acceptodds
Under review as a conference paper at ICLR 2027

Prospective Grounding: When Proxy Diagnostics Warrant Control over Inference-Time Search

Abstract

Inference-time search can increase proxy reward while losing content already satisfied by the current output. When should a diagnostic of this risk guide acceptance, verification, or refinement? We introduce the Prospective Grounding Certificate (PGC) to assess whether a diagnostic can guide decisions after search selection. It tests whether the diagnostic improves prediction, whether automatic outcomes reflect human judgment, and whether the resulting policy lowers semantic loss. A non-identification result establishes why repeatable proxy evidence cannot determine semantic downside without an outcome coupling. Before collecting outcomes, PGC screens out unattainable effects and unchanged actions. It then combines valid axis-wise tests to control family-wise false authorization. Controlled worlds isolate the role of each axis. In a text-to-image qualification analysis, 1,000 cases sampled from a 1,227-case frame received 3,000 blinded paired ratings. The reported predictions and labels satisfy all three declared criteria for the specified finite-frame policy. PGC makes explicit the evidence needed to connect a diagnostic's predictive role to the semantic value of the search decisions it informs.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
inference-time search, test-time scaling, proxy diagnostics, semantic grounding, post-selection risk, policy evaluation, statistical certification

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_cExsOpenReview ↗
Rating
2
Confidence
1
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The paper addresses the risk that inference-time search improves proxy scores while losing previously satisfied content. It proposes the Prospective Grounding Certificate (PGC), which qualifies diagnostics for search control based on three criteria: improved prediction, agreement with human judgment, and reduced cost-weighted semantic loss. The framework also requires feasibility and power checks, preregistered evaluation criteria, and independent outcome assessments. Theoretical analysis shows that proxy observations alone cannot reliably identify semantic risks. Through controlled experiments and a text-to-image study involving 1,000 cases and 3,000 human ratings, the authors show that the target-attribute diagnostic passes all three tests and reduces semantic loss, while the repeatable OU energy diagnostic fails to qualify. However, these guarantees are limited to the evaluated diagnostic, policy, and setting, without establishing broader generalizability.

Critical strengths
  1. Connect prediction quality with actual decision value:
  • A diagnostic can improve prediction without changing an action. It can also predict an automatic evaluator that disagrees with humans.
  • PGC checks these separately. The controlled experiments show cases where removing one test allows an invalid combination to pass.
  1. Careful evaluation with human outcomes:
  • The natural study uses disjoint development prompts, probability sampling, and 3,000 blinded paired ratings.
  • The policy comparison uses human judgments directly. The paper also reports evaluator agreement, unresolved-label sensitivity, and cost sensitivity.
  • These make the qualification result more convincing than a comparison using only proxy scores.
Critical weaknesses
  1. While the augmented policy improves over the baseline predictor, its gain over simply keeping the current image is very small. Moreover, the formal certificate only establishes improvement over the baseline, not over this simpler alternative. This raises concerns about whether the added complexity of the proposed framework translates into meaningful practical benefits.
  2. The natural validation covers only one diagnostic–policy combination, one generator, and a fixed evaluation set, requiring annotations for 1,000 out of 1,227 cases (81.5%). Although the authors acknowledge this limitation, the substantial annotation effort raises concerns about scalability. The additional generator experiments rely on prescribed couplings rather than independent natural validation, leaving it unclear whether the framework would remain effective and practical in broader settings.
Questions for authors
  1. Does the improvement over always retaining the current image have a confidence bound above zero? What practical improvement would justify the additional diagnostic and qualification cost?

  2. How much does the successful qualification depend on sampling 81.5% of the finite frame? What sample size would the planning procedure require for a population-level claim with the same margins?

  3. On the natural study, how much annotation or computation do the pre-outcome screens save? A comparison with directly evaluating policy value using the same human-label budget would help explain the practical benefit of the full protocol.

3 comments
AuthorsOpenReview ↗

Response to Reviewer cExs

Thank you for asking when the decision benefit justifies the evaluation effort. We now quantify the costs at which M1 improves over both constant policies and compare the annotation budgets for a direct decision test and the full three-axis rule. These post-hoc analyses of the existing audit are reported in Appendix F.5.

1. Is the improvement over retention reliably positive, and when is it practically useful?

At the original 19:1 cost ratio, the 95% confidence interval is [−0.00318, 0.00334], which includes zero; the sample gain is 0.00035–0.00135. To examine where the diagnostic provides practical value, we added the full cost curve. With cost-adjusted thresholds, both simultaneous lower bounds exceed the paper's 0.005 margin at every regular grid point from 0.12 to 0.41, where the parameter is false-reject cost divided by total error cost (Figure 8).

