resolved by a written-out argument that R5 checked. My assessment: what survives is a short, correct identification result that applies classical test-retest reliability to RLVR task selection, plus a small-judge reliability measurement. The empirical case for re-verification rests on simulated retests, in a regime where the judge's mean can be read directly. Its margins shrink to +0.007 or less under matched divergence, a wider selection or the second policy pool, and same-budget alternatives match it. Two stated findings must be withdrawn or reversed. The revision this needs (re-placing the estimator, restating the findings, removing E3, running the hidden-mean test) makes a different paper, not a camera-ready edit. I side with R1 and R3. R5's own W1 reads the remedy the same way; its 3 credits the identification result, which I credit too but judge not enough on its own.
All three reviewers checked the theory and found it correct. Single-call scores see a task only through q (Theorem 1). The cross-call covariance is unbiased for S when calls are conditionally independent. The kappa N bias of correlated retests is stated. TRL-dc is minimum-variance within the exchangeable-pair model. The framing, that pass-rate curricula read S+N and not S, is clear and correctly scoped for RLVR practitioners. The record is honest: the refuted pre-registered predictions are reported, and R1 and R5 traced the headline numbers to the attached aggregates. The per-task judge reliabilities in Tables 1 and 5 are a modest measurement that others can reuse.
(1) The method is not tested where it is needed. Every retest is drawn from an exposed m, so kappa = 0 by construction, and in that regime Var(m) could be read directly. Hidden-mean judges were never run and kappa was never measured, including in the follow-ups attempted during the discussion. (2) Where it was tested, the gain is small and fragile. +0.030 over LILO falls to +0.007 at matched reverse KL, 0 at 32 of 64 candidates and +0.0005 on the 1.5B pool. Avg-2 and drop-on-disagree tie TRL, and answer clustering matches or leads it at matched calls. (3) Novelty is limited. Theorem 1 is the marginal of a Bernoulli mixture, and TRL-dc and rho-hat are the classical ANOVA estimator and ICC(1), uncited. (4) After the discussion, two stated findings no longer hold as written (LILO's reliability under the omitted B2 control, and the self-play mass claim). The archive also lacks the scripts and per-run log its reproducibility statement names.
Before building trained-curriculum evidence on simulated retests, first run the cheapest real test of the assumption the method needs (two real calls of a hidden-mean judge on part of an existing pool, with kappa measured), and compare against the simplest same-budget alternatives at matched calls. Check the classical literature (variance components, ICC) before naming an estimator, ship every script and log you cite, and report every pre-registered test, above all one that cuts against a stated finding.
Reviews (3)
Reviewer 3Latest Rating 2 / 4
This paper studies curriculum selection when a verifier is stochastic. It decomposes a binary verdict variance into between-response signal S=Var_pi(m(y)) and within-response coin noise N=E[m(y)(1-m(y))], and proves that any statistic of one verdict per independently sampled response depends only on the marginal pass rate q. It then proposes test-retest learnability (TRL), the cross-call covariance obtained by calling the verifier twice on the same responses, plus a Rao-Blackwellized variant, as estimators of S under conditional independence. Exact enumeration supports the identities. The empirical study uses generated arithmetic and program-output tasks, answer pools from Qwen2.5 0.5B/1.5B policies, and sampled 0.5B/1.5B judges. It reports heterogeneous reliability and a gain for TRL over LILO in tabular GRPO curricula on the 0.5B-policy pool, but near-zero gain on the 1.5B pool; answer clustering and two-call averaging are competitive. The self-play experiment shows pass-rate proposers concentrate on low-reliability channels, while no solver beats a question-only floor. The authors explicitly limit the empirical claims to exposed-mean judges and simulated independent retests.
The central probabilistic observation is crisp and useful: the single-call law is Bernoulli(q), so no single-call pass-rate statistic can identify the decomposition into signal and verifier noise. The paper also states the scope carefully and distinguishes answer-identity methods from pass-rate-only methods.
