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Under review as a conference paper at ICLR 2027

Distribution-Level Conformal Screening for Prompt-Controlled LLM Synthetic Data

Abstract

Large language models (LLMs) can generate synthetic data at relatively low marginal cost, yet identifying prompts whose induced distributions are sufficiently aligned with a target population remains statistically challenging when only a small sample from that population is available. We cast this task as distribution-level set-valued inference and propose a conformal screening procedure that identifies, from a finite family of prompt-induced candidate distributions, those that are statistically compatible with the target population. Specifically, we construct a distribution-level nonconformity score using the empirical -divergence between real and \(N\) synthetic observations for each candidate. We then calibrate this score by its randomized conformal rank among \(m\) replicate scores generated from the candidate’s synthetic pool, and obtain the admissible subset by inverting the resulting conformal tests. Our first theoretical contribution is an exact finite-sample, candidate-wise validity guarantee. Under the compatibility null, exchangeability of the observed and calibration scores guarantees that each compatible candidate is retained with probability at least . Our second theoretical contribution is an asymptotic power guarantee: candidates separated from the target beyond a detection boundary of order , are rejected with probability tending to one. Simulations and an application to OpinionQA and MovieLens show that the retained prompts generate synthetic distributions closer to the full-data target than the empirical distribution based on the small real sample, thereby reducing downstream estimation error.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Conformal inference, Synthetic data, Large language models, Distribution-level hypothesis testing, Finite-sample validity

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_JF6LOpenReview ↗
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Paper summary

The paper considers screening a finite collection of prompt-induced synthetic distributions using a small sample from a target population. For each candidate, it compares a smoothed empirical distributional discrepancy with discrepancies computed from simulated calibration batches sharing a synthetic reference sample. Inverting the resulting randomized rank tests produces a retained set of candidates, with abstention when that set is empty. Theorem 1 establishes exact candidate-wise null retention under the sampling assumptions, and Theorem 3 claims an asymptotic power bound. Simulations and experiments on OpinionQA and MovieLens evaluate distributional agreement and downstream estimation.

Critical strengths
  1. The basic finite-sample validity argument is clean and useful. Under the equality null, the target batch and simulated calibration batches are identically distributed conditional on the shared synthetic reference. Their discrepancy scores are therefore exchangeable, and randomized ranking gives the stated candidate-wise calibration (Section 4.1, Theorem 1). Reuse of the reference is handled by conditioning rather than incorrectly treating all scores as unconditionally independent. The distinction between retaining a correct candidate and certifying that every retained candidate is close to the target is important and is stated in Remark 1.

  2. The application includes meaningful controls and abstention behavior. Screening prompt distributions is relevant when synthetic population data could otherwise introduce misleading precision. The OpinionQA evaluation compares synthetic controls beyond a real-only estimator, and the MovieLens study includes configurations where all candidates are rejected (Table 6). Allowing the procedure to decline augmentation is a useful part of the proposed workflow and provides evidence of behavior beyond always selecting a prompt.

Critical weaknesses
  1. The power proof does not establish the claim for the globally defined score as written. Equation (5), p. 16, integrates the smoothed divergence over all of R^d, and Theorem 3 uses the corresponding population Gaussian-smoothed KL divergence. However, Proposition 9 establishes the density-ratio and denominator bounds used in Lemmas 5–6 only for evaluation points in compact Ω (pp. 27–28). Compact support of the original observations does not provide a positive denominator lower bound over all of R^d after Gaussian smoothing. Page 23 explicitly acknowledges this tail issue, but Appendix D.6 nevertheless invokes Proposition 9 as sufficient for the concentration argument. This leaves a central claimed contribution unproved. A tail-aware analysis, or an explicitly defined compact-domain score with matching theory and implementation, is needed. The basic rank-validity theorem remains supported; the unresolved issue is the power argument for the implemented score.

  2. The multiple-question experiment is inconsistent with the stated candidate-retention rule. Appendix A.2 (and Corollary 11) states the retention rule, for Bonferroni, as "retained only if no question-level null is rejected"; no separate rule is stated for Holm, and the only rule under which Holm controls the familywise error rate across questions as asserted in Remark 2 is the same no-rejections rule. For the same vector of T p-values, both Bonferroni and Holm reject at least one null exactly when the minimum p-value is at most α/T. They must therefore retain the same candidates under this rule. Nevertheless, Appendix H.4 and Figure 13 report different retained-set sizes and systematically improved divergences for Holm. Different Monte Carlo draws or a different aggregation rule could produce different outputs, but would require an explicit account and would not by themselves establish the claimed advantage of the correction. The text on p. 42 treats the agreement of the two corrections at (N, n, m) = (600, 20, 40) as an exception to "their broader difference across the displayed settings"; under the stated rule, agreement must hold at every configuration, so the exception-versus-rule framing is inverted. This directly affects the experimental evidence for the multiple-question screening procedure.