At a 4:1 ratio, the lower bounds are 0.06324 against retention and 0.02787 against always-accept. Subtracting the 0.005 practical margin gives allowable additional average costs of 0.05824 and 0.02287, respectively, in the same normalized loss units. Thus, net benefit remains above the margin when the additional cost is below the corresponding threshold. This sensitivity calculation includes all additional costs relative to each comparator, including candidate generation when comparing with retention.

2. How much does the result depend on auditing 81.5% of the frame?

For the prediction bound, the finite-frame correction multiplies the uncertainty radius by 0.431 relative to the corresponding range-only population bound. We also subsampled the audit at five fixed budgets, with 200 nested replicates. At 900 cases, the full three-axis rule passes in 7.5% of replicates. The decision criterion alone passes in 97% using its original 0.015 error budget, or 99.5% when allocated the full 0.05 budget (Table 18). All use the same 0.005 decision margin. These percentages come from repeatedly subsampling the 1,000 audited cases.

For population-level planning, a conservative range-only calculation, assuming effects equal to the current audit estimates, gives sufficient sample sizes of approximately 9,000 for prediction and 109,000 for decision, each targeting 80% power at its allocated error level. These conservative sufficient bounds plan the prediction and decision axes separately; joint P/M/D planning also needs the measurement criterion.

3. What do the additional checks and pre-outcome screens provide?

The direct decision test addresses whether one fixed policy improves human-assessed loss. PGC additionally tests predictive contribution and agreement between the automatic and human endpoints under the specified criteria. Table 18 compares the annotation budgets for these different evidence requirements.

The pre-outcome screens identify comparisons that cannot meet their target. In the OU example, the maximum attainable improvement is 8.13 × 10⁻⁶, below the required 1.52 × 10⁻⁴, and the predictors induce no action changes. This provides a stopping criterion before collecting new qualification labels. For the natural study, we report the annotation-budget comparison above; we have no measured annotation or compute savings from these screens to report.

Thank you for the clarifications. The gain is potentially meaningful at 4:1, but the evidence does not show a gain large enough to justify the added complexity at 19:1 . The added complexity is therefore not sufficiently justified at the original operating point. I will retain my original score.

Thank you for reviewing the additional analyses and clarifying your assessment. We understand that your remaining concern is whether the benefit justifies the added complexity at the original 19:1 operating point.

We would like to clarify how we have addressed the role of that complexity in the revision. For the question of whether one fixed policy improves human-assessed loss, a direct human comparison is sufficient. The prediction and measurement checks address the additional claims that the diagnostic improves risk prediction and that the automatic endpoint agrees with human judgments. We now make these different evidence requirements explicit.

The simple-policy comparisons also make the practical scope more concrete: the original 19:1 result and the additional cost settings are reported separately. When acceptance thresholds are adjusted to the cost ratio, the additional analysis identifies conditions where gains over both always-retain and always-accept exceed the stated practical margin. We present these as post-hoc analyses.

We hope that the clearer distinction between these evidence requirements, together with the potential decision value you noted at 4:1, will be useful when weighing the paper’s overall contribution and recommendation. Thank you again for your careful consideration and for prompting these comparisons.

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

The paper asks when a diagnostic should guide inference-time search. For example, a candidate image may receive a higher proxy reward while losing the bicycle requested in the prompt. The authors propose three checks before allowing a diagnostic of such losses to affect candidate acceptance: it must improve risk prediction, the automatic evaluator must agree sufficiently with human judgments, and the resulting policy must reduce human-assessed loss. Predictors, policies, and evaluation criteria are fixed before testing, and the probability of wrongly approving a diagnostic is bounded. A text-to-image study with 1,000 image pairs and three human ratings per pair passes all three checks against the chosen baseline. However, always retaining the current image achieves nearly the same performance, leaving the diagnostic's practical benefit less clear.

Critical strengths

The paper asks a question that matters for a common practice. Adding a verifier or attribute check to inference-time search, to catch candidates that game the reward, is now common, and such checks are often justified by showing that they correlate with failures. The paper's central point is that this is not enough. A signal can predict failures without changing a single accept/reject decision, and an automatic evaluator can disagree with people about what counts as a failure. Both points are correct, the paper makes them concrete with small worked examples, and I think they will be useful to people who design search procedures.