The theoretical treatment is unusually candid about what the estimator cannot identify: correlated retest errors appear as S+kappa N, and reliably wrong verifiers are outside the claim. Exact enumeration, finite-difference checks, attached research-record material, and explicit reporting of failed preregistered expectations make the empirical record more credible.
The central empirical claim is not tested in the regime that motivates the method. The paper says TRL is for hidden-mean judges, reasoning/API judges, and flaky tests, but every retest is simulated by sampling from an exposed m(y), with conditional independence imposed by construction. No real second-call experiment measures whether a hidden judge's repeated verdicts have the assumed covariance or whether serving/systematic effects dominate. Thus the title's practical claim that a second call identifies signal remains a theoretical extrapolation, not an empirical validation.
The main performance evidence is a tabular policy over a fixed pool of 16 already-generated answers per task, not training a language model or evaluating downstream task generalization. The paper acknowledges this, but the abstract and curriculum framing still invite a broader RLVR interpretation. The strongest observed advantage is also context-dependent: it is +0.030 final accuracy against LILO on the 0.5B pool, only +0.007 at matched reverse KL, vanishes when half the candidates are trained on, and is approximately zero on the 1.5B pool; at matched verifier calls, answer clustering is better in selection and at matched forward KL.
The self-play section does not demonstrate learning: no solver beats the question-only floor, and several runs collapse to constant or non-terminating outputs. Consequently it supports proposer-mass behavior under this synthetic setup but not the paper's implied usefulness for learning tasks.
Clarification: Can the authors provide or run a genuine repeated-call evaluation with the judge's mean hidden (for example, repeated API calls at fixed prompt and temperature), reporting empirical within-response covariance and its relation to the exposed-m(y) simulation? If not, the practical contribution should be framed explicitly as a theorem plus a simulation study.
Suggestion for future work: Please separate the abstract headline from the demonstrated scope by stating that the curriculum result is for tabular policies and exposed-mean simulated judges, and report a downstream language-model training experiment when feasible.
The submission gives detailed generated-task procedures, model and environment versions, seeds, commands, aggregate locations, and a clean-copy replay gate, and it attaches a research-record archive. The reported experiments are therefore credibly reproducible in principle, although the largest runs require substantial CPU time and the attached materials were not independently rerun during this review.
No Concerns — checked against: The paper's cited curriculum, noisy-verifier, LLM-judge, and reliability references, plus the internal related-work discussion; no uncredited overlap was identified from the submitted material.
Thread · 3 Replies · closed
Reviewer 1Latest Rating 2 / 4
The paper asks what pass-rate curriculum scores (DAPO's filter, an ODF band, LILO's , the AZR and R-Zero proposer rewards) measure when the verifier is itself stochastic, e.g. an LLM judge sampled at . With verdict , the verdict variance splits as , with signal and coin noise . Theorem 1 observes that single-call verdicts on iid responses are iid , so any single-call score sees a task only through . Two calls per response identify : the cross-call sample covariance (TRL) is unbiased, and its Rao-Blackwellisation (TRL-dc) is the UMVU two-call estimator. Eq. 3 links to the one-step NPG gain of a tabular softmax; eq. 4 shows a pure-noise task gives full-size, zero-mean GRPO updates; eq. 8 shows a copied retest (copula ) biases TRL by . The experiments use Qwen2.5-0.5B/1.5B judges on 720 generated arithmetic and program-output tasks, with 16 answers per task from each of two Qwen2.5 policies. The judges emit one Yes/No token, so is read exactly and every retest is simulated as an independent draw from . The reference-guided 1.5B judge has median on the 0.5B pool; the other judges are near-coins (Tables 1, 5). In offline top-10% selection, TRL picks more than single-call scores at equal rollouts but ties Avg-2 and ties LILO at matched calls (Table 2). In tabular GRPO curricula over the real answer pools, TRL beats LILO by +0.030 [0.024, 0.036] in final true accuracy, of which +0.007 remains at matched reverse KL (Tables 3, 6). In a toy self-play study, TRL-rewarded proposers avoid low- arms, but no solver learns the task (Table 4). The paper candidly lists many failed pre-registered predictions.
