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Under review as a conference paper at ICLR 2027

Recovery Thresholds for Idealized Best-of-N Retraining

Abstract

Repeated best-of- distillation changes the model distribution over time, so rare errors may persist and the proportions of correct answers may drift. We study when mixing a fixed reference distribution into each retraining round guarantees recovery of the desired distribution. When all correct answers share the same score distribution, we give an exact necessary-and-sufficient condition for removing incorrect answers, based on a rare-error multiplier that measures whether selection amplifies a rare error. This shows that pairwise verifier accuracy alone does not determine long-run recovery. When correct answers have different score distributions, recovery further requires selection to preserve the reference distribution. Under this condition, we prove matching upper and lower bounds showing that, for fixed , the worst-case reference weight needed for global recovery scales as , where measures score-distribution differences. We also give sufficient conditions for the general heterogeneous setting, with exact or approximate recovery depending on preservation error.

Primary area:
learning theory
Keywords:
Best-of-N distillation, iterative self-training, verifier-guided selection, distribution recovery, stability analysis

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_gUNvOpenReview ↗
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Paper summary

This paper investigates the recovery threshold for an idealized recursive best-of-N distillation process operating under a reference-mixing mechanism. Its primary contributions include: (1) establishing precise necessary and sufficient conditions for achieving recovery, based on the rare-error amplification effect; (2) deriving a stabilization threshold of Θ(δ2)\Theta(\delta^2) for heterogeneous scoring distributions, while ensuring the target distribution remains invariant; and (3) identifying sufficient conditions that enable both error elimination and stabilization. The findings are validated primarily through population-level simulations, supplemented by limited diagnostic analysis using scores from a public verifier. The study does not involve actual iterative model retraining.

Critical strengths
  1. Theorem 1 establishes an exact recovery boundary, improving upon generic contraction-based sufficient conditions. The result that high pairwise verifier accuracy does not guarantee recovery, especially as NN increases, is insightful and theoretically meaningful.
  2. The matching bounds and explicit nonconvergence constructions demonstrate genuine mathematical depth. The dependence of stabilization thresholds on score-distribution regularity is also an interesting contribution.
Critical weaknesses
  1. The main results rely on highly restrictive assumptions: fixed answer-conditioned score distributions, exact population fitting, and unconstrained categorical probabilities. These assumptions abstract away representation learning, optimization, and statistical generalization. Consequently, the theory characterizes stability of an idealized dynamical system rather than establishing how recursive distillation scales or generalizes in actual learning models. The appendix extensions do not sufficiently bridge this gap.
  2. The Θ(δ2)\Theta(\delta^2) threshold requires exact target preservation, a restrictive condition that fails in common score families. Its lower bound relies on increasingly oscillatory score distributions, while stronger regularity assumptions substantially change the threshold. Moreover, the dependence on growing NN remains unresolved. The limited empirical study does not reproduce the predicted error amplification on held-out data, and no actual retraining experiments demonstrate its relevance.
Questions for authors

Q1: Can meaningful scaling guarantees be established under approximate rather than exact target preservation, particularly when preservation error is O(δ)O(\delta) and NN grows? This would materially strengthen the significance of Theorem 2.

Q2: Can the proposed rare-error multiplier predict error amplification across real iterative retraining rounds? The current held-out experiments do not reproduce amplification, while the recursive simulations assume fixed score distributions.

4 comments
AuthorsOpenReview ↗

Response to Reviewer gUNv — Q1: Approximate Preservation with Growing N

Thank you for the detailed comments. We have added a new result on approximate preservation when NN grows, including an explicit tradeoff between the reference weight and the limiting bias.

Q1. Approximate preservation with growing NN.

“Can meaningful scaling guarantees be established under approximate rather than exact target preservation, particularly when preservation error is O(δ)O(\delta) and NN grows? This would materially strengthen the significance of Theorem 2.”

1. Global convergence under approximate preservation.

We have added Corollary 8 in Section 4.4, with a proof in Appendix B.10.

When exact preservation fails, qq is no longer a fixed point of the update, so exact recovery is generally impossible. We instead study convergence to a nearby fixed point pαp_\alpha and quantify its distance from qq.

