- Rating
- 3(+1)
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 1
- Soundness
- 2
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Paper summary
The paper explores a mechanism for finding correction opportunities, i.e., predicting when more expensive (human, stronger llm) reviews are needed to supervise LLM outputs (e.g., active learning). They define EDO which chooses a selection policy that minimizes false omission rate (related to Type II error) within the constraints of some fixed edit budget and false discovery rate (related to Type I error) thresholds. The paper explores detection of likely edits, not necessarily of examples with the greatest downstream value (which motivates the work but is not demonstrated as far as I can tell). They propose an online method, EDIT, that approximates this structure using an edit score, a feedback-updated confirmation threshold, and a cost multiplier, which comes with deterministic cost guarantees and They conduct experiments on four QA benchmarks with Llama 3.3-70B across 4 edit score approaches and report improved discovery over prompted LLM selection, especially with an online linear probe learning over frozen representations. The finding that a 22.7M-parameter online probe strongly outperforms the 70B model's self-assessment is potentially interesting.
Critical strengths
(1) Intuition for EDO objective is clear and EDIT offers guarantees: high edit probability makes review more likely, global thresholds exclude low-impact reviews, and more expensive items require stronger evidence of a recommended edit. Using interaction-specific costs on generated responses makes the formulation relevant to real review situations. This problem definition/formulation and operationalization of resource constraints is an interesting contribution even if several mathematical components have close precedents.
Critical weaknesses
(1) Experimental conditions seem to favor proposed method. Resampling the responses on a model that can learn/adapt (EDIT-REP) means that it can possibly memorize previously labeled items (e.g., 2,500 draws from MATH-500's 500 items). There is no clear justification for this choice, which biases the main method claims. Additionally, choosing epsilon so the bound matches LLM-SELECT's error and thus does not itself ensure matched actual cost and pooled confirmation precision (and makes it a weaker baseline, and its prompt prohibits solving questions, likely weakening its ability to identify incorrect answers). It isn't clear that the methods generalize across LLMs, and Llama seems to avoid weirdness shown int Fig. 6/Tab 1 with Qwen shows that epsilon = 0 for PopQA (meaning a policy could move towards selecting nothing). Since eps ≈ 0.5 and is half the batch in many settings, the alpha controller may not contribute much, and the gains may come mostly from the probe. Basically, results establish superiority over one, weak prompted selector rather than superiority over plausible/comparable alternatives to the proposed approach.
(2) Experiments/results do not seem to match claims. "Edits" are identified incorrect answers on benchmarks with reference keys, so the editor is effectively a grader and the task becomes online error detection on closed-form QA. While sort of mentioned in conclusion, the motivations (subjective/partial corrections, ambiguity or style, customer/user intent) are not tested. The sole human annotator sees the reference answer, so it validates grading, not editing. Main experiments use unit costs, and the downstream value of discovered edits is not explored. Thus the construction doesn't distinguish between minor substantive correction from valuable failures and it doesn't seem to capture redundancy among discovered edits. With only correctness on. benchmark QA, it is unclear whether EDIT's advantages hold where real-world edit labels are noisy, subjective, and non-binary, which is precisely where the problem is hardest and most needed.
Questions for authors
(1) If EDIT-REP is able to learn and adapt, why is the sampling done with replacement? What justifies the resampling that includes identical prompt-response pairs (risking an online probe possibly memorizing previously labeled items)? Can you provide direct evidence of EDIT-REP without this advantage? What are the exact response-pool sizes, duplicate frequencies, and first-occurrence results? Are the 200 audited examples excluded from the online pools? What ablations can you provide to show whether the controller contributes, or whether EDIT-REP simply benefits from being the only method that learns from feedback? Can you rerun without repetition and with multiple streams and CIs for all methods?
(2) Why are costs defined as equal/unit? Even length-adjusted costs may not account for the amount of work taken by an expert to verify a complex scientific multiple choice results compared to a long but more easily Google-able PopQA result. How would costs be estimated in practical settings where observed LLM length may be less related to the cost of verifying the task?
(3) How sensitive are the EDIT methods to the specific EDO described? E.g, how would the results be different if there were a bound on Type-II error, recall, or regret relative to the oracle policy (as these, for a given downstream need, may be important to cost)? Can epsilon be defined without invoking LLM-SELECT? How would such epsilon definitions affect the performance?
(4) Can you evaluate on at least one dataset with genuine, non-answer-key-based edits, e.g., code-review/post-editing datasets, user-correction in public chat logs, or a human-editing study without reference answers?
