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Under review as a conference paper at ICLR 2027

Are You Sure Your LLM Is Sure? Repairing and Auditing Confidence

Abstract

Confidence scores determine whether an LLM answer is accepted, reviewed, or regenerated, yet scalar recalibration can only correct errors that are visible through the score itself. We introduce RADAR (Repair, Adopt, and Diagnose After Recalibration), a reliability framework that separates confidence repair from deciding whether the repair should be deployed and auditing the errors that remain. Under squared loss, we decompose prediction risk into outcome noise, information hidden by the score, and mapping error; restricting repair to order-preserving maps additionally introduces a pooling gap. For repair, we propose Probe-Anchored Isotonic Calibration (PAIC), which learns a monotone map from correctness-probe predictions on unlabeled target prompts. We show that PAIC's excess risk depends on the probe's score-conditional bias and fitting error, rather than on its overall prediction accuracy. For adoption, we derive a paired procedure with finite-sample control of false improvements. For auditing, we develop a prompt-clustered kernel test that detects feature-aligned residual errors while accounting for dependent answers from the same prompt. Across multiple LLM checkpoints, benchmarks, and distribution shifts, we find that richer predictors can improve confidence estimation, but projecting their information back to a scalar score can lose these gains, and lower prediction risk does not necessarily yield better review decisions. Across 47,400 replayed raw-score allocations, paired betting adopts candidates with lower held-out test risk in 42.95% of allocations, compared with 15.09% for one-sided empirical Bernstein. Together, RADAR provides a principled workflow to repair what a scalar confidence score can express, adopt a repair only when supported by evidence, and diagnose the systematic errors that recalibration leaves behind. Code and data will be released upon acceptance.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
LLM confidence, Confidence calibration, prediction-powered inference, Kernel residual auditing

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

This paper proposes the RADAR framework, which divides the processing of LLM confidence into three stages: Repair, Adopt, and Diagnose. Theoretically, the authors decompose the squared risk of scalar recalibration into outcome noise, information not included in the original score, mapping error, and the pooling gap introduced by monotonic constraints, thus demonstrating that scalar recalibration cannot recover information compressed by the score. In the Repair stage, the authors propose PAIC, which uses a source-trained correctness probe to fit a monotonic mapping of the original confidence onto unlabeled target prompts. In the Adopt stage, a paired betting-based test is proposed to control the probability of incorrectly deploying no-improvement candidates. In the Diagnose stage, a prompt-clustered kernel test is proposed to detect residual errors associated with given features and handle the dependencies between multiple answers under the same prompt. Experiments covering various models, tasks, and distribution shifts show that PAIC can reduce Brier risk in some settings, but information from richer predictors may be lost after projection back to the scalar score, and reduced prediction risk does not necessarily improve actual review decisions.

Critical strengths

1.The delineation of the scalar recalibration capability boundary is clear and important. Risk decomposition clearly distinguishes between mapping errors that can be corrected through remapping and information lost in the original score, and further analyzes the pooling gap caused by monotonicity. This explains why a score that can achieve calibration still systematically fails on identifiable subgroups.

2.RADAR separates fitting, deployment, and auditing, which has strong practical implications. In particular, the paired adoption procedure and prompt-clustered audit avoid using the same probe for self-validation and incorrectly treating multiple responses to the same prompt as independent samples. The paper also reports results showing that PAIC has no benefit or reduces downstream utility, making the conclusions more credible than simply showing positive benchmark gains.

Critical weaknesses

1.The core assumptions of PAIC are difficult to verify in its primary use cases. PAIC can fit without target labels, but this guarantee depends on a sufficiently small target-domain score-conditional probe bias, which itself typically requires target labels for evaluation; the final adoption phase also still requires independent target labels. The paper needs to more clearly explain when PAIC offers a substantial advantage in label cost or deployment performance compared to directly waiting for a small number of target labels before label-based recalibration.

2.The main adoption results provide weak support for PAIC itself, and its overall external validity is limited. In cached raw-score allocations, the vast majority of adoptions in paired betting chose richer direct predictors instead of PAIC. Therefore, these results primarily validate the statistical power of the adoption test and do not adequately demonstrate that PAIC is a frequently worthwhile repair in practical deployments. The experiments are also primarily based on cached responses, a limited-scale open-source model, and several overlapping refits; some results only provide pointwise or descriptive uncertainty.

Questions for authors

1.Could you report the adoption results separately, including only the original score and each PAIC variant, excluding richer direct predictors? For example, the PAIC certification rate, beneficial adoption rate, false adoption rate, and the target labels required to achieve a given adoption power. This result directly impacts my assessment of the actual value of PAIC.

2.Does the paper’s indistinguishability result imply that score-conditional probe bias cannot, in general, be diagnosed from unlabeled target data alone? If so, could the authors clarify the additional assumptions or labeled evidence that practitioners would need before relying on PAIC? It would also be helpful to report, using held-out labels, the empirical relationship between score-conditional bias and PAIC’s risk improvement.

8 comments
AuthorsOpenReview ↗

Response to Reviewer rfhz (Part 1/3)

Thank you for the careful review and for two precise questions. Q1 asked for exactly the analysis that isolates PAIC's value, and answering it has made the paper's case clearer. Page and line numbers refer to the revised manuscript.

Q1/W2. Report adoption with only the original score and the PAIC variants: certification, beneficial and false adoption, and the labels needed for a given power.

Done, and the result supports PAIC itself, not only the test: with PAIC repairs as the only candidates, the betting test certifies PAIC in 33 of 42 shift experiments, and in up to 72% of trials on the 30 experiments of the submission; no adoption was a false one (Section 4.3, page 10, lines 489–499).

