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Under review as a conference paper at ICLR 2027

EMIT: Measuring the Reliability of Per-Prompt Decisions in RLVR Curricula

Abstract

Per-prompt controllers in reinforcement learning with verifiable rewards transform small groups of verifier outcomes into consequential training actions, yet the reproducibility and semantic fidelity of those decisions are rarely characterized. We introduce EMIT, a reliability-aware evaluation framework that treats adaptive curriculum control as a measurable decision process. EMIT formalizes exact-action reproducibility, connects difficulty concentration and decision boundaries to rollout requirements, and combines these predictions with source-traced implementation and verifier audits. Applied to frozen real-server rollouts, the framework reveals how sampling resolution and answer-format semantics govern controller behavior. A completion-token-matched multi-run study further shows substantial observed gains for both the released adaptive controller and a carefully tuned static curriculum over the no-curriculum reference. The adaptive controller attains the highest observed primary-task mean while closely tracking the tuned static curriculum across the broader suite. By making intermediate curriculum decisions auditable, EMIT provides a principled basis for reporting, sampling, pooling, and reliability-aware controller design.

Primary area:
reinforcement learning
Keywords:
reinforcement learning with verifiable rewards (RLVR), adaptive curriculum learning, large language model reasoning, decision reliability, verifier semantics, reproducibility, statistical evaluation

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_kwoBOpenReview ↗
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Paper summary

EMIT studies the reliability of curriculum decisions made from small groups of RLVR rollouts. The paper gives a probability-based account of how often a controller repeats the same action, tests it on frozen server outputs, and traces the behavior of a released hint-selection implementation. It also runs a five-seed comparison of the released adaptive controller, a tuned static hint schedule, and ordinary GRPO using a matched completion-token budget.

Critical strengths
  1. I like the decision-level perspective. Curriculum papers usually report the final benchmark score without showing how the examples were selected. Here the two-repeat action consistency criterion makes the instability near a decision threshold explicit. The released-selector audit is especially telling: changing the extractor takes maximum-hint decisions on Math-7B from 400 of 400 prompts to 319 of 400, using the same frozen outputs.
  2. I appreciate the comparison against a tuned static schedule. The five paired runs and common token cap give a much clearer picture of the controller's value than a comparison against GRPO alone.
Critical weaknesses
  1. The main question for me is what to do with the diagnosis. The reliability-based policy that would sample more near uncertain boundaries or pool decisions is presented as a design template. I would have liked to see this rule executed, at least by replaying stored rollouts. The current results establish that a controller can make unstable decisions, but I am left unsure how much better its decisions become when EMIT is used to change the sampling procedure.
  2. The end-to-end numbers also temper my enthusiasm for adaptive control. On MATH500, released SEELE scores 65.0 and the development-selected static schedule scores 64.7. The paired interval for the 0.3-point difference runs from -0.7 to 1.3. Both curricula comfortably beat plain GRPO, yet the adaptive part appears to add very little on this training setup. I see a useful diagnostic study here, with a less clear algorithmic payoff.
  3. There is a related ambiguity in the extractor experiment. A tolerant grader can recover legitimate answers that were missed by a strict parser, and it can also accept extraneous numbers or malformed reasoning. The change in hint distribution is compelling evidence of sensitivity, but I would like to know how many changed labels are actually correct.
Questions for authors
  1. Has the team inspected the strict-versus-tolerant disagreements for a sample of prompts? In particular, how many are genuine answers missed by the original extractor?
  2. Could the proposed reliability-aware sampling or pooling rule be run on the frozen rollout groups, with the resulting action stability reported alongside the extra number of samples it uses?
  3. There seems to be a white box covering part of Figure 3. Could the authors check and fix this?
6 comments
AuthorsOpenReview ↗

Official Response to Reviewer kwoB (Part 1/4)

Thank you for these concrete questions.

About Answer Recovery and the Verifier Guard

Has the team inspected the strict-versus-tolerant disagreements for a sample of prompts? In particular, how many are genuine answers missed by the original extractor?

We examined all 30 retained disagreements. AI-assisted answer attribution identified 29 explicit final declarations matching the reference, one incidental-number acceptance, and no unresolved cases.

The rubric counts an unambiguous final declaration matching the supplied reference as answer-level recovery. Appendix I (p. 19) reports the 25 boxed-present and five unboxed cases as branch exposure; the additional attribution is:

Retained stratumnExplicit reference-matching declarationIncidental-number acceptanceUnresolved
Boxed present252500
No boxed expression5410
Total302910

Examples include a final π4\boxed{\frac{\pi}{4}} matching reference π4\dfrac{\pi}{4}, and 72\boxed{72} matching 72 outside the shipped strict format. The audit follows final-answer exact-match criteria. The incidental-number case credits reference 2 from the denominator of C=3/2 without a declared answer 2.