Questions for authors
  1. Is the implemented KL discrepancy integrated over R^d or a bounded region? How are the Gaussian-tail terms controlled in Theorem 3, given the domain of Proposition 9 and the qualification on p. 23?
  2. What exact aggregation rule and paired question-level p-values produced Figure 13? Under the stated no-rejections rule, how can Bonferroni and Holm retain different candidates, and were the same question-level p-values (same calibration batches and tie-breaking draws) used for both corrections?
3 comments
AuthorsOpenReview ↗

Response to Reviewer JF6L

Thank you for identifying the support/proof distinction and the implications of the multiple-testing rule.

W1. Does compact support conflict with Gaussian smoothing or the full-space KL proof?

Compact support concerns the original distributions, not their smoothed densities. Assumption 1 requires supp⁡(Pt)⊆supp⁡(Psθ)⊆Ω\operatorname{supp}(P_t)\subseteq\operatorname{supp}(P_s^\theta)\subseteq\Omega for compact Ω\Omega. With the common fixed Gaussian bandwidth σ>0\sigma>0 in Eq. (6), both population and empirical smoothed densities are positive throughout Rd\mathbb R^d. This is consistent with Eq. (5).

Proposition 9 gives bounds on Ω\Omega, not the full space. Compactness and kernel positivity give uniform upper and positive lower density bounds, and hence two-sided ratio bounds, on Ω\Omega. These also hold for empirical densities and single-observation replacements within Ω\Omega.

The full-space argument requires Gaussian-tail control. Bounded kernel centers yield common Gaussian upper and lower envelopes. Although density ratios may grow in the tails, density-weighted KL terms remain integrable. Under independent sampling and fixed bandwidth, these envelope estimates give O(1/n)O(1/n) and O(1/N)O(1/N) single-observation changes and an O(1/n+1/N)O(1/n+1/N) bias relative to the population Gaussian-smoothed KL, with constants depending on Ω,σ,d\Omega,\sigma,d. We will extend the Gaussian-tail estimates from Theorem 4's proof (Appendix D.1) to make the concentration and bias steps explicit in Appendix D.6.

The target-to-reference score is numerically integrated from the minimum to the maximum of the pooled target and synthetic reference samples, with bandwidth chosen by Silverman's rule. We will explicitly distinguish this computation from the fixed-bandwidth, full-space analysis. Theorem 1's finite-sample validity relies on conditional exchangeability, not the compact-support assumption used in the power analysis.

W2. Can Holm and Bonferroni retain different candidates with the same raw p-values?

Identical raw p-values imply identical candidate retention. For a fixed candidate θ\theta, let pjθ=1−Qjθp_j^\theta=1-Q_j^\theta, j=1,…,Tj=1,\ldots,T. Both Holm and Bonferroni operate across the TT questions, not the mm calibration replicates; a candidate is retained only if no question is rejected.

Bonferroni retains the candidate exactly when min⁡jpjθ>α/T\min_j p_j^\theta>\alpha/T. Holm uses the same first threshold: it either stops without rejection or rejects at least one question, excluding the candidate. Thus, both induce the same candidate-level global p-value:

pglobal,B=pglobal,H=min⁡1,Tmin⁡jpj,retain iff pglobal>α.p_{\mathrm{global},B}=p_{\mathrm{global},H}=\min\\{1,T\min_j p_j\\},\qquad \text{retain iff }p_{\mathrm{global}}>\alpha.

Their adjusted p-values and question-level rejections can nevertheless differ.

Figure 13 reports separate runs, with different raw p-value inputs. These differences reflect between-run variation, not an intrinsic screening advantage of Holm under our retention rule. We will make this distinction explicit in the figure caption and the multiple-output discussion.

With valid marginal p-values, both procedures control familywise error across questions for each fixed candidate without requiring question independence. Neither provides simultaneous control across candidates nor certifies retained candidates. The tests assess marginal distributions, not the full joint rating distribution.