Recall that δ=max⁡i,j∣Gi−Gj∣∞\delta=\max_{i,j}|G_i-G_j|_\infty measures score heterogeneity. Define the relative preservation error by

εrel=max⁡i∣SN(q)iqi−1∣.\varepsilon_{\mathrm{rel}}=\max_i\left|\frac{S_N(q)_i}{q_i}-1\right|.

Suppose all answers are correct, qq has full support, εrel≤Kδ\varepsilon_{\mathrm{rel}}\leq K\delta for a constant KK independent of NN, and 0<Nδ≤1/40<N\delta\leq1/4. Set

\qquad \alpha=\frac{2H}{1+2H}.$$ We prove that every trajectory converges to the unique fixed point $p_\alpha$, with $$\operatorname{TV}(p_\alpha,q) \leq\frac{K\delta}{4H} \leq\frac{\sqrt K}{4\sqrt N}.$$ The convergence is geometric, with $$D_{\mathrm{KL}}(p_\alpha\Vert p_t) \leq(1-\alpha/2)^{t-1}\log(2/\alpha), \qquad t\geq1.$$ In particular, if $N\to\infty$ while $N\delta\to0$, then both $\alpha\to0$ and $\operatorname{TV}(p_\alpha,q)\to0$. Thus, even with first-order preservation error, both the reference weight and the limiting bias can vanish. For example, when $N\asymp\delta^{-1/2}$, our sufficient reference weight is $O(\delta^{3/4})$, with limiting bias $O(\delta^{1/4})$. **2. Why first-order preservation error changes the threshold.** Proposition B.7 shows why a reference weight of order $\delta$ is not always enough to make the bias small. The proof uses a construction with just two answers. The construction starts from the CDFs $G_1(u)=u-2\delta u(1-u)$ and $G_2(u)=u+2\delta u(1-u)$ on $[0,1]$, with $q=(1/2,1/2)$. Their CDF diameter is exactly $\delta$, and $$\varepsilon_{\mathrm{rel}} =\frac{2\delta(N-1)}{N+1} =\Theta(\delta)$$ uniformly for $N\geq2$. Every trajectory converges, but the limiting bias satisfies $\operatorname{TV}(p_\alpha,q)\ge\frac14\min{1,(1-\alpha)\varepsilon_{\mathrm{rel}}/\alpha}.$ Hence, along sequences where $\alpha\to0$, vanishing bias requires $\alpha/\delta\to\infty$. This obstruction persists for smooth densities with uniformly bounded derivatives. It is a lower bound on recovery bias, not on the weight needed merely for convergence. **3. Dependence on growing $N$.** We have also made the dependence on $N$ in our bounds more explicit. Under exact preservation, the upper bound is $\alpha_{\mathrm{crit}}(N,\delta)\leq N^2\delta^2$ when $N\delta\leq1/4$. Our construction gives a lower bound of $N\delta^2/(3456\pi^2)$ for $N\geq3$, although it requires a more restrictive, $N$-dependent smallness condition on $\delta$. The bounds therefore do not yet match as $N$ grows. Corollary 8 establishes a sufficient scaling guarantee under approximate preservation, rather than an optimal joint threshold. We have stated this distinction explicitly in Section 4.4.
AuthorsOpenReview ↗

Response to Reviewer gUNv — Q2: Real Iterative Retraining

Thank you for raising this question. We tested the multiplier using real verifier scores, fresh Best-of-8 selection, and iterative LoRA retraining. We found selection-level amplification, but no consistent prediction across retraining rounds.

Q2. Rare-error amplification in real iterative retraining.

“Can the proposed rare-error multiplier predict error amplification across real iterative retraining rounds? The current held-out experiments do not reproduce amplification, while the recursive simulations assume fixed score distributions.”

1. Independent confirmation with real verifier scores.

As the reviewer noted, our original public-score experiment did not reproduce amplification on held-out data: none of the three error groups with calibration multipliers above one had a held-out estimate above one (Appendix F.5).

We therefore ran a separate GSM8K experiment with Qwen3-1.7B as generator and Skywork-Reward-Llama-3.1-8B-v0.2 as verifier. We selected two error groups from discovery data, then used 4,096 fresh responses per question for confirmation. For the candle question, the model reversed a “twice as many” relation and answered 80 instead of 50. At N=8N=8, its multiplier was 4.49, with a simultaneous one-sided 95% lower bound of 2.97, above the threshold 1/(1−α)=1.111/(1-\alpha)=1.11 at α=0.1\alpha=0.1. The second group involved a unit-scale mistake rather than a reasoning error.