(a) The 30 experiments of the submission that repair the model's own confidence, with the three PAIC repairs as the only candidates against the original score (Appendix F.5, pages 78–79, lines 4205–4215). A trial is one random draw of the labeled examples:

Labeled prompts50100250500
PAIC certification rate, betting15.2%29.6%58.4%72.1%
Beneficial adoption rate (adopted repair better on the test pool)15.2%29.6%58.4%72.1%
False adoption rate (adopted repair worse on the test pool)0%0%0%0%
PAIC certification rate, empirical Bernstein0%0.7%19.2%30.0%
Brier change of the betting policy−0.025−0.036−0.046−0.049

Every adoption was beneficial: each adopted repair has lower risk on the test pool, and the 10 of 90 repairs that do not improve were never certified. Under the stricter count of the appendix, where the gain must also be supported by the adopted repair's own test interval, the rates are 15.1%, 23.4%, 28.1% and 28.2%, and 76.9% with 500 labels on the 11 experiments that contain such a repair.

(b) An end-to-end pipeline on 42 shift experiments, with PAIC repairs as the only candidates and every stage (repair, test, audit) on its own prompts (Appendix F.4, page 76, lines 4059–4071): PAIC is certified in 33 (15 of 18 in the main benchmark, 18 of 24 into or within Humanity's Last Exam, HLE), and all 33 certified repairs are better on held-out test prompts (intervals below zero). Against the calibration in use, which was fitted on source labels, the deployed confidence lowers Brier risk by 0.1025 on average over the 24 HLE experiments and by 0.0136 over the 18 of the main benchmark (Table 35). Nothing is adopted in the six experiments where there is almost nothing to repair (headroom 0.003–0.005).

(c) A newer model (Appendix F.8, page 81, lines 4371–4373): on Qwen3.5-9B, the betting test certifies PAIC from 250 labels.

Labels for a given power: about 6 divided by the gain, where the gain is how much the repair lowers the Brier risk. Corollary 3.3.1 (page 7, lines 334–348) puts the count at the order of log⁡(1/α)/gain\log(1/\alpha)/\text{gain}. A test on 77 improving PAIC repairs, with gains from 0.0015 to 0.21, measures it (Appendix F.11, page 86, lines 4609–4621): labels scale as gain−0.97\text{gain}^{-0.97} (95% interval −1.07-1.07 to −0.92-0.92), about 6/gain6/\text{gain} for 50% power and 7/gain7/\text{gain} for 80%. The corollary's bound was never violated, and repairs that do not improve were certified in at most 0.025% of draws. The law also explains (c): under a second, more lenient grader the gain is a sixth as large, and 750 labels are then not yet enough. Because the test is valid at every sample size (Proposition A.36), labeling can stop at the first certification, so the gain need not be known in advance.

AuthorsOpenReview ↗

Response to Reviewer rfhz (Part 2/3)

W2 (continued). The main adoption results chose richer predictors, not PAIC. External validity: cached responses, limited-scale models, overlapping refits, pointwise uncertainty.

The full candidate family. You are right that when richer predictors are candidates and their inputs can be served, the betting test usually adopts them (Appendix B.10); PAIC is for deployments that can serve only the confidence, as with a hosted model (page 4, lines 186–191). On HLE, where PAIC beats the direct probes, the same rule adopted a PAIC repair in 13,072 trials and a richer predictor in 3,776 (Appendix F.3). In both experiments with the full family, 69,000 trials, the test never adopted a score that was worse on held-out prompts (Tables 15, 32), and in 168,000 simulated decisions with nothing to gain it never selected a harmful candidate. The theory says why: the adopted score is safe and near-best among the candidates that can be detected (Corollary A.37).

External validity. The revision extends the same protocol to fresh generation with a newer model (Qwen3.5-9B, 6,000 answers; page 9, lines 470–476), to a harder benchmark (HLE; Appendix F.3, pages 71–72, lines 3829–3858), and to the end-to-end pipeline of Q1, in which every stage uses its own prompts. The breadth study includes Qwen2.5-32B (Appendix C, pages 63–64, lines 3348–3420). Two further experiments from the discussion period, with a second new model (Gemma-4-12B-it) and on long-form question answering (ASQA), are reported in our response to Reviewer 5WG2. The new comparisons report simultaneous intervals, and the bias analysis of Q2 uses a cluster bootstrap over the 14 combinations of shift and model, because the refits of a combination overlap (Appendix F.1, page 68, lines 3632–3647).

Q2. Does the indistinguishability result mean that the probe's bias cannot be diagnosed from unlabeled target data? What must practitioners assume or label? Please report the empirical relation between this bias and PAIC's risk improvement.

Yes: in general it cannot, and Proposition 3.2.2 makes this precise (page 6, lines 270–274; proof in Appendix A.12, page 40, lines 2122–2147). It turns the indistinguishability result of the submission into a statement about the deployment decision: it constructs two populations in which every unlabeled quantity, the probe's predictions included, has the same distribution, while the same PAIC repair lowers risk by η2\eta^2 in one and raises it by η2\eta^2 in the other. Every label-free rule therefore has worst-case regret of at least η2/2\eta^2/2. Unlabeled data do bound the size of the change (Proposition A.26, page 39, lines 2065–2088), but not its sign.

What practitioners need. Without target labels, only an assumption helps: under covariate shift with a bounded density ratio, the ratio times the probe's excess risk on source data bounds the bias (Remark A.30, page 40, lines 2148–2159). This requires correctness given the inputs to behave as on the source, which unlabeled data cannot check. Otherwise a small labeled target set suffices: to certify the repair (about 6/gain6/\text{gain} labels), to estimate the bias directly, or to remove its constant part at rate 1/m1/m with mm labels (Corollary 3.2.3, page 6, lines 282–295).

