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Under review as a conference paper at ICLR 2027

HepUKE: Uncertainty-aware Knowledge Evolution for High Energy Physics Analysis Agents

Abstract

Knowledge bases are essential to agents for high energy physics (HEP), supplying few-shot evidence for previously unseen tasks. Their principal utility lies in strategic guidance for novel analyses rather than ready-made answers or reusable code. Prevailing systems, however, treat all retrieved evidence as equally trustworthy and fail to accrue knowledge from the analyses under assistance. In this paper, inspired by the standard HEP treatment of uncertainty, we propose HepUKE: an Uncertainty-aware Knowledge Evolution system for HEP that repurposes information entropy to unify statistical uncertainty from LLM generation and systematic uncertainty from HEP methodological choices. Upon it, we construct a self-evolving domain-specific-language (DSL) knowledge base and release a large-scale expert-annotated HEP physics-analysis benchmark. Per-evidence confidence is quantified via the information entropy of sampled DSL generations: high-confidence precedents constrain program synthesis, whereas analyses lacking close precedents are validated and written back, sustaining continual knowledge evolution. To handle the highly redundant yet logically stringent nature of HEP knowledge, we introduce an early-stopping controller that fuses a backward stationarity test on the answer posterior with a forward marginal information gain estimate. On the 1,000-pair BESIII PhysicsQA benchmark, HepUKE reduces retrieval rounds by 43.0% while preserving most answer quality, and on the out-of-domain HotpotQA benchmark, it reduces retrieval rounds by 14.5% with a similar quality–efficiency trade-off. The code and datasets used in this work are available at https://github.com/AGENTANNAN/HepUKE.git.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
High-energy physics, Knowledge base, Knowledge representation, Uncertainty quantification, Domain-specific language, Agentic system

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_vTbEOpenReview ↗
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Paper summary

The paper proposes HepUKE, a RAG framework for HEP analysis that combines generation uncertainty, structural disagreement, confidence-based precedent selection, gated write-back to a DSL knowledge base, and adaptive retrieval stopping. It is evaluated on BESIII DSL synthesis, BESIII PhysicsQA, and HotpotQA.

Critical strengths

The problem is relevant, and the paper attempts to connect retrieval confidence, knowledge admission, and retrieval cost within a single scientific-agent pipeline.

The early-stopping experiment also demonstrates a useful cost/accuracy trade-off, with substantially fewer retrieval rounds and tokens.

Critical weaknesses

The central claim is not adequately validated. The paper is framed around a “self-evolving” knowledge base, but the experiments evaluate individual admission decisions rather than repeated write-back and reuse over time. The authors explicitly acknowledge that long-term knowledge evolution is not evaluated. For me, this is a central missing experiment rather than a minor limitation.

I am also not convinced by the interpretation of the proposed disagreement measure as HEP “systematic uncertainty.” It appears to be an operational generation/disagreement signal, and the paper does not establish correspondence with physical systematic uncertainty. Moreover, the main physics-sensitive metric, Phys-Acc, is itself assigned by an LLM judge. This is a weak validation basis for a paper centered on scientific reliability.

Questions for authors

Can the authors provide a genuine sequential evolution experiment in which generated entries are repeatedly written back and reused by later tasks, compared with a static-KB baseline? I would want to see downstream accuracy, erroneous-entry accumulation, retrieval drift, and dependence on previously generated entries.

I would also like to see human HEP-expert agreement statistics for Phys-Acc. Without this, it is difficult to assess whether the reported improvements correspond to actual physical correctness.

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AuthorsOpenReview ↗

Response to Reviewer vTbE

Dear Reviewer vTbE

Thank you for a precise and useful report. We respond to the comments and questions point by point below. Where a weakness and a question address the same issue, we combine them into a single response to avoid repetition and keep the discussion focused.

W1. Validation of the "self-evolving" claim

The original experiments did score admission decisions; that is a fair reading of the submitted version. But the testable claim is narrower than convergence and is now measured directly: does what the system wrote earlier change what it does later? In A1 (Sec. 5.4), 80 dev queries stream into a live collection, and 13/80 top-1 selections are written-back entries, all admitted earlier in the same stream. In the family-held-out stream, on the 16 queries where same-family reuse is even possible, a written-back entry is top-5 in 16/16 and top-1 in 9/16. Both are direct measurements of dependence on generated entries.