2. Fresh Best-of-8 selection.

We fixed the forecasts before generating fresh candidates. In 512 independent races, the candle error won 174 times (34.0%), compared with a forecast of 28.5%, a random-selection baseline of 7.3%, and a pairwise-based baseline of 14.1%. The forecast passed the prespecified Brier-score comparisons against both baselines, though it underestimated the observed frequency by 5.5 percentage points. The second group failed the full selection criterion (Figure 2; Appendix F.6).

This confirms that a genuine reasoning error can have a supercritical multiplier and become enriched in fresh selection. Here, mjm_j describes the rare-error limit; the fresh-competition forecast instead uses the current-distribution weight Wj(p)W_j(p).

3. Actual iterative LoRA retraining.

We next ran three consecutive LoRA updates with three seeds and two reference weights fixed before training. Each round used 128 questions and two Best-of-8 competitions per question. We estimated the tracked error probability at each checkpoint using 512 samples per question and model state.

Change in candle-error probability from M0M_0 to M3M_3 (percentage points):

Seedα=0.643\alpha=0.643α=0.943\alpha=0.943No update
101+10.94−4.10−2.73
102+7.03+0.59−1.17
103−1.56+4.30+0.39

The prespecified cross-seed directional criterion was not met: at the lower weight, the error increased in two seeds and decreased in one; at the higher weight, it also increased in two seeds and decreased in one. The no-update control showed nonzero estimated changes. We therefore found no consistent evidence that the multiplier predicts error-probability changes over three retraining rounds.

Answer-conditioned score distributions also changed substantially. Under the lower weight, estimated multipliers moved from 4.57, 4.88, and 4.28 at M0M_0 to 0.66, 1.03, and 0.44 at M1M_1. We also observed degradation under reference-only fine-tuning, without incorrect winners in its targets. This suggests that selection alone does not explain the neural training dynamics, although these diagnostics do not identify a single cause.

4. Interpretation and scope.

The experiments confirm selection-level amplification with real verifier scores, but not reliable prediction across LoRA retraining rounds. Finite winner samples, shared model parameters, and changing score distributions can make training differ from the idealized population update. Appendix H.3 gives guarantees for time-varying scores and bounded fitting errors under a uniform subcritical margin, but we have not established these conditions for our trained models. We clarified this distinction in Section 6. Predicting neural retraining from score-based multipliers remains open.

I appreciate the authors' effort in addressing my concerns. Q1 is partially addressed but conditions remain restrictive; Q2 confirms the theory does not generalize to retraining. I will keep my score of 2.

AuthorsOpenReview ↗

Response to Reviewer gUNv — Scope and Theoretical Contributions

Thank you for the follow-up. We would like to clarify the scope of our work and the motivation behind its assumptions.

1. Scope and motivation of the model.

Our paper is a theoretical study of the population-level dynamics induced by repeated Best-of-N selection and reference mixing. We aim to understand when selection amplifies rare errors and when it destabilizes the proportions among correct answers.

We deliberately isolate the selection mechanism. Independent candidate and score draws define the Best-of-N winner distribution. Fixed answer-conditioned score distributions make the population update autonomous, allowing us to characterize its long-term behavior. Free categorical probabilities and exact population fitting separate selection effects from representation learning and optimization. This allows us to identify instability caused by selection alone.

Some assumptions also follow directly from our recovery objective. In particular, exact target preservation, SN(q)=qS_N(q)=q, is necessary for convergence to qq. Indeed, if pt→qp_t\to q, continuity of the update implies that qq must be a fixed point. For 0<α<10<\alpha<1, this requires SN(q)=qS_N(q)=q. Thus, this condition is mathematically necessary, not merely a technical convenience.

We also do not impose the common-correct-score assumption throughout the paper. It is used for the exact characterization in Theorem 1. Our subsequent results address heterogeneous score distributions. In particular, Theorem 5 gives a joint sufficient condition for recovery without requiring identical score distributions among correct or incorrect answers.

2. Theoretical extensions.

The paper also studies how recovery guarantees depend on the properties of the score distributions.