Thank you for the response and clarifications. I agree that the Gaussian-envelope argument offers a plausible way to repair the power proof, and I appreciate your explanation of the Holm/Bonferroni discrepancy. However, I still have concerns after checking the revised manuscript.

The proof in Appendix D.6 (p. 26) still relies on Proposition 9, whose bounds apply only on the compact set Ω. The full-space sensitivity and bias arguments needed for Theorem 3 are still missing. Showing that the KL terms are integrable is not enough to establish those bounds. I would need to see the promised derivation before considering this concern resolved.

The implementation clarification also leaves a gap: the experiments integrate over the pooled sample range and use Silverman's bandwidth, while Theorem 3 assumes full-space integration and a fixed bandwidth. Even a repaired proof needs to explain how it applies to this implementation, or clearly limit the theorem's scope. My positive assessment of the exchangeability argument in Theorem 1 is unchanged.

For multiple testing, I accept that different raw p-values across separate runs explain the different retained sets. But this also means that the comparison cannot support an advantage of Holm under the stated retention rule. Section 5.2.2 and Appendix H.4 still make that claim, and Figure 15 retains the comparison. The text should be corrected, with a paired check using identical p-values to confirm identical candidate retention.

The response helps clarify both issues, but the revised paper has not yet resolved them. I therefore keep my rating.

AuthorsOpenReview ↗

Response to followup of Reviewer JF6L

Thank you for identifying the gaps in the power proof and the multiple testing.

1. The role of Assumption 1 in the power proof.

The proof of Theorem 3 invokes Assumption 1 through Proposition 9 to verify Condition 1 and the empirical bounds in Lemmas 5 and 6 on Ω\Omega. The population ratio bound in Condition 1 permits unbounded supports. With Condition 1 and direct control of empirical sensitivity and bias, the same power argument yields the separation scale rn,N−1/2+m−1/2r_{n,N}^{-1/2}+m^{-1/2} under the stated cutoff and gap conditions. Appendix D.7 derives the full-space Gaussian sensitivity bounds O(1/n)O(1/n) and O(1/N)O(1/N) and bias O(1/n+1/N)O(1/n+1/N). The power analysis uses a fixed bandwidth and full-space integration. The experiments use Silverman's rule and the pooled sample range. Theorem 1's validity argument rests on conditional exchangeability.

2. A fixed-bandwidth example with unbounded support.

Take P=N(0,1)P=\mathcal N(0,1) and Q=N(1,1)Q=\mathcal N(1,1) with the Cauchy kernel k(z)=1/[π(1+z2)]k(z)=1/[\pi(1+z^2)]. For B(x)=2(1+x2)B(x)=2(1+x^2),

B(x)−1≤k(z−x)k(z)≤B(x),x,z∈R.B(x)^{-1}\le \frac{k(z-x)}{k(z)}\le B(x),\qquad x,z\in\mathbb R .

Averaging these bounds gives a global population ratio bound. The empirical averages of BB are bounded with exponentially high probability, which puts the empirical densities divided by kk in a fixed compact interval. Clipping to this interval in the proof allows bounded differences and a Taylor bias bound. The original score then satisfies

\le 2e^{-c r_{n,N}t^2}+e^{-c_0 n}+e^{-c_0 N},\qquad t > 0 .$$ **The score concentration scale is preserved up to exponentially small exceptional terms,** yielding consistency at this fixed alternative. **3. Holm and Bonferroni.** We removed the superiority claim and retained the figure as a descriptive comparison of separate runs.
Reviewer_XpUAOpenReview ↗
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Paper summary

This paper addresses the problem to make LLM-generated synthetic distributions valid using limited real human responses. It proposes distribution-level conformal screening to identify prompt configurations that are not statistically rejected as incompatible with the target distribution. The paper also establishes finite-sample validity and asymptotic screening power.

Critical strengths
  • The paper tackles an important problem. Simulating human response distributions with LLMs is an important and practical problem. Evaluating distribution-level reliability rather than individual responses is particularly meaningful.

  • The paper provides clean theoretical analysis. The finite-sample validity and asymptotic power analyses are clear and well-structured.

