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Under review as a conference paper at ICLR 2027

OPTIMAL FOR WHICH MEANING?

Abstract

An optimization solver can solve a model correctly even when the model does not match what the user means. We study when different meanings change the recommended decision and when they can be left unresolved. We make three contributions. First, we separate three checks: whether the model expresses its stated assumptions, whether it is solved correctly, and whether its answer meets the user’s requirements. Second, we give a rule for stopping clarification: the same action must satisfy every interpretation being considered and stay within an agreed loss limit. For problems with the same objective, this rule can reuse an optimization bound instead of solving every interpretation separately. Third, we test these ideas on existing model outputs and small controlled studies. In one production problem, an action that was optimal under the model’s assumption earned 1,000 less under the cost rule confirmed by our collaborator. In six test cases, reusing bounds reduced verification solves from fourteen to six with the same fifteen valid stopping decisions. Giving the language model mathematical evidence helped one earlier task but did not consistently improve later corrections. Our results show why evaluation should check assumptions and decisions, not only the final objective value. Guarantees remain limited to the interpretations that were checked.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Semantics, optimization

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

This paper studies how to evaluate LLM-based optimization under ambiguous or underspecified requirements. It proposes a regret-based criterion for determining when clarification can stop and a bound-based method to reduce verification solves. Experiments on existing model outputs and small controlled studies illustrate the limitations of objective-based evaluation and demonstrate reduced verification costs.

Critical strengths
  1. The paper highlights an important problem in LLM-based optimization: correctly solving a mathematical model does not necessarily mean solving the problem the user intended. It highlights the need to determine when clarification of user intent is necessary.
  2. The paper offers an interesting perspective that not every ambiguity needs to be resolved. If a candidate solution remains feasible across the considered interpretations and its regret stays within an acceptable threshold, clarification can be stopped without fully resolving the ambiguity.
Critical weaknesses

The methodology relies heavily on mathematical abstractions, assumptions, definitions, and propositions, while many practical details remain unclear.

  1. Unclear implementation of key steps. For For example: how is the interpretation set HH generated from the original request; how is model equivalence in Equation (1) verified in practice; how can an action acceptable under all interpretations be identified for Proposition 1?

  2. Limited methodological contribution to LLM-based optimization. The experiments suggest that many of these operations are performed through analyst-driven audits rather than automated by an LLM. The paper does not introduce a new optimization design for LLM-based systems, leaving its practical methodological contribution unclear.

The experiments have several limitations that make it difficult to assess the effectiveness and reliability of the proposed framework.

  1. Limited validation of the overall framework. The four experiments primarily examine individual mechanisms rather than the end-to-end effectiveness of the proposed framework. Moreover, no relevant baselines, such as OR-Clarify, are included for comparison.

  2. Insufficiently documented experimental details. For example, the paper reports 245 archived records, of which 244 match a reference, 212 support semantic comparison, and 204 support both semantic comparison and the released scorer, but does not clearly explain where these records came from or how they were selected and processed.

  3. Uncertain reliability of human judgments. Although the paper investigates user intent and semantic ambiguity, some key evaluation criteria rely on human judgments of intended meaning. The limited independent annotation and review make the reliability of these judgments difficult to assess.

Questions for authors

See weaknesses.

1 comment

Thank you for asking for clearer implementation and evaluation details. We simplified the paper, added a workflow figure, and ran the common-plan search and clarification procedure.

  1. How readings are obtained. Section 3.1 records the supporting text, quantity, unit, scope, corresponding constraint, and added assumption for each modeling choice. Language checks examine choices such as whether capacity applies before sales or only at month-end. The new policy experiment starts with supplied models; the LLM pilots separately test review prompts. We do not yet have a validated automatic procedure that finds all plausible readings. Figure 1 marks this boundary.

  2. How models are checked.The checker handles continuous LPs with fixed variable meanings. It searches for a plan satisfying one model while violating a constraint in the other. Checking both directions supports feasible-set comparison; objective expressions are checked separately. Numerical results are followed by rational certificate checks. Changes in variable meanings require a mapping. This is narrower than general projected-epigraph equivalence, and the revision states that scope explicitly.