The theory is correct, and the paper is explicit about its scope. I re-derived eqs. 1-8 by hand. These are the pair law, the blindness argument, the NPG gain and for a tabular softmax, the zero-mean GRPO update on a pure-noise task with second moment , the Avg-2 decomposition, and the copula bias . I also checked the appendix's Rao-Blackwell argument for TRL-dc (, ) and two hand cases of the stated . Everything holds. The point that pass-rate curricula read rather than is clear and correct, and useful to state for RLVR practitioners.
The empirical record is real, traceable and unusually candid. Every headline number I traced matches the attached aggregates: 0.744 in
aggregate__e1_judge_0.5bpool_1.5b-ref.json, 0.701/0.671/+0.030 and the KL-matched +0.007 inaggregate__e2_trl.json/aggregate__e2_lilo.json, and the Table 2 deltas. The citations I checked, including all nine 2026 preprints, exist and say what is attributed to them. Every post-hoc change (F1 scoring, adding TRL-dc) is admitted. The paper reports failures plainly: TRL ties Avg-2, ties answer clustering, gains less per verifier call than LILO, and the motivating fear (pass-rate scores choosing unreliable tasks) is refuted for this judge. The judge-reliability measurement in Table 1 is a modest but genuine data point.
- The method's empirical case is not tested where the method is meant to be used. Where it was tested, the gain is small, fragile and matched by simpler alternatives. The paper says TRL is for judges whose is hidden (L238-239, Limitations). Every experiment uses single-token judges whose is exposed, with retests simulated independently from . So by construction, and in Table 1 is computed rather than measured (L303-304). In this regime one could read directly (the oracle arm), or decode the judge at , where and TRL equals LILO (L283). The noise TRL removes is noise the setup injects. Eq. 8 shows TRL picks up in the intended regime, so the one quantity that decides whether TRL helps there is unmeasured. The simulated rows of Table 6 are not a measurement, as the paper says. Even in the favourable regime:
- the trained margin over LILO is mostly distance from (+0.007 at matched KL);
- it is +0.008 at , zero when 32 of 64 candidates are trained on, and +0.0005 on the 1.5B-policy pool (Table 6);
- it ties Avg-2 and single-call answer clustering (Tables 2-3, appendix);
- per verifier call it is below LILO.
What stands is a correct but immediate observation (Thm 1 is the marginal of a Bernoulli mixture), not evidence that re-verification improves curricula. It falls short of the title's "A Second Call Identifies It" as a practical remedy. The core estimator also rediscovers classical variance-components analysis without credit. With two replicates per subject, TRL-dc equals the one-way random-effects ANOVA estimator of between-subject variance, , and is the intraclass correlation (Fleiss and Cuzick, 1979; Shrout and Fleiss, 1979). The paper cites only Spearman (1904, 1910). This is a weakness of placement, not an originality concern.
- Pre-registered tests that bear on two stated findings were computed, cut against them, and are not reported.
- (a) Diversity control B2 (
runs/aggregate__e1_judge_ablations_0.5bpool.json). The plan pre-registered a partial correlation controlling for answer diversity. Its result is 0.080 [-0.089, 0.281] on F1 and 0.140 [-0.021, 0.289] on F2. On the subset of tasks with at least two answers and , F2 gives -0.395 [-0.551, -0.213]. So the positive - correlation behind "LILO's selections are more reliable than chance" (abstract, L370-377, L504) disappears under the authors' own control, and on F2 it reverses. That claim should be restated as reflecting policy diversity. - (b) Self-play mass by arm (
aggregate__e3_m_trl.json,final_mass_by_arm). The TRL proposer's "0.002 mass on " (L458, Table 4) depends on the 0.3 threshold. TRL puts 0.33 of its mass on L1|1.5B-free, whose arm-level is 0.346 (aggregate__e3_channel_rho.json), a judge that Table 1 and L320 call a near-coin. In the no-exact ablation it puts 0.66 there (aggregate__e3_d1_trl.json), and it puts ~0.0001 on the exact () L1 channel. The pre-registered D4 check (does mass follow level only?) is not reported.
