acceptodds
Under review as a conference paper at ICLR 2027

Stop or Continue: How Fine-Tuning Changes Evidence Use in Search Agents

Abstract

After every search, an agent must decide whether it has enough to answer or should keep searching. We ask which features of the retrieved page drive this decision, using matched edits that switch a mention of the question's entity, an answer-like string and the supporting fact on or off. Instruction-tuned models from three families are more likely to answer with an answer-like string when one appears, even if nothing supports it. After supervised fine-tuning on single answer-or-search decisions, Qwen2.5-7B-Instruct responds mainly to the mention instead: the effect of a mention on its rate of stopping (answering or declining) rises from 6 to 47 percentage points and that of an answer-like string falls from 29 to 5, a reversal no shift in its overall willingness to stop can produce. It held on preregistered held-out pages; Mistral-7B-Instruct-v0.3, fine-tuned the same way, showed it on development pages. Asked about pages that mention the entity but lack the fact, the fine-tuned agent says the fact is missing for 96% of them but answers on 54%. In real search episodes, fine-tuned agents often answer once the page about the question's entity arrives, even on questions this page cannot answer, where every answer was wrong. Instructions to check for the fact barely changed what the fine-tuned agent stops on. Unlike public search-agent trajectories, its training data almost never contain a page about the entity without the fact, a coupling measurable before training; in a preregistered study on new questions, counter-examples of this kind removed 82% of the mention's effect on stopping, while generic negatives had no measurable effect. Four larger open models rarely stopped on either cue alone, but with reasoning off, five of six models from five families often answered with the answer-like string on pages linking the right entities by the wrong relation.

Primary area:
interpretability and explainable AI
Keywords:
LLM agents, search agents, retrieval-augmented generation, supervised fine-tuning, shortcut learning

Reviews

Among:
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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_xQ6jOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper investigates how search agents use retrieved evidence to decide whether to stop or continue searching. Through controlled manipulations of entity mentions, answer-like candidates, and supporting facts, the authors find that fine-tuning shifts stopping behavior from candidate-based to mention-based cues, potentially reflecting correlations in the training data.

Critical strengths

1.Understanding what drives search agents to stop or continue searching is an important problem for reliable agentic search. Investigating how fine-tuning changes the evidence cues underlying these decisions is a promising direction. With a clearer research focus and stronger evidence of generalizability, this work has the potential to make a more substantial contribution.

2.The paper systematically manipulates entity mentions, answer-like candidates, and supporting facts to examine their effects on stopping decisions

Critical weaknesses

1.The main finding that fine-tuning shifts stopping decisions from answer-like candidates to entity mentions is primarily established using a specially constructed SFT dataset. However, the training data contain a strong shortcut: the presence of a page about the question's entity almost perfectly predicts the stopping label (AUROC = 0.98). More importantly, none of the 473 training examples labeled as "continue searching" contains the first-hop supporting page, meaning that the training data entirely omit a common multi-hop search situation where the first hop has been retrieved but further evidence is still needed. Under such conditions, it is not surprising that the fine-tuned model learns to rely on entity mentions when deciding whether to stop. The paper itself shows that this correlation is much weaker in public search-agent training datasets, and the externally evaluated models do not exhibit the same mention-dominant behavior. Therefore, it remains unclear whether the observed shift represents a general problem in search-agent fine-tuning or is mainly an artifact of the authors' training data construction. Evaluation with more representative SFT data would help establish the broader relevance of the findings.

2.The paper cites relevant studies on search stopping decisions, evidence sufficiency, shortcut learning, and counterfactual training, but does not sufficiently explain what new understanding it provides beyond these studies. Prior work has already identified premature stopping, unreliable evidence use, and training shortcuts in search agents, and has proposed methods to address these issues. While the paper provides a more fine-grained analysis of mention, candidate, and fact cues, it remains unclear which findings represent genuinely new insights rather than more specific demonstrations of known problems. The authors should more explicitly distinguish their contributions from the closest prior work and clarify what new understanding of search-agent behavior is established.

3.If the main objective is to understand how supervised fine-tuning changes search agents' stop-or-continue decisions, it is unclear how some of the additional experiments, particularly those comparing larger models with and without reasoning, directly contribute to this objective, since they do not examine fine-tuning effects. If fine-tuning is the central variable of interest, the authors should explain why reasoning is also investigated and what additional evidence these experiments provide for understanding the effects of fine-tuning. Alternatively, if the objective is to understand what determines search agents' stopping decisions more generally, the paper does not explain why fine-tuning is singled out for extensive analysis or provide a systematic framework for examining other influencing factors. As a result, although the individual findings are interesting, the connections between the central research question, experimental analyses, and overall conclusions could be made clearer.

Questions for authors

Please see the weaknesses.

2 comments
AuthorsOpenReview ↗

Response to Reviewer xQ6j (1/2): W1–W3

You wrote that "with a clearer research focus and stronger evidence of generalizability" the work could make a more substantial contribution. We ran the evaluation you suggested, and the revision reports what it found. [P] marks a prediction or criterion fixed before the run; "post hoc", an analysis designed after results were seen.

W1. A general problem, or an artifact of our training data? The paper's claim has two parts: "Features other than support move the decision substantially, and which of them matters most changes with fine-tuning" (Section 1). On the second part you are right: which feature it is depends on the training data. The first part holds beyond our data.

  • The evaluation you suggested. Same model and recipe on 706 decisions from public trajectories: mention effect +2.5 points [−1.1, 6.0], against +47.7 with our data [P: weaker, as Section 4.4 predicted; met]. The abstract, Section 4.4 and the limitations now tie the mention cue to data like ours.
  • The situation you named, on real states. On 39 states from public trajectories with the first hop retrieved and the second missing, the agents trained on public data answer on 4 to 6 and ours on 27 to 31 (descriptive).
  • Is it then "not surprising"? Less than it seems. In our recipe, adding counter-examples that mention the entity without the fact removes 82% of the cue [P]; whether leaving such states out by itself produced it is not identified, and the two properties you cite do not suffice. We re-sampled the public data (a post hoc design) so that no search example contains the first-hop page without the rest of the evidence (211 of 422 before, none after) and the entity's page predicts the stop label as in our data (AUROC 0.97, against 0.98); the mention effect stayed at +3.2 points [−1.4, 8.2]. The re-sampling also changed the search targets, so we cannot say which further property is needed, and the revision no longer offers the statistic as a way to anticipate the cue.
  • What holds beyond our data. Stopping on a feature that does not support the answer. An unsupported answer-like string raises stopping by 34 points in the agents trained on public trajectories and by 52 and 56 in two released R3-RAG checkpoints. In a test fixed in advance on held-out pages, naming the asked entity raised the RL checkpoint's stops from 55 to 112 of 166 questions when a candidate was on the page, and not without one (11 to 8); its answers that assert the candidate rose from 43 to 108 [P; primary outcome, met]. The name matters there too, but only next to a candidate.