  3. How a common plan is found. Section 3.3 first computes each reading’s optimum, then combines the hard constraints and minimizes the largest regret across readings. If the checked result is within tolerance, the plan is delivered. Otherwise, the controlled experiment asks which rule applies and returns a checked optimum for that rule. An unfinished check remains unresolved; one failed candidate does not prove that clarification is necessary.

  4. Validation and baselines. Section 4.3 reports the following comparison:

PolicyAcceptable plansQuestionsLP solves
Direct172/1920192
Ask all192/192128192
Different optima192/19240320
Regret192/19226448

All 768 runs finish, and final outcomes are rechecked with exact arithmetic. We also check 256 run pairs with identical public inputs but different hidden answers; their behavior is identical before the first question. This evaluates the procedure after candidate models are supplied, not the full natural-language pipeline. OR-Clarify/InterOPT is discussed but has not been run as a baseline.

  1. Data selection. Section 4.2 gives the new selection path: 245 existing ORLM/NL4Opt outputs, 43 eligible models with explicitly continuous variables and extractable affine expressions, and twelve selected using a fixed seed before the new reviews. Selection does not use review correctness. This differs from the earlier 245/244/212/204 scorer study, which is no longer a result in this revision. We report truncations and proposals outside the checker’s variable scope separately; checker rejection is not automatically a semantic error.

  2. Human judgments. We distinguish mathematical checks under stated assumptions, intended rules fixed by experimental construction, and independent semantic judgments. The fixed-output pilot still needs independent semantic labels. Model-reviewer agreement does not replace them. The production example now describes an explicitly stated assumption that differs from a collaborator-reported convention; the record does not establish independent approval of both readings or the timing of that judgment. Independent annotation and natural-language interaction remain the next steps for evaluating the full process.

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Paper summary

This paper studies that even if LLM establishes a mathematically correct optimization model and obtains the optimal solution through a solver when there is ambiguity in the user's natural language needs, it does not necessarily mean that the solution truly meets the user's needs. The author proposes a set of criteria for determining which ambiguities must be clarified, which can be ignored, and how to efficiently validate the final solution.

Critical strengths
  1. Important and well-motivated problem formulation.

  2. A mathematically rigorous framework for decision-aware clarification.

  3. Careful experimental analysis and transparent reporting of limitations.

Critical weaknesses
  1. The proposed decision-adequacy criterion and common-bound verification largely build on established robust optimization and regret-based principles. The paper does not sufficiently demonstrate novelty over existing clarification frameworks.

  2. The framework relies on manually specified interpretations, analyst-defined regret thresholds, and scripted user responses. Its effectiveness in realistic, interactive LLM-based optimization remains unverified

  3. The experiments involve small, partially reused problem sets and lack direct comparisons with existing methods. The reduction in solver calls does not establish end-to-end efficiency, while evidence-assisted correction shows no consistent improvement.

Questions for authors

Please see above.

1 comment

Thank you for the review. We narrowed the claim, added a direct policy comparison, and clarified what the experiments establish.

  1. Novelty. Sections 2–3 now present the mathematical criterion as an application of established regret reasoning. The contribution is a concrete process for connecting modeling choices to source text, checking their consequences, and deciding whether a common acceptable plan exists. Figure 1 shows these steps. We do not claim a new minimax-regret theorem.

  2. Supplied readings and scripted answers. Section 4.3 now executes common-plan search, asking, a scripted answer, and final delivery. Eight NL4Opt problems produce 192 settings covering irrelevant limits, restrictive limits, and clear controls. Intended rules and tolerances are fixed before execution; the hidden rule reaches the policy only through an answer after a question. This tests the decision procedure with supplied models. Automatic reading generation and real-user interaction remain unverified.

  3. Baselines and efficiency. We compare four policies on identical settings:

PolicyAcceptable plansQuestionsLP solves
Direct172/1920192
Ask all192/192128192
Different optima192/19240320
Regret192/19226448

Direct answering produces 20 infeasible plans. The three asking policies return acceptable plans in every setting. Regret asks fewer questions but uses more computation. Counts include plan generation and checking, with reuse within each policy. We removed the earlier 14-to-6 verification count from the main efficiency evidence. The supported result is fewer questions at greater solver cost, not lower end-to-end latency.