Theorem 7 shows that stronger regularity assumptions can substantially improve the stabilization threshold. With uniformly bounded density derivatives on a fixed score interval, the threshold is cubic in δ\delta for N=2N=2. For each fixed N≥3N\geq 3, every positive reference weight guarantees recovery when δ\delta is sufficiently small.

We also go beyond exact target preservation. In the all-correct setting, Corollary 8 establishes convergence to a unique fixed point under approximate preservation, with an explicit bound on its distance from the target. In particular, when the relative preservation error is at most KδK\delta, with KK independent of NN, both the reference weight and the limiting bias can vanish as N→∞N\to\infty and Nδ→0N\delta\to0.

Proposition B.2 further gives stability bounds under imperfect preservation and inexact updates for heterogeneous correct-answer scores. Proposition H.2 extends the analysis to time-varying score distributions and bounded fitting errors under a uniform subcritical margin in the common-correct-score setting.

Together, these results characterize how selection dynamics depend on score heterogeneity, distributional regularity, and deviations from exact preservation.

In particular, we believe that the exact recovery characterization, the matching worst-case stabilization bounds for fixed NN, and the extensions to regular score distributions and approximate preservation constitute a substantial contribution to the theory of iterative Best-of-N retraining.

Thank you again for your time and careful assessment. Your questions have helped us strengthen our analysis of approximate target preservation and clarify the scope of our theoretical results. We sincerely appreciate your thoughtful comments and the time you have taken to help us improve the paper.

Reviewer_VppeOpenReview ↗
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Paper summary

The paper presents exact population retraining on a mixture of best-of-N winners and a correct reference distribution. It proves a necessary-and-sufficient recovery boundary under common correct-score laws, matching quadratic stabilization thresholds under preserved heterogeneous scores, and joint sufficient conditions for error removal and proportion recovery. Population recursions and public verifier-score diagnostics illustrate the mechanisms.

Critical strengths

The rare-error multiplier provides an exact global recovery boundary, including the critical case and convergence rates, rather than merely a sufficient contraction condition. The examples with equal pairwise accuracy make clear why verifier accuracy alone cannot determine recursive recovery when N ≥ 3, offering useful insight into iterative distillation. The heterogeneous-score analysis is also substantial. It distinguishes eliminating incorrect answers from recovering the desired proportions among correct answers, establishes matching quadratic bounds for fixed N, and explains how those bounds change under normalized density regularity. The global convergence proof and the construction of instability using realizable scalar-score distributions strengthen the contribution beyond what a local linearization would establish.

Critical weaknesses

The main limitation is the gap between the idealized dynamics and practical retraining. The analysis assumes unrestricted answer probabilities, exact population fitting, and stationary, independently redrawn scores, leaving general finite-sample optimization, deterministic or correlated verifier scores, and verifier drift outside the established guarantees. Exact target preservation is also restrictive, particularly for common location-shift score families. Moreover, the stabilization threshold depends strongly on score regularity: the quadratic lower bound relies on increasingly oscillatory distributions, while smoother classes yield different thresholds, without an empirical diagnostic identifying the relevant regime. The bounds also lack matching dependence on growing candidate count, limiting quantitative guidance for test-time scaling. Finally, the real-score study covers only two GSM8K questions, and none of the three selected above-one subtype estimates replicates on held-out data; the frozen-histogram experiments therefore illustrate the theory rather than demonstrate failure in actual iterative retraining.

Questions for authors

Can measurable score diagnostics distinguish the oscillatory worst-case regime from the normalized regular-density regime, thereby identifying which stabilization threshold is relevant? How informative are the current upper and lower bounds when N grows with decreasing heterogeneity, rather than remaining fixed? What quantitative uncertainty remains in the required reference weight? What empirical conclusion about rare-error amplification is supported beyond the frozen-histogram illustration?

3 comments
AuthorsOpenReview ↗

Response to Reviewer Vppe Part 1/2 — Q1–Q2

We thank the reviewer for the thoughtful questions. We have added theoretical results and new experiments in the revised manuscript, and explain the main findings below.

Q1. Distinguishing the two regularity regimes.

“Can measurable score diagnostics distinguish the oscillatory worst-case regime from the normalized regular-density regime, thereby identifying which stabilization threshold is relevant?”

We found that the CDF distance δ\delta alone cannot distinguish the two regimes. Our quadratic lower bound uses densities that oscillate increasingly rapidly as δ\delta decreases. Theorem 7 shows that the required reference weight can be much smaller if we rule out such oscillations.