The empirical relation, with held-out labels. By Corollary 3.2.1, PAIC's gain is the headroom (what the shift left to repair) minus the probe's squared bias. So what PAIC loses against a fit on target labels, its shortfall, should follow the bias, and it does; the probe's accuracy does not (Appendix F.1, page 68, lines 3649–3660; 84 cases: 42 shift experiments, two probes; cluster-bootstrap intervals):

QuantityResult
PAIC's shortfall against the probe's biasSpearman 0.93 [0.78, 0.97], slope 0.96
The same, within the main benchmark (small bias)0.59 [0.28, 0.78]
PAIC's shortfall against the probe's MSE0.35 [−0.11, 0.77]
PAIC's risk change against the bias, adjusted for headroomPartial Spearman 0.46 [0.21, 0.61]: a larger bias, a smaller improvement
Controlled test: each probe's MSE raised by 0.010PAIC's risk rises by 0.0131 if the added error varies with the score, by 0.0012 if it cancels within score bins (larger in 83 of 84 cases); over 504 perturbed probes its change tracks the change in bias (0.92), not in MSE (0.38) (Appendix F.2, page 71, lines 3780–3791)

At the setting level, the shortfall in Table 1 matches the bias to within 0.002 where the bias is small and to within 0.008 on HLE, where it reaches 0.15 (page 8, lines 423–431; Figure 3).

AuthorsOpenReview ↗

Response to Reviewer rfhz (Part 3/3)

W1. The probe's bias needs target labels to check, and adoption needs labels too. When does PAIC beat simply waiting for a few target labels and recalibrating?

Before target labels exist and while they are few. With none, PAIC is already close to supervised recalibration; and the labels that do arrive make it better (Appendix F.6, page 79, lines 4245–4255; Appendix F.8; Tables 41, 44).

Target labels at handWait and recalibrate on themPAIC
NoneNot possible: the shifted confidence stays in useRepaired at once: 95% and 80% of the gain of a 750-label fit on MATH, 59–97% of the gap to a 250-label fit on HLE, a median 87% over the six shift settings
100Fitted (risk 0.2304 for Llama, 0.1464 for Qwen), not yet certifiedWith no labels, already level (0.2294, 0.1468); the 100 labels are free for the decision, or correct the probe: then better by 0.005 for Llama, level for both Qwen models
250 to 750Certified from 250 labels (Llama), 500 (Qwen3.5-9B), not within 750 (Qwen2.5)Certified from 250, 250 and 750 labels

Two results explain the table. Any calibration must be certified on labels independent of those used to fit it (Proposition 3.3), so PAIC, which uses none to fit, spends every target label on the decision. And a few labels remove the constant part of the probe's bias at rate 1/m1/m, against m−2/3m^{-2/3} for refitting the calibration (Corollary 3.2.3): shifting the probe lowers PAIC's risk in all 16 cases tested (page 10, lines 501–505). The corollary also says when to do which: shift the probe when its bias is nearly constant across scores, refit the calibration otherwise. With many labels the two routes meet, and the same test adopts whichever is better.

We sincerely thank the reviewer for their constructive feedback and thoughtful suggestions. We hope that our responses and additional experimental results have adequately addressed the concerns raised. We would be happy to provide any further clarifications or answer additional questions. If you find that your concerns have been satisfactorily addressed, we would be grateful if you could kindly reconsider and update your evaluation score accordingly.

Reviewer_5WG2OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The paper shows that LLMs’ confidence can look well calibrated but can still hide key information such as prediction errors, which scaler recalibration cannot fix. The author proposes RADAR, which looks at confidence calibration in three stages: repairing the score, deciding whether to adopt the repair, and diagnosing the errors that remain.

For repairing, the author introduces PAIC, which distills an independently trained correctness probe into a monotone function of the original confidence using unlabeled target prompts. For adopting, they use targeted prompts to decide whether a repaired score should replace the original. And for diagnosis, the authors propose a feature-aware residual audit that detects residual errors while treating prompts as an independent sampling unit.

Experiments are done across several models and benchmarks. Current results show PAIC helps only in limited cases; it improves over source-fitted recalibration under some distribution shifts, but the gains are inconsistent across models and settings.

Critical strengths
  1. The paper looks at a useful problem that shows that the confidence score can be calibrated yet still hide predictable errors, and that recalibration can help fix the score’s value but still not recover information that the score was missing.

  2. The analysis of PAIC shows that only the probe’s average error matters and not its overall accuracy.

  3. The paper shows that choosing a candidate based on the probe can select the wrong one, to avoid this, proposes a labeled betting test that avoids switching to a worse score while needing fewer labels than standard bounds. It requires only 1 quarter of the labels required by one-sided empirical Bernstein bounds.

Critical weaknesses
  1. The results are mixed: The main claim of the paper is that PAIC improves the confidence under distribution shift without any target labels. However the model PAIC only clearly wins only in the raw-score shift experiment. PAIC loses entirely in presentation gains, and the results are mixed in MATH (llama improves but qwen does not).

  2. The method still relies on targeted labels, which weakens the main claim of the paper.

  3. The method assumes that we have access to probes that are transferable to target distribution. The benefits are also inconsistent, for example in MATH PAIC helps llama but not qwen.

  4. All experiments use smaller and old models, the dataset also utilizes short answer MCQ questions. Open ended generations, sampling based confidence etc are missing from the paper.