  1. Review results and sample size. Section 4.2 reports that both follow-ups are correct on all 19 jointly completed constructed cases. In the fixed-output pilot, extra checks leave matched review decisions unchanged. We retain failures and distinguish a decision to keep a model from independent semantic validation. The 192 settings share eight source problems. Independent annotation and a direct comparison with an existing interactive system remain necessary to assess broader performance.
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Paper summary

The paper asks when ambiguity in a natural-language optimization request changes the decision an LLM assistant should recommend. It separates three relations that reference-objective scoring mixes: whether a generated model encodes a chosen reading (equality of projected epigraphs, Eq. 1), whether that model is solved correctly, and whether the returned action is decision-adequate for a finite set RR of retained readings, i.e., feasible under each and within tolerance of each reading's optimum (Def. 1, Eqs. 2-3). Prop. 1 ties adequacy to a minimax-regret threshold ρ(R)\rho(R) that is monotone in RR. Prop. 2 lets one relaxation bound certify regret when readings share an objective. The evidence is worked examples (OptiBench O012, MAMO EasyLP1, IndustryOR 23) and small development studies: a representation check of a formulation scorer on 204 archived ORLM/NL4Opt pairs, a cached verification study (6 cases, 14 models, 28 settings), 10 DeepSeek generations on O012, review ablations, 6 LeanOpt runs and a rescoring of 16 outputs. The headline results are three. The IndustryOR action loses 1,000 under the collaborator-confirmed cost rule. Bound reuse cuts verification solves from 14 to 6 with the same 15 stops. Supplying mathematical evidence helps in one pilot but not later.

Critical strengths

A usable evaluation lens, shown exactly on real outputs. The equivalence work the paper cites already checks formulation relations (l.73-76). The paper adds decision adequacy across retained readings (Def. 1), keeps it separate from fidelity (Eq. 1) and solver correctness, and gives a three-valued delivery status: "verified, refuted for the proposed action, or unresolved" (l.177-180). Once reading sets and tolerances are specified, this gives LLM-for-OR benchmarks a concrete alternative to scoring by reference value alone, and the paper shows the distinctions on actual model outputs. The GPT-5.4-mini IndustryOR action loses 1,000 under the confirmed reading, not the 2,500 gap between the reported objectives (l.252-255, Table 4). An O012 run that matches the reference value falsely claims that reading B has the same optimum, and the feasible point (188, 475) refutes that claim (l.404-405, 431-432). The mathematics is classical, but in this setting it makes the cost of skipping a question exactly computable once the readings are fixed: ρ\rho = 5,640 for O012 (l.232-234) and 840 for IndustryOR, attained at (0, 99, 217), a plan optimal under neither reading (l.257-258). The integer and MAMO controls (l.185-188, 236-241) cleanly separate nominal slack from decision relevance.

Correct and candidly scoped. The paper disclaims prevalence and superiority over existing systems (l.44, 82-83, 467-469), reports its null review results (l.420-421), keeps the earlier positive pilot "to avoid selecting only the later null results" (l.873-874), counts truncations as failures (l.753-754) and writes down the confirmatory study it did not run (App. E). My concerns are mostly about what the evidence can establish.