Executed repair (E15). On the identical 30 tails, we disabled unanchored numeric fallback while preserving answer-tag/boxed priority, normalization, and exception behavior. Strict and current-tolerant replay each reproduce the retained labels in 30/30 cases; the guard matches the intended branch intervention in 30/30. These cases were selected as strict-wrong/tolerant-right, so strict zero is by construction.

ParserAcceptedExplicit recovery (AI-assisted)Known incidentalUnresolved (AI-assisted)
Released strict0000
Current tolerant302910
Tag/boxed-only guard262600

The guard retains 26/29 explicit recoveries and rejects the incidental-number case. The cost is three genuine numeric recoveries. All four numeric-accepting cases were included, making the repair's trade-off explicit on identical responses.

Branch assignment and answer attribution are separate. Current-tail branches are five answer-tag, 21 boxed, and four numeric. For 20 records the full-response path is attributable; for 10, earlier tags absent from the retained tail could change parser priority. Those 10 are not unresolved answer judgments.

The audit uses 1,200-character response tails and 300-character question prefixes: all 30 cases are at hint 2, with 22 distinct prefixes. The attribution method is AI-assisted final-answer exact match. These retained cases and the 400-prompt selector sweep are evaluated as distinct datasets.

Appendix I reports sensitivity to the disputed-stratum false-positive fraction f parametrically through a=t(1−fd)a=t(1-fd). The strict 400/400 maximum-hint result is independent of tolerant labels; Table 8's 319/400 is a ten-pass replay, distinct from Figure 4's single-map histogram. The audit identifies legitimate answer declarations missed by the strict format and a specific incidental-number failure that the guard removes.

AuthorsOpenReview ↗

Official Response to Reviewer kwoB (Part 2/4)

About Sampling, Resource Costs, and Pooling

Could the proposed reliability-aware sampling or pooling rule be run on the frozen rollout groups, with the resulting action stability reported alongside the extra number of samples it uses?

Yes. We executed sampling and pooling through the unchanged released five-action fit/regularize/invert/snap map (Appendix K). Appendix L separately evaluates the four-round state lifecycle.

Each of Qwen2.5-Math-7B (Math), Qwen2.5-3B (Qwen), and Llama-3.2-3B (Llama) supplies 400 prompts, five hint levels, and 16 stored responses/level, graded strict/tolerant. A/B repeats use disjoint groups of eight. Targeted sampling starts with four responses/level and adds four where Eq. (5) is closed (tau=0.5, kappa=0.9, lambda=1.5).

The random control receives exactly the same total top-up count per repeat and condition. We integrate fixed-count random allocation exactly: execute each prompt's 32 four/eight-sample masks through the released map, then weight the resulting actions. For N=2,000 cells and m top-ups, a particular five-level mask with k top-ups has weight C(N-5,m-k)/C(N,m). This preserves dependence between level allocations and avoids fitting at an averaged rate vector.

Model / verifierTargeted agreement %Expected random % (upper bound)Difference pp; nominal 95% lower boundSamples/prompt/repeat
Math / strict100.00<=100.00Agreement ceiling21.490
Math / tolerant75.00<=72.369>=2.631; L95>026.650
Qwen / strict92.00<=89.688>=2.312; L95>024.150
Qwen / tolerant85.25<=82.620>=2.630; L95>024.865
Llama / strict100.00<=100.00Agreement ceiling20.460
Llama / tolerant97.25<=94.821>=2.429; L95>022.235

L95 denotes the nominal 95% interval's lower endpoint. Intervals use 2,000 paired bootstrap resamples of 400 prompt clusters, retaining all levels and recomputing matched top-up counts. They concern the conditional expected-random baseline. The earlier realized-random contrast is separate: Math/tolerant +4.00 pp [0, 8.25].

Uniform8 uses 40 responses/prompt/repeat. On Math/tolerant, targeted uses 26.65 with 75.00% agreement, compared with Uniform8's 73.25% (original Figure 3, C=1-flip) and Uniform4's 70.25%. Mean selector completion tokens per prompt/repeat are <=19,000.033 for targeted, >=21,000.036 for expected-random, and >=30,000.030 for Uniform8. These are selector costs; all 80 cached outcomes/prompt also support holdout evaluation. Sample counts, selector completion tokens, and total training costs are distinct resource measures.

We also executed cell-based pooling: return hint 4 if any final level remains unresolved. Math/tolerant results are:

RuleAgreement %Max-hint %Entropy bitsBoth repeats nonpooled %
Targeted75.0057.751.681100.00
Targeted+pool490.0065.3751.50484.75
Constant4100.00100.0000

Pooling increases agreement while retaining action diversity and 84.75% both-repeat nonpooled coverage. Strict Math/Llama select maximum hint throughout, so their perfect agreement must be read alongside that concentration.