  5. The paper is also very hard to read, the main text is not standalone and most of the information is available in the appendix. For example, most results are in the appendix.

The text is hard to follow and looks very AI generated + scores 100% on pangram even for abstract and intro

Questions for authors

the 5 questions above and:

  1. The paper requires extensive restructuring, since most of the main results / tables are in appendix, what table should be referred to understand the main takeaway?

  2. Did the authors test their methods on other newer models like qwen3.5? And newer datasets?

8 comments
AuthorsOpenReview ↗

Response to Reviewer 5WG2 (Part 1/4)

Thank you for the detailed and constructive review, and for recognizing the paper's two core insights: only the probe's average error at each score matters, and the betting test needs far fewer labels than standard bounds. Page and line numbers refer to the revised manuscript.

W1. Results are mixed: clear gains only under raw-score shift, losses under a change of presentation, and on MATH a gain for Llama but not for Qwen.

PAIC improves in most settings: in 81 of 84 cases across the main benchmark and Humanity's Last Exam (HLE), and on a newer model. The paper also offers more than a method that wins: a theory that predicts where a repair made without labels helps, where it cannot, and by how much. The three cases you list are that theory's predictions, confirmed on held-out labels.

The idea. The calibration in use was fitted on labeled data from one setting (the source). When the model is then used on other data (the target: a new domain, harder questions), a confidence of 0.8 may no longer mean 80% correct. This change is the shift, and a repair can only recover what the shift has altered. We measure a confidence by its Brier risk, its mean squared error against correctness (lower is better), and call gain the amount by which a repair lowers it. Two quantities set the gain:

  • How much there is to repair: the headroom. It is the most that any order-preserving re-mapping of the confidence can gain over the calibration in use, that is, how far the shift moved the meaning of the confidence (Theorem 3.1).
  • How wrong the guide is: the probe's bias. PAIC has no target labels; it learns from a probe, a predictor of correctness trained on the source. What it loses is the square of the probe's average error among answers with the same confidence (Theorem 3.2).

Corollary 3.2.1 (page 5, lines 257–263) combines them: gain = headroom − squared bias. To our knowledge it is the first two-sided condition, in true target risk, for when recalibration toward an imperfect reference improves on the calibration in use. For each case you noted (Table 1, page 9, lines 432–447):

Case you noted (Llama / Qwen)HeadroomPredicted gainMeasured gain
Raw confidence, harder questions0.0150 / 0.01550.0123 / 0.01200.0128 / 0.0138
MATH, learned confidence0.0094 / 0.00190.0041 / −0.00040.0052 / −0.0004
Same questions, presented differently0.0023 / 0.0003at most the headroom−0.0029 / −0.0053
Raw confidence, new domain (GSM8K to HLE)0.299 / 0.1960.151 / 0.0710.154 / 0.072
  • Raw confidence under shift. The shift moved the meaning of the confidence and the probe's bias is small, so PAIC gains what the theory says: it lowers the risk by 4.9–16.4%, below every baseline fitted on the source in all six settings, and on HLE by 9–56% and 34–85% with the two probes (page 9, lines 456–462).
  • MATH: a gain for Llama, none for Qwen. Same method, same data. For Llama there is five times more to repair than for Qwen, where the headroom is smaller than the probe's bias. The theory predicts +0.0041 and −0.0004; the data give +0.0052 and −0.0004.
  • A change of presentation. Here the same questions are only presented differently (other names, another order of the facts, added irrelevant context). The answers do not change, so the confidence keeps its meaning and there is almost nothing to repair: no re-mapping, fitted with or without labels, can gain more than the headroom, 0.0023 and 0.0003 (page 9, lines 478–481).

So a setting without a gain is not a failure of the method. It is a prediction, of size as well as sign, that the data confirm, and that is a stronger result than winning everywhere: a practitioner knows when to expect a benefit, and how large; and where there is none, the adoption test (W2) keeps the calibration in use: it approved no repair in the six experiments whose headroom is only 0.003–0.005. Over all of Table 1, predicted and measured gains differ by at most 0.002 on the main shifts and 0.008 on HLE (Figure 3).

AuthorsOpenReview ↗

Response to Reviewer 5WG2 (Part 2/4)

W2. The method still relies on target labels, which weakens the main claim.

The claim stands: the repair is fitted with no target label, and it is already close to supervised recalibration. Labels enter only in the decision to deploy it, where no method can do without them, and few are needed.

StepTarget labelsWhy
Fit the repairNonePAIC is fitted to the probe's predictions on unlabeled target prompts; about 100 suffice (Appendix F.7)
Decide whether to deploy itAbout 6 divided by the gain: 90 labels for a gain of 0.07, 125 for 0.05, 560 for 0.01Two deployments can look the same in everything that can be measured without labels, while the same repair helps in one and harms in the other. So no method, ours or any other, can decide without labels (Proposition 3.2.2)
Improve it (optional)The same labelsUsed to correct the probe, they lower PAIC's risk in all 16 cases tested (Corollary 3.2.3)

Why so few labels? The decision is made by the betting test, a sequential statistical test: it looks at labeled examples one at a time, accumulates evidence that the repair is better than the calibration in use, and stops as soon as the evidence is conclusive, with a guaranteed error rate. A larger gain shows sooner, so Corollary 3.3.1 predicts a number of labels proportional to 1/gain1/\text{gain}. We measured it on 77 repairs with gains from 0.0015 to 0.21: about 6 divided by the gain (Appendix F.11). On HLE, where gains are about 0.3, 100 labels suffice every time. As you noted, the test needs far fewer labels than standard bounds: with 100 labels it certifies PAIC as often as the empirical-Bernstein bound does with 500, and in 69,000 trials (random draws of the labeled examples) it never certified a confidence that was worse on held-out data (Tables 15, 32).