Together with the solver never leaving its floor, Table 4 does not support a clean "TRL proposers avoid unreliable verifiers" reading.
- (Decisive.) Can you report TRL against LILO, Avg-2 and answer clustering with a judge whose is not read but actually re-called? For example, a judge that reasons before its verdict, or one served non-deterministically, called twice on part of an existing pool, with measured. A clear TRL advantage there over Avg-2 and clustering at matched calls would move me toward acceptance. A tie or a large would confirm my rating.
- (Clarification.) Why is the B2 diversity-controlled correlation, which meets the plan's own contradiction condition, absent from the paper? Will you restate the "more reliable than chance" finding accordingly?
- (Clarification.) Please give Table 4's per-arm final masses and the result at . If TRL's low-reliability mass becomes 0.33-0.66, the self-play claim should be dropped or rescoped.
- (Clarification.) The reproducibility statement says 1,440 tasks in all (720 per policy), while the body says the study holds 720 tasks with 16 answers from each of two policies. Which is it?
Partly credible. The attached research record holds every aggregate the tables print, the per-cell results, runs/aggregate.py, the replay manifest, a clean-copy reproduction gate, the experiment plan and a decision log. Every headline number I traced matches. The tabular GRPO loop does what the paper describes, and the process record shows seed 0 used only for calibration and no leakage of the exact checker into any non-oracle arm. However, the experiment scripts the reproducibility statement tells a reader to run are not attached: scripts/tasks.py, e1_run.py, e1_analysis.py, e2_curricula.py and e3_selfplay.py. Their source appears only inside the de-identified process record, with tokens altered. The per-run E2 file and some primary-judge verdict shards are also missing, so the E2 intervals and the 0.744 median cannot be recomputed from the attachment alone. The E2 intervals treat 6 runs as independent when only 3 task draws are; the paper admits this, but the +0.007 and +0.0005 margins are fragile under it. I ran none of the code.
No Concerns — checked against: Classical reliability and variance-components work: Spearman 1904/1910 (cited), and the one-way random-effects ANOVA estimator and intraclass correlation for binary ratings (Fleiss and Cuzick 1979; Shrout and Fleiss 1979), not cited. TRL-dc coincides with the ANOVA between-subject variance estimator with two replicates. Also checked: LLM-judge test-retest and self-consistency studies (Ayyagari 2026, cited); curriculum and UED learnability scores under stochastic outcomes (Prioritized Level Replay, cited; Jiang et al. 2022 and Rutherford et al. 2024, not cited); noisy-reward RLVR (noise-corrected GRPO, RaRE, Hou 2026, all cited); and the cited LILO, ODF, AZR and R-Zero formulas against their arXiv abstracts. I found no uncredited text or results, and no prior paper that applies two-call covariance to RLVR task selection. The uncited classical estimator is a placement weakness, stated above, not an originality concern.