Critical weaknesses
  1. Unclear practical utility of the set-valued output
  • When applying conformal inference to a new task, it is important to justify whether a set-valued output is sufficient for the intended application.
  • The goal of this paper is to approximate the target human response distribution. However, the proposed method returns a set of prompt configurations (\Theta^\ast), rather than a single synthetic distribution.
  • A set-valued output is not inherently problematic. However, a large retained set requires an additional selection or aggregation procedure.
  • In many OpinionQA settings, more than 2,900 out of 3,003 candidates are retained.
  • It remains unclear how the final distribution should be selected or combined, and what guarantees support this decision. This raises concerns about the practical utility of the output and its alignment with the downstream task.
  1. Limited technical novelty
  • Distributional testing and synthetic data validation using conformal methods have already been explored. A. Testing Exchangeability between Real and Synthetic Data, Löfström et al. (2024): Testing exchangeability between real and synthetic data. B. Conformal C2ST: Turning weak classifiers into strong two-sample tests, Bansal et al. (2026): Conformal two-sample distribution testing.

  • The proposed method similarly computes distributional discrepancies and uses conformal ranks to screen candidates.

  • The technical contribution beyond applying existing ideas to LLM prompt configurations remains unclear. Stronger differentiation from prior work is needed.

Questions for authors
  • When the retained set is large, how should the final synthetic distribution be selected or combined? Are there further statistical guarantees for this decision?

  • What are the main technical contributions of the proposed method beyond existing work on conformal two-sample testing and synthetic data validation?

4 comments
AuthorsOpenReview ↗

Response to Reviewer XpUA (Part1)

Thank you for these questions.

W1. Using the retained set.

Augmentation uses only retained candidates. If the retained set is empty, we abstain from augmentation (Section 3.2). The finite candidate set is constructed independently of the screening data (Section 3.1). Retention does not identify an optimal candidate or certify distributional closeness (Remark 1). Choosing among multiple retained candidates is a separate downstream decision. We explicitly described the selection rule used in each downstream experiment in Appendix H.5 of the revised manuscript.

To clarify how the retained set is used for augmentation, we have added a comparison of averaging, MLE, and MaxEnt in Section 5.2.1 and Appendix H.5.

The original MAE experiment averages retained candidates before n:Nn:N augmentation. We keep instructions/questions fixed and vary six ideology profiles, including Refused. Their LLM-induced distributions GgG_g define Psπ=∑gπgGgP_s^\pi=\sum_g\pi_gG_g; a step-0.1 simplex yields 3,003 weights.

On WORRYA_W26, DeepSeek-R1-Distill-Llama-8B (temperature 0.7) generates six branches. A uses four; B shares two and includes two farther branches. We use disjoint 828/621/621 construction/screening/evaluation splits, 286 weights per family, n=20,N=600,m=40,α=.05n=20,N=600,m=40,\alpha=.05, seed 123, and 1,000 rounds.

All-mix averages all candidates; Conformal averages retained candidates; Random-KK averages K=∣Θ∗∣K=|\Theta^*| randomly chosen full-grid candidates. MLE maximizes observed-answer mixture likelihood using the screening sample; MaxEnt maximizes −∑gπglog⁡πg-\sum_g\pi_g\log\pi_g. Both rules select one grid point from retained candidates (CS). We report augmented KL(p^aug∥p^E)\mathrm{KL}(\widehat p_{\rm aug}\Vert\widehat p_E) against the independent evaluation distribution p^E\widehat p_E. The results are summarized below.

MethodFamily AFamily B
Real0.06300.0630
All-mix0.05410.5063
Conformal0.05070.2663
Random-KK0.05760.5964
CS-MLE0.02870.0472
CS-MaxEnt0.05380.5387

In family B, Conformal reduces All-mix KL from .5063 to .2663 (47.4%). CS-MLE further improves KL in both families; CS-MaxEnt does not. Averaging still loses to Real only in B.

Submitted MovieLens likewise shows worse Random performance and rejects the misspecified family entirely at n=80,100n=80,100, enabling abstention.

Shared components, similar induced distributions and small real samples explain the large retained sets in the original experiment. This broad overlap helps explain why Random and Conformal are close; similar performance is not assured for a worse candidate family. The added experiment shows benefits for averaging and that the downstream selection rule matters under fixed pools and splits; guarantees remain candidate-wise, not post-selection.

Appendix B.2 discusses probabilistic prompt sampling: one can draw candidates from a proposal independent of the screening data, test them, and stop after a desired number pass or a budget is exhausted.

AuthorsOpenReview ↗

Response to Reviewer XpUA (Part2)

W2. Relation to prior work and contribution.