The natural study sets a higher standard of evidence than is usual in this area. Claims about reward hacking and verifier-guided search in text-to-image generation usually rest on automatic evaluators alone. Here the decisions are judged against blinded human ratings under an analysis plan fixed in advance, and the paper reports the comparison that weakens its own headline result. I appreciate that this is reported rather than left out.

Critical weaknesses

1. At the prespecified cost ratio, the diagnostic-guided policy does about as well as never accepting a replacement. The decision test certifies that the policy using the diagnostic (M1M_1) has lower human-judged loss than the baseline policy (M0M_0), by about two percentage points. Table 14 also reports a policy that never accepts a replacement, which amounts to skipping the second round of search. It does almost exactly as well as M1M_1: the gain of M1M_1 over it is about a tenth of a point, well below the paper's own margin.

The cost ratio explains why. When a false accept costs 19 times a false reject, a replacement is worth taking only if its risk of losing the attribute is under 5%, and about 15% of replacements lose it. Keeping the current image is then close to the best available policy, and M0M_0, which accepts many more replacements than M1M_1, does worse than that.

This changes what the certified gain means. The paper's Theorem 7 implies that the best policy using only the baseline features cannot do worse than a constant policy such as retention. So M1M_1's advantage over a well-calibrated baseline is at most its advantage over retention, which is below the margin. The prespecified comparison mostly measures how poorly calibrated M0M_0 is on these prompts and tells us little about the value of the diagnostic itself. The diagnostic may well carry information, but the experiment does not show that it should control search at this cost ratio. Decision curve analysis (Vickers & Elkin, 2006) includes treat-all and treat-none as standard references for this reason, and here always-accept and always-retain should be part of the prespecified comparison.

2. The paper does not show that all three checks are needed, and in the natural study two of them mostly repeat the human comparison. The synthetic worlds in Table 2, each built so that exactly one check fails, show that the checks are logically distinct. They do not show that someone deciding whether to use a diagnostic should require all three. In one of those worlds the diagnostic-guided policy does reduce semantic loss, and the protocol still withholds it because the predicted probabilities are poorly calibrated. The paper also acknowledges that a human comparison on a random sample is enough to establish that one fixed policy beats another.

In the natural study, humans labeled more than 80% of the prompts that the authorization covers, and the automatic evaluator agreed with them almost perfectly. The prediction and measurement checks therefore add little to what the human labels already show. If those checks are meant to justify using the diagnostic on new prompts where only the automatic evaluator is available, that would be a good reason to require them, but the paper neither states that goal nor tests it.

On novelty, I have no concerns about correctness; my question is how much is new. The individual checks use standard confidence bounds, and requiring all of them to pass is a standard intersection-union argument. The non-identification result that the abstract features holds almost by construction: proxy data cannot identify semantic loss when nothing links the two. I would present it as a motivating remark. The three-part structure is close to how biomarkers and medical tests are evaluated in stages (e.g., Pepe et al., 2001), which is not discussed. I see the contribution as bringing this kind of evaluation to inference-time search, which is useful, but the paper presents the protocol as more novel than it is.

A smaller point on presentation: much of the main text is written in the protocol's own vocabulary (frozen tuples, attainability, action feasibility, authorization), and the numbers needed to interpret the natural study appear only in the appendix.

Questions for authors
  1. How were M0M_0 and M1M_1 developed for the natural study (data source, prompts, fitting procedure), and was M0M_0 meant to represent a policy someone would actually run, given that it does worse than never accepting a replacement? Could you report, labeled as post hoc, M1M_1 against a recalibrated M0M_0 or against an M0M_0 thresholded to accept as many replacements as M1M_1? It would also help to add always-accept and always-retain to the cost sweep in Table 16. If M1M_1 clearly beats both constant policies at some cost ratios, that would address much of my first concern.

  2. What does authorization establish beyond the human comparison of the two policies? If the goal is to use the diagnostic on prompts outside the audited set, where only the automatic evaluator is available, which part of the evidence supports that transfer? If the goal is the audited set itself, why require the prediction and measurement checks before using a policy that the human comparison already supports?

  3. Where and when were the predictors, endpoints, margins, costs, and sampling plan fixed, and is there a timestamped record? Were other diagnostics, cost ratios, or margins examined on these prompts before the final choice was made? The error guarantees depend on these choices preceding the outcomes, and the paper says "registered" throughout without saying where.