Critical weaknesses

The stopping rule is not tested as a decision procedure, as the paper states, and the review status behind its stops is unreported. The paper's question (l.46-47) is answered by Def. 1 and two elementary propositions ("set-inclusion facts, not new active-learning bounds", l.633-634; "The proof is the ordering", l.198). Eq. (3) is finite-scenario min-max regret (Kouvelis & Yu, 1997). Stopping once it is at most ε\varepsilon is the stopping test of regret-based elicitation and of decision-region determination (Boutilier et al., 2005; Javdani et al., 2014). Both are cited as "established foundations" (l.85-87), and the paper says its common-bound rule "applies classical principles" (l.88-89), but neither is mapped onto Def. 1. Because the criterion is classical, the case for significance rests on evidence that the rule makes good decisions, and the paper is explicit that it does not test this: its studies are "separate studies, not components of a measured end-to-end system" (l.287-288), and it claims neither prevalence nor an advantage over existing systems (l.44, 82-83, 467-469). I therefore count the missing test against significance, not as a flaw in what is reported. It bears on the paper's own claims only where the abstract states the Study 1 and review results (l.20-22) without the qualifiers that the body attaches to them (l.399-402, 413-421, 707-708; see my second weakness). Three further limits, each acknowledged in the paper, bear on significance. First, Table 1's three methods all verify the same acceptance rule on the same anchors, and no policy baseline is run (nominal-slack skipping, always-ask, ask-when-optima-differ); App. E names the first of these and the right metrics for a confirmatory study (l.790-794). Second, decision adequacy is never scored on a sample of outputs ("Unknown intent or tolerance remains unscored", l.767). Third, the rule needs "an agreed loss limit" (l.15-16), but no tolerance in the studies comes from a user, as the paper states (l.114-115, 703-704, 782-783), and whether the lead example counts as a decision error depends on that choice. Study 1 uses τ=ηmax⁡(1,∣vanchor∣)\tau=\eta\max(1,|v_{\rm anchor}|) with η∈{0,0.05}\eta\in\{0,0.05\} (l.702). Applying the 5% setting to IndustryOR gives τ\tau = 1,075 for B, or 1,200 when anchored at the A optimum, and both exceed the original action's regret of 1,000 under B (4.7% of the B optimum; its regret under A is 0). At that setting the action is decision-adequate for {A,B}\{A,B\} without asking, and even for B alone; it is a decision error only at tolerances below 1,000, such as η=0\eta=0. The 1,000 loss itself is exact (l.253-255); only the Def. 1 verdict depends on the tolerance. Apart from this case, whose reading A the paper does not report as permitted, I found no case where the paper reports both the outcome specific to this rule (delivering because licensed readings share an acceptable action) and a review status for the readings involved. O012 is the only Study 1 case whose alternatives the paper reports as reviewed and accepted as reasonable (l.215), and it cannot stop at either η\eta: 5% of the B optimum is 4,557, and 5% of any plan within the budget stays below 5,040, while ρ\rho = 5,640. So all 15 valid stops come from L001, L050 and L072, whose review status the paper does not report (the IDs appear only at l.699), or from L081 and O000, whose groups include variants that "contradict explicit source conditions" (l.700-701). Those variants "remain negative controls after review" (l.701), so review took place at least there; what the paper does not report is which readings behind the stops were judged licensed (Q1). The only other candidate, App. H's rent rows ("no further question", 6/6/6 in Table 5), scores LLM answer-scope labels on undescribed private data (l.279-280, 505). The rest of the evidence is small and dependent, as the paper says (l.693-695): about 125 recorded DeepSeek calls, one IndustryOR generation per condition (l.309-310), O012 reused across Studies 1, 2, 3 and 5, LeanOpt descriptions screened in advance (l.342-343), and all intent judgments relayed through one collaborator (l.300-303, 503-504). This limit on significance. What the authors say is needed, "new problems, independent review, and user-defined loss limits" (l.469), is the App. E study, which is new work rather than a revision. A small version of it could change my assessment:

  • 50 to 100 randomly drawn NL4Opt, IndustryOR or OptiBench items, with two independent annotators marking the licensed readings;
  • the fraction of items where the readings change the decision, and where a common acceptable action exists at stated tolerances;
  • one or two systems rescored under decision adequacy versus reference matching;
  • the stop/ask rule run with LLM-generated readings against the simple policies above, reporting wrong unconditional deliveries and unnecessary questions.

