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Under review as a conference paper at ICLR 2027

When One More Constraint Is Added: Decomposing Multi-Constraint Failure in Instruction-Following Evaluation

Abstract

Multi-constraint instruction-following benchmarks usually reduce a response to one score: did it satisfy every constraint at once? When that score falls as constraints are added, it does not say why. Did the model fail the new constraint, lose one it had already satisfied, or did the evaluation change its judgment while the behaviour stayed the same? We follow each constraint as the prompt grows, separating two events: satisfying the newly added constraint, and breaking one that previously passed. On FollowBench this needs two automated steps, and both are fragile. Software extracts the text of each added constraint, and an LLM judge decides whether a response satisfies it. Two plausible judging protocols disagree by as much as 55.9 percentage points on identical outputs. On a slice of Llama responses with rule-based checkers, the judge marks 30.2% of rule-passing constraints as failed, and 13 of 14 constraints that failed and then passed again were judge errors, not real recoveries. Human annotators confirm 297 of the 392 tracked constraints, counting every disagreement or ambiguous case as not confirmed. Under our frozen analysis, constraints already satisfied show no detectable steady rise in breakage across four instruction-tuned models, though rises up to 4.7 points per added constraint remain compatible with the data, and dropping the 95 unconfirmed constraints gives the same answer. We then repeat the question on ManyIFEval, where instructions are listed separately and checked by a program, so neither step is needed. Following one instruction while four more are added, its satisfaction changes by between -1.44 and +1.20 points per added instruction, with every 95% interval inside [-2.36, +2.64]; only Qwen declines detectably. Yet the chance that an instruction satisfied at one step fails at the next rises in two models. How often a constraint is satisfied and how often a satisfied constraint is lost give different answers about the same responses, even under exact scoring. Multi-constraint evaluation therefore depends not only on how many constraints are satisfied, but on which change is measured and how it is judged.

Primary area:
datasets and benchmarks
Keywords:
instruction following, multi-constraint evaluation, LLM evaluation, LLM-as-a-judge, measurement validity, benchmarks, FollowBench, ManyIFEval

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_rpPVOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2(+1)
Presentation
2(+1)
Soundness
2(+1)
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Paper summary

The paper introduces an analysis over multi-constraint instruction-following tasks, specifically suggesting a finer-grained metric that tracks how different constraints are satisfied across different levels of prompt complexity. The suggested metric differentiates between different types of LLM errors over constraints - for example, a constraint that was successful with a simpler prompt (level k) but fails when a new constraint is added to the prompt (level k+1), versus a mistake on the newly added constraint. They verify the performance both via an LLM as a judge, human annotations, and rule-based evaluations. They evaluate a few different LLMs such as Llama and Qwen.

Critical strengths
  • The setup is highly relevant to LLM evaluation, as it reflects real use cases of users.
  • The finer grained metric is novel and can be useful to analyze LLM behavior.
Critical weaknesses
  • The paper does not back up many of its claims. There is a severe lack of empirical backing, with a lot of vague sentences, missing examples, and missing citations to back up statements that the authors make.

  • The paper mentions scores which are not clear. For example, the abstract mentions metrics of "-1.44 and +1.20" without clarifying what these numbers mean, what the base score is, or how they are calculated. Forcing the reader to guess the units or the mathematical basis of the primary findings in the abstract is a major writing issue.

  • The terminology is confusing and not standard (e.g., level?). Vague terms are introduced with little clarity, obscuring the basic testing environment on the first few pages. Furthermore, the transition-based vocabulary can mislead a reader into thinking the evaluation is a multi-turn conversation, when in reality each level is a completely independent, single-turn prompt.

  • Human evaluation is mentioned, but the setup in which humans annotate is not explained. The paper relies on human annotations to audit constraint extraction and judge errors, but it fails to describe the human annotation pipeline. There are no details on who the annotators were, what instructions or guidelines they were given, how many annotators graded each item, or how annotator disagreement was resolved. This makes the human validation impossible to replicate or verify.

  • The writing of the paper makes it really difficult to follow. At certain points it sounds more like prose than scientific writing. A lot of the sentences remain vague and not explained properly, and further context is missing.

Questions for authors
  1. Is the setup that the model was tested on single turn or multi turn? what is the meaning of "level" in your setup?

