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Under review as a conference paper at ICLR 2027

Mirage Discoveries: Separating Signal From Selection Noise in LLM-Driven Program Search

Abstract

Autonomous discovery systems increasingly pair language models with evaluators to generate, test, and select new programs end to end. When the same evaluation regime both guides search and decides acceptance, the search optimizes against its own evaluator: as more candidates are tried, those selected increasingly exploit noise in the evaluation slice rather than transfer to unseen data. We measure this winner's curse in LLM-guided evolution of learning-to-rank pipelines over noisy logged user behavior. Fitness-based acceptance identifies the held-out best candidate in 5 of 12 runs, and equal-budget random search transfers as well as guided search. We introduce audited acceptance, which separates search from deployment: candidates are optimized on a cheap fitness fold but enter the deployable set only when their improvement persists on an audit fold, disjoint from both the fitness fold and the final test fold, by a margin calibrated to the paired-bootstrap noise floor of the search evaluator, with all audit usage counted and reported. The same criterion yields a pre-search headroom gate that determines whether a search space contains enough measurable signal to justify autonomous optimization at all. In a search space that passes the gate, all three discovered executable pipelines outperform an Optuna-tuned LambdaMART baseline by up to 0.0057 NDCG@10 on roughly 60k untouched test queries, and the discovered programs are readable code that recovers the structure of the original challenge winners. As autonomous experimentation scales, acceptance, not candidate generation, becomes the binding constraint on what these systems can reliably promote.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM-guided program search, autonomous discovery, evolutionary search, selection bias, evaluation noise, audited acceptance, agentic ML engineering

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_MNHJOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper addresses an overlooked issue within the LLM-driven autonomous program discovery system (such as the "LLM-generated program + evaluator scoring + selection iteration" closed loop): when the evaluator itself has noise, the selection process will overfit the evaluator's noise, resulting in the "winner's curse" a significant improvement on the training set, but an illusion on the validation set. The authors used the Ctrip hotel search ranking dataset (ICDM 2013, 9.9M impressions) as the test bed and employed Claude Sonnet 5 as the mutation operator to conduct experiments in two search spaces.

Critical strengths
  1. No need for new models or new search algorithms. Instead, simply adopt the mature statistical discipline from ML competitions; and use the positive-negative contrast of "failure without headroom space / success with headroom space" to prove that it can distinguish between true signals and false signals.
Critical weaknesses
  1. The task domain and dataset are too narrow, and the extrapolation boundary is unclear. All the evidence comes from a learning-to-rank task (Expedia/Booking.com hotel search), and the reward is pairwise NDCG@10; the typical task families in the LLM program discovery literature - combinatorial optimization, code generation, theorem proving - have zero coverage. The "discovered programs" in the pipeline space are essentially a combination of feature engineering and ranking heads, not the discovery of algorithmic logic or program structure. In the pairwise ranking scenario where "evaluators are cheap and can run tens of thousands of queries repeatedly", disjoint audit folds + paired bootstrap are easy to implement; but in tasks where the validator is expensive (each run takes 30 minutes) or noisy (human review), the cost and margin calibration methods of this mechanism have not been discussed.
  2. The Headroom gate has circular reasoning, and the sample size of the pipeline space is too thin. The gate requires a hand-built reference candidate to test whether there is headroom in the space, but the reference in the paper is a strong baseline "created after two weeks of work" - this is equivalent to "knowing the answer, having a strong baseline, before deciding whether it is worth searching", which is not operational for true exploratory discovery (open questions without a ready reference). More critically, the pipeline space has only run 3 independent runs, and the authors themselves admit in Limitations that "three runs are sufficient for the paired-bootstrap noise, but three is not enough to characterize how variable the search itself is" - all three runs beat the baseline, and statistically neither can rule out "the headroom of this space is so large that randomly searching can win", nor can it estimate the variance between runs.
  3. Key ablation is missing, making it impossible to separate the causal contribution of audited acceptance from the headroom of the space. The success in the pipeline space is observed under the condition of "having headroom + using audit". If the audit is turned off in the same pipeline space and returned to naive fitness-gated selection, what would be the final test NDCG of the three runs? The paper did not run this control. This leads to an unanswered question: What is the role of audited acceptance - is it "preventing false positives from being treated as true" (diagnostic value), or "really improving the quality of the final solution" (therapeutic value)? If shutting down the audit process still allows one to beat the baseline in this space, then the contribution of this paper would merely be "helping you avoid unnecessary searching in the objective space", while the success in the pipeline space is more a result of the existence of sufficient room in the space itself.
Questions for authors