With no target label, PAIC is already close to supervised recalibration. It closes a median 87% of the gap to a fit on target labels over the six shift settings (Appendix B.3), reaches 95% and 80% of the gain that supervised recalibration obtains from 750 target labels (Appendix F.6), stays within 0.005 of it on Qwen3.5-9B, and without a shift matches a fit on labels to within 0.0004. Under the same test it is certified as early as supervised recalibration, or earlier: on Qwen3.5-9B from 250 labels, against 500 (Appendix F.8).

W3. PAIC assumes access to a probe that transfers to the target distribution.

It needs less than that: as you noted among the strengths, only the probe's average error among answers with the same confidence matters (its bias), and it need only be smaller than what the shift left to repair (Theorem 3.2, page 5, lines 239–243, with a matching lower bound; Corollary 3.2.1). The data agree (page 9, lines 450–454; Appendices F.1, F.2):

  • A probe that transfers poorly still repairs: from GSM8K to HLE its squared bias reaches 0.15, the headroom is 0.30, and PAIC gains 0.154 (Table 1).
  • Across the 84 cases, what PAIC loses follows this bias (rank correlation 0.93 [0.78, 0.97]), not the probe's overall error (0.35 [−0.11, 0.77]).
  • When we add the same amount of error to a real probe in two ways, PAIC's risk rises by 0.0131 if the error shifts the probe's average at each confidence level, and by only 0.0012 if it cancels out there.
  • The same quantity tells which probe to use: in every shift into HLE from another dataset, the probe with the smaller bias gives the lower risk.

Nor is a hidden-state probe required: any predictor of correctness can play the probe's role. With a second pass of the same model, which judges its own answer, PAIC lowers risk from 0.213 to 0.197 (Appendix B.8, page 55, lines 2951–2954); agreement with a sampled answer works as well (W4/Q2). The probe is trained once on 500 labeled source prompts and is not needed at serving time.

AuthorsOpenReview ↗

Response to Reviewer 5WG2 (Part 3/4)

W4/Q2. The experiments use small, older models and short-answer or multiple-choice data; newer models such as Qwen3.5, newer datasets, open-ended generation and sampling-based confidence are missing.

Thank you for pushing on this. We extended the same shift experiments:

  • A newer model, as you suggested: Qwen3.5-9B (2026), 6,000 fresh answers. Under the primary grader, PAIC lowers Brier risk from 0.247 to 0.199 (19%, simultaneous interval 15–24%), below the calibration fitted on the source as well; and with no target label it stays within 0.005 of supervised recalibration on 100 to 750 target labels (Section 4.2, page 9, lines 470–476; Appendix F.8).
  • A newer dataset: HLE (2025): 1,567 graded questions, eight free-form answers each. The model's own confidence ranks answers worse than chance (AUROC 0.43, 0.41); with no HLE label, PAIC with the linear (ridge) probe beats every calibration fitted on the source in 24 of 24 runs and lowers ECE from 0.20–0.47 to 0.09–0.16 (Appendix F.3, pages 71–72, lines 3829–3858).
  • Sampling-based confidence: here the probe's role is played by agreement with an independently sampled answer (Corollary A.40, pages 46–47, lines 2474–2491). PAIC with the probe matches or beats it (Brier 0.199 against 0.200 and 0.213).

On Qwen3.5-9B all three stages work: the betting test certifies PAIC from 250 labels, the audit finds subjects that stay over-confident, and a per-subject correction fitted on 250 labels lowers held-out risk from 0.199 to 0.171, below supervised recalibration on the same labels (0.196; Appendix F.12). Under a second, more lenient grader there is less to repair and the gain is smaller, as Corollary 3.2.1 predicts (predicted gains 0.045 and 0.003; observed 0.051 and 0.006).

Two further experiments were run during the discussion period. They are not in the PDF, and we report them here:

  • A second new model: Gemma-4-12B-it, 6,000 fresh answers, GSM8K to MATH. Under the primary grader, PAIC, with no target label, lowers the Brier risk of the model's own confidence from 0.201 to 0.176 (simultaneous bootstrap interval of the gain 0.016–0.035), the level of supervised recalibration on 100 to 750 target labels, and the betting test certifies it at 750 labels. Under the second grader there is almost nothing to repair (0.0463 against 0.0460 for a fit on target labels), so Corollary 3.2.1 predicts no gain: the selected repair would have raised risk to 0.055, and the betting test rejects it at every number of labels tried and keeps the model's own confidence. As you noted among the strengths, the labeled test avoids switching to a worse score.
  • Open-ended generation: ASQA, closed-book long-form question answering, with both new models. The model's own confidence is badly over-confident there: its mean is 0.58 and 0.78, while about 2% of answers pass the official completeness criterion. PAIC, fitted on unlabeled target prompts, lowers ECE from 0.56 and 0.77 to 0.003 and 0.002 and Brier risk from 0.340 and 0.609 to 0.021 and 0.016, level with supervised recalibration on 100 to 500 target labels, and the betting test certifies the repair from 100 labels, the smallest number tried. With QA-F1 as a graded outcome, squared loss falls from 0.236 and 0.445 to 0.060 and 0.057.

In the paper, GSM8K, MATH, the 10K set and HLE also score sampled free-form answers; only BoolQ and ARC are multiple choice. The breadth study includes Qwen2.5-32B (Appendix C).