Specifically, under a fixed score scale and uniformly bounded density derivatives, the worst-case threshold improves from Θ(δ2)\Theta(\delta^2) to Θ(δ3)\Theta(\delta^3) for N=2N=2. For each fixed N≥3N\geq3 and any fixed positive reference weight, recovery is guaranteed once δ\delta is sufficiently small.

We also studied which assumptions can be checked from data (Appendix H.5). Lemma H.4 shows that a uniform CDF estimation error of at most ρ\rho gives an error of at most 2ρ2\rho in δ\delta and at most N2ρN^2\rho in the selection weights and preservation error. These quantities can therefore be estimated with confidence bounds.

The density-derivative assumption is different. We show that highly oscillatory densities can be statistically indistinguishable from smooth ones at any fixed sample size. Thus, although we can estimate the relevant CDF-based quantities, we cannot reliably identify the regular-density regime from finite samples alone. Applying its stronger threshold requires additional assumptions about the verifier.

Q2. Bounds when N grows.

“How informative are the current upper and lower bounds when N grows with decreasing heterogeneity, rather than remaining fixed?”

We derived explicit bounds that remain valid when NN grows as δ\delta decreases. Under exact target preservation, we obtain

\qquad (0<N\delta\leq1/4).$$ In particular, this gives a vanishing sufficient reference weight whenever $N\delta\to0$. For the lower bound, we obtain $$\alpha_{\mathrm{crit}}(N,\delta)\geq \frac{N\delta^2}{3456\pi^2},$$ for $N\geq3$ and $\delta\leq2/K_*(N)$, where $K_*(N)>4N(N-1)$. The bounds differ by a factor of order $N$ where both apply, and the lower bound requires a more restrictive range of $\delta$. Closing this gap remains open (Section 4.4). We also extended the analysis to approximate preservation (Corollary 8). Suppose the relative preservation error is at most $K\delta$, with $K$ independent of $N$. When $N\to\infty$ and $N\delta\to0$, we give an explicit choice of $\alpha\to0$ such that every trajectory converges to a fixed point $p_\alpha$ and $\mathrm{TV}(p_\alpha,q)\to0$. This is approximate rather than exact recovery. Proposition B.7 shows why the distinction matters: even with only two correct answers and preservation error of order $\delta$, vanishing bias can require $\alpha/\delta\to\infty$.
AuthorsOpenReview ↗

Response to Reviewer Vppe Part 1/2 — Q3–Q4

Q3. Uncertainty in the required reference weight.

“What quantitative uncertainty remains in the required reference weight?”

In the common-correct-score setting, Theorem 1 gives the exact population condition (1−α)m∗≤1(1-\alpha)m_*\leq1. Thus, the critical reference weight is

α∗=max⁡(0,1−1/m∗)\alpha_* = \max(0, 1 - 1/m_*)

for m∗>0m_*>0. The uncertainty comes from estimating m∗m_* rather than from the population characterization. Lemma H.4 bounds how errors in the estimated score CDFs affect the multipliers. If the estimated CDFs have uniform error at most ρ\rho, then each multiplier satisfies

∣m^j−mj∣≤N2ρ.|\widehat m_j-m_j|\leq N^2\rho.

If all relevant error types are covered, the same bound holds for m∗m_*. Let f(m)=max⁡(0,1−1/m)f(m)=\max(0,1-1/m) for m>0m>0, with f(0)=0f(0)=0. We then obtain

f((m^∗−N2ρ)+)≤α∗≤f(m^∗+N2ρ)f((\widehat{m}_{\ast}-N^{2}\rho)_{+}) \leq \alpha_{\ast} \leq f(\widehat{m}_{\ast}+N^{2}\rho)

where x+=max⁡(x,0)x_+=\max(x,0). Combined with standard CDF confidence bands, this gives finite-sample bounds on the required reference weight. Although the N2ρN^2\rho bound is conservative, it shows why estimating the threshold becomes harder as NN grows. Our public-score experiments illustrate why estimating the full multiplier is useful. At α=0.1\alpha=0.1, all 140 pooled multiplier estimates have pointwise 95% bootstrap intervals below the recovery threshold 1/(1−α)1/(1-\alpha). In contrast, bounds based on pairwise accuracy alone straddle this threshold in 94 of 140 cases (Appendix F.3). These intervals describe uncertainty for the measured error groups. They do not certify the maximum over all possible errors, especially those rarely observed. For heterogeneous correct scores, our stabilization bounds are also worst-case guarantees rather than exact thresholds for an individual verifier.