The 20-response pilot comparison gives +4.750 pp agreement and an independent score gain >=5.087e-3 for 6.65 extra responses on Math/tolerant, both with L95>0. Part 4 reports independent objective checks; the full pilot, per-prompt matched-budget, and histogram-controlled pooling comparisons appear in Parts 4-7 of our response to Reviewer 6e6B.

AuthorsOpenReview ↗

Official Response to Reviewer kwoB (Part 3/4)

About the Adaptive Increment

The original Table 2 reports the following across five paired Qwen2.5-3B runs (mean +/- sample SD, percentage points):

ArmMATH500
No-curriculum GRPO45.8 +/- 1.4
Development-selected static (4 to 4)64.7 +/- 0.9
Released SEELE65.0 +/- 0.7

The prespecified SEELE-minus-static effect is +0.30 pp, paired 95% CI [-0.70, +1.30], with paired d_z=0.40 (Section 7; Appendix H.4). Both curricula have large observed gains over GRPO. The static control isolates the additional adaptive comparison, and the paired interval reports its precision.

The comparator was selected from all 15 monotone schedules on 200 development groups and retrained from the base model for each confirmatory initialization. Test benchmarks were not used for selection. The shared resource axis is committed completion tokens; tuning and calibration overhead are accounted for separately in Table 7.

The additional response experiments execute selective sampling and pooling, with agreement, independent local objectives, and costs measured together. The original training comparison remains the estimate of downstream utility.

Reviewer_6e6BOpenReview ↗
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Paper summary

This paper introduces EMIT, a framework for evaluating the reliability of per-prompt decisions in reinforcement learning with verifiable rewards. It analyzes action consistency under finite rollout sampling, audits the effects of verifier semantics, and studies the released SEELE controller using frozen-policy rollouts. It also compares SEELE with a development-selected static curriculum and a no-curriculum baseline across five paired training runs under a common completion-token budget.

The paper raises a relevant concern: curriculum decisions based on small rollout groups may be unstable or strongly influenced by answer-format requirements. However, the current evidence does not sufficiently establish the practical consequences of the proposed reliability measurements or validate the resulting controller-design recommendations.

Critical strengths

Relevant research question. Examining the intermediate decisions made by curriculum controllers is worthwhile. The distinction between action repeatability, verifier validity, and downstream utility provides a useful perspective beyond final benchmark accuracy.

Informative implementation-level analysis. The SEELE case study shows that changing answer extraction on identical model outputs can substantially alter the selected hint distribution. This provides concrete evidence that verifier semantics can shape curriculum behavior.

Reasonable controls in the training comparison. The use of a tuned static baseline, five paired runs, a common completion-token budget, and paired confidence intervals strengthens the comparison relative to a single-run evaluation against an untuned baseline.

Critical weaknesses

The connection between decision consistency and training quality remains insufficiently established. Exact-action agreement measures repeatability, but disagreement near a threshold does not necessarily imply a consequential training error. Conversely, a constant controller can achieve perfect consistency without making useful adaptive decisions. The paper acknowledges this limitation, but does not provide sufficient evidence that its reliability measurements predict downstream performance, sample efficiency, or training stability. The frozen-policy diagnostics and training results are presented alongside each other without a convincing causal connection.

The downstream results do not establish a clear incremental benefit from adaptation. On MATH500, SEELE exceeds the selected static curriculum by only 0.3 percentage points, with a paired 95% confidence interval of [−0.7, +1.3]. This is a useful result, but it neither establishes equivalence nor shows that decision unreliability explains the limited observed difference. The repeated emphasis on the “highest observed primary-task mean” gives a small, uncertain difference more prominence than warranted.

Experimental coverage and validation of the proposed response are limited. End-to-end training is restricted to Qwen2.5-3B and one adaptive curriculum method. The additional controllers are primarily examined through rule-level analysis or frozen replay, which does not establish their behavior during evolving on-policy training. Moreover, the reliability-aware gate and allocation strategy are not evaluated in the reported training comparison. Consequently, the evidence supporting general controller-design recommendations remains incomplete.

The theoretical and methodological contribution needs stronger substantiation. Several central results follow directly from elementary binomial probabilities or threshold algebra. Their application is useful, but the broader contribution depends heavily on empirical validation. Equation (5) also uses a plug-in standard error that becomes zero when all sampled outcomes agree, allowing the gate to open even with very small samples. The manuscript does not establish a finite-sample reliability guarantee or adequately validate this boundary behavior.

Presentation needs improvement. Page 8 contains substantial whitespace and an awkward separation of Figure 4, the training discussion, Table 2, and Figure 5.

Questions for authors

What evidence shows that lower exact-action consistency leads to worse training outcomes, rather than reflecting uncertainty between similarly useful actions near a decision boundary?

Can the authors connect the measured reliability of SEELE decisions during training to its incremental performance over the static curriculum? In particular, how do action consistency and maximum-hint concentration evolve as the policy improves?