Study 1's agreement appears to follow from its setup, and the review ablations are at ceiling. The abstract says bound reuse "reduced verification solves from fourteen to six with the same fifteen valid stopping decisions" (l.20-21, Table 1), but this appears to follow from the setup as C.2 describes it. Fourteen is the number of models and six the number of cases (l.313-314, 705-706), and τ\tau is "fixed across its interpretation group" (l.702-703). F0F_0 is "the analyst-supplied largest-set relaxation" (l.705). Suppose it is the largest reading of a nested family and LL is its optimum, as l.705-708 suggest. Then L=min⁡hvhL=\min_h v_h, and the Prop. 2 test f(xˉ)−L≤τf(\bar x)-L\le\tau is equivalent to f(xˉ)−vh≤τf(\bar x)-v_h\le\tau for every hh. Identical stops and zero safe-unresolved cases are then guaranteed (both methods run the same 72 feasibility checks), and zero invalid stops simply restates Prop. 2. The full method is the reference that defines validity, so its zero invalid stops and zero safe-unresolved cases hold by definition. Since the anchors are "Fourteen model optima" (l.702), the 14 excluded anchor-generation solves also appear to supply every vhv_h already. The paper calls these families "supplied, favorable" (l.400) and notes that the saving "does not automatically extend to non-nested model families" (l.707-708). If F0F_0 is one of the readings, "favorable" understates "guaranteed". Both qualifiers are correct as far as they go, but the abstract (l.20-21) carries neither. The informative case is a strict relaxation with L<min⁡hvhL<\min_h v_h, where the bound can fail to certify (B.3, l.641-644), and the paper does not report whether any Study 1 case has that form. The review studies are at ceiling:

  • every arm retracts the false O012 claim in all four v29 repetitions (l.742);
  • targeted self-review scores 11/11 in Table 2, and all 29 completed verdicts are correct (l.417-418);
  • every arm is told which claim to check (l.740-741, 744);
  • the verdict differences between arms come only from outputs truncated under a 4,096-token cap (l.747, 752-754).

The paper keeps this null rather than claim a benefit (l.420-421), but summarizes it as "no added correction benefit" (l.63-64), "helps some tasks, but not all" (l.411) and, in the abstract, "did not consistently improve later corrections" (l.21-22), none of which mentions the ceiling; "no detectable difference at ceiling" would be more precise. The positive pilot (App. H, Table 5) is five answers from one private family. The facts arm used 36-38% more output tokens over the whole pilot, and the fact sheets are never shown (l.876, 901-902), limits the paper partly states (l.413-414). Of the abstract's three results, the IndustryOR case is therefore the one that depends on neither the Study 1 design nor a ceiling, and it rests on a single generation per condition, as the paper states (l.309-310). The fix has three parts:

  • if F0F_0 is one of the readings in each case, say in the abstract and Sec. 6 that the agreement holds by construction;
  • add cases where F0F_0 is a strict relaxation (the LP relaxation of integer readings, or a hull of non-nested readings), reporting per case the readings, L−min⁡hvhL-\min_h v_h, the stops, and the solves with and without anchor reuse;
  • rerun the review study with untargeted prompts ("find the error, if any"), inputs on which self-review fails, and budgets that avoid truncation.
Questions for authors
  1. Per Study 1 case, is F0F_0 a reading or a strict relaxation (with L−min⁡hvhL-\min_{h}v_h), were the readings behind its stops reviewed (L001, L050, L072), and do the 14 cached solves re-solve the anchor models?
  2. IndustryOR 23: did the collaborator deem A permitted and confirm B before seeing the output? As the answer states its assumption (l.844, C.6), is "differs from the confirmed convention" more accurate than "wrong assumption" (l.370, 465)?
  3. Please show App. H's "analyst-checked facts" (l.876): did they spell out the fields Tab. 5 scores? Were v33's five constructed controls designed after v29 showed targeted self-review retracting the O012 invariance claim?
  4. On your own cases, how often does the stopping rule's ask/deliver decision differ from "ask whenever per-reading optimal actions differ" and from nominal-slack skipping? This is the cheapest partial answer to my first weakness.
  5. Please map Def. 1 and Eq. (3) onto min-max regret (Kouvelis & Yu, 1997), regret elicitation, decision-region determination, robust satisficing and clarification-question work (Rao & Daumé III, 2018; CLAM; KnowNo), saying what the optimization setting adds.
  6. References: Zhai et al. (2025), arXiv:2502.14760 -> ICML 2025, PMLR 267:74288-74305; Miehling et al. (2024), arXiv:2403.15115 -> Findings of EMNLP 2024, pp. 14420-14437, and "human-ai" -> "Human-AI"; "bayesian" -> "Bayesian" (Javdani et al., 2014); "ask the DUST!" -> "Ask the DUST!" (Wildenburg et al., 2024); "Optibench meets resocratic ... llms" -> "OptiBench Meets ReSocratic ... LLMs" (Yang et al., 2025).
1 comment

Thank you for the detailed review. We added a controlled ask/stop experiment, corrected the earlier cost accounting, and simplified the paper.