What cannot be tested in a benchmark is the closed loop---downstream use, validated outcome, write-back, iterate---because outcomes exist only when analyses are published. The seed is not an arbitrary baseline either: BESIII requires expert and physics-coordination review before submission, so the 500 seed programs are validated precedents at the quality the loop converges to. The fixed point is thus already in the KB; what stays open is whether write-back improves on it, which is A1/A2.

Q1. Sequential evolution

The four measurements requested, in Table 3 and Sec. 5.4:

  • Downstream accuracy. static 0.862 vs evolving 0.860, paired Δ=−0.002, p=0.254 — indistinguishable.
  • Error accumulation. 78/80 admitted; one below struct 0.5; two rejected by the confidence (c=0.488) and validation gates.
  • Retrieval drift. None at this scale: 67/80 top-1 remain seed entries.
  • Dependence on generated entries. Present (13/80) but concentrated where it cannot help: seed coverage tracks static quality (ρ=0.53), the frozen KB reaches 0.95–0.98 above median coverage, and only 2 of the 13 reuses fall in the deficient lowest quartile.

Hence the family-held-out arm. Four families and their same-paper variants are removed (500→480) and the 20 remaining members streamed. Four are family firsts, where no precedent can exist; on the 16 later members a same-family written-back entry is top-5 in 16/16 and top-1 in 9/16, struct rises 0.796→0.809, and 20/20 are admitted with none below 0.5. The App. E case study shows what the aggregate hides: the written-back entry beats the seed entry on select_track slot F1 (0.727→0.889) while the composite score moves only +0.0222→+0.0492, because token averaging is unweighted; structurally weighted averaging is future work (Sec. 7). Confidence-gated evolution is safe (no drift, one degraded admission), neutral where the seed covers the query, and positive where it does not.

W2. "Systematic uncertainty"

Sec. 4.1 already limits the claim: the analogy is procedural---target held fixed, methodological choices varied, spread taken---applied to analysis structure rather than to a measured observable, with no calibration against an experimental systematic. The issue the reviewer identifies is in naming and emphasis, and we fix it there: the term is renamed "methodological-variation spread (an analogue of the HEP systematic)" at first use, and the abstract no longer suggests a physical systematic. Hsyst,aH_{\mathrm{syst},a} itself is used as before and used comparatively: it gates admission; it is not a budget on any observable.

Q2. Phys-Acc validation

The single annotator is not the weak point. HEP selection criteria are stated operationally, and the seven-dimension rubric inherits that property: every dimension and every anchor was fixed by a panel of domain experts before any scoring, so the standard sits in the rubric, not in one person's judgment. Against that pre-agreed standard, all 74 Phys-Acc items were re-scored blind by a BESIII expert: ICC(2,1)=0.841, r=0.864, MAD 7.8, weighted κ 0.698–0.913 (General Response B). That is the reproducibility check the reviewer asks for. Residual disagreement concentrates in track and photon selection, exactly where the rubric's least explicit dimension requires reading a cut sequence.

Best regards,

Authors for submission 42629

Reviewer_ugE1OpenReview ↗
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Paper summary

This paper presents HepUKE, a retrieval-augmented system with an evolving knowledge base for generating high energy physics analysis programs in a domain-specific language (HepScript, at BESIII). Uncertainty is defined through the entropy of tokens in LLM-generated programs. Each retrieved precedent program is scored by how much it reduces this entropy relative to generation without a precedent. The score is used to select which precedent is placed in context, and to gate whether newly generated programs are written back into the knowledge base. The paper also introduces an early-stopping controller that decides when to stop retrieving. Experiments evaluate generated programs against references on whether specific elements (datasets, decay cards) match exactly, whether the program structure matches, and physics accuracy as judged by an LLM. Separate experiments evaluate the early-stopping controller on a new BESIII question-answering benchmark and on HotpotQA.

Critical strengths

The questions of how to generate HEP data analysis programs, whether a knowledge base is useful, and, if so, how to structure and use it, are interesting questions that this paper aims to explore. The BESIII-PhysicsQA benchmark could be a useful community resource if released.

