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Paper summary
The paper asks whether a confidence estimator for an LLM keeps tracking the model's knowledge as that knowledge changes, without new supervision. The authors call this persistent calibration. They study it with pre-training checkpoints of Olmo 3 (7B and 32B) and Marin 8B. Estimators are trained on earlier checkpoints, or are training-free (self-consistency), and are evaluated on later ones.
The main evaluation uses knowledge contrast sets, meaning questions that one checkpoint answers correctly and another answers incorrectly. This is meant to remove the confound that correctness is highly correlated across checkpoints. Confidences on a contrast set are renormalized per question (Eq. 1), and the main metric is a class-balanced pairwise score . The methods are self-consistency (SC), LoRA verbalized-confidence adapters (optionally trained on several checkpoints), an "oracle" adapter trained on the evaluation checkpoints, a trivial end-correct baseline, and an external verifier (GCM). Surrogate and copy ablations control for knowledge already present in an earlier checkpoint.
The headline claims are that SC and adapters trained on earlier checkpoints fall short of the oracle on contrast sets even when full-set AUC is similar, that multi-checkpoint training helps, and that many confidence functions fit one checkpoint equally well while only some generalize.
Critical strengths
- The question is timely and well posed. Confidence estimators are usually built and tested on frozen snapshots, and model updates make that assumption fragile.
- The contrast-set idea is a useful diagnostic. The copy ablation shows crisply that full-set AUC is inflated by correlation across checkpoints (0.83 to 0.85 on TriviaQA while contrast AUC is 0.5).
- Several design choices are careful, including the class-balanced , per-checkpoint ECE and a dependence-aware paired bootstrap. The end-correct, surrogate and copy controls are the right ones.
- Open checkpoints make the setup reproducible in principle, and the paper reports negative domain-transfer results and full appendix tables.
Critical weaknesses
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The main target is never formally defined. Persistent calibration is described only informally, and the main tables report ranking metrics (AUC and ) while ECE appears only in the appendix. On full-set ECE, SC with an undefined "Post-hoc" step beats the oracle in all six settings (Table 11). The title and the claims speak of calibration, but the headline results are about ranking, and the ECE results point the other way.
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Contrast sets do not isolate the model's own knowledge. On a contrast question the two checkpoints give different answers, so any estimator that can judge the answer can score well. The paper's own results show this. The GCM, which sees only the question and answer, matches the oracle on Olmo 3 7B. On Marin Jeopardy, an older checkpoint scoring the new answers beats the oracle ( 0.515 and 0.504 against 0.459). The claim that contrast sets are "designed to require meta-knowledge" does not follow. It is also unclear whether the GCM's TriviaQA training data overlaps the evaluation split.
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Non-oracle training fails the paper's own test. The paper says that beating the surrogate and copy ablations is necessary for a nontrivial demonstration. In Table 12, non-oracle training never significantly beats its surrogate on in any of the six settings, and SC does so in only 2 of 6. The text frames this as mixed results, but the test is failed for non-oracle training in every setting, and Appendix C is worded more positively than Table 12 supports.
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The headline contrast AUC mostly reflects that later checkpoints are right more often. For the end-correct baseline, contrast AUC equals the share of improvements exactly, and my recomputation matches Table 1 to three decimals in all six settings. The abstract example (SC 0.760 against oracle 0.825) should be read against a trivial 0.735. The abstract and Table 1 lead with the unbalanced metric, and gains on it can reflect this prior. On Marin TriviaQA, multi-checkpoint training raises unbalanced from 0.213 to 0.460 but only from 0.221 to 0.227. Solving from the end-correct share (0.783) and these two metrics gives roughly +0.64 on improvements and -0.19 on regressions. This is approximate, since the tables aggregate over checkpoint pairs. It suggests the gain comes from improvements, and the paper does not show that it detects forgetting.
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The multi-checkpoint claims go further than the numbers. Table 4 says that both the training data and the checkpoint views contribute, but single-checkpoint data scores 0.373 against 0.379 for the full method (not significantly worse), and on Jeopardy it scores 0.517 against 0.506. Non-oracle gains from multi-checkpoint training are absent on Olmo 7B and Marin TriviaQA. The clear gains are in the oracle setting, which cannot be deployed.
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The normalization rests on questionable assumptions. Eq. 1 assumes the two checkpoints' correctness is independent, but different answers to a single-answer question make correctness mutually exclusive. It also needs joint calibration, not only marginal calibration. The robustness check in Appendix B.1 forces an antisymmetric map and is fit on the evaluation labels, so it cannot detect this alternative. The effect is on contrast AUC, Brier score, ECE and , though not on .
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Contrast sets may be dominated by unstable flips, and there is no noise floor. Regressions are 22 to 37% of contrast items, and between Olmo 7B at 90% and 100%, 538 questions flip while accuracy moves from 64.8 to 65.6. Correctness comes from one deterministic beam search under one fixed prompt, judged by an LLM. The paper does not report contrast sets between two prompts at the same checkpoint, or results stratified by SC margin or flip persistence.