  2. Could authors provide concrete examples of the setups in which you evaluate models? grounding the terminology used in the paper (e.g., "level") to actual prompts, and showing how "broken" or "acquired" will look like in the data

3 comments

Thank you. Your two questions identified a real failure in the submission: the setup was not stated clearly enough for a reader to reconstruct it. We answer both here and have revised the paper.

Q1: Is the setup single-turn or multi-turn?

Single-turn, with independent generations. Each level is a separate prompt. The model is shown level k on its own, with no history of earlier levels and no dialogue, and generates a fresh response. A transition compares judgments about the same requirement in two independently generated responses. It is not a conversational turn, a memory test, or a model revising its own earlier answer.

You were right that the submission invited the opposite reading. The phrase "single-turn" appeared once in the whole paper, in the Limitations. It is now stated in Section 2 (p. 2), where the setup is introduced.

Q2: What is a level, and what do breakage and acquisition look like?

A trajectory is a sequence of prompts designed to add one requirement per level, though surrounding wording can also change. New Figure 1 (p. 3) shows a real FollowBench trajectory rather than notation:

  • Level 1: ways to deal with stress, "presented in the soothing and eloquent style of Mr. Rogers".
  • Level 2: the same request plus "an added sprinkle of Shakespearean flair in phrasing and word choice".

For Llama-3.1-8B the judge records the Mr. Rogers constraint as satisfied at level 1 and not at level 2, which is breakage, while the new constraint is satisfied, which is acquisition. Panel (b) shows the four outcomes for a previously satisfied constraint and states that recovery is not in that table, because it conditions on a previous failure.

Appendix Z (p. 25) gives the same example with excerpts from both actual responses, so the verdict can be inspected: level 1 opens "Neighbor, I'm so glad you asked", level 2 opens "Dear friend, I see that thou dost struggle with the weight of stress". We say there that Style has no rule-verifiable coverage, so this is the judge's verdict and is not independently certified, and that a reader may reasonably think some of the original register survives. This illustrates why we distinguish recorded verdicts from independently verified outcomes. Section 4.4 quantifies judge disagreement on a separate rule-verifiable subset, which contains no Style constraints.

On the human annotation setup

Section 4.3 (p. 5) now gives the protocol in the main text. Two annotators labelled the 392 constraints entering the breakage pool as correct, incorrect or ambiguous, under a plan frozen before labelling. One is an author of this paper and labelled all 392; the second is not an author, labelled 155 for agreement, and was compensated. The interface showed neither model outputs nor the other annotator's labels, but both could view a word-level diff of the adjacent prompts, which is the signal the extractor itself uses, so the check is not fully independent of extraction. Ambiguous labels and unresolved disagreements count as not confirmed; agreement on the 155 shared items is 77.4% with Cohen's kappa 0.394, and no adjudication was performed.

This study validates constraint extraction, not the correctness of the judge's response-level verdicts. Those are assessed separately against deterministic verifiers in Section 4.4.

On the abstract's numbers

Corrected. The abstract now says the slopes are percentage-point changes in the probability that the tracked instruction is satisfied, per added instruction, and gives the base for the one model that declines detectably: Qwen, 92.6% satisfied alone and 88.0% with four more added.

On empirical backing

The supplement contains both annotators' raw labels, the frozen protocols with their dated amendments, generation provenance and configuration audits, and a numerical claim ledger that recomputes 108 reported values from the frozen artifacts and fails if any disagrees. We would be glad to clarify the evidence or provenance behind any particular result that remains unclear.

I thank the authors for the detailed response. The revised version is much clearer now. However, some of my concerns about soundness remain. The FollowBench null result seems fragile (flipping a few labels changes it) and relies on a judge with quite high error rates, and the ManyIFEval effects are small. Overall, I’m raising my score to reflect the improvements.

Thank you for revisiting the revised manuscript and for reconsidering your assessment. We appreciate your recognition of the improved clarity.

We agree that the FollowBench estimates are instrument-dependent, which is why we now limit their interpretation explicitly and report the adversarial-flip sensitivity. One clarification: the small flip counts come from an adversarial oracle that selects, with knowledge of the fitted trend, the changes that move it most. Under the non-adversarial perturbations we tested, random flipping at rates up to 50% and level-dependent corruption rising from 5% to 35% produced no positive trend intervals. Base-rate randomization at 50% produced rare positive intervals (fewer than 5% of draws for two models). These simulations are not calibrated to the actual judge-error process, so we do not interpret them as ruling out other error patterns (Appendix T).