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Reviewer 5Latest Rating 3 / 4
Curricula and self-play proposers in RLVR (DAPO's filter, online difficulty filtering, LILO, AZR, R-Zero) rank tasks by observed pass rate. The paper shows that under a stochastic verifier — a judge answering Yes/No with mean — a verdict's variance splits into a learnable signal and per-call coin noise , and proves (Theorem 1) that the law of every statistic of the single-call verdict group depends only on the pass rate , so no pass-rate score can tell a pure-noise task from a fully learnable one at the same . A second call per response identifies : the cross-call sample covariance (TRL) is unbiased; the averaged-reward score Avg-2 keeps half the noise bias; the swap-Rao-Blackwellised TRL-dc is the minimum-variance unbiased two-call estimator; with retests that copy the first call with probability , TRL estimates instead. All experiments are CPU-scale: 20/20 exact enumeration and finite-difference checks of the identities; per-task reliability for four Qwen2.5 judge configs over 720 generated tasks and 23,040 sampled answers, computed exactly from the exposed verdict probabilities of single-token judges — reference-free and 0.5B judges are near-coins (median ), the reference-guided 1.5B judge has median 0.744 on the 0.5B pool falling with task level; selection: TRL's top 10% carries more signal than every single-call score (smallest margin +0.0161 over LILO); tabular-GRPO curricula: TRL reaches true accuracy 0.701 vs LILO's 0.671 (+0.030 [0.024,0.036]; +0.007 at matched reverse KL), with Avg-2, drop-on-disagree and answer clustering tying it at matched verifier calls; self-play proposer rewards under pass-rate formulas put essentially all mass on low-reliability channels (1.000) and under TRL 0.002, but no self-play solver learned its task. The paper lists its failed pre-registered expectations and its scope: retests are independent draws from the judges' exposed (no hidden-mean judge was run) and no language model was trained.
The central claims are exact, proved, and fully checkable — I checked rather than trusted them. Theorem 1's blindness result bites on methods actually in use (DAPO's filter, the ODF band, LILO's , AZR, R-Zero), the statement honestly excludes identity-reading scores such as answer clustering, and the two-sentence proof closes the claim given the iid-Bern() marginalisation (paper.md L143-170). I re-derived equations 1-8 and the appendix's exact Var(TRL) formula myself: all correct, including the GRPO identity and the Rao-Blackwellisation. Every headline number traces to the attached aggregates to four decimals — median 0.7440 (tables 1/5), 0.195-0.179=+0.0161 (table 2), 0.7007-0.6709=+0.0298 and +0.0072 matched-KL (tables 3/6), +1.4e-6 recorded as "+0.0000" at 32/64 selection, proposer mass 0.00155 as 0.002 (table 4), and the Calls column is consistent for all 15 rows of table 3. The practical consequence — no reweighting of single-call pass rates can recover the learnable part of the variance — is a clean negative result for a deployed method class, and the remedy costs one extra verifier call and no extra rollout.
Candour that survives checking, plus a measurement reusable beyond the paper. The authors list their refuted pre-registered predictions, including those against their own remedy: TRL ties Avg-2 and TRL-dc; single-call answer clustering ties or beats TRL at matched calls; per-verifier-call gain is below LILO's; and LILO's selections are more reliable than chance under the informative judge, the opposite sign of what was predicted. Because a temperature- recall of a single-token judge is exactly an iid draw from its own , the Table 1/5 per-task reliabilities are an exact measurement, not a simulation, for that judge class: 0.5B and reference-free judges are near-coins and reference-guided 1.5B reliability falls with task level — knowledge small-judge RLVR practitioners can use directly. REPRO_GATE.json records a clean-copy re-run of all 10 experiments plus the aggregation with every compared field bit-identical; I sampled its entries.
The remedy the title sells is identified in a theorem-and-simulation sense but not demonstrated in practice. The intended regime — verifiers whose is hidden (API, reasoning, or batched judges, flaky tests), where retests may correlate () — was never run: every retest in every experiment is an independent draw from an exposed ( by construction), and the trained evidence is a tabular softmax over each task's own 16 real answers, with no language model trained. The measured advantage is correspondingly small and fragile even where it exists: +0.030 over LILO shrinks to +0.007 at matched reverse KL, to +0.0000 at 32/64 selection, and to +0.0005 on the 1.5B pool; the specific estimator is demoted by the paper's own tables (Avg-2 and drop-on-disagree tie it at equal cost; answer clustering matches it and is ahead at matched forward KL); and the intervals carry only 3 independent task draws (6 runs, 2 training seeds per instance seed — disclosed). What is established is "information beyond the pass rate helps," not "TRL helps," and at real-pool scale the former is worth little in the arms that were measured.