  1. Policy evaluation and baselines (Q4). Section 4.3 now runs common-plan search, asking, a scripted answer, and final delivery. Eight NL4Opt problems produce 192 settings:
PolicyAcceptableQuestionsLP solves
Direct172/1920192
Ask all192/192128192
Different optima192/19240320
Regret192/19226448

Regret avoids 102 questions versus Ask all and 14 versus Different optima, with the same final acceptability but more computation. Counts include plan generation and checking, with reuse within each policy. Appendix J separately reports 576 preparation/scoring solves. Across 48 settings at each tolerance, Regret asks 10/10/6/0 questions at 0%/1%/5%/20%; Different optima asks 10 throughout. These are supplied, nested model pairs with scripted answers—not 192 independent language examples. The requested independent evaluation of LLM-generated readings remains incomplete.

  1. Bound reuse and reading review (Q1).Our audit confirms that F0 was a supplied model in all six original cases, with bound gap zero. Agreement therefore follows from the construction. Reusing the fourteen anchor solves leaves zero additional optimization solves for all three verifiers. We removed the 14-to-6 result from the main efficiency evidence. For reading review, L001 has collaborator-relayed agreement without separate reviewer notes; L050 has provisional assistant review; L072 retains an unresolved horizon choice. These do not establish independent validation of the original stops. A separate strict-relaxation audit found a gap of −11.25 in the handbag case and −0.5 in three constructed non-nested controls; each left one acceptable setting uncertified.

  2. Production example (Q2).The output states convention A explicitly. We now say it differs from collaborator-reported convention B. Records do not establish that B was confirmed before seeing the output or that both readings were independently approved. The original plan loses 1,000 under B. Below tolerance 840, no common acceptable plan exists; from 840 to below 1,000, a compromise passes; at 1,000 or above, the original plan passes. Thus, it passes at 5% of B’s optimum (1,075), as you noted.

  3. Review ceilings and fact sheets (Q3). We now report the ceiling directly: both follow-ups are correct on all 19 jointly completed constructed cases. In the fixed-output pilot, source-based and linguistic review agree on ten completed pairs; self-review and mathematical feedback agree on nine. These latter agreements are not semantic accuracy scores. Failures remain reported. The earlier fact sheets supplied results closely related to the scored fields, including conditional dimensions, the rent optimum, and nonattainment under a strict inequality. We no longer use that pilot to claim general correction gains. We lack a blind design freeze for the five later controls, so treat them as development examples. An untargeted rerun completed all 33 calls; all arms correctly classified the five controls, without evidence of an added correction benefit.

  4. Nominal-slack comparison (Q4). This baseline is absent from the new test. On the original 28 fixed-candidate settings, exact checking delivered 15 times, Different optima 12, and nominal-row-slack skipping 12. Six slack-based deliveries failed, all on explicit-condition negative controls. This is not a natural-language error rate. The new experiment searches for a common plan rather than treating one failed candidate as a reason to ask.

  5. Prior work (Q5).We now identify Equation (2) as finite-scenario minimax regret and Equation (1) as the intersection of feasible, within-tolerance decision sets. The stopping logic follows regret elicitation and relates to decision-region determination: a unique reading is unnecessary when remaining readings share an acceptable action. Our application adds explicit source support, hard-feasibility checks, and aligned physical actions. We claim an operational process and measured behavior, not a new regret theorem. OR-Clarify/InterOPT is discussed, but a system-level comparison and broader coverage of the clarification methods you listed remain outstanding.

  6. References and presentation (Q6). We corrected EquivaMap to ICML 2025, protected “Bayesian” and “Ask the DUST!” capitalization, and updated ORLM to its journal publication. Miehling and OptiBench are absent from the shorter bibliography, rather than claimed as corrected. The revision uses simpler language, a workflow figure, and separate sections for cases, review pilots, and policy evaluation.

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