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

RADAR, a framework for repairing, validating, and auditing LLM confidence scores. It proposes PAIC to recalibrate confidence using correctness probes and unlabeled target data, a paired betting procedure to certify improvements, and a prompt-clustered kernel test to detect residual errors. Also, theoretical analysis captures the limitations of scalar recalibration, while experiments across multiple LLMs and distribution shifts show that improved calibration does not necessarily lead to better decisions.

Critical strengths

The paper provides a analysis of the limitations of scalar recalibration, with theoretical guarantees for confidence repair, adoption, and residual auditing, and also conduct extensive experiments across multiple LLMs, benchmarks, and distribution shifts, including analyses of when improved calibration fails to benefit downstream decisions.

Critical weaknesses
  1. NO INTRODUCTION??? why? and also the section before related work which I assume this is the introduction is really poorly-written....
  2. The font and format for Figure 2 is really wired, maybe you can fix that.
  3. The experimental section is fragmented and difficult to follow. It combines multiple datasets, evaluation settings, and statistical procedures without a clear overarching narrative. The authors should better organize the experiments and clearly explain which results support each contribution.
  4. Although the framework improves prediction risk in some settings, these improvements do not consistently translate into better downstream decisions. The paper should provide stronger evidence of when and why the proposed framework is practically beneficial.
Questions for authors
  1. Could the authors clarify the key methodological contributions beyond existing isotonic regression, prediction-powered inference, and kernel calibration tests and what is fundamentally new compared to combining these established techniques?

  2. PAIC does not consistently outperform simpler baselines, and improvements in prediction risk do not always translate into better downstream decisions. Under what conditions should practitioners expect RADAR to provide meaningful benefits?

  3. Although PAIC performs recalibration without target-domain labels, the adoption stage still requires labeled target data. How does the overall framework compare with conventional supervised calibration methods in terms of labeling cost and practical efficiency?

6 comments
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Response to Reviewer Chpr (Part 1/3)

Thank you for the candid review, and for recognizing the theoretical guarantees and the breadth of the experiments; your comments helped us state the paper's message clearly. Page and line numbers refer to the revised manuscript.

W1. No Introduction, and the opening section is poorly written.

The opening section was the Introduction; it now carries that title. We have also simplified it for a broader audience, with concrete examples (Section 1, pages 1–3, lines 38–125).

W2. The font and format of Figure 2 look odd.

Fixed: Figure 2 is redrawn at its true proportions, with readable labels (page 8).

W3. The experiments are fragmented; it is unclear which results support which contribution.

Section 4 keeps the experiments of the submission and orders them by the question each one answers (page 8, lines 406–408):

QuestionResultEvidenceWhat the data show
What does a single confidence number miss?Theorem 3.1Section 4.1, Figure 2A richer predictor loses accuracy when it is reduced to one number per answer
When does a repair without labels help, and by how much?Theorem 3.2, Corollary 3.2.1Section 4.2, Table 1, Figure 3Predicted and measured gains agree to within 0.002 (0.008 on Humanity's Last Exam, HLE)
What are labels from the new data needed for?Proposition 3.2.2, Corollaries 3.3.1, 3.2.3Section 4.3Not to fit the repair; only to confirm it, and few suffice
What does the audit find?Theorem 3.4Section 4.4Errors that no recalibration can fix; correcting them lowers the error
Does a better confidence give better decisions?Eq. (3)Section 4.5Yes: accept-or-review decisions cost less, on average over review costs

W4/Q2. Lower risk does not always give better decisions, and PAIC does not always beat simpler baselines. When should practitioners expect a benefit?

When the model is used on data unlike the data its confidence was calibrated on (a new domain, harder questions); and the theory says how large the benefit will be.

Such a change of data, a shift, alters what a confidence value means: 0.8 may no longer correspond to 80% correct answers. A repair can only recover what the shift has altered. Theorem 3.1 says how much that is: the headroom, the most that any order-preserving re-mapping of the confidence can gain over the calibration in use (fitted on labels from the original data). Theorem 3.2 says what PAIC loses for having no labels and learning instead from a probe (a predictor of correctness trained on the original data): the probe's bias, its average error among answers with the same confidence, squared. So gain = headroom − squared bias (Corollary 3.2.1, page 5, lines 257–263), where the gain is how much the repair lowers the Brier risk, the confidence's mean squared error. Held-out labels confirm it (page 8, lines 423–431):

Situation (Llama / Qwen)HeadroomPredicted gainMeasured gain
New domain (GSM8K to HLE)0.299 / 0.1960.151 / 0.0710.154 / 0.072
Harder questions0.0150 / 0.01550.0123 / 0.01200.0128 / 0.0138
Harder questions (MATH), learned confidence0.0094 / 0.00190.0041 / −0.00040.0052 / −0.0004
Same questions, presented differently0.0023 / 0.0003at most the headroom−0.0029 / −0.0053

Across Table 1, prediction and measurement differ by at most 0.002 on the main shifts and 0.008 on HLE. The benefit is large after a new domain or harder questions. When the same questions are only presented differently (other names, another order of the facts, added irrelevant context), the answers do not change and the confidence keeps its meaning: there is almost nothing to repair, so the theory predicts no benefit, and none is found.

Against simpler baselines. Under shift, PAIC has a lower risk than every baseline fitted on the original data in all six settings (by 4.9–16.4% against isotonic recalibration; on HLE by 9–56% and 34–85% with two probes), than the closest published method, group-wise recalibration (Chen et al., 2024), in all six, and in 67 of 72 comparisons in which every method receives the same labels and unlabeled prompts (page 9, lines 456–462; Appendices B.3, B.4). It improves on the calibration in use in 81 of 84 cases.