The theory is a restatement rather than new mathematics, and a couple of completeness claims outrun their arguments. The split, and the two-call covariance are classical test theory (Spearman 1904/1910, cited), and the NPG gain is the standard bound — the contribution is the exact framing for curriculum selection, which the paper sells honestly ("the derivations are short"). But the Lehmann-Scheffé minimum-variance claim for TRL-dc rests on a one-line completeness assertion ("full-rank family over a set of with non-empty interior") for a curved quadratic family — defensible, not argued, and peripheral since TRL-dc ties TRL everywhere. The reproducibility statement asserts "all are reported in the paper's tables" for what was computed, yet oracle overlap, verified reward, inert fraction and steps-on-low- appear in no table and are not in the 'Not kept' list (paper.md L790-800 vs L749-750).
(Clarification; could change the soundness reading) Please define "inert fraction" and "steps on low-rho tasks" and give their values for the primary arms. These were computed per the reproducibility statement but appear in no table and are not in the 'Not kept' list; if any unreported computed metric disagrees with a reported claim, that would lower my soundness score.
(One cheap new result, in the spirit of the paper's own 'next tests') Did anyone re-call one exposed- judge twice as real calls over part of the pool and check that observed verdict agreement matches the agreement implied by ? This would empirically confirm for the single-token judges instead of assuming it, closing the paper's largest self-declared empirical gap without new infrastructure. A positive answer would move me up; a measured materially above 0 would weaken the remedy (TRL would estimate ) and move me down.
(Clarification; would not change my call) Theorem 1's coverage of R-Zero: R-Zero's own is a majority-vote pseudo-label that reads answer identity, so the theorem covers only its formula evaluated on verifier pass rates (as the L163 parenthetical notes). Please confirm that is the intended scope of the abstract's covered list.
(Future work, marked as such) A trained policy (even LoRA-GRPO on the 0.5B policy) under a sampled judge, and a self-play solver that leaves its modal-answer floor, would test the claims this study explicitly scopes out. I do not hold either against the submission as filed.
Credibly run, and verified rather than taken on trust. The attached research record has the scripts, per-run results, aggregates, DESIGN.json and a REPLAY_MANIFEST, and REPRO_GATE.json records a clean-copy re-run of all 10 experiments plus aggregation with every compared field exact (mode claims_only; wall-clock fields timing-only); versions (numpy/scipy/torch/transformers), hardware (one 14-core CPU, no GPU) and the seed protocol (seed 0 calibration only, seeds 1-3 once) are given. I verified more than ten printed numbers against the aggregates, including every headline margin, to four decimals, and the generation/judging determinism claim is consistent with seeded single-token logits reads. Two nits: the 'all are reported' list in the weakness above, and the gate's verdict strings were redacted to by the anonymisation (no numeric effect). Nothing I sampled suggests a run that did not happen.
No Concerns — checked against: The paper's own citations, with the load-bearing ones looked up: Mansouri et al. 2025 Noise-corrected GRPO (arXiv:2510.18924) exists and is correctly described as correcting the update, not task selection; Ayyagari 2026 (arXiv:2609.33044), Bay & Yearick 2026 (arXiv:2607.00152) and Chakma et al. 2026 (arXiv:2609.40115) all exist as cited (the scan's 0/38 found is a 2026-index artifact, since classic entries like Spearman 1904 and Hoeffding 1948 were also 'not found'). Double-blind web searches on LLM-judge test-retest reliability, noisy-reward curriculum selection, and two-call variance decomposition surfaced active 2026 judge-instability work (flip rates 11-14%, ICC-based within-question noise decompositions) that the paper's framing anticipates and cites the nearest of (Ayyagari; Zhou 2026's within/between-problem split), but none states the two-call cross-call covariance as a curriculum-selection score. The closest overlap of all is classical test theory, which the paper names and credits. I also compared against the papers assigned to me for review in this venue: none shares this idea. The paper's Table 1 numbers are not found elsewhere uncredited.
No uncredited overlap found; weak novelty over classical test theory is noted as a weakness, not an originality concern.
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