Our contribution is classifier-free batch calibration and prompt-set inference, not conformal testing itself. Löfström et al. (2024) assessed real/synthetic exchangeability using conformal scores and test martingales. Bansal et al. (2026) calibrated classifier scores for two-sample testing. Their Uniform test uses fresh calibration for each test point and provides finite-sample validity; power depends on classifier ranking quality.

Our method scores the real batch and synthetic calibration batches against a common synthetic reference. Under distributional equality and the stated sampling assumptions, conditional exchangeability yields candidate-wise finite-sample validity. No classifier training or allocation of real observations to a training split is required. Inverting these tests produces a retained prompt-control set, with abstention when the set is empty.

To compare empirical screening selectivity with related conformal tests, we have added a matched-budget Tri-Hedge experiment in Section 5.1 and Appendix G.2.

On Tri-Hedge, we evaluate 1,000 candidates over 100 rounds at α=0.05\alpha=0.05, with budgets of nn real and N+mnN+mn synthetic observations. Classifier-based baselines split the real sample for training and testing. Löfström-SJ denotes the independent-calibration adaptation. Each cell reports mean acceptance ratios for N=1000/2000N=1000/2000; rows use n=50,150,250n=50,150,250 for both mm values. The mean acceptance ratios are summarized below.

mmnnOursC2ST-UniformLöfström-SJ
20500.851/0.8380.927/0.9270.999/0.999
201500.635/0.6050.914/0.9130.977/0.976
202500.468/0.4240.890/0.8900.958/0.958
40500.842/0.8300.927/0.9270.999/0.999
401500.610/0.5780.913/0.9140.976/0.976
402500.436/0.3930.888/0.8870.957/0.958

The experiment shows that our method retains fewer candidates throughout the evaluated settings. The complete 28 configurations are reported in Appendix G.2.

Thank you for the detailed rebuttal and additional experiments. The improved KL divergence with CS-MLE, particularly in Family B, and the demonstration of abstention under misspecification are encouraging.

However, I remain uncertain about the benefit of conformal screening when the final candidate is selected using MLE. While the candidate-wise validity guarantee remains intact, it does not appear to extend to the final MLE-selected distribution.

One potential advantage would be filtering out misleading candidates that achieve high likelihood on limited human data but are actually far from the target distribution. This would provide a compelling justification for conformal screening, but the current experiments do not clearly demonstrate such a benefit.

Could the authors compare CS-MLE against unrestricted MLE over the full candidate set? Without this comparison, it remains difficult to determine what conformal screening contributes beyond MLE-based selection.

I'll reply quickly during the remaining rebuttal period, so if the authors can solve my question, please leave an answer. Thank you.

AuthorsOpenReview ↗

Response to followup of Reviewer XpUA

Thank you for this helpful follow-up. We now report the requested unrestricted-MLE comparison.

1. Full-candidate comparison on OpinionQA.

We keep the original WORRYA_W26 candidate pools, splits, and settings (n=20n=20, N=600N=600, m=40m=40, α=.05\alpha=.05; 1,000 rounds). ALL-MLE and ALL-MaxEnt optimize over all candidates; CS-MLE and CS-MaxEnt restrict the same objectives to retained candidates. The table reports mean augmented KL(p^aug∥p^E)\mathrm{KL}(\widehat p_{\rm aug}\Vert\widehat p_E); lower is better.

MethodFamily AFamily B
Real0.06300.0630
All-mix0.05410.5063
Conformal0.05070.2663
Random-KK0.05760.5964
ALL-MLE0.02820.0471
CS-MLE0.02870.0472
ALL-MaxEnt0.05330.5084
CS-MaxEnt0.05380.5387

ALL-MLE has lower mean KL in both families. Thus, the earlier CS-MLE gains over averaging cannot be attributed to screening alone. With a unique likelihood maximum, if ALL-MLE survives screening, CS-MLE selects exactly the same distribution. Small or unrepresentative samples can nevertheless favor a high-likelihood candidate far from the target; we therefore examine these risks below.

2. MLE and MaxEnt with small or biased samples. We use a fixed Tri-Hedge family with target weights (0.5,0.3,0.2,0)(0.5,0.3,0.2,0) and KDE--KL screening (Nref=2000N_{\rm ref}=2000, m=40m=40, α=0.05\alpha=0.05), with a fixed tie rule, repeated 300 times. ALL methods optimize likelihood or entropy over the full grid; CS methods restrict the same objective to retained candidates. All retained sets were nonempty.