W2. What new understanding beyond prior work? Four statements; prior work is described as in Section 5.

  1. What makes the agent stop is not what it then says (Table 5). The name triggers the stop (12 → 63 of 112); the candidate adds few stops (58 → 63) but decides what the answer asserts (3 → 59).
  2. What triggers the stop changes with fine-tuning, in a direction set by the training data: the candidate before fine-tuning, the mention after our data [P, held-out]; after public data hardly the mention (2.5 points) but still the candidate (34.3). Known before: agents stop too early or search redundantly (Zhang et al., 2026a); shortcuts in training tasks let agents answer with less search (Deng et al., 2026).
  3. An agent can judge that the fact is missing and still answer: ours says so on 96% of the mention-only pages and answers on 54% of them. Known before: models answer from insufficient context (Joren et al., 2025); agents can fail to act on knowledge they state (Schmied et al., 2026).
  4. Removing a cue is not learning the evidence: targeted counter-examples removed 82% of the cue [P] without a gain in accuracy at matched searches [P, not met], and deletion-based ones did not make the agent better at telling a fact from a near miss (post hoc). Known before: counterfactual data reduce reliance on a feature (Kaushik et al., 2020); minimal pairs teach when to stop (Liu et al., 2025).

W3. Focus and framework. The paper asks one question: which features of the retrieved page drive the decision to answer or to keep searching. One instrument, the edited pages, serves three purposes: identifying the cues, comparing the same model before and after fine-tuning, and testing how far the result extends. Fine-tuning is the factor we vary (Section 3 before; 4.1–4.3 after; 4.4 why; 4.5 what removes the cue). The larger models serve the third purpose. We run them with and without reasoning because our fine-tuned agent acts without a reasoning step. Without it most of them answer on near misses, but none responds more to the mention than to the candidate. We did not vary their training, so we do not attribute their behavior to the cause we identify for our agent.

Revised: the abstract, the end of Section 1 (a five-step map), Sections 4.4 and 5, the limitations and Appendix H.

AuthorsOpenReview ↗

Response to Reviewer xQ6j (2/2): details for W1 and W3

Agents by training data (Qwen2.5-7B; effects on stopping in points, development pages).

AgentMentionCandidateFactCandidate answers on near missesAnswers on 157 natural first results
Before fine-tuning4.925.23.079.4%44.6%
Our data (three seeds)47.714.441.056.0%51.6%
Public trajectories, same recipe (three seeds) [P]2.534.360.622.8%9.1%
R3-RAG cold start / after RL (released)6.0 / 13.256.0 / 52.122.7 / 30.662.0% / 59.3%3.2% / 1.9%
Search-R1 (released)1.92.827.86.2%not run

"Fact" is the stopping rate on a page that states the fact minus that on its near miss (small before fine-tuning, when the model stops on nearly all of both, answering or declining). The natural first results contain the entity's page but not all the evidence.

Is it the statistic (W1)? We re-sampled the public data in two steps (same recipe, three seeds each; the design is post hoc). The first replaces all 211 search examples that contain the first-hop page without complete support, so that the entity's page remains in 5% of the search examples instead of 55%; the AUROC rises from 0.56 to 0.81. The second also replaces stop examples and raises it to 0.97. Mention effect: +2.5 [−1.1, 6.0], +2.3 [−1.4, 6.0] and +3.2 [−1.4, 8.2]; candidate effect: +34.3, +26.1 and +20.8. Relative to the candidate the mention gains 14.2 points [6.5, 23.1], so a higher coupling shifts the balance between the two cues, but the mention effect itself changes by only +0.8 points [−3.1, 4.9]. The re-sampled examples remain states of real trajectories and differ from ours in page format, query targets and the share of answer examples; the result does not show which property of our data produces the cue.

The situation you named, on real states. 40 states from public trajectories with insufficient evidence, verified by two blind reviewers; in 39 the first hop is present and the second missing. On these 39 the agents trained on public trajectories answer on 4, 4 and 6 (three seeds) and ours on 29, 31 and 27; on 40 states with sufficient evidence they answer correctly on 32, 32 and 34, and ours on 34, 35 and 37. The comparison is descriptive and was specified before the outputs. The states come from the same public source as the first group's training sample (other questions), so they favour that group.

A second public source. RQ-RAG trajectories, same recipe, three seeds, test fixed before any output, on pages from 80 new questions: mention effect −0.3 points [−2.6, 1.3], against +46.8 [32.4, 61.0] for our data on the same pages [P: direction; met]. These agents stop on only 19.5% of the pages that state the fact, so this shows the direction and little more.

The released R3-RAG agents. On development pages the name raises candidate answers by 35.2 points [25.5, 45.1] (after RL) and 28.5 [16.4, 40.5] (cold start) when it stands in the passage that states a relation of another entity, and by 6.9 [0.7, 12.7] and 3.2 [−4.2, 11.1] when the two stand in separate passages: the effect is several times larger when the two share a passage. For the checkpoint after RL we fixed a test in advance on held-out pages (166 questions; candidate shown, fact absent): it answers with the candidate on 108 when the passage names the asked entity and on 43 when it names another (+38.5 points [28.5, 48.4]; 103 against 39 by string match) [P; met]. Its stops rise from 55 to 112, and without a candidate go from 11 to 8 (difference 35.6 points [25.6, 45.5]). The error is shown on constructed pages only; on the 157 natural first results the two checkpoints answer on 3.2% and 1.9%.

One instrument for all agents (W3). Measured the same way as the 7B agents of the table, seven API models with reasoning on show mention and candidate effects of at most 7.5 points and fact effects of 20 to 92 points (one-hop pairs, short and long pages; given here only); two of them without reasoning show fact effects of 26 and 4 points.