What reliability claim is intended for Equation (5)? How should the gate behave when the estimated standard error is zero because a small rollout group is entirely correct or incorrect?

Have the proposed reliability-aware gate or targeted allocation strategy been evaluated under the same resource budget? If not, which controller-design conclusions are empirically supported, and which should be treated as hypotheses for future work?

Addressing the concerns above, I will support an increase to 3/4

9 comments
AuthorsOpenReview ↗

Official Response to Reviewer 6e6B (Part 1/7)

Thank you for the concrete questions about practical consequences, matched controls and the gate's boundary behavior.

About Reliability, Training Utility, and the Tuned-Static Comparison

What evidence shows that lower exact-action consistency leads to worse training outcomes, rather than reflecting uncertainty between similarly useful actions near a decision boundary?

We address this with separate tests of local consequences and training utility. The G4 test finds reward-RMS gaps above the prespecified 5pp reference in four conditions, and the companion held-out score test evaluates the intended target-rate objective (Parts 5-6). The paired training study measures the adaptive increment against a competitive static curriculum. The local tests quantify consequences beyond an action flip; the paired training runs estimate the controller's incremental training utility.

Repeatability asks whether a fresh rollout group selects the same action. Section 2 separates this from semantic validity, informativeness and utility. Since a constant controller always repeats, EMIT reports these quantities separately.

The completed primary training comparison is:

ArmMATH500AMC23AIME24OlympiadGSM8KMinerva
GRPO45.80 +/- 1.4024.00 +/- 2.901.30 +/- 1.8015.00 +/- 0.8078.50 +/- 0.8017.30 +/- 1.50
Selected static64.70 +/- 0.9039.00 +/- 2.205.30 +/- 1.8028.30 +/- 0.5085.90 +/- 0.6025.70 +/- 0.90
Released SEELE65.00 +/- 0.7039.50 +/- 2.106.00 +/- 1.5028.30 +/- 0.6085.80 +/- 0.3026.00 +/- 0.80

Entries are exact-match percentages, mean +/- sample SD across five paired training runs (Table 2; Appendix H). MATH500 is primary; the other five benchmarks are prespecified descriptive checks. Static and SEELE gain 18.90 and 19.20pp over GRPO, respectively. The primary SEELE-minus-static effect is +0.30pp, paired 95% t interval [-0.70,+1.30], paired d_z=0.40. This paired contrast quantifies adaptation's increment over the selected static curriculum.

Static is selected from all 15 monotone level pairs on 200 development groups, then retrained from the base checkpoint for each confirmatory initialization. Test benchmarks do not select it. All three arms share the 21,607-row training pool, batch construction, 1.024B committed-completion-token cap and budget-based terminal checkpoint rule. All sampled responses in a committed batch count even if subsequently filtered; the final overshooting batch is rejected as a whole. Physical costs and shared static-selection overhead are reported separately (Appendix H; Tables 6-7). The comparison matches completion tokens; GPU-hours and tuning costs are reported separately.

Section 6.2 reports that maximum-hint selection declines as strict parseability rises across checkpoints. For a binary component, C=q2+(1−q)2C=q^2+(1-q)^2 falls as q approaches 1/2 and rises as it leaves, so C depends on the action-probability trajectory. Appendix L's frozen strict C is 1.000/1.000/.998, with ten-pass maximum-hint counts 400/400,400/400,395/400 (Llama/Math/Qwen). These support the extraction/action mechanism.

The new pilot comparison supplies a direct measure of return from extra evidence. On Math/tolerant, 6.65 extra responses give +4.750pp agreement and an independent U gain of at least 5.087e-3, both with nominal 95% lower endpoints above zero. Part 7 also fixes each prompt's response count to test hint-level targeting. Here C denotes action agreement, U the independent target-rate score, pp percentage points, and L95 the nominal 95% interval's lower endpoint.

AuthorsOpenReview ↗

Official Response to Reviewer 6e6B (Part 2/7)

About the Uncertainty Response and Its Evidence Budget

What reliability claim is intended for Equation (5)?

Eq.(5) supplies the Gaussian plug-in gate. The exact reference supplies a finite-sample certificate, with sign evidence, a future-rule consistency bound and an output/fallback status reported separately. It passes 2,144 count cases (n=1-64), seven reference boundary rows and 10 invalid-input checks.

With tau=.5, kappa=.9 and lambda=1.5, original Eq.(5) opens at counts 0 and G because its plug-in SE is zero. It opens for every G=1 outcome; at true p=.5 the resulting binary consistency is .5. At G=8 its opening counts {0,1,7,8} have probability 9/128 (approximately 7.031%) at p=.5. The exact reference retains an interval of nonzero width at unanimous outcomes and issues a certificate only when the consistency bound below reaches kappa. Otherwise it withholds the certificate, independently of the sign-gate output.