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The setting is narrow and the explanation is untested. "Evolving knowledge" means consecutive pre-training checkpoints of one run, with English factoid QA. There is no fine-tuning on new facts, no knowledge editing and no post-training. The one domain shift (BioASQ) collapses all methods. The "vast hypothesis space" explanation rests on full-set AUC with no copy reference per cell, random labels with an unexplained below-chance AUC (0.310) and hidden-state variance that is not normalized for activation scale.
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The baselines, statistics and reproducibility have gaps. There is no P(True), probe, semantic-entropy or label-free adaptation baseline. There is no per-seed standard deviation, Section 4 uses one seed, and Marin conclusions rest on two checkpoint pairs that both involve phoenix. The judge is a closed model with no prompt given, the audit covers 100 TriviaQA items and leaves out incomplete references, and the LoRA loss and code or data release are not stated.
Questions for authors
- Can you report contrast-set results where every checkpoint scores the same fixed answer, so that answer plausibility is held constant? Can you also stratify results by whether the estimator's own backbone answers correctly (the earlier checkpoint for the surrogate, Qwen3-8B for the GCM), and state what deduplication was applied between the GCM's training data and the evaluation split?
- Since non-oracle training never significantly beats its surrogate on , is there evidence that the adapters track the new checkpoint's knowledge beyond the earlier one? Why is Appendix C phrased positively?
- What do contrast sets look like between two prompts at the same checkpoint, and how many flips persist at later checkpoints? Can you stratify results by SC margin?
- Can you report a class-balanced contrast AUC and include the end-correct row in every table? Can you also report separately for improvements and regressions per checkpoint pair, and the AUC of for separating improvements from regressions? That AUC is invariant to a constant shift, so it would show whether the estimators do more than apply a checkpoint-level offset.
- What is "Post-hoc" in Tables 11 and 16, and why does it beat the oracle on full-set ECE but not appear in the main text?
- Can you report contrast results under the mutual-exclusivity normalization and without the antisymmetry constraint?
- Why is the Fig. 2 AUC below chance (0.310) with random labels, and what is the copy-ablation AUC for each cell?
- What are the LoRA loss, the confidence prompt and the judge prompt, and will code, contrast sets and adapters be released?
7 comments
Response to reviewer cFbs (Part 2)
W2: Whether contrast sets require meta-knowledge
Our practical objective is to obtain informative confidence estimates from a lightweight extension of a continually updated generator model, without recurring supervision for confidence estimation or reliance on an external verifier whose capabilities must keep pace with it. The generator’s evolving representations are a natural source of features for this purpose. We use persistent calibration to describe the desired behavioral property, rather than a particular introspective mechanism. Knowledge contrast sets test whether confidence distinguishes changes in answer correctness that unchanged question-level scores cannot capture. However, because our estimators observe the candidate answer, success can also arise through answer verification using existing or newly acquired capabilities. Our evaluation therefore does not uniquely identify meta-knowledge: it tests behavior consistent with knowledge tracking, while the surrogate ablations assess whether access to the updated generator provides benefits beyond verification by an earlier checkpoint. Nonetheless, we believe that meta-knowledge is a promising direction to pursue for persistent calibration. Furthermore, we can require meta-knowledge with a simple modification to our setup: require the confidence estimator to predict, from the question alone, whether the generator will predict the correct answer. In this setup, even an external oracle that knows every correct answer cannot predict the generator's correctness without knowledge of the generator's knowledge. This is a cleaner test of introspection, though not the practical setup we adopt in this paper, given that confidence estimation in practice is improved by conditioning on the candidate answer (Orgad et al., 2025; Ni et al., 2025). We have added this discussion to Section 2.
We acknowledge that Marin 8B on Jeopardy is the one case out of six in which SC or non-oracle training surpasses the oracle on \Delta^b_0. We emphasize that the surrogate ablations do not consistently match oracle performance, and that the surrogate’s performance often doesn’t extend to other metrics such as full-set and contrast-set ECE (contrast-set ECE 0.182 or 0.154 vs. 0.123; full-set ECE 0.126 or 0.048 vs. 0.027). We describe one intuition for why the surrogate ablations achieve higher contrast-set AUC than one might expect, given that they use an earlier checkpoint that often did not predict the correct answer. Although different checkpoints are generally not independent with regard to their predictions, it may be instructive to approximate them as such, especially for questions where some of them made different predictions. Since the checkpoints are similarly performant (Table 7), ensembling their predictions by taking the majority vote can be expected to achieve a higher accuracy than any individual checkpoint (Huang et al., 2017; Garipov et al., 2018). This would suggest that, for a question on which two evaluation checkpoints produce differing predictions, a third checkpoint (i.e. the surrogate checkpoint) can distinguish the correct answer from the incorrect answer with nontrivial probability, leading to a nontrivial contrast-set performance. Intuitively, different checkpoints' incorrect predictions tend to differ, so even if the surrogate checkpoint predicted an incorrect answer, it is likely to consider the correct answer more plausible than an incorrect answer that is different from its own. We have added this discussion to Appendix B.4. However, we emphasize that it is far from a reliable occurrence for the SC or non-oracle training surrogate to surpass oracle training. Furthermore, although the above explains why surrogate ablations can often achieve strong discrimination between the correct answer and the non-self-generated incorrect answer, it does not suggest that they would be calibrated (in the sense of ECE/BS), and indeed, they are highly miscalibrated (as measured by ECE/BS) compared to oracle training or even to the non-surrogate versions of SC or non-oracle training. Overall, our results position the surrogate ablations as a diagnostic tool rather than a reliable confidence estimator.