Disclosures.

  • The released agents entered through a supplementary eligibility check after our original gate was not passed; one further agent, ReSearch, did not pass it. The two R3-RAG checkpoints come from the same group.
  • R3-RAG and Search-R1 have no before-fine-tuning row. In their prompt formats the untuned base model gave invalid decisions too often (15.3% and 7.5%; limit 5%).
  • The public-trajectory arm entered through a follow-up eligibility check designed after the first attempt stopped at its gate. The prediction and both criteria had been fixed before any training: "weaker than with our data" was met, "still present" was not.
  • One of the three RQ-RAG seeds missed our answer-correctness check (19 of 40 correct; threshold 20).
  • The held-out pages were used twice during the discussion (Appendix H).
Reviewer_mgdJOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper explores a timely topic on how fine-tuning changed a search agent's behavior in evidence use, specifically ablating on whether a semantically related cue without support can trigger early stop of the agent's search. The paper focuses on two variants "mention" and "candidate", and shows that fine-tuning reverses the trend that the before-fine-tuning model stops more on "candidate" while after-fine-tuning model stops more on "mention".

Critical strengths
  1. The problem the paper investigates is very important for search agents and is well-motivated with clear gaps of existing models;
  2. The paper conducts a relatively thorough investigation with extensive ablations and analysis;
  3. The experiments are well-documented and seem to be reproducible;
Critical weaknesses
  1. My most outstanding concern is about the paper's scope: results in section 4.6 imply that this gap is diminishing and almost fixed for the more recent, stronger reasoning models ("None of them stopped on pages that mention the subject but contain neither the candidate nor the fact...and on pages with a mention and a candidate but no fact they stopped in 1–7%", line 397-399). One limitation from the current setup is that the evaluation uses short, controlled passages with explicit relation links (although with the near miss variant), but does not require challenges such as resolving ambiguous references, evaluating competing answer candidates, or resolving conflicting evidence, which would require extra reasoning capability from the model. So section 4.6 is inconclusive about whether the gap still exists for current reasoning models (and if so, how to address them), while this part is believed to have a larger impact on the current research community of search agents.
  2. The paper does not have an explicit recommendation for how to strengthen the agent's evidence use capabilities motivated by this study.
  3. The writing can be significantly improved, in particular, the results section could contain at least one highlighted, summarizing sentence for the major takeaways; current writing has findings buried by a lot of numbers and setup descriptions, making it very dense to read.
Questions for authors
  1. Can more results on the recent reasoning models be established for more realistic, challenging tasks that may involve resolving ambiguous references, evaluating competing answer candidates, or resolving conflicting evidence that requires extra reasoning from the models, so to better answer if the observed gaps still exist for the recent models?
  2. What are some effective mitigations to strengthen the agent's evidence use capabilities, motivated by the study?

I genuinely appreciate the motivation and the research problem of this work. If the above two questions can be properly addressed, I'm willing to raise to a higher rating.

4 comments
AuthorsOpenReview ↗

Response to Reviewer mgdJ (1/2): answers to Q1 and Q2

Thank you for stating what would change your assessment. [P] marks a criterion fixed before the run; "post hoc", an analysis designed after results were seen.

Q1. Does the gap still exist for recent reasoning models on harder pages? By the criterion fixed in advance, not on the three challenges you name (failure rates: at most 6.1% in 27 of 28 model–page-type pairs, 16.7% in one). It remains in two narrower forms; without reasoning, most models answer on near misses.

We ran your test (ambiguous reference, two versions of competing candidates, conflicting evidence) on seven reasoning models.

  • No persistent gap on your three challenges [P]. No pair has a failure rate whose 95% interval lies above 10%. The highest is 16.7% [8.8, 24.5] (Kimi K3, conflicting evidence; our 7B agent, without reasoning: 84 of 104, first judge). This is not reluctance (post hoc): on 90 of the 104 questions DeepSeek-V4-Pro stops on the fact page, stops again when a second value without a relation is added, and searches when a second passage conflicts.
  • Pages that link the right entities by the wrong relation still mislead some models. On near misses, four of the seven answer with the unsupported candidate on 12.5–31.1% of pages. This depends on wording: on newly written film pages, the two highest did so on 5.9% and 0.7% [P: replication; not met]. The reasoning step makes the difference: with it switched off, the two DeepSeek models answer with the candidate on 84 and 108 of 112 pages, against 3 and 5 with it (four models from other families: 108, 108, 40 and 13).
  • In real search the models stop rarely, but often beyond the text. On 199 real first results that lack part of the evidence, the seven models stop in 120 of 1,393 decisions (our 7B agent: 54%). In 69 of the 120, both judges found the answer not fully supported by the retrieved text; 51 of the 69 are still correct, so accuracy misses them (post hoc). Example: a page gave Charles Servizio's birthplace, Lynn, Massachusetts, without its county; three models answered the correct county and four searched.

Q2. Which mitigations does the study motivate? Four, by kind of agent, each with its gain and its cost or limit.

  • A model that reasons: instruct it to check the evidence. DeepSeek-V4-Pro, complete episodes from the 199 states: answers without full support fell from 57 to 28, and correct, fully supported answers rose from 106 to 118 (+7.3 points [2.3, 12.5]). Cost: searches rose from 2.63 to 3.29 per question, and all correct answers went from 143 to 136 (−3.6 points [−8.3, 1.1]). A replay of the episodes that reached the search limit, with a notice that no search is left (designed afterwards; 2/2), gives −0.9 points [−5.1, 3.2]. On 118 selected harder states the instruction cost correct answers (94 → 84).
  • A model that reasons: for one of two models, a targeted check kept more correct answers than a general caution. Asked which passage links the candidate to the subject in the asked role, GLM-5.3-Flash answered on 64 of 67 fact pages, against 47 under a general caution [P; met]. Limit: no further drop on near misses (8 under both; [P] not met), and no advantage on MiniMax M3.
  • An agent that cannot be retrained: let a second model check the first proposed answer against the retrieved text. Our 7B agent, 600 questions (post hoc): of 120 first-step answers that the checker lets through, 115 are correct and supported, against 70 of 120 kept by a threshold on its own stop score (+7.5 per 100 questions [5.0, 10.1]). After continued search: 10 more final answers are correct and supported (+1.7 per 100 questions [0.5, 3.0]; +1.2 [0.0, 2.5] under both judges) at nearly the same number of searches (−0.002 per question), for 350 checker calls.
  • An agent that is fine-tuned: change the training data, not the instruction; then test accuracy at equal cost. Counter-examples removed 82% of the mention effect [P] where instructions and generic negatives failed, but alone gave no detectable accuracy gain (−0.4 points [−4.3, 3.6] on 600 new questions; [P] not met). A variant that adds the missing first-hop state gained 7.1 points with one search per arm (selected development questions) and, in complete episodes, 3.6 [1.0, 6.3] on the 600 new questions ([P] met; +8.3 on bridge questions, −2.0 on the rest). Limit: there the interval for its extra searches is not inside our ±0.25 band ([P] not met); a later test on 455 new bridge questions met all criteria (our update).

