- Rating
- 1
- Confidence
- 4
- Informativeness
- 1
- Presentation
- 1
- Soundness
- 1
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Paper summary
The paper studies the confidence estimation problem for LLMs in the black-box settings. It seems to proposing training an output head on a held-out set to improve confidence estimation.
Critical strengths
None
Critical weaknesses
- The paper is very poorly written and it is very difficult to follow. Numerous important terms such as "survive", "commitment", "corroboration", "monotone environment link" were introduced without clear definitions.
- In addition to the poor writing, the three contributions (ln54-76) are either method descriptions or empirical observations, with no emphasis on the actual value related to the research around confidence estimation.
- Methods such as the fixed-answer framework were poorly introduced with little to none explanation or justifications to the design choices.
Questions for authors
None
3 comments
Thank you for the response. My main concern on the presentation quality still remains and I will keep the original score.
Reply to Reviewer NMF1 (follow-up)
Thank you for reading our response and for telling us where you stand. The revised PDF, posted before your comment, already includes a change for each of your comments about presentation, and it marks the main-text changes in blue.
- Terms. "Survive" and the "monotone environment link" are replaced by plain words, and commitment and corroboration are defined at first use (pp. 1-3).
- Value of the contributions. Each of the four contributions now states its value for confidence estimation (pp. 2-3).
- Design choices. Sec. 1 now gives the reason for each choice, including fixing the answer before scoring it.
- Plain writing. The abstract, Sec. 1, the Figure 1 caption and the conclusion are rewritten in plain terms (pp. 1-3, 10), and the appendix is reworded for readability.
- Headings and tables. The headings of Secs. 3-6 state their results. Sec. 6 has a table of the labels and calls each use needs, and Sec. 7 opens with a table that compares each result with the closest earlier work.
For the final version we will also add a worked example that follows one question from the model's answer to its final score. We cannot tell which parts still fall short for you, so one example of a passage that is hard to follow would let us fix it directly.
For reference, here are the paper's two main results. Both can be checked from their numbers, without relying on the paper's wording.
1. A simple score carries over to new models without their labels. Our score, a small logistic regression we call the head, is trained only on other models and questions. Every method is then tested on the same answers of held-out models and questions, and none uses labels from the model being scored. The head ranks first against eight published methods on GSM8K, TriviaQA and MMLU-Pro, tied with cross-model TU on TriviaQA (AUROC, as in point 1 of the general response).
| Method (venue) | GSM8K | TriviaQA | MMLU-Pro |
|---|---|---|---|
| Our head, A+C | .938 | .933 | .859 |
| Cross-model total uncertainty, TU (Hamidieh et al., ICLR 2026), as published | .522 | .933 | .500 |
| Cross-model TU, our improved version | .861 | .933 | .770 |
| Perturbation composite (Pedapati et al., TMLR 2025), five of six families | .901 | .848 | .750 |
| Correctness model, 8B (Xiao et al., ICML 2026), as released | .808 | .863 | .714 |
| APRICOT (Ulmer et al., ACL 2024), better of two variants | .630 | .511 | .555 |
| Calib-n (Xia et al., ACL 2025), our extension to unseen models | .610 | .671 | .618 |
| Fine-tuned BERT (Devlin et al., NAACL 2019) | .606 | .620 | .669 |
| Stated confidence (approach of Tian et al., EMNLP 2023, and Xiong et al., ICLR 2024) | .804 | .774 | .756 |
| Semantic entropy (approach of Kuhn et al., ICLR 2023, and Farquhar et al., Nature 2024) | .805 | .726 | .650 |
The perturbation composite is scored only where every perturbation is valid, and A+C keeps its lead on those answers. Where a baseline could be made stronger, we used the stronger version, as the two cross-model TU rows show.
2. An exact rule for when other models help. Suppose another model, a peer, agrees with the right answers of the model being scored, the target, at rate and with its wrong answers at rate . The information one peer adds is the Jeffreys divergence between these two rates, and it equals exactly , where is how far one agreement moves the log-odds (Eq. 2). So a peer does not need to be accurate, but it must agree with right answers more often than with wrong ones. We call the gap separation.
A much stronger target can close this gap, since old peers cannot agree with right answers they themselves get wrong. The agreement rate mixes separation with the target's accuracy , as , so it can stay flat while separation falls. The paper therefore predicts that old peers stop helping at a model upgrade while their agreement rate barely changes. After first seeing this on GPQA-Diamond, we registered five predictions before collecting the MMLU-Pro data, and all five held (Table 3). Earlier work found that the value of other models depends on their capability (Hamidieh et al., ICLR 2026). Another study found that a judge's true-positive minus false-positive gap governs aggregate evaluation with imperfect judges (Feng et al., ICLR 2026). Neither setting asks how much one peer's agreement says about a single answer of a new model, which the identity above answers exactly (point 3 of the general response).
Our question. Beyond the three points of your review, is there a claim or an experiment you consider incorrect, or a result you consider already known? If so, a pointer or a reference would let us answer it during the discussion. We would be grateful to learn where, in your view, these results still fall short.
Reply to Reviewer NMF1
Thank you. Your points on undefined terms, the value of the contributions and the fixed-answer design guided the revision. If you can point us to the claim or experiment behind your soundness concerns, we will answer it during the discussion.
W1. Terms were introduced without definitions. We replaced two terms with plain words and now define the other two at first use.
In the revision, the definitions are in the abstract, Sec. 1 and the contributions, marked in blue.
W2. The contributions do not state their value for confidence estimation. Each revised contribution now states its value. The main value is that a new model's answers can be ranked before any of them is labeled. This matters because deployed models are replaced every few months.
Compared on the same answers, our output head ranks first, or tied for first, against eight published methods, listed with their venues in point 1 of the general response. Point 3 of the general response sets out what is new.
The four revised contributions are on pp. 2-3, marked in blue.
W3. The fixed-answer framework and its design choices lacked justification. The fixed-answer framework has every method score the same answer, the one the user sees. So all of them estimate the quantity a deployment needs, which is whether that answer is correct (Eq. 1).
Without fixing the answer, a resampling score can rate an answer the user never sees. In our runs the most frequent resampled answer is not the answer the user sees for 16% of GSM8K and 6% of MMLU-Pro answers. On those answers, a score that reads the most frequent resample reports a confidence of about .53 on GSM8K and .65 on MMLU-Pro. The answer the user sees is right only 12% and 28% of the time (App. B).
Sec. 1 now gives the reason for each choice, and App. B reports the resample mismatch.
Your summary reads the method as training an output head on a held-out set. We train a small output head on other models and questions, not on the held-out set. No label from the evaluated model enters training. It is tested on the held-out models and questions.
The revision states this split in contribution 1 on p. 2 and in Sec. 2.3.