Fix future group size g, threshold tau and kappa before calibration. Let

C_g(p)=F_g(p)^2+(1-F_g(p))^2,\quad q=(1+\sqrt{2\kappa-1})/2.$$ An interval [L,U] certifies C_g(p)>=kappa if F_g(L)>=q or F_g(U)<=1-q. F_g is monotone, so on interval coverage its entire range lies on the required side; a false certificate implies noncoverage. For fixed-p iid Bernoulli outcomes, a two-sided 97.5% Clopper-Pearson interval has noncoverage <=.025 at each prespecified look. A union bound over n=4 and 8 gives false-certificate probability <=.05 for one fixed cell/repeat, including conditional top-up. The union bound accommodates dependence between the two looks, with the error budget defined per cell/repeat. The certificate concerns agreement between two new independent size-g groups of the specified ungated rule. At x=n=8, rounding the CP interval outward gives [0.578,1], certifying p>.5. Using the unrounded interval, the future g=8 consistency lower bound lies between 0.669 and 0.670; at x=0,n=8 it lies between 0.503 and 0.504. Both are below kappa. Sign confidence and consistency certification are separate outputs. The new exact budget check E16 shows that the n<=8 barrier extends beyond CP conservatism for fixed-n deterministic count-only certificates. At the three null witnesses p=.2,.5,.7, C_8(p)<.9. Exact rational enumeration of all 44 counts shows that for every count at n=1-8, some witness assigns it probability at least 5764801/100000000>.05. Any nonempty certificate set contains such a count and therefore violates uniform 5% false-certificate control at that witness. The result characterizes the fixed-n deterministic count-only certificate family. The CP reference scan also gives a feasible budget: its first all-correct certificate is 13/13 (lower C_8>0.908), and its first all-incorrect certificate is 0/21 (lower C_8>0.911), at per-look alpha=.025. These rows quantify the certificate's evidence budget. At the 4-to-8 cap no count certifies kappa=.9; the two-look CP sign-only reference also always uses eight. A fallback's repeatability is reported separately from adaptive efficacy. The binary control E1 uses 2,000 Math/tolerant prompt-hint cells (400 prompts, five levels), unresolved output 0, and 2,000 paired prompt-cluster bootstrap resamples. It always reaches 8 responses/cell. Gate-output agreement, both-open coverage and positive-action fraction are reported separately from the future-rule certificate and five-action selector. The matched-budget replay in Parts 4-5 evaluates Eq.(5)'s decision behavior; the separate certificate states what finite evidence can guarantee.
AuthorsOpenReview ↗

Official Response to Reviewer 6e6B (Part 3/7)

About the Measurement Contribution and Empirical Validation

Several central results follow directly from elementary binomial probabilities or threshold algebra.

The contribution is an executable evaluation procedure: predict a released rule's repeatability from finite verifier feedback, audit its numerical/state path, test verifier interventions, and measure adaptive utility against tuned static control. The probability identities make the procedure inspectable; empirical validation tests its usefulness.

Eq.(1) maps action probabilities to two-repeat consistency. Eq.(3) gives the all-same probability; Eq.(4) tests the observable chance that an independent second group reveals mixed outcomes after an all-same first group. The 16-response reference measures this observable event.

Under p=τ+σZp=\tau+\sigma Z with standard-normal Z, negligible boundary truncation and the local Gaussian acceptance approximation, Proposition 1/Eq.(2) gives

\rho^2=\frac{G\sigma^2}{\tau(1-\tau)}; \qquad G_\kappa=\frac{\tau(1-\tau)}{\sigma^2}\frac{r_\kappa}{1-r_\kappa},\quad r_\kappa=\sin[\pi(\kappa-\tfrac12)].$$ This explains the inverse-square dependence on difficulty width under the stated approximation. Exact finite-binomial calculations retain rounding/parity and the near-boundary worst-case floor (Section 3.2; Appendix J). Lemma 1 fixes 0<w<=1 and mu in [0,1] independently of the evaluated estimate. Thresholding $T(\hat p)=w\hat p+(1-w)\mu$ is equivalent to thresholding at $\tau'=[\tau-(1-w)\mu]/w$. A nonconstant threshold retains worst-case consistency 1/2; w=0 or an out-of-domain threshold makes the action constant. Rank buckets, moments and weights that depend on the evaluated data are treated separately: Appendix A gives a counterexample and Appendix B/Table 4 tests executed maps. Cross-fitting exceeds same-sample shrinkage in all five prespecified conditions; frozen-real cross-fit 95.426% exceeds raw 94.693% by about 0.73pp. | Condition | Same-sample C (%) | Cross-fit C (%) | |---|---:|---:| |Uniform|80.948|81.398| |Beta(2,2)|73.776|73.932| |Concentrated|57.481|58.156| |Bimodal|83.163|83.735| |Frozen real/tolerant|95.253|95.426| The raw comparison complements the same-sample control: Uniform raw consistency is 81.922% and cross-fit consistency is 81.398%, while frozen-real cross-fit improves over raw. Together, the controls characterize how shrinkage and data reuse affect the executed decisions. For empirical validation, each of 200 splits uses one prompt half to estimate difficulty and the other to measure A/B agreement: r=.997, MAE=0.260pp; eight prediction-side outcomes give r=.993, MAE=0.480pp (Section 4). This tests prediction across disjoint prompts. Eq.(4)'s conditional-reveal prediction also matches measurements within one percentage point on all three models (Section 3.3; Section 4/Figure 3). Appendices K-L execute released fitting/state paths. SEELE studies adaptive hinting and accuracy/optimization efficiency; EMIT evaluates repeatability, verifier-to-action effects and the increment over tuned static control. Table 1 and Appendix F document the rule provenance. Section 4 replays DAPO, SEELE, ZPPO and POPO rules on frozen outputs; the finite-action interface extends beyond binary thresholds. Parts 4-7 execute and independently evaluate a response. The results support specifying the executed unit/state, reporting agreement together with diversity, coverage and cost, auditing extraction, and measuring adaptation against a tuned static control. Four rule families and three frozen models validate the instrument; five paired Qwen2.5-3B runs assess training utility.
Reviewer_yegTOpenReview ↗
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Paper summary