In any evaluation, score what the agent does on matched pages, not what it says. Ours says the fact is missing on 96% of mention-only pages and answers on 54%; as a gate, its judgment did not beat a stop threshold [P; not met].

W3. Each results subsection opens with its conclusion in bold; Section 1 ends with a five-step map; Section 6 states three checks and two measures.

AuthorsOpenReview ↗

Response to Reviewer mgdJ (2/2): numbers per model, real first results, instructions

Per model, reasoning on. Failures were defined per page family before the run. The last column is post hoc.

ModelCompeting candidatesAmbiguous referenceConflicting evidenceNear misses: candidate answersReal first results (199 states): wrong answersFact pages: stops
DeepSeek-V4-Pro0%1.5%1.0%4.2%5.1%97 of 104
deepseek-flash0%2.3%0%5.6%3.5%87 of 104
GLM-5.30%0%0%2.8%1.5%42 of 102
GLM-5.3-Flash0%0%0%31.1%1.8%97 of 102
Kimi K30%4.5%16.7%17.6%2.4%101 of 104
MiniMax M30%6.1%3.9%19.4%0%40 of 104
Qwen3.8 Max0%0%2.0%12.5%3.5%65 of 104
GPT-6.1 Sol, default setting0%1.5%3.9%0.9%1.2%103 of 104

GPT-6.1 Sol rarely produced reasoning tokens at its default setting, so it is not counted among the seven. In the paired contrast of the first comment, Kimi K3 stops on 101, 101 and 26. The near-miss column is a re-run. In the submission's run, six weeks earlier, MiniMax M3 answered with the candidate on 47 of 112 near misses, against 19.4% now; we have not established why. On newly written pages about who reviewed and who directed a film, GLM-5.3-Flash and MiniMax M3 asserted the candidate on 0.7% and 5.9% of 136 pages [P: replication; not met]. The subjects of our pages are invented names, so a model that searches again on a fact page may be verifying the entity; we count this as extra searches, not as an error.

Real first results. The states are first results of real retrieval that contain the page about the named entity and lack a supporting passage: 199 from the 600 questions of Appendix D and 118 from its selected questions. Wrong answers are at most 5.1% per model [P: no persistent gap]. Answers that both judges found not fully supported by the retrieved text (post hoc): 69 of 1,393 decisions on the 199 states (5.0%; 69 of 120 stops) and 15 of 826 on the 118 states (1.8%; 15 of 78 stops). In the example of the first comment, an unrelated passage on the page mentions Essex County, New Jersey; three models answered "Essex County", which is also the county of Lynn, Massachusetts, and four searched for it.

The evidence-check instruction (DeepSeek-V4-Pro). The prompt was fixed before the run. First step, baseline → with the instruction: stops whose answer the passages do not state, 17 → 3 of 199; all stops, 24 → 9; correct answers on 104 fact pages, 97 → 101. Full episodes, up to five turns (descriptive, no criterion):

Full episodes199 states118 states
Correct143 → 136 (−3.6 points [−8.3, 1.1])94 → 84 (−10.2 [−18.4, −2.6])
Correct and fully supported106 → 118 (+7.3 [2.3, 12.5])66 → 69 (+1.7 [−2.9, 6.5])
Substantive answers without full support57 → 2829 → 17
No answer within the turn limit28 → 3711 → 19
Searches per question2.63 → 3.292.25 → 2.72

Differences are means over question clusters; support is judged by one LLM judge, blind to the arm, over every passage retrieved in the episode. When the episodes that reached the search limit are replayed with a notice that no further search is possible (designed after these results), the differences are +8.1 points [3.3, 13.3] and −0.9 [−5.1, 3.2] on the first set, and +1.7 [−1.9, 5.6] and −5.1 [−11.2, 1.0] on the second. The instruction buys support with searches and, on the selected questions, with correct answers.

Instructions on two more models (long pages, 67 page pairs; neutral prompt / general caution / targeted check):

ModelNear misses answered with the candidateFact pages answered
GLM-5.3-Flash25 / 8 / 861 / 47 / 64
MiniMax M36 / 7 / 433 / 19 / 21

Both instructions were added to an instruction to ground the answer in the retrieved text. The criteria compared the targeted check with the general caution: fewer candidate answers on near misses was not met for either model (GLM-5.3-Flash: 8 against 8, with 7 removed and 7 new); answers kept on fact pages was met for GLM-5.3-Flash (47 → 64: 17 regained, none lost). The comparison with the neutral prompt is post hoc.

Public trajectories on BrowseComp-Plus (GPT-5 and o3, two retrievers). In episodes in which no annotated gold document was retrieved, GPT-5 gave a substantive final answer in 132 of 227 and 53 of 110 cases, and o3 in 43 of 258 and 32 of 145. Most of these answers state a confidence below 50. The public files carry no correctness labels, and other passages may support an answer, so we give these counts as context, not as an error rate.

Appendix H of the revision reports these analyses with the criteria that were not met; the last column of the first table, the first-step counts, the example and the BrowseComp-Plus counts are given here only.

Thanks the authors for the comprehensive rebuttals, which have covered all the points raised in my original review, including experiments with the suggested challenge variants.

I appreciate the authors' honesty with negative results and maintain my concern about the scope of the identified gap in evidence use ("this gap is diminishing and almost fixed for the more recent, stronger reasoning models").

On the other hand, the paper did explicitly acknowledge this limitation and did not over-claim. Meanwhile, there exists some remaining gap with the harder "near-miss" type for some reasoning models, suggesting the issue is not completely solvable through longer reasoning.