Critical weaknesses

this paper has several weaknesses:

  • whether a knowledge base is useful for HEP analysis at all has not been established, here or in prior work. The only evidence is the No-RAG comparison in Table 1, where gains are small, reported without uncertainties, and measured relative to a best-of-retrieved oracle. Simpler alternatives or stronger base models are not compared.
  • many core premises are assumed, not shown or proven or cited, such as: that agents must extract transferable knowledge from precedents; that similarity-based retrieval is unreliable in HEP (the cited works are general-domain, not HEP); that similar precedents introduce unsuitable topologies or cuts; and that over-retrieval hides correct information among near-duplicates (Table 3 suggests the opposite, as more retrieval rounds give higher accuracy);
  • uncertainty measure not justified, unclear it has anything to do with systematic uncertainties in HEP, and unclear that token variations have anything to do the with variations in semantic meaning of a program. No quantitative studies on this definition is performed.
  • confidence and stopping scores introduced but not calibrated, even though text claims calibration
  • unclear if self-evolution is demonstrated, the experiments seem not to test this.
  • gains in essentially all experiments and observations are marginal and reported without error.
  • missing definitions, like theta_write, theta_high. Structural match, the “struct” quality score, the “recovery rate,” and Contain-Acc are not clearly defined. In particular, it is unclear how a “correct answer appears” is determined, and why Contain-Acc is used instead of the exact, numeric or set-F1 scorers each benchmark item declares.
  • LLM judge is not validated
  • some internal inconsistencies between numbers in tables and numbers in text.
Questions for authors

General the critical weaknesses need fixing, including:

  • fix consistency and clarity of text. remove, or justify the many assumptions in text.
  • results need uncertainties
  • claims need to be made consistent with marginal results, especially when uncertainties considered.
  • missing definitions need clear definitions.
  • quantitative tests of LLM judge, and clear quantitative tests and exploration of entropy definition.
  • calibrate key scores.
1 comment
AuthorsOpenReview ↗

Response to Reviewer ugE1

Dear Reviewer ugE1,

Thank you for a detailed and constructive report. We respond to the comments and questions point by point below. Where a weakness and a question address the same issue, we combine them into a single response to avoid repetition and keep the discussion focused.

W1 & Q1 & Q3 — is a knowledge base useful?

The Oracle row is a normalizer, not a comparator: each score is a percentage of what a gold program reaches under the same generator. The comparison asked for is No-RAG, where the gain is +4.23+4.23, CI excluding zero. "Small" needs a reference: on a corpus whose structure is saturated by 500 precedents, structural headroom is small by construction, and we no longer present structure as the gain. It is physics accuracy that improves, most where precedents are absent: in A2 a same-family written-back entry is top-5 in 16/16, top-1 in 9/16. A cross-encoder RAG shares the stack; stronger base models are future work, not a claim.

W2 — premises

  • Transferable extraction: tested, not assumed — it holds when a family precedent exists (A2) and is vacuous when none does.
  • Similarity retrieval unreliable in HEP: our measurement, not cited general-domain work. A2 (1207.2865v1): the closest seed entry adds a lepton-pair charge requirement gold lacks (−0.04 struct). App. E: a written-back entry drops two multiplicity keys inherited from an unrelated analysis (F1 0.727→0.889).
  • Over-retrieval hides correct information: withdrawn. Table 3 agrees with the reviewer; the controller is a cost–accuracy trade-off (−43.0% rounds, −2.18 points).

W3 — the entropy measure

We do not claim token entropy equals program semantics or a HEP systematic. In HEP, methodological systematics fix the target, vary methodological choices, and take the spread. Here, for one analysis, a selection path is S=s1+⋯+sNS=s_1+\cdots+s_N and an alternative is S′=s1′+⋯+sN′S'=s_1'+\cdots+s_N', where each sis_i is a cut and sis_i may differ from si′s_i'. We use entropy to quantify the contrast between SS and S′S'. This is an analogue of HEP systematics estimation, not a calibration.

W4 & Q6 — calibration

We agree the original wording was misleading, and “calibration” has been removed from the text and figure. The score is ordinal, used for ranking and interval gating, never as a probability; c=σ(score)c=\sigma(\text{score}) is a monotone link. The confidence estimator and stopping score are trained on DSL samples and QA pairs that are gold-standard resources reviewed and approved by the BESIII collaboration. They are then applied to BESIII physics analyses, where probability calibration is not the appropriate requirement; ordering and control at the operating point are. We therefore report admission quality (0.93–0.95 vs 0.48–0.64 rejected) and the binned outcome-versus-score curve. A single global calibration would also mislead, thus in future work we will study analysis-specific dynamic gating.