(5) With the same EDIT-REP score and learning protocol, how much improvement comes from the adaptive update versus simpler fixed-threshold or budget-only selection?
3 comments
Reference for our response to Reviewer 7Z2V
[1] Niu et al., RAGTruth: A Hallucination Corpus for Developing Trustworthy Retrieval-Augmented Language Models, ACL, 2024.
[2] Arora, Nyberg, and Rosé, Estimating Annotation Cost for Active Learning in a Multi-Annotator Environment, NAACL Workshop on Active Learning for NLP, 2009.
[3] Wei et al., Cost-aware Active Learning for Named Entity Recognition in Clinical Text, Journal of the American Medical Informatics Association, 2019.
Thank you for your response.
Repetition and memorization:
thank you for directly addressing my question and for the evidence from First-occurrence evaluation in Table 9 and Nonrepeated streams in Figures 16–17 showing EDIT-REP can identify problems before receiving labels for those exact interactions. As I understand it, the nonrepeated experiment changes the model (D.11 says EDIT-REP uses Qwen3-1.7B representations and probe learning rate 4.0, rather than the main MiniLM setup. That says EDIT-REP configuration can work without repetition but not necessarily that removing repetitions keeps the original lightweight setup advantage. With the first-occurrence stuff, we see an improvement in missed-edit behavior with substantially lower precision (Table 9, PopQA)
- Could you clarify the "2,500 distinct interactions without replacement on MATH-500" which only has 500 items?
- Could you explain how the observed pool is constructed, how duplicate observations are handles, and how that corresponds with the held-out audit mentioned?
Baselines and controllers
Thank you for directly responding to the request with Apx D.9. Sharing representations and the online probe is a substantial fairness improvement with the additional comparisons. They resolve my concerns with weak baselines.
However, I don't think they “isolate” the adaptive controller’s benefit or quantify the size/robustness of its effects, because
- selective feedback, different selection policies acquire different training labels and therefore develop different probes and thus measure the total effect of the combined selection-and-learning policy,
- best-frontier-point reporting (across hyperparamter searches) seems to obscure this (and also I'm not clear why we exclude the first 20 rounds for these comparisons if we're comparing deployment conditions),
- RAGTruth configurations are selected on the same test streams and the EDIT-REP curve is labeled “larger search.” I interpret this as a implying a exploratory frontier, not an unbiased held-out evidence over the baselines.
Questions:
- Could you provide a non-exploratory statistical test that addresses the confounds in the combined effect and share the measured effect size and robustness of the controller?
- could you provide rationale for and the comparability of dropping the first 20 rounds?
𝜀
Thank you for the clarification and comparisons in Figs 12-18. They clarify its role and measurement. This doesn't yet resolve my concern of 𝜀=0 affecting the adaptive update rule. The exact controlled metric and low-tolerance behavior seem to need more careful interpretation. Theorem 2 uses an unweighted average of roundwise confirmation fractions, not the pooled fraction across all reviewed items making your statement "tolerance for unnecessary confirmations" a necessary descriptor (instead of a guarantee on aggregate review precision, which I think would be more helpful and intuitive)
Relevance and construct validity
Thank you for the RAGTruth update and softens my "only answer-key-based grading is tested" concern. RAGTruth seems to be a materially stronger response. The annotator given agreement, however, doesn't directly answer my core construct-validity concern around what is represented by editing. The experiment converts those annotations into a binary label about the presence of any qualifying hallucination in the text span. It is still a test of evidence-grounded factual-correction identification, not actual post-editing or the value of collected corrections. To be clearer, my concern about construct validity arose becuase of the interpretation and tests that would demonstrate its performance with respect to correction severity, downstream utility, subjective editor disagreement, actual editing time or correction quality, etc.
So far, the new experiments improve empirical credibility. As I understand them, they do not make the approach or its utility conceptually more valid (e.g., based in actual edits) nor do they fully demonstrate the mathematical and practical superiority of components with close precedents. For the latter, I could settle for an unambiguous statistical test that positively and specifically attributes controller gains over the baselines based on the most realistic and comparable deployment condition, or, alternatively if there are null results, an explanation for the mechanism giving rise to observed successes and conditional statements and qualifications for its use. I think we're closer to what I would expect and hope one more update could hopefully show that.
Response to Reviewer 7Z2V
We thank the reviewer for their time and helpful comments. We have expanded the experiments to address the concerns below.