As said in the original review, I genuinely appreciate the motivation. I will raise the rating to 3 while highlighting my remaining concern about limited generality and impact due to weaker results on reasoning models.

AuthorsOpenReview ↗

Thank you for the constructive discussion

Thank you for your careful reading and constructive discussion. Your observation helped us clarify the paper's scope and motivated the real-retrieval comparison reported in point 3 of our update.

Point 1 also reports a new result relevant to your Q2: a separate training variant improved complete-episode accuracy at comparable search cost on bridge questions. We distinguish this result from the original counter-example intervention and explain its connection to the paper's diagnosis.

We appreciate how your feedback helped us make the findings, practical implications, and limits clearer.

Reviewer_tmr3OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper examines how search agents decide whether to answer or keep searching. Supervised fine-tuning shifted the tested agent’s main stopping cue from answer-like text to mentions of the entity in the question, even when key evidence was missing. Training on examples where the right entity appeared but more searching was needed reduced reliance on this shortcut.

Critical strengths
  1. The paper is well organized, with a clearly stated research question and a logical progression from the initial observations to the follow-up experiments
  2. The study combines controlled comparisons, real search episodes, and a targeted training intervention.
  3. The paper uses held-out data to verify key findings and clearly distinguishes preregistered tests from exploratory analyses.
Critical weaknesses
  1. The main finding relies on a fine-tuning dataset where finding the entity’s page almost perfectly predicts the target action. It is unclear how often the same behavior occurs in search agents trained on other data.
  2. The intervention reduces reliance on entity mentions, but whether it improves answer accuracy at a comparable search cost is unclear.
  3. Reliance on answer-like text increased slightly in some runs after the intervention. This leaves open whether the agent learned to check the underlying facts more reliably.
Questions for authors
  1. Among pages the agent correctly identifies as lacking the evidence needed to answer, what distinguishes the cases where it answers anyway from those where it keeps searching?
  2. If the current search result is held fixed, how does the evidence gathered in earlier steps affect whether the agent stops?
3 comments
AuthorsOpenReview ↗

Response to Reviewer tmr3 (1/2): W1–W3, Q1 and Q2

As you note, the paper "clearly distinguishes preregistered tests from exploratory analyses". [P] marks a criterion fixed before the run; "post hoc", an analysis designed after results were seen.

W1. "It is unclear how often the same behavior occurs in search agents trained on other data."

Which cue is learned depends on the data, as Section 4.4 predicted; what recurs is stopping on unsupported cues.

  • Same model and recipe on public trajectories [P: weaker than with our data, met; still present, not met]: a mention raises stopping by 2.5 points [−1.1, 6.0], against 47.7 with our data.
  • On 157 natural first results with incomplete evidence, these agents answer on 9.1%, ours on 51.6%, and two released R3-RAG checkpoints on 3.2% and 1.9%.
  • An unsupported answer-like string raises stopping by 34.3 points with public data, and by 56.0 and 52.1 in those checkpoints. On held-out pages, naming the asked entity raised the RL checkpoint's candidate answers from 43 to 108 of 166 questions [P; met], and its stops from 55 to 112 (11 to 8 without a candidate).

W2. "… whether it improves answer accuracy at a comparable search cost is unclear."

Updated. For the paper's counter-examples as they are: no detectable gain (−0.4 points; [P] not met). For a variant that keeps the first hop on the added page, which shows what to search next: yes, +9.0 points on 455 new bridge questions at comparable search cost (685 against 480 of 2,275 episodes; all five seed pairs gain; [P] met).

Section 4.4 notes a gap in our training data: they never show the first hop found and the second missing (a page names a film's director, not the director's birthplace). The paper's counter-examples weaken the cue without filling it: they delete the first hop from the entity's page. The variants modify the same 144 search examples; the closer comparison also differs in target visibility and 48 distractor passages.

EpisodesQuestionsAccuracySearches[P]
Next step shown (entity's page, first hop kept, in 120 of the 144) vs control (another entity's passage)455 new bridge+9.0 [6.0, 12.2]+0.04 [−0.20, 0.23]met
Next step shown vs cue removed (entity's page, first hop deleted)235 bridge+5.7 [1.8, 9.7]−0.18 [−0.33, −0.03]met
Paper's counter-examples vs none600−0.4 [−4.3, 3.6]−0.01 [−0.22, 0.20]not met
  • Why showing the next step matters. In row 2 both versions show the entity's page; the one that keeps the first hop is more accurate, with fewer searches. Against the control, with one search each from the same first result and the same answering model, its query turns 53 answers from wrong to right and 3 the other way ([P]; 141 development questions).
  • The next-step version relies less on the paper's cue: on the edited pages the name raises its stopping by 17.6 points, against 45.2 for the control (25.9 less at matched stopping; [P] met).
  • Scope. The added examples teach one step: search for the entity named on the entity's page. Bridge questions need it and are what our pages and training data use; on comparison-type questions, absent from the training data, none gained. Details: 2/2.

W3. "This leaves open whether the agent learned to check the underlying facts more reliably."

It learned to stop less on the entity's page alone, not to check the relation (deletion counter-examples; post hoc). At matched overall stopping they lower the mention effect by 12.2 points [6.8, 18.7], but separate a fact from a near miss no better (−0.8 points [−5.4, 3.4]) and shift stops toward candidate-only pages (+6.0 [2.2, 10.8]); our training-data check did not support the explanation proposed for this rise. Wrong-relation counter-examples did not meet the checking criterion [P].

Q2. Earlier evidence, with the current page held fixed: a first hop found earlier makes the fine-tuned agent answer almost as often as the complete chain does; before fine-tuning the model does not.

Earlier resultirrelevantfirst hop onlyboth hops
Current page has neither feature: answers, of 112990101
The same before fine-tuning1920105
Current page only mentions the entity: stops649099
… answers that contain the reference value2798

Row 3 had a criterion fixed in advance [P: met in all seven fine-tuned runs, not before fine-tuning].

New: the next-step version of W2 answers less than half as often once only the first hop has been found (row 1, "first hop only"): 174 of 560 cases, against 383 for its control (−36.3 points [−50.2, −23.4]; [P] met). After an irrelevant one: 63 and 72.