We enforce a train-test split between the GCM’s training data and our evaluation data. We have added this clarification to Appendix A.4.
Response to reviewer cFbs (Part 3)
W3, Q2: Wording of non-oracle vs. surrogate results
We agree that non-oracle training fails to consistently outperform its surrogate ablation. The mixed results refer to contrast-set AUC, where non-oracle training outperforms its surrogate ablation in 3/6 cases in Table 16. Nonetheless, we acknowledge that this does not hold across metrics, as you point out with \Delta^b_0. We have updated the wording in Section 3.2, Table 2, Table 16, and Appendix C to reflect this.
W4: Breakdown of \Delta^b_0 into improvement and regression
We agree that contrast-set AUC reflects the end-correct prior, but we believe that this does not affect the validity of the revealed trends. For example, in the contrast-set AUC example you give with [end-correct baseline 0.735, SC 0.760, oracle 0.825], the main finding that the oracle outperforms SC still holds, regardless of the moderate performance of the end-correct baseline.
Based on your suggestion, we have added the breakdown of \Delta^b_0 into \Delta_0 for improvement and regression; see our response to Q4. We agree that an improvement on \Delta^b_0 does not guarantee an improvement on both the improvement and regression components. However, we argue that such a guarantee is not actually desirable, and that \Delta^b_0 captures the faithfulness (independent of begin/end-correct priors) that we want to capture. Consider the end-correct baseline, which scores \Delta_0 = 1 on the improvement set but \Delta_0 = -1 on the regression set, and the begin-correct baseline, which scores \Delta_0 = 1 on the regression set but \Delta_0 = -1 on the improvement set. Consider also a confidence estimator that scores \Delta_0 = 0.8 on both the improvement and regression sets. Clearly, this confidence estimator is more faithful to a checkpoint’s knowledge than the begin/end-correct baselines, and yet it does not improve over both baselines on both the improvement-set \Delta_0 and regression-set \Delta_0, because each one can be independently exploited without any faithfulness. On the other hand, \Delta^b_0 captures faithfulness by not rewarding a prior favoring either the earlier or the later checkpoint (unless \Delta^b_0 is currently below the trivial 0). We have added this discussion to Appendix A.2.
W5: Multi-checkpoint training ablations, significance of results
We agree that the multi-checkpoint views are most responsible for the gains of multi-checkpoint training, as suggested by the strong performance of the single-checkpoint data ablation. The reason we do not state that multi-checkpoint views are the sole contributor is that the single-checkpoint data ablation consistently has worse calibration than multi-checkpoint training (Table 23, e.g. contrast-set ECE of 0.096 vs. 0.061 on TriviaQA, and 0.087 vs. 0.057 on Jeopardy), suggesting that the training data also plays a role. We have updated the caption of Table 23 to highlight this.
Our contributions in this paper are introducing the problem setting of persistent calibration, establishing contrast-set calibration as a distinct and necessary criterion, and exploring the viability of explicitly training a confidence estimator to work on multiple checkpoints. We do not claim to solve persistent calibration. Nonetheless, our results suggest an avenue for improving persistent calibration with multi-checkpoint training. Notably, in the oracle setting, which has respective-checkpoint training as a strong baseline that trains a dedicated confidence estimator for each checkpoint and does not require any transfer, multi-checkpoint training still does better. Furthermore, we would like to highlight that also in the non-oracle setting, multi-checkpoint training always at least matches single-checkpoint training, and sometimes delivers drastic improvements: when measuring contrast-set AUC in 6 cases (3 models * 2 datasets; Tables 17-18 extend main Table 3), multi-checkpoint training is statistically significantly worse in 0 cases, statistically significantly better in 5 cases, and 2 of those cases are drastic (0.806 vs. 0.642 TriviaQA, 0.759 vs. 0.562 Jeopardy; Marin 8B).
Response to reviewer cFbs (Part 1)
Thank you for describing our research question as “timely and well-posed”, our contrast sets as a “useful diagnostic”, and our design choices as “careful”. We address your comments below. We have also uploaded a revised version of our paper, which we reference in our responses, with revisions in blue. Note that the revised manuscript contains different table, etc. numbers from the original manuscript.
W1: Evaluation metrics
The main targets are the evaluation metrics given in Section 2. We have now clarified this in the introduction: “Persistent calibration requires both full-set and contrast-set calibration, which we concretely evaluate using the metrics defined in Section 2.” Based on your suggestion, we have expanded the main tables to include the metrics BS and ECE for the contrast set and full set. In our response to Q4, we describe the other metrics we added based on your suggestions. In our response to Q5, we discuss post-hoc calibration and the discrepancy between full-set ECE and other metrics.