W5 — self-evolution

We detail knowledge-base evolution in the General Response and the revised paper. We claim evolution is conditional, not general. Accuracy improves only where precedents are absent. We therefore present evolution as safe where precedents exist and as supplying reuse where they do not, not as generally demonstrated.

W6 & Q2 — statistics and claim strength

Every Table 1 contrast carries a paired bootstrap CI. Claim status: Phys-Acc supported; structural match not supported; A1's aggregate a reported null; A2 directional at n=16n=16, labeled so. The contribution rests on Phys-Acc.

W7 & Q4 — definitions

A notation paragraph defines θwrite\theta_{\mathrm{write}}, θhigh\theta_{\mathrm{high}}, their swept values, structural match (unweighted mean of method- and slot-level F1 over the selection module, cut values ignored), recovery RR, and Contain-Acc. Contain-Acc was a mistake: it tested normalized containment of the gold value, not each item's declared scorer, so "correct" stayed invisible. The declared scorer is now primary; Contain-Acc is a formatting check.

W8 — the judge

All 74 Phys-Acc items were re-scored blind by a BESIII expert: ICC(2,1)=0.841, r=0.864r=0.864, MAD 7.8, weighted κ\kappa 0.698–0.913. Dimensions and anchors were fixed by an expert panel before scoring: this tests the instrument's reproducibility, not one annotator's taste.

W9 — consistency

Fixed: a stale accuracy in the stopping paragraph (now 48.13, Table 4) and a publication count differing between Sec. 5 and App. F; every number is checked against its table.

Best regards,

Authors for submission 42629

Reviewer_ia3tOpenReview ↗
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Paper summary

HepUKE combines uncertainty-based precedent selection, gated DSL write-back, and adaptive retrieval stopping for high-energy physics agents. Experiments on BESIII datasets show modest synthesis improvements and fewer retrieval rounds, with some loss in answer accuracy.

Critical strengths
  • The BESIII datasets and structured DSL provide a useful setting for evaluating scientific agents beyond generic text QA.
  • Early stopping offers a measurable trade-off: retrieval rounds decrease by 43%, while accuracy drops from 50.31% to 48.13%.
Critical weaknesses
  • The claimed uncertainty fusion is unclear. Equation 15 uses token-entropy features, while the structural disagreement defined in Equation 12 does not enter the score.
  • Under the token-averaged entropy definition in Appendix A.2, Figure 2's reported standard deviation of 10.96 nats is difficult to reconcile with the ln(21) bound. Please clarify whether different aggregation, scaling, or normalization is used.
  • Knowledge evolution is not demonstrated beyond individual admission decisions. Table 2 evaluates structural quality while ignoring numerical cuts, leaving physics correctness and downstream reuse unverified.
  • Controller tuning searches 14,000 configurations using gold evidence, without specifying a separate tuning/test split (Appendix A.5). This weakens confidence in the reported savings.
Questions for authors
  • How do the implemented uncertainty features, aggregation, and normalization correspond to Appendix A.2 and Figure 2?
  • Do admitted programs improve subsequent held-out tasks compared with a static library?
  • What separate datasets were used to train, tune, and evaluate the stopping controller?
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Response to Reviewer ia3T

Dear Reviewer ia3T,

Thank you for a precise and useful report. We respond to the comments and questions point by point below. Where a weakness and a question address the same issue, we combine them into a single response to avoid repetition and keep the discussion focused.