Q1. Mainly how firm its own "no" is: acting follows the same signal as judging, with a much lower bar. Of 213 pages judged to lack the fact, the agent answers on 10 of 54 where "no" is firmest and 42 of 52 where it is weakest (descriptive).

AuthorsOpenReview ↗

Response to Reviewer tmr3 (2/2): Q1, further numbers for W1–W3, end-to-end comparisons

Q1, further. Pages answered, by quartile of the agent's judgment from the firmest "no" to the weakest: 10 of 54, 18 of 55, 35 of 52 and 42 of 52 (descriptive). By position of the mention: 7 of 38, 25 of 60, 30 of 47 and 43 of 68. With and without a candidate on the page: 54 of 104 and 51 of 109.

W1, further. Released agents, mention effect on edited pages: +6.0 and +13.2 (R3-RAG), +1.9 (Search-R1). A second public source, RQ-RAG [P: direction; met]: −0.3 points [−2.6, 1.3]; these agents stop on only 19.5% of pages that state the fact, so this shows only the direction. In the held-out test of the RL checkpoint, answers with the candidate rise from 43 to 108 (+38.5 points [28.5, 48.4]; 39 to 103 by string match; both labels primary [P; met]). Stops, recorded in the same test, rise by 33.7 points with a candidate on the page and not without one (difference 35.6 [25.6, 45.5]). On development pages the effect is larger when the name and a relation of another entity stand in one passage (35.2 points, against 6.9 when they are apart).

W3, further. Held-out pages, one-hop near misses answered with the candidate: 43.9% without counter-examples, 30.0% with deletion-based ones, 23.9% with an added wrong-relation sentence; pages that state the fact answered: 99.4%, 94.9%, 90.5%. On 39 real states with the first hop retrieved and the second missing, the agents answer on 19 to 27 with the deletion-based counter-examples and on 27 to 31 without (−13.7 points [−23.1, −5.1]; descriptive).

End-to-end comparisons of training data (W2). Points and searches per question; 95% intervals over seed pairs and question clusters.

ComparisonQuestionsFixed before the runAccuracySearches
Deletion-based counter-examples against none, archived runs200 developmentcriteria only+3.0 [−0.5, 6.3]+0.02 [−0.16, 0.20]
The same comparison, new runs600 developmentyes−2.1 [−4.8, 0.8]+0.32 [0.22, 0.43]
Targeted counter-examples against none, calibrated600 newyes [P; not met]−0.4 [−4.3, 3.6]−0.01 [−0.22, 0.20]
Next step against control, calibrated200 developmentyes+11.4 [7.1, 16.1]0.00 [−0.21, 0.20]
The samethe 600 newyes [P: accuracy met; cost not met]+3.6 [1.0, 6.3]+0.16 [−0.07, 0.39]
of which 235 bridge questions+8.3 [4.3, 12.5]+0.07 [−0.21, 0.32]
of which 365 comparison-type questions−2.0 [−5.9, 2.1]+0.23 [0.02, 0.46]
The same, searches matched per adapterthe 600 newpost hoc+3.2 [0.7, 5.9]+0.03 [−0.08, 0.13]
The same, new confirmation455 new bridgeyes [P; met]+9.0 [6.0, 12.2]+0.04 [−0.20, 0.23]

In the counter-example test, the subgroup fixed in advance showed no gain either (−3.6 points [−17.0, 10.3]; [P] not met).

Details of the new tests.

  • The questions. The 600 comprised two groups listed in advance, 235 bridge questions (answered through an intermediate entity) and 365 comparison-type questions. With equal weight per question the gain over all 600 is +2.0 [−0.7, 4.6]. After these results we chose the 2Wiki "inference" type for the confirmation: 468 eligible questions in 455 clusters, one per cluster, none run by any version; no unused MuSiQue question was left. On the 370 that had appeared in none of our tables, accuracy holds (+8.7 [5.4, 12.1]); the upper bound for searches, 0.29, exceeds the criterion.
  • Why the next search. Removing the cue without showing the first hop gave no detectable gain over the control (+2.6 [−0.8, 6.0]); showing it beats that version by 5.7 points with fewer searches [P] (+2.8 [0.3, 5.5] over all 600). On the new questions, when both agents search first, the next-step version ends with 122 more correct answers (317 against 195 of 1,040); its first query names the next entity in 405 of 960 episodes against 186 (post hoc).
  • Search cost. The stop thresholds were fixed on earlier questions. Without them the gain is the same (+9.1) at +0.18 searches [−0.14, 0.44], missing the cost criteria. Against the cue-removed version none is needed: +5.6 points [1.8, 9.6] at −0.04 searches ([P] met).
  • On the edited pages (W3). The next-step version relies less on the name (1/2) but, like the counter-examples, does not check the relation better ([P] not met); its stops shift toward pages with an unsupported candidate (+12.4 points [6.0, 18.9]), and three of four harm bounds fixed in advance were not shown to hold (e.g. correct answers on fact pages: −2.3 [−6.1, 0.6]).
  • Limits. One 7B model. The versions were trained before the deadline, but the tests were designed after the results on the 600. The next-step and cue-removed versions also differ in whether the search target can be read off the added passage. On the 90 yes/no questions the next-step version loses (−10.2 [−20.4, −1.3]; post hoc).
AuthorsOpenReview ↗

A short note on W2 and Q2

Thank you for W2. We have updated W2 in our first reply, “Response to Reviewer tmr3 (1/2).” The original counter-examples weakened the name cue without a detectable accuracy gain. A follow-up variant showed whom to look up when the first link was known but the answer was still missing.

An earlier mixed-set test showed a gain on bridge questions and prompted this focused follow-up. We took one new question from each of the 455 eligible clusters of 2Wiki bridge questions. With the variant's stopping thresholds fixed on earlier data, it gained 9.0 percentage points in final-answer accuracy over its training control at comparable search cost.

On Q2, the same variant answers less than half as often when only the first hop has been found: 174 of 560 cases, against 383 for its control (first reply).

Comments on the paper

3 comments
AuthorsOpenReview ↗

Response to all reviewers (1/2): what the paper shows, what the discussion added, what we corrected

Final summary (edited 18 Nov): the reviews' three open questions (generality, reasoning models, accuracy) now have tests fixed in advance (points 1–3); all results are in the revised PDF.

[P] marks a criterion fixed before the run, reported whether met or not; "post hoc", an analysis designed after results were seen.