Q4. Evidence beyond frozen-histogram simulations.

“What empirical conclusion about rare-error amplification is supported beyond the frozen-histogram illustration?”

We added a GSM8K experiment using Qwen3-1.7B as the generator and Skywork-Reward-Llama-3.1-8B-v0.2 as the verifier (Section 5, Figure 2, Appendix F.6). Unlike the frozen-histogram simulations, this experiment uses independently generated responses to test both the rare-error multiplier and actual best-of-8 selection. We selected two error groups from 24,576 discovery responses and then evaluated them on fresh data. At N=8N=8 and α=0.1\alpha=0.1, both groups had confirmed multipliers above the theoretical threshold 1/(1−α)=1.1111/(1-\alpha)=1.111.

ResultCandlesMortgage
Discovery multiplier4.8244.223
Confirmation multiplier4.4864.531
95% lower bound2.9663.013
Forecast win rate28.5%23.0%
Observed win rate34.0%17.2%
Selection testPassedFailed

We used 4,096 fresh responses per question to confirm the multipliers, followed by another 4,096 responses per question for 512 independent best-of-8 races.

The candle group represents a genuine reasoning error: the model reverses a “twice as many” relation and answers 80 instead of 50. This error appeared in 7.3% of the original responses but won 174 of 512 fresh races (34.0%). It also passed the prespecified selection test against both random and pairwise baselines. The observed win rate was 5.5 percentage points higher than predicted, so the multiplier does not provide an exact quantitative forecast. The mortgage group also had a confirmed supercritical multiplier, but its observed selection rate did not pass the prespecified test.

The earlier public-score experiment remains a separate negative result: none of its three above-one calibration groups reproduced an above-one estimate on held-out data (Appendix F.5). These results show that rare-error amplification can occur under real verifier scores and fresh best-of-N selection. They do not establish whether such amplification persists across actual retraining rounds.


Thank you again for your thoughtful questions and suggestions. They helped us clarify our theoretical results and better explain what our experiments show. We hope the revised manuscript addresses your concerns, and we would be happy to discuss any remaining questions.

Reviewer_VppeOpenReview ↗

Response to author

Thank you for the detailed response and the new theoretical and empirical results. The explanation of why finite score samples may fail to distinguish the two regularity regimes addresses my first question. The explicit bounds for growing NN and the finite-sample interval for the critical reference weight also clarify the theoretical guidance, though the upper and lower bounds still differ by a factor of order NN where both apply.

My main remaining concern is whether the amplification observed during selection persists through retraining. The Candles result demonstrates that a rare reasoning error can be amplified in a fresh best-of-8 selection experiment with a real verifier. Given that Mortgage did not pass the prespecified selection test, it remains unclear how broadly this effect occurs, or whether fitting to the selected responses increases the error’s frequency in subsequent rounds. Do you have evidence from even a small multi-round retraining experiment that tracks the error frequency on freshly generated responses after each update? If that experiment is outside the scope of this revision, I would encourage the manuscript to state explicitly that the empirical evidence supports single-round selection amplification, while the multi-round conclusions follow from the idealized population dynamics.

Reviewer_TBAYOpenReview ↗
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Paper summary

The paper studies a model in which best-of-N is viewed as a retraining/distillation step (i.e. the outputs could be used to come up with the next model). In this setting, one could therefore add in the reference distribution to regularize the potentially multi-step re-training process: I would compare this concept to e.g. the reference distribution in DPO, a distant cousin. In this model, the paper shows that under some assumptions on the score distributions, there is an exact characterization of when the process will recover the reference distribution in the limi --- where the criterion depends on the mixture weight of the reference distribution (naturally) and on quantities that the authors dub "rare-error multipliers" of incorrect candidate answers. This quantity essentially reflects the thought experiment where this candidate response beats many correct candidates. Secondly, the paper also shows, under some different assumptions, that in the toy setting where all answers are correct, but all possibly have differently-distributed scores, the minimax mixture weight for the reference distribution must be on the order of squared error term in order for the retraining dynamics to converge to the reference distribution as opposed to oscillating around the space of other possible distributions on all the correct outcomes.