(a) Low Representative samples, n=5n =5. The same five target observations are used for likelihood and screening; source observations do not enter either MLE objective.

(b) Biased samples, n=20n=20. The 20 observations are sampled from the 60% probability subregion of the true support instead of the full region, leading to incomplete coverage in simulation sampling. The table reports the mean and sample variance of population KL(Pt∥Qπ^)\mathrm{KL}(P_t\Vert Q_{\widehat\pi}).

MethodRepresentative: mean KLRepresentative: varianceBiased: mean KLBiased: variance
ALL-MLE0.55241.1000690.29860.027335
CS-MLE0.55241.1000690.29860.027335
ALL-MaxEnt0.13290.0002340.13280
CS-MaxEnt0.13290.0002340.13300.000346

Screening leaves MLE selection unchanged in both experiments. ALL-MLE survives screening, so CS-MLE selects exactly the same candidate each time; the paired KL difference is identically zero. ALL-MaxEnt yields zero variance since it selects the same parameter configuration across all runs.

MaxEnt is more stable and accurate at nA=5n_A=5. in (a) Both MaxEnt rules have lower mean KL and variance than MLE; screening adds a .0029 mean KL reduction for MaxEnt.

MaxEnt is more robust under biased sampling in (b). Both MaxEnt rules have lower mean KL and variance than either MLE rule. The advantage mainly reflects entropy selection: CS-MaxEnt improves on ALL-MaxEnt by only .0028 (paired 95% interval for CS minus ALL: [−.0066,.0007][-.0066,.0007]). ALL-MaxEnt selects a fixed distribution, hence its zero variance.

Reviewer_3n8MOpenReview ↗
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Paper summary

The paper focuses on the following problem: in many settings (e.g., social sciences), researchers have started turning to LLMs to create synthetic data to augment the existing (but scarce) human data they have. However, the challenge of making sure that the synthetic data is “sufficiently aligned” with the target distribution of human data remains unaddressed. The paper introduces “conformal screening”, which is a statistical testing framework for selecting among synthetic data distributions in a way that is aligned with the target human data. Concretely, the setting is the following: let Θ\Theta be the set of candidate ways to create the synthetic data; each θ∈Θ\theta \in \Theta induces a synthetic distribution PsθP_s^\theta. The aim here is to assess the compatibility of PsθP_s^\theta with the true human distribution PtP_t through the hypothesis H0θ:Pt=PsθH_0^\theta: P_t = P_s^\theta. Let nn be the number of real human observations. For each θ\theta, we draw NN independent observations and mm calibration batches, each with a size of nn. Now, if H0θH_0^\theta is true it should be the case that the real and calibration batches are identically distributed — this is what gives the conformal set of the present paper.

Critical strengths

[S1] I think that the problem considered here is both very important for the application of LLMs to social science research and very interesting independently.

[S2] I appreciated that the paper was mostly clear.


[S3] I found the procedure used to achieve the guarantees both natural and kind of smart.

Critical weaknesses

[W1] If I’m interpreting the results correctly, it seems that the paper doesn’t control for accepting a sufficiently incorrect candidate and then using its answers. I think the authors allude to that in their Remark 1 (to their credit). This is important particularly for applications, because it may end up being the case that we’ll be using synthetic data that may flip the conclusions of the experiment entirely. I think this is something that relates to the size of nn, which isn’t addressed in this work.

[W2] I think that the usefulness of the method depends on how good of a representation of the true human population the manually chosen profile library is. For some experiments (eg the MovieLens) I totally agree with the authors on the way that they chose the profile library. But for opinion datasets (like OpinionQA) I’m not so sure. Independently, I couldn’t find the OpinionQA persona prompts that the paper used.

[W3] It seems that the gains from the approach are very modest in terms of MAE: I’m comparing between “Random” and “Conformal” in Figure 3(b). If I’m interpreting this correctly, then we have a method which spends significant computation to do the screening but ultimately ends up achieving very little gains.

Questions for authors

Am I interpreting Figure 3(b) correctly? If yes, then what do you see as the biggest contribution of your work and a good rebuttal for the (very) modest gains that the method achieves?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 3n8M (Part1)

Thank you for highlighting incorrect retention, profile bias, and the modest gain over Random.

W1. What risk is controlled, and how does the real sample size matter?