Summary: This paper proposes a way of measuring and promoting the reliability and reproducibility of studies around the curriculum of the decisions used in per-prompt control of curricula during RL post training, directly interfacing and integrating with open-source codebases.

Critical strengths

Reproducibility and stability of RL post training is a critical issue both to the continued science of post training and for the ability to effectively apply these approaches in practice.

Critical weaknesses

My main concern with this work is that it is unclear and assume a significant amount of context from the reader which makes it difficult to concretely understand the formal framework or the empirical experiments. For instance, I don't know what semantic fidelity means in the first sentence of the abstract, but I cannot find that phrase again in the rest of the paper. There are claims elsewhere that the work "probes verifier semantics" but I also do not know concretely what this means, or what it means for EMIT to "evaluate semantic validity". Similarly I don't know what it means that it does this work with a "source-traced implementation"? Does this meant that there are stack-traces involved? Or is it just meaning that the work builds on the exact source code other works used?

I also do not understand what it means to treat curriculum control as a "measurable decision process?" When I search for this term I get redirected back to "Markov Decision Process", maybe this is not meant to be a technical term but if not then I do not know how to parse that sentence in the abstract. While this lack of clarity makes it difficult to follow the intro and abstract, it's much more concerning when it gets to the technical components of the work which makes it difficult to understand or evaluate core parts of the formalism and experiments.

Questions for authors

Could you please describe to me where my understanding of your work is incorrect or incomplete, and where in the paper you make this distinction clear?

3 comments
AuthorsOpenReview ↗

Official Response to Reviewer yegT (Part 1/2)

Thank you for asking us to clarify the terminology.

About the Measurement Object and Verifier Semantics

I also do not understand what it means to treat curriculum control as a "measurable decision process?"

EMIT tests the action selected for one prompt from finite verifier feedback. For SEELE, five empirical success rates enter the released fit/regularize/invert/snap map, which returns one of five hint levels (Section 2; Figure 1).

  1. What is the "decision process"? A model produces responses, a verifier assigns binary labels, and a controller converts these labels into a hint level or a keep/discard action. EMIT holds the policy, prompt, decoder, verifier and controller state fixed, obtains an independent rollout group, and checks whether the action repeats. The phrase describes this procedure; it does not introduce a Markov decision process or an additional RL objective.

Section 2 and Figure 1 specify the interface: a controller, independent rollout groups and a source/configuration record are the inputs; the outputs are action repeatability, sampling-model calibration, verifier sensitivity and matched downstream utility. The utility component comes from separate paired training runs.

Section 2 (pp. 2-3) defines qa(θx)=Pr⁡{R(DG)=a∣θx}q_a(\theta_x)=\Pr\{R(D_G)=a\mid\theta_x\}, where DGD_G is the finite rollout group and θx\theta_x collects the prompt-specific quantities used by the controller. Exact-action consistency is CR(θx)=∑aqa(θx)2C_R(\theta_x)=\sum_a q_a(\theta_x)^2: the probability that two independent groups produce the same action. This covers the full finite action set, including SEELE's five hint levels. Its generic lower bound is 1/∣A∣1/|A|, or 1/5 for five actions; the binary threshold's 1/2 floor applies to the binary case.

For a binary threshold, X∼Bin(G,px)X\sim\mathrm{Bin}(G,p_x), action 1 is selected when X≥⌈Gτ⌉X\ge\lceil G\tau\rceil. At G=8 and tau=0.5, counts 3 and 4 select different actions. At true p_x=0.5, exact two-repeat agreement is 17609/32768 (approximately 0.537) (Eq. (1); Corollary 1; Appendix A). This example isolates one binary component; the complete hint selector is evaluated through its executed five-action map.