What the paper shows. What makes a search agent stop can differ from what it then answers. On 112 pages that name the asked entity but lack the fact, adding an answer-like string raised our fine-tuned agent's stops only from 58 to 63, but its answers asserting it from 3 to 59. Fine-tuning reversed the two cues' effects on stopping (string 29 to 5 points, mention 6 to 47), confirmed on preregistered held-out pages and seen in Mistral-7B (development pages). Asked directly, the agent calls the fact missing on 96% of such pages, yet answers on 54%.

1. General, or an artifact of our data? (tmr3 W1, xQ6j W1) Which cue is learned depends on the training data, as Section 4.4 predicted; stopping on unsupported cues recurs beyond our data.

  • With public data instead of ours, the mention effect fell from 47.7 to 2.5 points in Qwen2.5-7B and from 60.3 to 7.3 in Gemma-2-9B-it [P met]. These agents stop on unsupported answer-like strings instead, as do two released R3-RAG checkpoints; in one, naming the asked entity raised such answers on held-out pages from 43 to 108 of 166 [P met].

2. Relevant to today's reasoning models? (mgdJ W1, Q1) With reasoning, none of seven models met our criterion for a persistent gap on mgdJ's harder pages (28 model–page pairs [P]); near misses and early answers beyond the retrieved text remain.

  • Near misses (right entities, wrong relation): with reasoning off, five of six models often assert the unsupported string; with it, four of seven still do on 12.5–31.1%.
  • On 199 real first results missing some evidence, DeepSeek-V4-Pro gave 55 first-step answers without full support with reasoning off and 10 with it on [P met, as for deepseek-flash]; 8 of the 10 were correct, which accuracy counts as successes.

3. Does the diagnosis lead to better agents? (tmr3 W2, W3; mgdJ W2, Q2) Weakening the cue alone gave no detectable accuracy gain; a variant that also shows what to search next gained 9.0 points [6.0, 12.2] on 455 new bridge questions at comparable search cost [P met].

  • Our counter-examples removed 82% of the mention cue [P], but on 600 further questions at matched searches accuracy changed by −0.4 [−4.3, 3.6] [P not met].
  • In bridge questions (all our pages and training questions), finding a film's director gives the next search target while the birthplace is still unknown; about half of such search examples in three public training sets are in this state, 10 of our 444 by the same rule. The variant's examples show this state, targeting a search for the next entity; its control shows other entities' passages.
  • On the 600 it gained 3.6 points (8.3 on bridge questions, listed in advance) but missed the cost criterion [P not met]. We chose this type afterwards (MuSiQue had no unused two-hop development question) and took one question from each of the 455 2WikiMultiHopQA bridge clusters no model had run on, with stop thresholds set on earlier questions: all five seed pairs gain; searches +0.04 [−0.20, 0.23].
  • Why it helps: given the same first result and answering model, swapping in the variant's one query turned 53 answers from wrong to right and 3 the other way (141 development questions). It also beat a closer control, trained on the entity's page but without the first hop, by 5.7 [1.8, 9.7] with fewer searches (235 bridge questions; [P met]).
  • Limits: one 7B model; bridge questions only (no detectable gain on comparison questions, absent from our fine-tuning data).

What a developer can do (Section 6). For fixed questions, switch the entity name, an answer-like string and the stated fact on and off, recording stopping and answers separately; accuracy misses this. After the variant gained accuracy, this test showed its mention cue cut to 17.6 points, against 45.2 [P met], but more stops on unsupported strings and no detectable gain in relation checking (tmr3 W3), as with deletion-based counter-examples (post hoc). When changing training data, show what to search next and compare accuracy at equal search cost. Test agents on near misses, with and without reasoning.

What we corrected. (i) Public data re-sampled to our coupling (0.97) did not produce the mention cue (+3.2 [−1.4, 8.2]); we no longer offer the statistic as a warning sign. (ii) With overall stopping matched, a prefilled "Thought:" did not lower the mention effect ([P] not met). (iii) On questions one run got wrong from the entity's page, no answer matched the reference string, but two judges accepted 11 of the main agent's 60 (post hoc).

Writing, novelty, focus (mgdJ W3; xQ6j W2, W3): 2/2 and replies; details: our update (18 Nov).

AuthorsOpenReview ↗

Response to all reviewers (2/2): changes in the revision

Changes in the revision (new and changed text is blue; everything not listed here is as submitted, including the title, the section titles and their order, and the figures and tables of the main text; the main text has ten pages)

  • Abstract: one clause is deleted ("a coupling measurable before training"), one is replaced ("even on questions this page cannot answer, where every answer was wrong" by "before all supporting passages have been retrieved"; correction (iii)), and two sentences are added: no detectable gain in accuracy at comparable search cost with the counter-examples, and the result of the same recipe on public trajectories.
  • Section 1: a five-step map is added at the end (xQ6j W3; mgdJ W3); two clauses that presented the training-data statistic as a way to flag the risk before training are deleted (correction (i)); one sentence is reworded (correction (iii)).
  • Section 2: the number of recent models (nine; one was added on the harder pages).
  • Sections 3 to 4.5: the sentence that states each section's conclusion is set in bold; its wording is unchanged (mgdJ W3).
  • Section 4.2: what separates answering from searching on pages judged to lack the fact (tmr3 Q1).
  • Section 4.3: earlier evidence with the current page fixed (tmr3 Q2); correction (iii).
  • Section 4.4: the same recipe on public trajectories, with the prediction fixed before training, on edited pages and on real first results; released agents, with one test fixed in advance on held-out pages; public data re-sampled to a similar value of the statistic (tmr3 W1, xQ6j W1).
  • Section 4.5: the "Thought:" result after matching for overall stopping (correction (ii)); what the counter-examples change and what they leave unchanged; the end-to-end result on 600 new questions (tmr3 W2, W3); the conjectured reason for the slight rise of the candidate effect is deleted, here and in Section 6, because a check of the training data did not support it (Appendix H).
  • Section 4.6: a sentence that states its conclusion; the open sentence at the end of its first paragraph is replaced by the results for seven reasoning models on harder pages, near misses and real first results (mgdJ W1, xQ6j W3).
  • Section 5: three short additions state what the paper adds to the closest prior work (xQ6j W2), and one statement about the statistic is hedged (correction (i)).
  • Section 6: the sentences on the statistic and on the prefilled thought are corrected (corrections (i) and (ii)); the implications are stated as three recommended checks, with two measures that need no retraining (mgdJ W2); the limitations that have now been tested are updated.
  • Appendix B: the "Thought:" rerun. Appendix D: how answers were scored, and the judges' recount (correction (iii)). Appendix F and the AI use statement: a pointer to Appendix H. Appendix H (new): every analysis of the discussion period that tests a statement of the paper, with its status (fixed in advance or post hoc), the deviations from its plan, the criteria that were not met, and each use of the held-out pages; two short additions give that check of the training data and the fine-tuned agent's counts on the harder pages.
  • Ethics statement: one clause is updated (public trajectories are now also used to fine-tune comparison agents).
  • No result of the submission is removed; one exploratory clause on the "Thought:" run now stands only in Appendix B.