A practitioner need not guess. RADAR deploys a repair only after a statistical test on a few labels has certified it, that is, confirmed with a guaranteed error rate that it is better. Over 42 shift experiments the test certified PAIC in 33, each time with lower risk on held-out data, and nothing in the six experiments whose headroom is only 0.003–0.005 (page 10, lines 489–499).

In practice: where only the confidence can be served, as with a hosted model, about 100 unlabeled prompts fit the repair, about 125 labels certify a gain of 0.05, and the audit shows what remains.

AuthorsOpenReview ↗

Response to Reviewer Chpr (Part 2/3)

W4/Q2 (continued). Do the improvements give better downstream decisions?

Yes. A confidence is used to decide which answers to accept and which to send for review, and a better confidence makes these decisions cheaper.

  • The link is exact. Let a review cost cc and a wrong answer that is accepted cost 1. Eq. (3) (page 5, lines 216–224) shows that lowering the Brier risk lowers the cost of these decisions, averaged over cc, by exactly half as much.
  • One repaired confidence serves every review cost. With the ideal repair, the simple rule "accept when the confidence is at least 1−c1-c" is the best threshold for every cc at once, with no tuning (Proposition A.38).
  • The data agree. In the 42 shift experiments, the confidence that RADAR deploys costs less on average than the model's own confidence at every review cost tested, and never more than the calibration in use. At c=0.2c=0.2 it is better than the calibration in use in 21 experiments, with intervals, and worse in none (on HLE from 0.244 to 0.201; on the main shifts from 0.222 to 0.201), because wrong answers are no longer accepted (Appendix F.4). On Qwen3.5-9B, PAIC costs less than the model's own confidence at every review cost from 0.03 to 0.57 (Appendix F.10).

Q1. What is fundamentally new beyond combining isotonic regression, prediction-powered inference and kernel calibration tests?

Three results are new, and none of them follows from combining the tools: a condition for when, and by how much, a repair fitted without labels improves on the calibration in use; a proof that no method can decide without labels whether to deploy it, and a count of how few labels suffice; and a kernel calibration test that stays valid when several answers come from the same question. Together they make RADAR, to our knowledge, the first framework in which a label-free repair comes with a condition for when it helps, a finite-sample test before deployment, and an audit of what it leaves (Introduction, page 2, lines 84–89; after every result in Section 3, the text states what is new).

Established toolWhat it leaves open hereWhat the paper proves
Isotonic regressionIt needs labels, and the new data have nonePAIC fits it to a probe's predictions instead. The price is only the probe's average error among answers with the same confidence, not its inaccuracy (Theorem 3.2), and no repair that uses only the confidence and the probe can avoid it (lower bound, Appendix A.5). Hence the gain over the calibration in use: what the shift left to repair, minus that error squared (Corollary 3.2.1), to our knowledge the first such condition
Prediction-powered inferenceIt compares two confidences using a predictor and a few labels, but does not say whether labels are needed, or how manyThey are needed: no method can decide without labels whether a repair helps (Proposition 3.2.2). And few suffice: a sequential test certifies the repair with a number of labels proportional to 1/gain1/\text{gain}, not 1/gain21/\text{gain}^2, and labeling stops as soon as it does (Corollary 3.3.1)
Kernel calibration testsThey assume independent answers, and wrongly reject a well-calibrated confidence when several answers come from the same questionA test that stays valid in that case, to our knowledge the first (Theorem 3.4). When it finds an error, the matching correction provably lowers the Brier risk (Proposition A.39)

These results make predictions, which a combination of tools would not, and the data confirm them: what PAIC loses follows the probe's bias (rank correlation 0.93), not its overall accuracy (0.35); measured gains are within 0.002 of the predicted ones on the main shifts (Table 1); the labels needed fall as 1/gain1/\text{gain} (measured exponent −0.97-0.97 over 77 repairs, Appendix F.11); and the audit's corrections lower held-out risk, from 0.199 to 0.171 on Qwen3.5-9B (Appendix F.12). The stages also need each other: a repair fitted without labels cannot vouch for itself, so a labeled test decides; a certified repair can still hide errors in a group of answers, so the audit follows (it finds some in 31 of the 33 certified repairs).

AuthorsOpenReview ↗

Response to Reviewer Chpr (Part 3/3)

Q3. Adoption still needs labeled target data. How does the labeling cost compare with conventional supervised calibration?

RADAR needs no labels from the new data to fit the repair, and a small, predictable number to decide whether to deploy it. Supervised recalibration needs labels for both, and with no labels PAIC already comes close to it.

Labels from the new dataSupervised recalibrationRADAR
To fitAll the labels it is givenNone: PAIC is fitted to a probe's predictions on about 100 unlabeled prompts
To decide whether to deployA further set, separate from the fitAbout 6 divided by the gain: 90 labels for a gain of 0.07, 125 for 0.05, 560 for 0.01
Certified by the same test from250 labels (Llama), 500 (Qwen3.5-9B), not within 750 (Qwen2.5)250 (Llama), 250 (Qwen3.5-9B), 750 (Qwen2.5)

With no labels, how close to supervised recalibration? PAIC reaches 95% and 80% of the gain that supervised recalibration obtains from 750 labels (Appendix F.6, page 79, lines 4245–4255), stays within 0.005 of it with 100 to 750 labels on Qwen3.5-9B, and closes a median 87% of the gap to a fit on labels over the six shift settings (Appendix B.3). On MATH, PAIC with no labels (risk 0.2294 for Llama, 0.1468 for Qwen) is level with supervised recalibration fitted on 100 labels (0.2304, 0.1464). So it is certified as early as supervised recalibration, or earlier, on all three models.