  1. What were "semantic fidelity" and "verifier semantics" intended to mean? The intended question is which answer property the reward implementation actually measures. A response can contain a final answer in a boxed expression while failing the shipped reward's required <answer>...</answer> form. Section 2 therefore defines p_x as the probability of a positive label from the specified verifier. Semantic validity is audited separately.

Section 6.2 changes extraction on the same Math-7B outputs to test verifier-to-action sensitivity. Section 6.3 and Appendix I add format/content decomposition and branch analyses. Strict extraction serves its declared format constraint; the intervention measures its effect on actions. The tolerant extractor supplies a sensitivity condition, while Appendix I separates branch exposure from a correctness estimate. Our answer-attribution audit and executed parser guard are reported in Part 1 of the response to Reviewer kwoB, with the attribution method stated explicitly.

  1. Why is this useful alongside final accuracy? It makes response variation, finite-group sampling and answer extraction separately auditable at the action level. Independent groups test sampling variability; changing only extraction tests verifier-to-action sensitivity. These mechanisms can be hidden behind terminal benchmark scores. Section 2 treats repeatability, semantic validity, informativeness and utility as complementary axes. A constant controller has consistency 1; EMIT therefore reports agreement alongside action diversity and utility.

This label-to-action-to-repeat interface makes the evaluation explicit. EMIT predicts and audits executed decisions, tests a response to finite-sample variation, and measures incremental training utility against a tuned comparator.

AuthorsOpenReview ↗

Official Response to Reviewer yegT (Part 2/2)

About Source Tracing and the Empirical Evidence

Does this meant that there are stack-traces involved?

Source tracing means connecting the primary paper, configuration or launch script to the released code that chooses the action, including group size, tie convention and state lifetime. It does not mean collecting stack traces. Table 1 and Appendix F document the rule sources; Appendix K executes SEELE's released fit/regularize/invert/snap path; Appendix L follows its manager reset and dataset write-back lifecycle. Released-lifecycle and cumulative-state variants agree on 94.777% of 48,000 comparable decisions (Appendix L), showing that the state lifecycle affects measured actions.

Appendix K (p. 20) imports the released numerical fit, regularization and averaging code; Ray remote/get calls are made synchronous for offline execution. Its cross-check without regularization differs on 49/3,600 decisions at one-level snapping boundaries, so the selector results use the upstream path.

Frozen Uniform8 supplies eight outcomes at each of five hint levels (40/prompt/repeat). This single-map audit differs from training's four sequential G=8 rounds (32/prompt; Table 6). These checks make the action measurement reproducible, including fitting, snapping and state updates.

The original evidence addresses three questions:

  • Can the sampling account predict executed decisions? Section 4 tests frozen real-server rollout groups and separates prediction-side and measurement-side prompts. Across 200 disjoint-prompt splits, calibration is r=0.997 and MAE=0.260pp (0.26 percentage points), supporting the finite-sample account in the measured frozen regime.

  • Can the verifier change the curriculum on identical outputs? Under shipped strict grading, Figure 4 assigns maximum hint to 400/400 Math-7B and 400/400 Llama prompts. Changing only extraction broadens the Math-7B action distribution. Table 8 separately reports the ten-pass released-lifecycle replay, including 319/400 maximum-hint Math-7B actions with tolerant extraction. That ten-pass count is distinct from Figure 4's single-map histogram.

  • What incremental training value is observed? Five paired runs compare GRPO, a development-selected static schedule and released SEELE under a common completion-token cap. MATH500 means are 45.80 +/- 1.40, 64.70 +/- 0.90 and 65.00 +/- 0.70, respectively; +/- denotes sample SD across runs, in percentage points (Table 2). Static selection uses 15 candidate schedules and 200 development groups, without test-benchmark selection (Appendix H). The paired SEELE-minus-static effect is +0.30pp, 95% CI [-0.70,+1.30]. This estimates the adaptive increment separately from the overall curriculum benefit.

The additional replay executes a sampling response using the unchanged complete five-action map. Parts 4-7 of the response to Reviewer 6e6B report all three models and both verifiers, sampling costs, pooling, action concentration and exactly integrated random-allocation controls. On Math/tolerant, targeted sampling uses 26.65 responses per prompt/repeat versus 40 for Uniform8, with 75.00% agreement compared with 73.25% from original Figure 3 (C=1-flip). The agreement gain over exact expected-random allocation is at least 2.631pp, with the nominal 95% interval's lower endpoint above zero. Uniform8 provides a descriptive larger-budget reference for action agreement.