We also agree that the ManyIFEval effects are modest in magnitude. Our main conclusion is not that adding constraints universally causes large increases in breakage, but that marginal satisfaction and conditional breakage answer distinct questions even under deterministic scoring.

We appreciate your careful engagement and have retained these limitations explicitly in the revised paper.

Reviewer_4NGMOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

The paper studies what changes when another constraint is added to an instruction: whether the new constraint is satisfied, whether previously satisfied constraints break, and whether failed constraints recover. Its main contribution is an empirical measurement study. On FollowBench, the authors audit constraint extraction, supersession, judging protocols, and judge errors, then estimate breakage trends across four models. They find no statistically detectable increasing trend under their primary analysis, while explicitly allowing nontrivial positive effects within the confidence intervals. A second study on ManyIFEval uses deterministic checks and shows that relatively stable marginal satisfaction can coexist with increasing conditional breakage. The validation includes human checks of extracted constraints, a rule-verifiable judge audit, alternative judging, and sensitivity analyses.

Critical strengths
  1. The measurement audit changes how the results should be interpreted. The large disagreement between judging protocols on identical responses and the finding that 13 of 14 audited recoveries were spurious are consequential results, not merely implementation details. The paper shows how judging errors affect both transition labels and the population conditioned on a previous pass or failure. This is useful for researchers who would otherwise interpret these statistics as model behavior.
  2. The deterministic study gives the paper a positive finding beyond an inconclusive trend test. On ManyIFEval, Llama has a small, statistically inconclusive anchor-satisfaction slope but a clearly positive pooled breakage trend. Section 6 also examines anchor-only transitions, so the argument does not rest entirely on comparing different instruction populations. I found the combination of a concrete measurement failure and an example that survives exact scoring persuasive. The authors also acknowledge the closely related forgetting and correction metrics in Multi-IF; the value here is the audit and empirical analysis rather than a claim to have invented transition rates.
Critical weaknesses

My main reservation concerns the strength of the FollowBench robustness interpretation. Section 5.2 concludes that the result is “safe against the judge error we measured.” However, Appendix T perturbs the existing judged labels; it does not establish what the trend would be after correcting the actual errors. The audit itself shows that errors can change the risk set and vary with level. The human-cleaned analysis checks constraint identity, rather than response-level judgment accuracy. These checks support stability under the tested perturbations, but do not establish robustness to the measured error mechanism. I would narrow this sentence and give the deterministic study more weight. This concern does not invalidate the measurement audit or the ManyIFEval result.

Questions for authors

Is any corruption model in Appendix T calibrated to the audit’s joint errors across adjacent levels, including errors in the preceding pass that determines eligibility? If not, would you limit the robustness claim to the perturbations actually tested? This affects how much substantive weight I place on the FollowBench trend estimates.

1 comment

Thank you for the close reading. Your objection is correct and we have changed the paper because of it.

Your question: is any corruption model in Appendix T calibrated to the audit's joint errors across adjacent levels, including errors in the preceding pass that determines eligibility?

No. None of them is. Appendix T contains four perturbation families, and all four alter recorded labels either through randomization procedures we specify or through adversarially selected changes: random flipping, randomization to each model's base rate, level-dependent corruption on a schedule we choose, and a greedy adversarial selection of flips. None is estimated from the joint distribution of the errors we observed, and none reproduces the dependence you identify, where a mistaken pass at level k-1 changes which constraints enter the risk set at all rather than only the verdict at level k. The level-dependent model varies a rate by level, which is not the same thing.

Three corrections follow from this.

  1. The robustness claim is narrowed (Section 5.2, pp. 7-8). We no longer claim the result is robust to the judge error we measured. The text now limits the conclusion to the perturbations actually applied and says why they are not a substitute: they flip recorded labels at chosen rates, whereas real errors vary by level and can fall both on the verdict at k and on the recorded pass at k-1 that decides which constraints are at risk.