Our guarantee controls the erroneous exclusion of compatible candidates. Theorem 1 applies to each prespecified candidate with Pt=PsθP_t=P_s^\theta. Conditional on the synthetic reference, its rejection probability is exactly α\alpha. This result assumes the stated sampling conditions and randomized tie-breaking. Retention alone does not certify distributional closeness, safe augmentation, or valid downstream inference. We have stated this scope explicitly and removed stronger claims in the revised manuscript.

Theorem 3 separates score uncertainty of order 1/n+1/N\sqrt{1/n+1/N} from calibration uncertainty of order m−1/2m^{-1/2}. The Type II error vanishes when the stated regularity and separation conditions hold, and the population score gap asymptotically dominates the combined uncertainty. The full-space KDE–KL analysis additionally requires explicit Gaussian-tail control. For N≫nN\gg n, score uncertainty remains of order n−1/2n^{-1/2}. Increasing NN yields diminishing returns; increasing mm refines the calibrated cutoff. Neither removes the limitation imposed by the real sample size nn.

W2. How are candidates constructed, and can profile bias remain?

In our experiment, survey instructions and questions remain fixed. We use six POLIDEOLOGY profiles, five ideology levels plus Refused, and construct one reusable local pool for each profile-induced distribution GgG_g. The candidates are

\qquad \pi_g\in\\{0,0.1,\ldots,1\\}, \qquad \sum_{g=1}^{6}\pi_g=1.$$ This grid contains 3,003 weight vectors. Each weight $\pi_g$ represents the probability of selecting profile $g$. Our implementation uses these weights to allocate sample counts across the six pools and then samples responses within each pool. **Profile bias can remain after mixing.** A profile label does not ensure that the LLM's responses match those of the corresponding human group. Changing $\pi$ only changes the relative contributions of the six component distributions. It does not guarantee that any candidate represents the target population. The usefulness of augmentation therefore depends on how well this family can approximate the target population. We have added the complete OpinionQA persona prompts and clarified the construction procedure and this limitation in Appendix H1. **Random sampling provides an alternative to grid enumeration (Appendix B.2).** We can instead draw $k$ candidate controls independently from a proposal distribution over a compact feasible domain. The proposal must assign positive probability to every neighborhood in that domain. Appendix B.2 shows that for any fixed $\epsilon>0$ these samples form an $\epsilon$-net with probability approaching one as $k$ grows. This means that every feasible control lies within distance $\epsilon$ of at least one sampled control. The result concerns coverage of the chosen control domain. It does not guarantee that the resulting response distributions represent the target population. Candidate construction must remain independent of the real screening sample. Any target data used to design or tune candidates must come from a separate development split.
AuthorsOpenReview ↗

Response to Reviewer 3n8M (Part2)

W3. What does screening add beyond Random?

To highlight how candidate-family mismatch affects the gain over Random, we have added a candidate-family comparison in Section 5.2.1 and Appendix H.5.

All 3,003 candidates in the original OpinionQA experiment mix the same six components (W2).

On WORRYA_W26, we use DeepSeek-R1-Distill-Llama-8B (temperature 0.7) to generate six branches. Family A uses four; Family B shares two with A and includes two more mismatched LLM-generated branches. Both use disjoint construction/screening/evaluation splits of 828/621/621 observations, 286 step-0.1 weight vectors, n=20n=20, N=600N=600, m=40m=40, α=0.05\alpha=0.05, seed 123, and 1,000 rounds.

We compare All-mix (average all candidates), Conformal (average retained candidates), and Random-KK (average KK randomly chosen candidates, matching the retained count each round). We also compare single-candidate selection: MLE maximizes observed-answer mixture likelihood on the screening sample, whereas MaxEnt maximizes weight entropy −∑gπglog⁡πg-\sum_g\pi_g\log\pi_g. Both rules select one candidate from the retained set (CS). We report augmented KL(p^aug∥p^E)\mathrm{KL}(\widehat p_{\rm aug}\Vert\widehat p_E) against the independent evaluation distribution p^E\widehat p_E; lower is better, and Real uses no synthetic data. The separate DctrlD_{\mathrm{ctrl}} averages candidate-level divergences; it does not measure the divergence of the final averaged distribution.

At m=40m=40, Figure 3(b) reports mean macro MAE of approximately 0.0440 (Conformal), 0.0453 (Random), and 0.0585 (Real only). Conformal improves on Random by 0.0013, or 2.9%. The new A/B results are summarized below.