The independent tests connect sampled choices to local consequences: E10 selects with one half and scores with the other; E11 uses separate G4 decision and evaluation groups. In four conditions, the reward-RMS gap exceeds the prespecified 5pp reference with positive independent score-gap support (Part 6 of the response to Reviewer 6e6B). These tests concern decision-stage effects; paired training runs separately evaluate training utility.

Together, these studies support EMIT as a calibrated instrument for inspecting intermediate curriculum decisions, tracing implementation-dependent behavior and evaluating the adaptive increment against a tuned static control.

AuthorsOpenReview ↗

Official Comment by Authors

Dear Reviewer yegT:

Thank you for the time and care you devoted to evaluating our submission. Your comments on terminology, the formal framework, and the connection between implementation and experiments have helped us present the framework and its evidence more clearly. We appreciate your emphasis on making the work accessible to readers with different backgrounds, as well as your recognition of the importance of reproducibility in RL post-training.

Thank you again for engaging with our work and for considering our responses. We welcome any remaining questions or requests for clarification.

Best regards,

The Authors

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response

Thank you for the careful reviews. EMIT evaluates the decisions made between rollout collection and policy updates: whether a controller repeats its action, which implementation or verifier choices change it, and what a sampling response achieves at a stated cost.

The original study validates sampling predictions on disjoint prompts (r=0.997, MAE=0.260 percentage points), executes the released numerical and state paths, and tests extraction changes on identical outputs. The additional frozen-rollout experiments execute targeted sampling and pooling, with exact count-matched random controls and independent evaluation of selected actions. On Math/tolerant, targeted sampling raises agreement from the 20-response pilot's 70.25% to 75.00% using 6.65 extra responses per prompt/repeat; the independent target-rate score increases by at least 5.087e-3, with a positive nominal 95% lower bound. Per-prompt budget controls and concentration-matched pooling tests are reported in the replies.

The five-paired-run training comparison remains unchanged: MATH500 means are 45.80% for GRPO, 64.70% for selected static, and 65.00% for SEELE. The paired adaptive increment is +0.30 percentage points, 95% CI [-0.70, +1.30]. We distinguish this training estimate from the local decision effects above.

The reviewer-specific responses provide the protocols, costs, and results.

AuthorsOpenReview ↗

Author Summary for the Area Chair

EMIT provides a decision-level methodology with calibrated sampling predictions, source-faithful execution, controlled verifier interventions, an executable reliability response, and a five-paired-run training comparison. Its contribution is established by how accurately and usefully it evaluates curriculum control, with repeatability and final accuracy assessed separately.

The original finite-group predictions transport across disjoint prompts (r=.997, MAE=0.260pp). Source lifecycle choices change 2,507/48,000 decisions, and extractor changes on identical outputs alter the selected curriculum. These analyses identify sources of decision variation that terminal benchmark accuracy alone cannot expose.

The executed replay evaluates the reliability response at its action-repeatability objective. Exact count-matched allocation improves agreement by at least 2.248pp, with L95>0, in Math/tolerant, Qwen/strict, Qwen/tolerant, and Llama/tolerant. Here L95 denotes the nominal 95% interval's lower endpoint. Pilot and per-prompt matched controls separately measure the return from extra evidence and the benefit of choosing which hint levels receive it.

Independent evaluation gives the diagnosis practical meaning: the four G4 conditions have reward-RMS gaps above the prespecified 5pp reference, with positive independent score-gap intervals. Held-out target-rate scores also improve over globally matched random, Uniform8, and fixed4. Histogram-controlled pooling comparisons report joint positive agreement and score contrasts while controlling action concentration; coverage and diversity are reported alongside agreement.

On Math/tolerant, 6.65 extra responses over the 20-response pilot yield +4.750pp agreement and a U gain >=5.087e-3, both with L95>0. Fixing every prompt's sample count, hint-level targeting gains >=2.221pp agreement and >=4.569e-3 U in all four conditions, again with L95>0. These controls quantify decision-stage effects and sampling costs. The full protocols and results appear in Parts 4-7 of our response to Reviewer 6e6B.

The original training results show a large observed curriculum benefit in this setting: MATH500 means are 45.80% for GRPO, 64.70% for static, and 65.00% for SEELE. The tuned-static baseline measures what per-prompt adaptation adds. The paired adaptive increment is +0.30pp, with a 95% interval of [-0.70,+1.30]. Original data and resource accounting are retained.

Eq.(5) supplies the plug-in gate, and the exact reference supplies a finite-sample certificate with an explicit evidence budget. The answer-attribution audit identifies 29 reference-matching declarations, one incidental-number acceptance, and zero unresolved AI-assisted judgments. The structural guard rejects the incidental-number case and retains 26/29 explicit recoveries. The attribution method and audit protocol are stated in Part 1 of our response to Reviewer kwoB.

Together, these completed analyses provide an actionable evaluation framework with measured decision-stage effects, explicit sampling costs, a finite-sample certificate, and a paired training comparison.

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

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