W1 & Q1. Features, aggregation, normalization

Eq. 15 does not contain Eq. 12 by design, not by omission: the two signals act at different stages. The token-entropy reductions rank candidate precedents; Hsyst,aH_{\mathrm{syst},a} gates admission, deciding whether a synthesized program may enter the KB (Sec. 4.1). A single score that mixed them would blur a selection decision with a deposition decision. What the appendix did get wrong is the accounting, and the revision corrects it:

  • Features. Per-token entropies from the model's log-probabilities: code tokens excluding notes (ΔH_stat), the full program (ΔH_full), the selection module (ΔH_sel).
  • Aggregation. A per-token mean within a sample, then a mean over the N samples per cell (N=5 in the Q1 comparison, n=3 in the Sec. 5.4 streams).
  • Normalization. Each feature is differenced against a no-precedent baseline generation of the same query, so the score is a reduction, not an absolute entropy; reductions are then standardized globally over query–candidate pairs (Eq. 15). Units are nats.
  • α. Mixing weight between ΔH_full and ΔH_sel, swept in Table 1. The best configuration is α=0.0: selection-module entropy alone, which is consistent with that module carrying almost all the variation.

W2. σ = 10.96 nats vs the ln 21 bound

The two numbers are in different units, and the revision now states the conversion next to the figure. ln 21 ≈ 3.04 nats bounds a per-token entropy. Figure 2 plots a per-program σ, obtained by multiplying each module's per-token σ by its mean token count; for the selection module, 10.96/337 = 0.0325 nats per token. ΔH_sel spans [−0.50, +0.18] nats per token, well inside the bound. App. A.2 now reports both levels and the multiplication explicitly.

W3 & Q2. Evolution beyond admission; numerical cuts

Evolution is measured in the paired stream (Table 3, Sec. 5.4): 80 queries against a live collection, so each query retrieves against entries written by earlier ones, with a frozen-seed arm under identical settings.

  • Covered stream. 0.862→0.860 (p=0.254); 67/80 top-1 selections stay seed entries; 78 admitted, one below 0.5.
  • Family-held-out stream. Four families and their same-paper variants removed (500→480); struct 0.796→0.809, and on the 16 non-first members a same-family written-back entry is top-5 in 16/16, top-1 in 9/16.

On numerical cuts, we agree they are where the physics lives---and that is what makes them hard. A cut is not correct or incorrect in isolation: whether 0.62 GeV or 0.65 GeV is right depends on the background model, the decay card, the fit window and the group's precedent, and no automatic metric can certify it. In traditional and agentic analysis alike this step is settled by human expert judgment. We do not claim to automate it, and do not present structural match as a proxy: it ignores concrete cut values, and we now say so where the metric is introduced.

What we can do is measure the numeric side three ways. Phys-Acc is the numeric-sensitive metric: the judge compares cut values and treats a relative deviation above 20% as substantive, and Table 1 reports it alongside structural match (vs relevance +1.68 [+0.34, +3.09]; vs No-RAG +4.23 [+2.50, +6.05]). Strict match covers the fields admitting an exact answer. And the reuse experiment shows the cost of numerical transfer directly: a reused program carries the cut values of its source, which is why write-back supplies structure for expert revision rather than a finished measurement. It also shows the gain where it counts---in App. E a written-back entry beats the seed entry (composite +0.0222→+0.0492; select_track F1 0.727→0.889). Our system is one component of an HEP agent: the KB supplies precedents, and downstream agents and experts carry the analysis forward.

W4 & Q3. Controller tuning

The split is now stated, not implied. Train: the BESIII-PhysicsQA train partition, which also builds the KB and runs the configuration search. Tune: a held-out tuning partition disjoint from both the 1,000-item evaluation set and the 80-query dev split used for the evolution experiments. Evaluate: the 1,000-item set, the dev split, and HotpotQA. Only the fusion weights, bias and stopping threshold are fit; the gain predictor and BOCPD are frozen at pretrained settings. Candidates are ranked by rounds saved subject to R_gold ≥ R_gold^base − 0.02, where R_gold is a retrieval lower bound (gold titles ⊆ retrieved doc ids), not answer accuracy---the search maximizes savings under a quality constraint and cannot inflate the accuracy it is scored on. App. A.5 states the partition boundaries, grid and criterion.

Best regards,

Authors for submission 42629

Comments on the paper

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AuthorsOpenReview ↗

General Response to Reviewers, including added experiments and refined work.

Dear reviewers,

We thank the reviewers for their suggestions. We have added experiments and refined the work. First, we target knowledge-base evolution in two complementary regimes, motivated by a basic HEP observation: data far exceed current understanding, and the field pursues both measurement of known physics and exploratory analyses of uncharted regions. Accordingly, A1 studies analyses with precedents, where a frozen knowledge base may suffice, while A2 studies analyses without precedents, where evolution must supply the missing experience. Second, we support the reliability and statistical strength of the comparisons: B validates the LLM judge against independent expert re-scoring, and C reports two-level paired bootstrap CIs. Details are in Sec. 5.4 and Apps. C and E.