1. Repeated interactions and adaptive selection
We acknowledge that repetitions can ease online learning. Given our distribution-free guarantees, we initially sampled with replacement to reduce the cost of long-horizon runs. We now report first-occurrence results (D.11, Table 9). More directly, we ran 2,500 distinct interactions without replacement on MATH-500 and PopQA, with both Llama-3.3-70B-Instruct and Qwen3-32B, averaging five orderings (Figs. 16–17). Importantly, EDIT-REP retains favorable Type-I–Type-II trade-offs without repeated examples. RAGTruth test streams are also nonrepeated (D.14, Figs. 21–22).
We added Top-K, Fixed Threshold, Online Conformal Selection, Conformal Alignment, stream active learning, and Thompson sampling (D.9, Figs. 12–13). All score-based methods share frozen representations, online logistic probe, initialization, and budget. Fixed Threshold ablates adaptive αt, retaining the learned scorer but fixing the threshold; Top-K tests score ranking under the same budget. These isolate the benefit of adaptive selection beyond scoring.
2. LLM-Select prompts and operating-point fairness
In response to the prompt-sensitivity question, we tested reasoning, verification, and risk-ranked LLM-Select prompts (D.12, Fig. 19; prompts in D.4.2). Type-I and Type-II errors are relatively insensitive to prompts despite cost differences; none consistently closes the gap to EDIT-REP.
ε can be specified independently of LLM-Select. It is a user-defined tolerance for unnecessary confirmations, chosen according to the application. We used LLM-Select only to choose a comparable operating point in the original experiments. EDIT's theoretical Type-I upper bound was approximately matched to LLM-Select's observed Type-I error. Neither EDIT nor its guarantees require LLM-Select. To demonstrate this, Fig. 18 sweeps ε independently and reports the achieved Type-I error. We also report Type-I–Type-II frontiers (D.9, Figs. 12–13), matched realized-cost comparisons (D.10, Fig. 14), and oracle-relative missed edits (Fig. 15).
3. Generalization across response models
To address model generalization, we also evaluate Mistral Small 3.2 24B (D.5, Fig. 7 and tables). EDIT-REP attains edit recall of 0.821, 0.648, 0.534, and 0.632 on MATH-500, MMLU-Pro, PopQA, and GPQA, versus 0.446, 0.492, 0.377, and 0.248 for LLM-Select. Improvements thus extend beyond the original response-model families.
4. Human relevance, edit labels, and review costs
Regarding the validity of correctness-based edit labels, we conducted a 200-example human audit (D.2, Table 4). As illustrated in Fig. 3, the annotator inspected the candidate response, reference answer, and solution steps, and judged whether the whole response (not only the final answer) required an edit. Agreement with benchmark-derived labels was 96.5%.
Beyond benchmark correctness, we added RAGTruth [1] (D.14, Figs. 21–22), using human-annotated hallucination spans in evidence-grounded QA, summarization, and data-to-text responses. On 450 held-out, nonrepeated responses, both EDIT-REP and EDIT-LLM achieve lower Type-II error than LLM-Select and EDIT-RAND with train-selected parameters (Fig. 21); EDIT-REP also shows favorable Type-I–Type-II frontier comparisons against additional selection baselines (Fig. 22).
For the cost question, we use unit costs to isolate selection from cost estimation and test nonuniform length-based costs as well (D.6, Figs. 8–9). We agree that length alone may not reflect verification difficulty. In deployment, costs could be predicted from timed expert reviews using task difficulty, domain, and verification requirements, following prior work on annotation-cost estimation [2,3]. These estimates can be refined as more reviews are collected and incorporated directly into EDIT.
5. Alternative constraints and robustness
A Type-II or recall constraint, as the reviewer suggests, would define a different optimization problem. EDO minimizes missed edits subject to control of unnecessary confirmations among reviewed items and a per-round budget; Theorem 2 guarantees average roundwise Type-I control up to a vanishing finite-horizon term, not Type-II control. On arbitrary streams, unobserved labels for skipped items preclude a nontrivial Type-II guarantee without additional assumptions. Oracle-relative missed edits (D.10, Fig. 15), matched costs (Fig. 14), and the independent ε sweep (D.11, Fig. 18) show these trade-offs. We test distribution shift (D.7 and D.13, Figs. 10 and 20). Please let us know if further clarification on the choice of constraint would be helpful.
We hope these results address the reviewer's concerns and would appreciate reconsideration of the assessment and score.
References are provided in a follow-up response.