Added on 18 Nov (also in blue; the main text still has ten pages): Abstract: one clause on a variant that also shows what to search next (9.0 points over its control on 455 new bridge questions). Section 1: "and whether accuracy follows" in the map. Section 4.4: the Gemma-2-9B-it numbers. Section 4.5: three sentences on that variant, a closer comparison and the limits. Section 4.6: one sentence on reasoning on and off from real first results; two words elsewhere in the section are cut for space. Section 5: one clause shortened, with the same meaning. Section 6: the recommendation, the Qwen3-8B result and the limitations are updated. Appendix H: the confirmation on 455 bridge questions, the third variant, two post hoc analyses, the variants on the development pages and with earlier evidence, Gemma-2-9B-it with both training sets and the counter-example study, reasoning on and off from real first results, and Qwen3-8B with thinking off and on, with Tables 16 and 17 (continued) and Table 19; in the earlier paragraph on the variant, two sentences are updated (the third variant has since been run; on the 600 questions a gain at comparable cost was not established).

AuthorsOpenReview ↗

Update (18 Nov): the paper's diagnosis leads to a confirmed accuracy gain on bridge questions at comparable search cost (tmr3 W2), with further tests in two more models and in real retrieval

Matched page edits separate what changes a search agent's answer from what makes it stop. After our fine-tuning, an answer-like string mainly changed what the agent answered, but a mention of the asked entity had the larger effect on stopping, even without the supporting fact; before fine-tuning, the string did. This reversal held on held-out pages. The criteria below were fixed before the runs; Appendix H lists all, met or not.

1. A training variant that shows what to search next raises accuracy on bridge questions at comparable search cost (tmr3 W2; xQ6j W1; mgdJ Q2).

In bridge questions, the type of all our pages and training questions, finding a film's director gives the next search target while the birthplace is still unknown. As Section 4.4 notes, none of the paper's 473 search examples includes the first-hop passage (10 of 444 by page titles), and its counter-examples, which removed 82% of the name cue in a preregistered study, do not show the first hop. The variant (Appendix H; trained before the submission deadline) shows this state in 120 training examples, with a search for the next entity as target; its control has other entities' passages and the same targets.

Complete episodesQuestionsΔ accuracy, pointsΔ searches per questionCriterion
Variant vs its control455 new bridge+9.0 [6.0, 12.2]+0.04 [−0.20, 0.23]met
Paper's counter-examples vs none600−0.4 [−4.3, 3.6]−0.01 [−0.22, 0.20]not met
  • A confirmation on new questions. On 455 bridge questions of 2WikiMultiHopQA on which no model had been run, one per cluster, with the variant's stop thresholds fixed on earlier questions and the criteria before the run, all five seed pairs gain. We chose this narrower test after an earlier one on 600 mixed questions showed the gain (+3.6; +8.3 on bridge questions) but missed the cost criterion. Without the thresholds the gain is the same (+9.1), but the search interval exceeds the ±0.25 band.
  • The variant changes the behaviour the paper measures (both criteria met). On the edited pages the name raises its stopping by 17.6 points, against 45.2 for its control. With an earlier result stating only the first hop and neither feature on the current page (tmr3 Q2), it answers less than half as often: 174 of 560 cases, against 383.
  • It also beats a closer control. A third version pairs the asked entity's page with the same targets but does not state the first hop. On the earlier test's 235 bridge questions, the variant beat it by 5.7 points [1.8, 9.7] with fewer searches (without thresholds: +5.6, no more searches; met); that version gained nothing detectable over the control (+2.6 [−0.8, 6.0]).
  • Limits. On comparison-type questions, absent from the training data, no version showed a detectable gain. Matched pages also show what accuracy cannot (tmr3 W3): the variant checks the relation no better, and its stops shift toward unsupported answer-like strings. One 7B model.

2. The paper's training-data prediction held in another model family and in a model with a thinking mode (tmr3 W1; xQ6j W1, W3).

  • Gemma-2-9B-it: the name raises stopping by 60.3 points after our data and by 7.3 after public trajectories (difference 53.1 [41.2, 64.4]; met). The paper's targeted counter-examples removed 72% of the name's effect, far more than generic negatives (met).
  • Qwen3-8B, fine-tuned without thinking: with thinking off, the name raises stopping by 39.0 points after our data and by 2.0 after public trajectories (criteria met); with thinking on, the same weights keep a third of it (13.9 [7.9, 19.8]; reduction met).

3. In real retrieval, reasoning cut a strong model's early unsupported answers at a higher cost; most of those left were correct, so accuracy misses them (following mgdJ's observation). In a fresh run on 199 first results lacking part of the evidence, DeepSeek-V4-Pro gave 55 unsupported first-step answers with reasoning off and 10 with it on (criterion met, as for deepseek-flash); 35 of the 55 and 8 of the 10 were correct. Over complete episodes, reasoning raised correct answers from 141 to 156 (fully supported: 89 to 118), at about one more search per question and 5.5 times the output tokens. The modes also differ in sampling.

What developers can take (Section 6). Score what an agent does on matched pages, not what it says: neither accuracy nor our agent's own judgment showed which cue it stopped on. After changing its training data or instruction, repeat the edits and compare accuracy at equal search cost: weakening the cue gave no detectable gain; showing what to search next did (point 1). Test agents with and without reasoning.

Changed in earlier comments: our summary (1/2, now final) and both replies to tmr3 (W2, Q2), now reporting point 1. The revised PDF includes these results (Appendix H). We thank the reviewers, whose points led to these tests.

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

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