See Critical Weaknesses

2 comments
AuthorsOpenReview ↗

Audit-off control is diagnostic, wider task coverage

Thank you for the detailed review. On the audit-off ablation, the answer is that the check is mainly diagnostic. In 34 earlier Expedia pipeline-space runs, the short-list audit shipped a program with the same test score as no audit every time. In eight fresh LLM runs on MSLR-WEB30K, scoring the winner once on held-out data ships the same candidate and moves the over-statement from about a third of the test gain to about zero (resolved). Only a short list can change what ships. It does so resolvably in a 180-run hyperparameter search, a non-LLM control (+0.0036+0.0036 test gain), and not in the fresh ranking runs (+0.0012+0.0012). Less reporting bias alone does not show fewer harmful deployments. We see the diagnostic value as the contribution: it says what a reported gain is worth.

On the gate and the three runs, we agree with both points. That analysis is removed, and the evidence no longer rests on three runs: it now rests on eight fresh and eight earlier LLM ranking runs, 20 LLM bin-packing runs and 180 non-LLM control runs. On whether random search would win in the Expedia pipeline space, with 50 evaluations per arm it shipped the same test NDCG@10 as guided LLM search (0.4334).

On scope, the revision adds a tabular task and a code-generation task, in which an LLM writes online bin packing heuristics (20 runs). There the candidates were near-duplicates and almost nothing needed correcting. Theorem proving and human validators are not covered. The theorems are stated for any evaluation outside the loop that uses a fresh sample, such as a human rater, a simulator or an A/B test, but only held-out data was tested, and rater or simulator bias is not covered. For costly validators, one pre-chosen winner has zero expected bias at any sample size.

What is new for self-improving loops is listed in our general comment. We are glad to answer anything further.

Thanks for the response. After reading through the response, I find that my previous concerns remain unaddressed. Taking into account the comments from the other reviewers, I have decided to maintain my original score.

Reviewer_vRjMOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

The paper studies selection bias in LLM-guided evolutionary program search, in the setting where one noisy evaluator both guides search and decides what is accepted. The testbed is the Expedia ICDM 2013 learning-to-rank data, with an LLM as the mutation operator. There are two search spaces: (i) the LambdaMART gradient function as the objective space and (ii) full pipelines covering features, model family, loss, and ensemble. The paper makes two proposals: audited acceptance and headroom gate. The main findings include that in objective space, fitness-fold gains do not transfer, and in pipeline space, about 70% of the gain transfers.

Critical strengths
  1. A practically important problem and failure analysis.

  2. Separation of search and acceptance, supported by experimental controls.

Critical weaknesses
  1. All evidence comes from a single dataset. The limitations section restricts the claims to ranking and recommendation, but that is not a narrow scope, and both areas have many public datasets. These include standard learning-to-rank benchmarks such as JDsearch, MS MARCO Web Search, and Yambda-5B.

  2. The central methodological claim is not tested where it matters. The winner’s curse is demonstrated in objective space (Section 5.1), but audited acceptance is evaluated only in pipeline space (Section 5.2).

  3. Two obvious baselines are missing as well. The headroom gate’s reference candidate, built from the 2013 winners’ features, already gained +0.013 on the fitness fold before any search. That may put it close to the final picks of s0 and s1, but its test score is not reported. Random search, which matched guided search in objective space, is not reported for pipeline space.

  4. Some of the practical claims are stated more strongly than the results allow.

Questions for authors
  1. What is the test score of the headroom-gate reference candidate, and how does random search do in pipeline space?