Critical strengths

I believe this paper represents a substantial mathematical effort that clarifies some --- though far from all --- convergence/recovery regimes of re-training/best of N dynamics in the presence of a mixed-in reference distribution. In particular, to a substantial extent, the authors have made an effort to derive assumptions/criteria that would be "distribution-free" in the sense of not requiring particular a shape or tail behavior of the score distributions but rather more general conditions such as homogeneity/heterogeneity of the individual score distributions. (Of course, eventually one does have to specialize somehow ---- e.g. for some constructive parts of the statements/proofs, one does need to construct suitably particular CDFs.)

More on the topic of the mathematical substance being a strong suit, the needed arguments dealing with both rotational terms and "dissipative" ones are far from trivial, and besides carrying them out, the authors have also made a decent expository effort in explaining some key steps in the main part of the paper.

Critical weaknesses

In terms of critical weaknesses taken literally --- None. The paper is reasonably well-written and so can be parsed by (human) readers without too many issues. The mathematics appears to be correct so far as I've checked. A proper, if minimal, comparison to related literature has been done.

In terms of subtler points that I consider weaknesses, there are a couple:

First, the various geometry-influencing choices in the theorems/proofs would have been good to clarify. For a simplest example, several different notions of distance are in circulation: thus, some are measured in TV distance, such as convergence in Theorem 1, but some are measured e.g. in CDF-L-infinity norm, such as heterogeneity in Theorem 2. Due to the delicate nature of the derivations, I was not able to clearly see how robust the recovery rates, thresholds, and characterizations are to different choices of geometries --- I suspect that the qualitative picture would stay similar but the quantitative aspects would shift, and had hoped that this would be worked out at least in a dedicated appendix.

Second, while the exposition is generally quite good, it's not always ideal. For instance, Sections 3 and 4 just get "plunged into", as opposed to somehow more explicitly explaining/executing the flow of "statements, then proof outlines". Moreover, for some of the material, I wonder if it could be mathematically simplified for the reader's benefit --- for instance, in Section 4.3, the definitions of h_i(u) are quite ugly, with multiple numerical coefficients, so I wonder if the same point could be gotten across with a more frugal example.

Questions for authors

I would specifically invite the authors to improve both the exposition of the manuscript, in general, and also to spend more effort justifying the usefulness of this setting and its connections to other related retraining-style settings in the LLM literature. Currently, there is an appendix G in which the comparison with the closest related paper (Zhao et al, 2025) is crammed, but that should be brought back out, in a substantial way, into the main part, as well as generally motivating the setting of mixing in the reference distribution more broadly beyond the current best of N setting --- and motivating other aspects that the readers may find critical for assessing the contributions' broader interest, such as why jumping around among the all-correct choices is even an issue to eliminate.

3 comments
AuthorsOpenReview ↗

esponse to Reviewer TBAY (1/2): W2 & Q1, Presentation, Motivation, and Related Work

Thank you for your detailed comments and helpful suggestions. We have revised the presentation, motivation, and related-work discussion in response to your review. All references below are to the revised manuscript.

① [W2 & Q1] Improving the exposition, simplifying the example, and explaining the motivation and relation to prior work.

(1) Proof organization. We have revised the openings of Sections 3 and 4 to explain the main arguments before the technical details. Section 3 (p. 5) now shows how the local rare-error multiplier leads to the exact recovery condition: convexity gives a global bound on incorrect mass, and a matching invasion argument proves necessity. Section 4 (p. 6) explains how monotonicity and KL divergence give global recovery, while rotational instability shows why a quadratic reference-mixing scale can be necessary.