2 comments
AuthorsOpenReview ↗

Response to Reviewer mdrj

Thank you for suggesting the constant-policy and acceptance-matched comparisons. M1 retains a positive gain at the same acceptance budget, and the full cost curve identifies settings where it improves over both constant policies. We have added these post-hoc analyses of the existing audit in Appendix F.5 and clarified the data sources and predictor inputs in the manuscript.

1. Comparison at the same acceptance budget

Following your suggestion, we rank the full 1,227-case frame by M0's predicted risk and accept its 262 lowest-risk candidates, matching M1's acceptance count. On the 1,000 audited cases, the two policies accept 206 and 207 candidates, respectively. Accepted downside cases decrease from 19–20 to 9–10, and M1 reduces normalized loss by 0.00905–0.01105, with a 95% confidence interval of [0.00244, 0.01711]. The sample ranges account for the five unresolved human labels.

At this acceptance budget, the interval supports a positive selection benefit. Its lower bound is below the original 0.005 practical margin.

2. Does M1 outperform always-retain and always-accept?

Yes, across a range of costs. We added both constant policies to the complete 52-point cost grid, with simultaneous 95% bounds across all costs and all three comparators. When policy thresholds follow costs, M1's lower bounds against both constants exceed 0.005 at every regular grid point from 0.12 to 0.41, where the grid parameter is false-reject cost divided by total error cost. At a 4:1 false-accept/false-reject ratio, these lower bounds are 0.06324 against retention and 0.02787 against always-accept (Figure 8).

At the original 19:1 ratio, the retention comparison has a 95% interval of [−0.00318, 0.00334]. Together, these comparisons identify costs where M1 improves over both simple policies and quantify selection benefit at the original operating point.

3. What information do M0 and M1 use?

We used prompts from GenEval 2 and DPG-Bench and collected human judgments for this study. The evaluation frame contains 456 GenEval 2-derived cases and 771 DPG-Bench-derived cases; 1,000 cases received three paired human judgments each.

M0 uses the current image's global proxy score, the candidate-minus-current proxy change, the current attribute score, and the prompt-source indicator. M1 adds an attribute diagnostic computed from the current and candidate attribute scores. Each predictor produces a risk score, which is compared with the cost-defined threshold to decide whether to accept the candidate.

Thus, M0 already has information about the current image's attribute. The comparison asks whether candidate-relative attribute information improves risk prediction and the resulting replacement decisions.

4. Does the gain persist against a threshold-adjusted M0?

We evaluated all distinct global threshold policies available from the recorded M0 scores, as well as thresholds selected separately for the two sources. At 4:1, M1's sample gain over the best global M0 threshold is 0.01540, with a simultaneous lower bound of −0.000163 over the full cost/threshold family. The source-specific comparison also crosses zero. At 19:1, the sample-optimal M0 threshold has slightly lower loss. Appendix F.5 reports these threshold-adjusted comparisons alongside the equal-budget comparison in point 1.

5. What does PGC add to a direct human comparison?

For the claim that one fixed policy improves human-assessed loss, a direct human comparison is sufficient. PGC assesses the broader claim that a diagnostic improves risk prediction, its automatic endpoint agrees with human judgments, and its policy improves human-assessed loss. The three criteria correspond to those three claims.

Under the stated probability-sampling design, the finite-frame bounds concern all 1,227 cases, including the 227 unaudited cases. The bounds estimate average performance across the full 1,227-case frame. For a new prompt distribution, the corresponding claims require evaluation on that distribution.

Following your references, we now discuss decision-curve analysis and staged biomarker validation. We position the contribution as specifying these claims for inference-time search, together with exact checks for unattainable predictive gains and unchanged policy actions before collecting qualification outcomes.

To make the evidence easier to follow, the main text now specifies the predictor inputs and acceptance rule and reports the retention and acceptance-matched comparisons alongside the original M0 comparison.

Thanks for running the new comparisons. The clear gain over both constant policies at milder cost ratios is useful. But the diagnostic still isn't shown to beat a properly tuned baseline. At your prespecified cost ratio it does no better than keeping the current image, and at the milder ratio its edge over a thresholded baseline isn't certified. Since a direct human comparison is enough to justify a fixed policy, I'm also still unsure what the other two checks buy. I'm keeping my score at 2.