  2. Can the authors repeat the main experiments on a second ranking dataset? They don’t need conversion or revenue labels.

  3. Could the authors replay the objective-space runs under audited acceptance?

1 comment
AuthorsOpenReview ↗

Second ranking dataset and two further settings

Thank you for the review. On your second question, partly: we ran the revised protocol on a second ranking dataset, MSLR-WEB30K (eight fresh pre-registered LLM runs, plus eight earlier ones). We also added a 180-run hyperparameter search on forest cover type, which uses no LLM and serves as a control, and 20 runs in which an LLM writes bin packing heuristics. Expedia remains the first test bed.

On your third question, no. The objective-space runs saved only their final picks, so they cannot be replayed, and the paper says so. What we can show is the effect and its correction where everything was saved. In the fresh ranking runs the search score over-states the test gain by about a third, and the held-out score of the same winner is unbiased on average. In the control, the search score over-states by more than the whole test gain.

On your first question, random search in the pipeline space shipped a test NDCG@10 of 0.4334, equal to guided LLM search, so we make no claim that the LLM helps. The reference candidate was used only for the headroom gate, which we removed, so its score no longer enters any claim.

On claim strength, we agree, and the main contrasts are marked as resolved or not. In response to your presentation score we rewrote the paper around one figure, one algorithm and a stated scope, and moved detail to the appendix. What is new for self-improving loops is listed in our general comment. We are glad to answer anything further.

Reviewer_WtypOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper explores the problem of overfitting induced by the "selection" process in Large Language Model (LLM)-driven evolutionary program search. The study focuses on scenarios where the same noisy evaluation mechanism is used both to guide the generation of candidate solutions and to determine which candidates are retained. In the context of "learning-to-rank" experiments, the authors quantify the discrepancy between performance on the "fitness-fold" (used for evaluation) and a "held-out set." To address this, they introduce an "audited acceptance" mechanism, which requires that any improvement shown by a candidate solution on an independent "audit set" must exceed a noise threshold calculated via a paired-bootstrap method. Furthermore, the authors propose a "pre-search headroom gate" designed to filter for search spaces that offer a genuine potential for measurable improvement.

Empirical results highlight a critical distinction between "progress observed on the fitness-fold" and "improvements that generalize to unseen data." In pipeline search scenarios, the "audited acceptance" mechanism consistently performed at least as well as the traditional "fitness-based acceptance" strategy across three independent runs; in two of these runs, it outperformed the traditional approach in terms of NDCG@10 on the test set. The best-discovered pipeline achieved an NDCG@10 score 0.0057 higher than a LambdaMART baseline tuned via Optuna, though the difference in terms of revenue was not statistically significant.

Critical strengths

The paper is well organized, with a clear and logical progression from problem formulation and methodology to experimental evaluation and discussion of limitations.

Critical weaknesses
  1. Lack of global statistical guarantees for the "audited acceptance" mechanism. This mechanism employs a nominal one-sided threshold of 1.645 when repeatedly testing candidate solutions, without any correction for the problem of multiple comparisons. Because the audit fold is invoked dynamically as the search progresses, the method fails to provide a global-level guarantee against "false acceptance." This undermines the core claim that the "audited acceptance" mechanism can reliably control overfitting resulting from the selection process.
  2. Insufficient validation of the "pre-search headroom gate." This gating mechanism uses an empirically set threshold—2.5 times the noise baseline—to determine whether a search space is worth exploring. However, the evaluation in the paper covers only those search spaces that passed this gate; the authors do not verify whether the gate can accurately identify "unproductive" search spaces that ought to be filtered out. Consequently, while the existing evidence supports the mechanism’s effectiveness in making "proceed" decisions for the reported cases, it is insufficient to establish its reliability as a general criterion for "execute/terminate" decision-making.
  3. Failure to adequately isolate the contribution of "LLM-guided program evolution." The paper compares the proposed method against "random search with an equivalent computational budget" and an "Optuna-tuned single-model baseline," but it omits comparisons with "manually tuned ensemble models" or "off-the-shelf AutoML baselines" that utilize the same feature space. Furthermore, certain feature selection steps are incorporated into the initial domain knowledge provided to the LLM. These factors make it difficult to discern how much of the reported performance improvement is attributable to the "LLM-guided evolutionary process" versus the broader search space or the pre-injected domain knowledge.
Questions for authors
  1. Did the authors evaluate or control the cumulative false-acceptance risk from repeated audit checks?
  2. Did the authors test the headroom gate on search spaces that fail or lie near the proposed threshold?
  3. Did the authors compare against a hand-tuned ensemble or an AutoML baseline using the same feature space and a comparable computational budget?
2 comments
AuthorsOpenReview ↗