(2) Simplifying the example. Following your suggestion, we replaced the expanded polynomial expressions for hi(u)h_i(u) in Section 4.3 with shifted Legendre polynomials:

\qquad \theta_i=\frac{2\pi i}{3}.$$ The explicit formulas for $P_2$ and $P_3$ are now in Appendix B.7. This form makes the symmetry of the construction easier to see. The densities remain positive, have uniformly bounded derivatives on $[0,1]$, and give the same fourth-order instability at $N=2$. **(3) Motivation.** We have expanded the Introduction (pp. 1–2) to explain why proportions among correct answers can matter. For example, different valid derivations or programs may represent alternative solution strategies worth retaining. We also clarify that recovering these proportions is a task-dependent goal: if only correctness matters, removing incorrect answers is sufficient. Reference mixing provides a way to control the changes caused by repeated selection, and the revised Introduction connects this mechanism to broader work on curated recursive training. **(4) Related work.** We have brought a substantial comparison with Ferbach et al. (2024) and Zhao et al. (2025) into the Introduction (pp. 2–3). Zhao et al. show that finite-pool recursive curation under stationary noise is a TV contraction when $N(1-\alpha)<1$. This guarantees convergence to a fixed point, which need not be the reference. Our results instead give score-dependent conditions for recovering the specified reference itself, including regimes where much smaller mixing weights suffice. We also explain how the models differ. The stationary-noise Plackett–Luce model corresponds to a common-location score family, while our framework allows score distributions with different shapes. Conversely, Zhao et al. study more general answer spaces, infinite-pool regimes, and reward perturbations. Further details are in Tables 6–7 and Appendix G.
AuthorsOpenReview ↗

Response to Reviewer TBAY (2/2): W1, Robustness to Different Probability Metrics

② [W1] "Several different notions of distance are in circulation ... how robust the recovery rates, thresholds, and characterizations are to different choices of geometries."

Response-W1: We examined this question and found that the answer depends on which distance is changed. Changing the norm used to measure recovery of the answer distribution does not change the recovery condition, but changing the metric used to compare score distributions can change the stabilization threshold. We have added an explanation in Section 2.1 (pp. 3–4) and new results in Appendix H.4 (p. 44).

(1) Answer-distribution metrics. Since the answer space is finite, all norms on its probability simplex are equivalent. Thus, the exact recovery condition in Theorem 1 remains unchanged under a different norm. Convergence bounds may change by dimension-dependent constants, but whether recovery occurs does not. We use TV because it gives bounds independent of the number of answers, and Pinsker's inequality allows us to control it through KL divergence.

(2) Score-distribution metrics. Here the choice matters. We use the Kolmogorov distance dK(Gi,Gj)=∥Gi−Gj∥∞d_K(G_i,G_j)=\|G_i-G_j\|_\infty because best-of-NN selection depends only on score rankings. This distance is unchanged under common strictly increasing transformations of the scores.

Appendix H.4 now establishes the following comparisons:

CDF uniform distance. Theorem 2 gives the matching Θ(δ2)\Theta(\delta^2) stabilization threshold for fixed NN, under exact target preservation.

Total variation. Since dK(Gi,Gj)≤TV(Gi,Gj)d_K(G_i,G_j)\leq \mathrm{TV}(G_i,G_j), the O(δ2)O(\delta^2) upper bound also holds when score heterogeneity is measured in TV. However, the oscillatory distributions in Theorem 6 have vanishing CDF diameter but TV diameter bounded away from zero, so this construction does not establish a quadratic lower bound in the TV class. At N=2N=2, we obtain an Ω(δ4)\Omega(\delta^4) lower bound and an O(δ2)O(\delta^2) upper bound. The tight exponent remains open.

Wasserstein-1. Scaling all scores changes their Wasserstein distances without changing any best-of-NN selection decision. Consequently, without fixing the score scale, a small Wasserstein diameter alone cannot guarantee a vanishing stabilization threshold.

Thus, the recovery characterization is independent of the norm on answer distributions, but the stabilization threshold can depend on how score distributions are compared. The proofs are given in Lemma H.3 and Appendix H.4.


Thank you again for your thoughtful suggestions. They helped us explain our results more clearly and place them in the context of related work. We hope the revised manuscript addresses your concerns, and we would be glad to discuss any point further.

Thank you for your detailed responses to me and the other reviewers; as well as for the improvements/extensions to the manuscript's various aspects. They definitely help with the clarity (as well as with the positioning relative to the closely related manuscripts). It does appear, based on your additional investigations, that extensions of your results to other metrics lead to a variety of new considerations; this will be reasonable to leave for future work to fully handle, I think. Overall, the paper remains quite technically dense in nature, with results depending intricately on concrete definitions of the modeling aspects of retraining dynamics; but the improvements you made during this discussion period point in the right direction. I am happy to keep my current score.

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