  2. Identity validation and verdict validation are now separated (Sections 4.3-4.4, pp. 5-6). The human-cleaned refit tests whether the extracted constraint text names the right requirement; it does not test whether the judge's verdict on that text is correct. We also removed an unsupported assertion that errors are correlated across adjacent levels. Our audit establishes variation by level, not that dependence structure.

  3. The estimands are distinguished (Section 5.2, p. 8). Our previous closing said no check produced a detectable rise, which our own subsection contradicts: Gemma's exploratory within-constraint fit does find a positive association. The claim is now scoped to the population-averaged trend, with Gemma's result named as a different estimand over a different population. As you recommend, the deterministic study now carries more of the argument (Section 6, pp. 8-9).

What we did not do. We did not fit a calibrated joint-error model. Doing so would mean estimating a dependence structure across adjacent levels from 93 rule-verifiable constraints, drawn from one model and with no Style coverage, and then using it to correct the trend. That would be a stronger claim than this evidence supports, so we have stated the limit rather than simulated past it.

The revised position is narrower and, we think, more defensible. Under the non-adversarial perturbations we tested, the FollowBench population-averaged result shows no consistently detectable positive trend, though rare positive intervals do appear under 50% base-rate randomization, in under 5% of draws for two models. Adversarially chosen changes can overturn it: along the greedy path, the pre-specified GEE interval turns positive after 4 flips for Llama and 19 for Qwen, out of 392. Its validity therefore remains instrument-dependent. Neither the measurement audit nor the ManyIFEval result depends on our corruption simulations reproducing the real error process.

Reviewer_kmNSOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2(+1)
Soundness
3
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Paper summary

This study provides a detailed analysis of why model scores deteriorate as different constraints are sequentially added to the same query in the evaluation of multi-constraint generation tasks. Specifically, it investigates whether the performance degradation is caused by violations of previously satisfied constraints or by failures to satisfy newly added constraints while maintaining compliance with the existing ones. While no statistically significant results were observed on FollowBench, which uses LLM-as-a-Judge evaluation, ManyIFEval, which employs rule-based evaluation, showed that previously satisfied constraints were increasingly violated as the number of constraints grew.

Critical strengths
  • The paper provides a highly detailed description of the experimental preprocessing procedures and carefully examines the statistical reliability of the results.

  • The authors maintain a neutral and statistically rigorous perspective when interpreting their experimental findings. Even when the results do not support their hypotheses or are unfavorable to their expectations, they avoid overly optimistic interpretations and instead provide an objective assessment grounded in statistical evidence.

Critical weaknesses
  • Organization of the Paper

    • The experimental pipeline is difficult to follow for me. An overview figure illustrating the complete evaluation procedure would substantially improve the clarity and accessibility of the paper.
    • My understanding is that the primary research question of this paper concerns whether previously satisfied constraints become more likely to be violated when additional constraints are introduced. In other words, the study aims to investigate the consistency of models' instruction-following behavior as task complexity increases. However, Section 4 devotes considerable space to issues such as evaluation protocols and the reliability of constraint extraction, which appear somewhat indirect relative to this central research question. If the reliability of evaluation benchmarks is intended to be a major focus of the paper, I would encourage the authors to emphasize this aspect more explicitly in the Introduction. In its current form, Section 4 feels disproportionately focused on preprocessing and evaluation procedures, making it difficult to see how these analyses contribute to the main research question.
  • Experimental Scale and Setup

    • The experiments are conducted on FollowBench and ManyIFEval, but the two benchmarks differ substantially in their evaluation methodologies. Consequently, it is difficult to determine whether the observed differences in results arise from the evaluation procedures or from differences in the benchmark samples themselves. This raises concerns about the generalizability and reliability of the findings.

    • The authors primarily use GPT-4o-mini as the judge model, whereas the generation models include relatively strong models released after GPT-4o-mini, such as Gemma-3-12B-it and Mistral-Small-3.1-24B-Instruct-2503. I question whether GPT-4o-mini is sufficiently capable of reliably evaluating the outputs of these models. In fact, Section 4.4 explicitly identifies substantial issues with the judge's evaluation accuracy. Given these acknowledged limitations, I would appreciate further justification for why a stronger judge model was not adopted for the primary evaluation.