Acceptance claim removed, bias bound for any proposer

Thank you for the careful review. Your first point is correct: the original rule did not control cumulative false-acceptance risk, so we removed the claim. The single-search rule in the revised paper has no accept step, and the rounds rule promotes a candidate when it is ahead on a fresh slice, with no false-adoption control of its own. The guarantee is the bias bound: for any proposer, the report over-states the true gain on average by exactly zero for one pre-chosen winner, and by at most σ2ln⁡k\sigma\sqrt{2\ln k} for a short list of kk. This bounds the average, not a single report.

On your second question, the headroom gate is no longer part of the paper.

On your third question, we make no claim that the LLM helps. In the Expedia pipeline space, with 50 evaluations per arm, guided LLM search (0.4334 test NDCG@10) matched random search (0.4334) and was not ahead of TPE (a standard Bayesian tuner, 0.4357), a hand-built ensemble tuned by TPE (0.4368) or AutoML (0.4346). The comparison covers one space at one budget and does not isolate the LLM; the paper's question is how to read a reported gain from any loop.

On the evidence for that question: in eight fresh LLM runs on MSLR-WEB30K the search score over-states the test gain by about a third, while the held-out score of the same winner is unbiased on average. Across rounds, summed per-round gains over-state progress by about 1.6 times the real gain in a 180-run hyperparameter replay (a non-LLM control), and by about 45% to 80% in replays of the stored LLM ranking runs, while one final check does not. The proposer is fixed throughout, and eight LLM runs are few.

Thanks for the response. After reading through the response, I find that my previous concerns remain unaddressed. Taking into account the comments from the other reviewers, I have decided to maintain my original score.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of changes in the revision

We thank the reviewers. The question of the paper is unchanged: how much of a gain reported by a search loop is real, and how to tell. The title is unchanged too. The revision narrows the claims and widens the evidence, so we summarize it here.

Withdrawn: audited acceptance with a threshold, and the headroom gate. The single-search rule has no accept step, the rounds rule promotes a candidate when it is ahead, and the guarantee is a bound on average bias.

New for self-improving loops, in four items. Compounding: when each round's winner becomes the next baseline and every round is checked on a fresh sample, the bias of each reported gain adds up (Theorem 3), and one final untouched sample removes it. Summing per-round gains is a reporting design, not a claim about current practice. In a hyperparameter-search replay the summed report over-states progress by about 1.6 times the real gain. In replays of the stored LLM ranking runs it over-states by about 45% on the fresh runs, where the difference from one final check is not resolved, and about 80% on the earlier runs, where it is. Adaptivity: the bias bound holds for any proposer, including one that reads all earlier scores, as long as each evaluation sample is read once. Assessor: the theorems are stated for any evaluation outside the loop that uses a fresh sample, such as a simulator or an A/B test; only held-out data was tested. Predictability: a noise scale calibrated on a few runs bounds the over-statement of the search score in our settings, but only with the same proposer; a scale taken from non-LLM heuristics gave a bound 19 times the measured value.

New evidence: eight fresh pre-registered and eight earlier LLM runs on MSLR-WEB30K, a 180-run non-LLM control on forest cover type, and 20 LLM bin-packing runs, alongside the original Expedia work.

Not shown: a better final program, any advantage of the LLM, a modified proposer, or a benefit from adaptive stopping.

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

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