Why labels at all, and why so few? Two deployments can look the same in everything that can be measured without labels, while the same repair helps in one and harms in the other; so no method can decide without labels (Proposition 3.2.2). The test (the "betting test" of the paper) then looks at labeled examples one at a time and stops as soon as the evidence is conclusive. A larger gain shows sooner, so the number of labels falls as 1/gain1/\text{gain} (Corollary 3.3.1; measured on 77 repairs, Appendix F.11). Labels beyond the decision are not wasted: used to correct the probe, they lower PAIC's risk in all 16 cases tested (Corollary 3.2.3).

Practical efficiency. Serving PAIC is one table lookup on the confidence: 9–15 microseconds per answer, against 143–263 for a ridge probe on hidden states (Appendix B.13).

We sincerely thank the reviewer for their constructive feedback and thoughtful suggestions. We hope that our responses and additional experimental results have adequately addressed the concerns raised. We would be happy to provide any further clarifications or answer additional questions. If you find that your concerns have been satisfactorily addressed, we would be grateful if you could kindly reconsider and update your evaluation score accordingly.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response to all the reviewers and AC

We thank the reviewers for their careful and constructive feedback. We are encouraged that they found the problem useful (5WG2) and the limits of scalar recalibration clear and important (rfhz), and recognized the theoretical guarantees and the extensive experiments (Chpr).

What the paper contributes. An LLM's confidence decides which answers are accepted and which are checked. When the model is used on new data (a new domain, harder questions), a confidence of 0.8 no longer means that 80% of such answers are correct, and the labels needed to recalibrate it do not exist yet. RADAR handles this in three stages, each resting on a new result. To our knowledge it is the first framework in which a label-free repair comes with a condition for when it helps, a finite-sample test before deployment, and an audit of what it leaves:

  • Repair, with no labels. PAIC re-maps the confidence on unlabeled questions from the new data, guided by a probe: a small predictor of correctness trained where labels exist. New: only the probe's average error among answers with the same confidence matters, not its accuracy (Theorem 3.2). Its gain over the existing calibration, that is, how much it lowers the Brier risk (the confidence's mean squared error), is how far the new data moved the meaning of the confidence, minus that error squared (Corollary 3.2.1): to our knowledge the first condition for when such a repair helps and by how much.
  • Adopt, with a few labels. New: no method can tell from unlabeled data alone whether a repair helps (Proposition 3.2.2). A statistical test on labeled examples decides, with a guaranteed error rate, and the larger the gain, the fewer labels it needs (Corollary 3.3.1).
  • Audit. Some errors survive any recalibration. New: to our knowledge the first kernel calibration test that stays valid when several answers come from the same question (Theorem 3.4); when it flags an error, the matching correction provably lowers the Brier risk (Proposition A.39). On real answers it isolated 510 truncated ones with mean confidence 0.92 and accuracy 1.2%.

The framework and its main results are those of the submission (results 2.1–2.4 there, 3.1–3.4 now that the Introduction is numbered). The revision states their consequences explicitly, extends the same experiments to a newer model and a harder benchmark, and makes the paper easier to read. Changes are in blue. The principal points:

  1. The theory predicts where the repair helps, where it cannot, and by how much (Table 1). Predicted and measured gains differ by at most 0.002 on the main shifts and 0.008 on Humanity's Last Exam (HLE). The two cases without a gain noted in the reviews are predicted too: when the same questions are only presented differently, the confidence keeps its meaning and there is nothing to repair; for Qwen on MATH, the probe's error exceeds the little there is to repair. PAIC improves on the existing calibration in 81 of 84 cases. [Chpr W4/Q2; 5WG2 W1, W3; rfhz Q2]
  2. With no label from the new data, PAIC comes close to supervised recalibration. It reaches 95% and 80% of the gain that recalibration on 750 such labels achieves, closes a median 87% of the gap to a fit on such labels over the six shift settings, and on the newer model stays within 0.005 of supervised recalibration given 100 to 750 labels. [Chpr Q3; 5WG2 W2; rfhz W1]
  3. Labels are needed only to decide, and few suffice. No method can decide without labels (Proposition 3.2.2 sharpens the indistinguishability result of the submission); the test needs about 6 divided by the gain, 110 to 150 labels for a gain of 0.05. With PAIC as the only candidate, it approves PAIC in 33 of 42 shift experiments, always with lower risk on held-out data. [Chpr Q3; 5WG2 W2; rfhz W1, Q1]
  4. A newer model and a harder benchmark. On fresh answers from Qwen3.5-9B, PAIC lowers Brier risk by 19% under the primary grader. On HLE, where the model's own confidence ranks answers worse than chance, it lowers risk by 9–56% and 34–85% (two probes), with no HLE label. [5WG2 W4/Q2; rfhz W2]
  5. Downstream use: better decisions about which answers to trust (Eq. 3). If answers above a confidence threshold are accepted and the rest are sent for review, a lower Brier risk is exactly a lower cost of these decisions, averaged over the cost of a review. In 42 shift experiments, the confidence that RADAR deploys costs less on average than the model's own confidence at every review cost tested, and never more than the existing calibration. [Chpr W4/Q2]
  6. Presentation. The Introduction is titled as such and simplified; each result is followed by a plain explanation and by what is new; the experiments follow the predictions they test (main takeaway: Table 1); Figure 2 is redrawn. [Chpr W1–W3, Q1; 5WG2 W5, W6, Q1]

Two additional experiments (a further new model, Gemma-4-12B-it; long-form answers, ASQA) are reported in our response to Reviewer 5WG2.

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

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