  • Evaluation Design

    • Validity of the constraint classification in Section 4.1
      • Would it be possible to classify constraints according to whether they are independent of or related to one another? Such a classification might provide a more direct way to investigate interactions between constraints.
      • Furthermore, the paper provides relatively few concrete examples illustrating the proposed classification scheme. Without representative examples, it is difficult to assess whether the classification is appropriate. I would encourage the authors to include specific examples for each category.
  • Interpretation of Experimental Results

    • Interpretation of the results in Section 5
      • I found the interpretation of the results in Section 5 somewhat overly cautious and inconclusive. The authors correctly note that the absence of a detectable steady increase in breakage does not imply that interference never occurs at particular transitions. Nevertheless, the results also indicate that no clear, systematic increase in interference was detected. This raises a question about the practical usefulness of the proposed metric. If no consistent increase in breakage is observed, would conventional level-wise performance scores or analyses of constraint-satisfaction transitions already be sufficient to characterize the model's behavior? I would appreciate a clearer explanation of what additional insights the proposed metric provides beyond these existing evaluation approaches.
      • Reporting breakage rates alone does not make it clear how many constraints were originally satisfied at each level. I suggest that the authors also report conventional evaluation metrics, such as level-wise accuracy or constraint-satisfaction rates, in the main tables and discuss these results alongside the breakage rates. This would provide readers with a more comprehensive understanding of the observed behavior.

Overall, I find it difficult to understand the motivation behind this paper and the main message the authors intend to convey. The authors should explain more concretely why this study is necessary and what specific problem it aims to address. The lack of statistically significant results also lead readers to conclude that the factors investigated are not particularly important.

Furthermore, I have some concerns about the reliability of the evaluation framework. Although the authors acknowledge issues with the accuracy of the judge model, they still report the results without fully addressing these limitations. This raises questions about how reliable the resulting conclusions are.

Questions for authors
  • Why is reporting simple accuracy insufficient?
    • Even if the breakage rate increases as the number of constraints grows, it is not entirely clear why this should be regarded as a particularly serious problem. If increasing breakage represents a fundamental limitation of current models, it may warrant specific interventions or mitigation strategies. However, it also seems plausible that such behavior could naturally diminish as models become more capable. I would appreciate further discussion of the practical significance of increasing breakage rates and why this phenomenon deserves attention beyond conventional measures of instruction-following performance.
4 comments

Thank you. You asked what conditional breakage adds over accuracy, and why Section 4 reads as preprocessing. Both pointed at real gaps in how we presented the work, and we have revised the main paper for each.

1. What the transition rate adds over accuracy

We agree this had to be shown on the same sample rather than asserted, so the conventional score is now in the main results.

Table 1 (p. 7) reports whole-response satisfaction beside breakage, recomputed from the same frozen Protocol-B verdicts on the same 107 trajectories. The in-force-masked score falls by 6.5 to 10.2 points per added constraint, from 77.6-87.9% at level 1 to 34.6-53.3% at level 5. An unmasked Protocol-B variant falls more steeply, 12.2 to 15.8 points per level. Neither should be read as FollowBench's own Protocol-A score, which differs from Protocol B by as much as 55.9 points on identical outputs (Section 4.2).

Over the same responses, breakage runs at 8 to 24% of previously satisfied constraints at every step, and none of the four trend intervals excludes zero.

We want to be careful about what this does and does not establish. It does not show that old-constraint loss contributes little to the aggregate decline: a breakage rate of 8 to 24% per step is substantial and can contribute to cumulative losses across levels. What it shows is that the steep fall in whole-response accuracy does not establish that the probability of losing an already-satisfied constraint rises with load. The two quantities answer different questions, and the first cannot stand in for the second.

Table 3 (p. 9) makes the same point where scoring is deterministic. On one set of ManyIFEval responses, Llama's fractional credit moves -0.94 points per added instruction, its all-pass score -12.50, and conditional breakage +1.82. Three numbers, same responses, different conditioning populations. Breakage trends are positive in all four models and detectably so in two.

On the FollowBench null itself we would put it this way: no model shows a detectable positive steady trend, and the 95% intervals remain compatible with trends as large as +4.7 points per added constraint. That is a limit on what we can rule out, not evidence of no effect.