Reviewer_TcB3OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper proposes the PGC protocol, which determines when an automated risk diagnostic can be trusted to govern inference-time search decisions in generative models. The key insight is that an observable proxy process does not guarantee semantic alignment, identical proxy trends can correspond to opposite semantic risks. The authros propose a multi-axis qualification framework that requires clearing 3 components simultaneously under family-wise error control: prediction, measurement, and decision. The framework enforces pre-outcome feasibility screens to filter out unviable comparisons before collecting expensive human labels. The authors validate the framework through controlled component deletions and a text-image study.

Critical strengths
  1. The observation that identical proxy process can mask opposite semantic tasks makes sense. It challenges the naive assumption that a stable or repeatable metric is automatically useful for steering search.

  2. The use of exact outcome-blind support checks is practical. It prevents wasting resources on extra diagnostics.

  3. The text-image study is substantial, backed by 3000 human ratings, rigorous finite frame bounds, and explicit handling of unresolved human majority votes.

Critical weaknesses
  1. PGC requires fixing a dense stack of elements beforehand. While mathematically sound, this friction may limit adoption in fast-moving iterative research where search policies and reward models change weekly.

  2. The decision axis relies heavily on a fixed cost ratio to establish the acceptance threshold. More discussion on how practitioners set these cost parameters in complex generative tasks is encouraged.

  3. The paper contains a dense web of notation. While precise, it makes the key mechanics hard to parse. To improve readability, consider streaming definitions or moving some notations to earlier paragraphs.

Questions for authors
  1. How sensitive is the PGC authorization outcome to misspecification of the cost ratio or threshold?

  2. Since prompt distributions is real-world workflwos shift dynamically, how fragile is a granted PGC certificate when the search policy encounter out-of-distribution prompts nt covered by the orginal qualification frame?

  3. For domains with ingerently high subjectivity, what happends to the feasiblity of clearung the measurment and decision bounds if the rate of unresolvd majorities scales up significantly?

1 comment
AuthorsOpenReview ↗

Response to Reviewer TcB3

Thank you for your suggestions on practical use and readability. We have clarified the predictor inputs and acceptance rule in the main text, and added post-hoc cost and unresolved-label analyses in Appendix F.5. Below we explain how costs affect decisions, which prompts the result covers, and how unresolved human judgments affect the three criteria.

1. How sensitive is the result to the cost ratio?

We examined two settings: adjusting the acceptance threshold with the cost ratio, and keeping the original actions fixed while changing the evaluation costs. Figure 8 shows both over the complete 52-point grid, with simultaneous 95% bounds within each panel.

When thresholds follow costs, M1 improves over both constant policies with positive lower bounds at every regular grid point from 0.11 to 0.50. When actions remain fixed at the original threshold of 0.05, the corresponding region is 0.09–0.16. The grid parameter is false-reject cost divided by total error cost. These intervals describe decision value; full PGC qualification also requires the prediction and measurement criteria.

In practice, the cost ratio should reflect the consequences of accepting a harmful replacement versus rejecting a safe one. A 19:1 ratio represents a strongly downside-averse application; 4:1 places relatively more value on accepting safe replacements. The ratio should be specified from that application preference before outcome evaluation. The curve then shows the sensitivity around the chosen setting.

2. Does the certificate carry over to out-of-distribution prompts?

It applies to the declared prompt frame or sampling distribution; it does not automatically cover a shifted population. For a changed prompt distribution, the practitioner should evaluate the intended policy on a sample from that new distribution and reassess its measurement properties. The two-source analyses in our appendix describe variation within the current study.

For frequent model updates, the protocol evaluates a specified version of the diagnostic, evaluator, and search policy. An update calls for reassessment of the claims it affects. We have clarified the predictor inputs and acceptance rule in the main text and collected the sensitivity analyses in Appendix F.5.

3. What happens when more human judgments remain unresolved?

In our masking experiment, the measurement criterion is the first to stop passing. Keeping the five original unresolved cases, we randomly masked additional resolved endpoints in 200 nested replicates. With 14 unresolved cases, the decision criterion passes in all replicates, while the measurement criterion does not pass because the bound on between-source sensitivity differences exceeds its tolerance. With 24 and 54 unresolved cases, the decision criterion passes in 95% and 37.5% of replicates, respectively.

This gives a concrete interpretation of the protocol's response to ambiguity: it separates evidence for policy value from evidence that the automatic endpoint has been measured accurately enough. For a subjective task, the human endpoint and treatment of ties or uncertainty should be specified before evaluation. Our experiment quantifies random missingness on the existing endpoint; evaluating a genuinely subjective endpoint requires its own audit.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.