MethodFamily AFamily B
Real0.06300.0630
All-mix0.05410.5063
Conformal0.05070.2663
Random-KK0.05760.5964
CS-MLE0.02870.0472
CS-MaxEnt0.05380.5387

In family B, screened averaging reduces KL by 47.4% relative to All-mix and 55.3% relative to Random-KK, although it remains worse than Real only. CS-MLE yields substantially lower KL than Conformal in both families; CS-MaxEnt offers no comparable gain.

In the MovieLens experiments, only 10–285 of 43,758 candidates are retained at n=60n=60, and none at n=80,100n=80,100.

The original gain over Random is modest; most of the gain over Real only is already achieved by unscreened augmentation. Random varies mixture weights rather than choosing arbitrary prompts. Similar components can produce overlapping mixtures, and uniformly averaging retained probability vectors before n:Nn:N real/synthetic augmentation can further reduce differences between candidate sets. Small real samples also limit discrimination. The added experiment shows an empirical benefit over unscreened averaging under fixed pools and splits; it also shows that the downstream selection rule matters. It does not establish universal superiority across families or selection rules. The reported Tri-Hedge core timings exclude sampling and do not establish cost-effectiveness over Random on OpinionQA.

Thank you to the authors for their response. I'm having a bit of a hard time understanding some parts of it, so let me try to articulate what I understand and don't understand here:

[W1] Wrt W1, do you agree with my stated weakness? It seems that you reiterate what is covered by your paper, but you didn't engage much with my point. It is completely fine to not engage, just wanted to flag it.

[W2] I think i understand your response here.

[W3] It seems that your response agrees with me that your improvement is rather modest over Random, is that correct? I think one way of framing this in the next version of the paper is to explain to the reader what are some reasons why you are seeing this. Or what are some levers that future work could pull in order to make the gains over Random be bigger.

AuthorsOpenReview ↗

Response to followup of Reviewer 3n8M

Thank you very much for your follow-up comment.

In Theorem 3 of our paper, we characterize the risk you raised of accepting a sufficiently incorrect candidate and then using its answers. We show that the convergence rate of this risk is controlled by 1/n+1/N\sqrt{1/n + 1/N} and 1/m\sqrt{1/m}, which bears a connection to the true sample size n, as you anticipated.

Regarding W3, our explanation is as follows: the modest improvement over the Random baseline arises because the component distributions adopted in the OpinionQA experiment are fairly accurate. Consequently, the mixing parameter π\pi has limited influence on the final synthetic distribution. We conducted additional tests on another set of component families (Family B in our response). When the family contains misspecified components, the mixing parameter π\pi exerts a stronger effect, fewer parameters survive screening, and the gains over Random become larger (from 0.5964 to 0.2663).

Thank you again for your comments. We have updated the discussion regarding the improvement over the random baseline in Appendix H5 of the revised manuscript.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Title: To All Reviewers: Updated Manuscript and Additional Appendix Experiments

We thank all reviewers for their constructive feedback. In addition to our individual responses, we have revised the manuscript and added supplementary experiments in Appendices D.7, G.2, and H.5, which are highlighted in blue, to address the questions and suggestions raised. The main additions are summarized below:

  1. @Reviewer XpUA: Comparison with related conformal tests. Added Tri-Hedge comparisons with C2ST-Uniform and an independent-calibration adaptation of Löfström et al. in Appendix G.2, reporting empirical screening selectivity and core runtime under matched data-budget caps.

  2. @Reviewer 3n8M and Reviewer XpUA: Candidate-family mismatch and downstream selection. Added OpinionQA experiments in Appendix H.5 comparing two candidate families with different degrees of mismatch. We evaluate screened averaging, count-matched random averaging, and single-candidate selection using MLE or MaxEnt to clarify how candidate-family quality and downstream selection affect augmentation performance.

  3. @Reviewer JF6L: Scope of Theorem 3 and the full-space proof. Clarified the scope of Theorem 3 in Section 4.2. In Appendix D.7, we explain how Assumption 1 enters the proof, derive the sensitivity and bias bounds for the fixed-bandwidth Gaussian-smoothed KL score over the full space, and establish consistency for fixed alternatives with unbounded support under the stated conditions.

  4. @Reviewer JF6L: Holm and Bonferroni on MovieLens. Removed the Holm superiority claim in Section 5.2.2 and Appendix H.4. We explain why the two corrections retain the same candidates on identical raw p-values and present the figure as a descriptive comparison of separate runs.

We appreciate the reviewers’ suggestions, which have helped us clarify the practical benefits and limitations of the proposed framework.

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

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