2. Section 4 as preprocessing

You are right that we never said why it belongs. The opening of Section 4 (p. 4) now states that the checks are not interchangeable: human labels test whether the extracted text names the right requirement, rule verifiers test whether a verdict on that text is correct, and neither tests the other. New Figure 2 (p. 4) shows both pipelines and marks which instrument checks which stage, which also makes visible that ManyIFEval needs neither the extraction nor the judging stage.

3. GPT-4o-mini, and comparing two benchmarks

Section 3 (p. 3) now gives the reasoning rather than only the cost: it was chosen because repeated scoring of the full set was affordable at this scale, we do not assume its verdicts are reliable, Section 4.4 measures its disagreement with deterministic verifiers, Appendix V reports a GPT-4o second judge, and Appendix F reports what a reasoning prompt changes. Under GPT-4o every breakage interval still contains zero, though for Llama that comparison uses archived rather than matched generations.

On the benchmark comparison, we agree and say so earlier: Section 6 (p. 8) opens by stating this is a cross-benchmark test, not a judge-free ablation of FollowBench, and Figure 2 shows exactly which stages differ.

4. Classifying constraints as independent or related

We think this is the right question and we cannot answer it reliably here. FollowBench does not label it, and our own analysis shows that even deciding whether a later constraint is the same requirement is contested: annotators confirm only 75.8% of extracted constraints, and Section 4.1 documents cases where a later level supersedes an earlier requirement outright. A dependence taxonomy would need its own annotation study, and we would rather not infer one from data that cannot support it.

Practically, separating failure on a new requirement from loss of an established one identifies different evaluation targets. We do not claim these observational transitions identify a causal mechanism or a specific training remedy.

Thank you for your clarification. I raise my presentation score, but I would like to maintain my overall score.

While I understand the cost constraints against using more expensive models, it is standard practice in LLM-as-a-Judge evaluations to employ a frontier (or near-frontier) model. Moreover, the evaluated model, Mistral-Small-3.1-24B-Instruct-2503, outperforms GPT-4o-mini, which casts doubt on the reliability of the evaluation. GPT-4o should be used as the primary judge, with a model of comparable capability serving as the second judge.

Additionally, when quantitative evaluations cannot establish definitive conclusions, qualitative analysis becomes a key contribution. However, this study lacks a detailed analysis of why constraints break, as well as concrete remedies, which considerably limits the contribution of the work.

AuthorsOpenReview ↗

Updated paper and supplement zip

Thank you for reconsidering the presentation score and clarifying your remaining concerns. We have added two analyses to the revised appendix.

1. What kinds of constraints break? (Appendix Z.3)

Using deterministic ManyIFEval scoring, we examined 7,226 at-risk instances across four models and 15 instruction types, with task-clustered bootstrap intervals. Breakage varies substantially: all-capitals requirements break at 17.1% [11.9, 22.8], bullet-list counts at 14.1% [11.5, 17.0], versus 1.4% [0.6, 2.4] for forbidden-word constraints.

A concrete example illustrates the diagnostic value. For Llama (task 106), a one-bullet requirement passes at load 1. Adding a quotation-mark requirement at load 2 produces a response that satisfies quotation but fails the bullet checker. The requirements are compatible; the model's changed output format produces a deterministically verified transition.

These findings reveal where recorded breakage occurs, not its general causal mechanism. The pooled differences are exploratory and unadjusted for task difficulty, instruction position, and model composition.

2. Stronger judge sensitivity (Appendix Z.2)

We also applied the same GEE trend specification to GPT-4o verdicts. Under both GPT-4o and GPT-4o-mini, all four population-averaged breakage-trend confidence intervals include zero.

This supports the same statistical conclusion about detectability, not judge accuracy. Agreement is moderate (κ = 0.58), and Llama's GPT-4o evaluation used archived rather than matched generations. The independent rule-verifiable audit (§4.4) remains essential.

3. Practical implications

We have not experimentally evaluated model-level remedies. Our supported recommendation is to report conditional breakage by instruction type alongside aggregate scores and audit the evaluation instrument.

The new analyses, worked example, and reproducibility artifacts are provided in Appendix Z.2–Z.3 and the updated supplement.

We appreciate your feedback, which prompted these additional analyses.

Thank you for your effort. I have no remaining questions about the paper. As for the score, I plan to revisit the manuscript during the Reviewer–AC discussion period to make my final decision.

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

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