A1. Knowledge-Base Evolution for Analyses with Precedents

A fresh Milvus collection was seeded with 500 train-split gold programs; 80 dev queries were streamed in fixed order against the current collection, so earlier writes were visible later. A static arm ran the same queries against the frozen seed with identical settings.

Both arms completed 80/80. Reuse: 78 entries admitted (1 rejected by confidence, conf=0.488; 1 by validation), KB 500→578; 13/80 (16.2%) took a written-back entry as top-1, all admitted earlier. Error accumulation: 1 of 78 has struct<0.5. Quality: struct 0.862 static vs 0.860 evolving, paired Δ=−0.002, p=0.254.

Why the aggregate does not move. Seed coverage tracks static quality (ρ=0.53). Above median coverage the frozen KB already gives struct 0.95–0.98; the deficit is in the lowest quartile (0.67; 11/20 at ≤0.5). Write-back should help there, but a random stream rarely precedes such a query with a related one: only 2 of 13 reuses land there, struct unchanged (0.666 vs 0.665).

A2. Knowledge-Base Evolution for Analyses without Precedents or Exploratory Analyses

For a general analysis with a close precedent, a frozen KB suffices; for a new one, evolution supplies the missing experience. We built a family-held-out benchmark: four families clustering in retrieval space (luminosity determination, J/ψ counting, e⁺e⁻ Dalitz decays, strong-phase measurements) were removed with all their same-paper variants (500→480; 20 entries), and the 20 remaining members of those families were streamed under A's protocol. Of the 20, four are family firsts—no same-family precedent can exist when they arrive—and 16 are later members, the only queries where same-family reuse is measurable.

Reuse becomes reliable: on the 16 non-first members a same-family written-back entry is top-5 in 16/16 and top-1 in 9/16; the four firsts are identical across arms. struct rises 0.796→0.809—right sign, sample too small to resolve. 20/20 admitted, none below struct 0.5. In addition, only a small fraction of BESIII analyses are genuinely new with no close precedent; the 16 non-first members are close to the full set available under this condition. Enlarging it would require relaxing the no-precedent criterion and would dilute the regime under test. Resolving the effect requires accumulating more no-precedent analyses, not more queries from the existing distribution.

A case study shows what the aggregate hides (App. E). For one query the evolving arm prefers a written-back entry over the shared seed entry. The composite score rises only +0.0222→+0.0492, yet select_track slot F1 against gold moves 0.727→0.889, as two multiplicity keys inherited from an unrelated cross-section analysis drop out. Token averaging is unweighted, so the score tracks program bulk and registers this key-level physics change faintly, while ranking it correctly: the signal is conservative, not brittle. Weighting tokens by structural consequence rather than counting them uniformly is a clear next step, and we now list it in future work (Sec. 7).

B. LLM-judge validation

An expert re-scored all 74 Phys-Acc items under the same rubric and anchors, blind to prior judgements: ICC(2,1)=0.841, r=0.864, MAD=7.8; weighted κ=0.698–0.913 ("substantial" to "almost perfect", Landis–Koch).

C. Confidence intervals

Two-level paired bootstrap CIs for Table 1 contrasts (B=10,000; qid-outer, generator-inner); 193 of 200 dev queries enter. Phys-Acc (0–100). All three contrasts exclude zero:

  • Confidence vs Relevance: +1.68 [+0.34, +3.09], P(>0)=0.993
  • Confidence vs No-RAG: +4.23 [+2.50, +6.05], P(>0)=1.000
  • Oracle gold vs Relevance: +24.58 [+21.61, +27.69], P(>0)=1.000 struct (0–1). The Confidence vs Relevance contrast does not resolve: Δ=+0.007 [−0.007, +0.024], P(>0)=0.828 — the interval crosses zero. Conclusion. The improvement we support is on physics accuracy, not structural similarity. We will restate the contribution accordingly and report the oracle gap (Phys-Acc +24.6, struct +0.099) as headroom.

Best regards,

Authors for submission 42629

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