- Rating
- 3
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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Paper summary
This paper introduces Offline Parametric Multi-Objective Optimization (Offline PMOO), where a method must reconstruct a Pareto set for a previously unseen operating condition using only an archive collected at other conditions, without additional oracle evaluations. The paper formalizes the setting, states applicability assumptions, provides an unidentifiability result for unrestricted zero-query optimization, and proposes a benchmark containing 27 synthetic and engineering instances.
The proposed methods, Parametric Scalarized Diffusion (PSD) and Parametric Pareto Flow Matching (PPFM), learn a task-conditioned generative prior from the nondominated portion of each archived task slice. At inference time, candidates are initialized from a nearby archive slice, improved through gradient descent on a learned surrogate scalarization, and refined with guided diffusion or flow matching. The experiments compare these methods with several task-conditioned surrogate models, nearest-archive reuse, a warm-start-only method, and a modified parametric Pareto-set-learning baseline.
Critical strengths
- Important and clearly motivated problem setting. The paper identifies a practically relevant gap between offline optimization and parametric multi-objective optimization. The zero-query deployment regime is clearly distinguished from contextual Bayesian optimization, dynamic MOO, and standard offline MOO.
- Thoughtful problem formulation. The applicability conditions A1–A4 are useful for understanding when Offline PMOO can be expected to work. Even though the theoretical results are limited, explicitly connecting archive coverage, task distance, surrogate reliability, and support displacement is conceptually helpful.
- Sensible algorithmic design. Combining an archive-supported initialization with a learned elite prior is a natural way to reduce surrogate exploitation. The division of labor between the surrogate, which provides preference-specific directions, and the generator, which regularizes candidates toward supported designs, is well motivated.
- Broad and unusually candid empirical analysis. The paper evaluates 27 instances across three suites and reports several informative diagnostics. In particular, it openly identifies regimes where a surrogate solver or even nearest-archive reuse is preferable. The archive-composition, parameter-sparsity, surrogate-exploitation, and inference-time sensitivity studies are valuable.
- Well presentation and implementation detail. The paper is generally well organized, and the appendix contains enough architectural, optimization, and data-collection information to make reproduction plausible.
Critical weaknesses
- The main comparison uses unequal candidate-set sizes. The main Table 2 comparison is not cardinality-matched: PSD and PPFM return candidates, whereas the surrogate solvers return an NSGA-II population of 100. Since hypervolume is monotone with respect to adding nondominated candidates, this confounds method quality with output-set cardinality. Appendix I.2 is useful, but it covers only four selected tasks and shows that rankings can change with , most notably on DF10. The main 27-instance ranking should therefore be recomputed at a common candidate budget.
- The baseline coverage remains incomplete. The paper discusses ParetoFlow, Preference-Guided Diffusion, and Pareto-Conditioned Diffusion, but does not evaluate natural task-conditioned adaptations of these closely related offline-MOO generative methods. In addition, the PPSL-MOBO baseline replaces the original hypernetwork LoRA preference-to-design map with concatenation. This may be a reasonable simplified variant, but results from HN-LoRA surrogate predictors do not establish that the corresponding PPSL parameterization would behave similarly. These omissions weaken claims about the benefit of the specific PSD/PPFM construction relative to prior generative approaches.
- The uncertainty reporting for the main ranking is incomplete. Table 2 reports only average ranks, while Appendix J averages EHV over seeds and reports variation primarily across task parameters. This does not quantify training-seed uncertainty, and task parameters evaluated by the same trained model should not be treated as independent replicates. There is also an apparent inconsistency: Appendix C.2 describes ranking separately for each seed and task parameter, whereas Appendix J describes ranking seed-averaged hypervolumes and states that this reproduces Table 2. These two procedures are generally not equivalent. The authors should clarify the aggregation rule and report seed- or problem-level confidence intervals, preferably using paired or hierarchical resampling.
Questions for authors
- How do the Table 2 rankings change when every method returns exactly the same number of candidates, e.g., , on all 27 benchmark instances?
- Do the advantages of PSD and PPFM persist under a matched inference budget, such as the same number of surrogate/gradient evaluations or comparable wall-clock time, in addition to matched output cardinality?
- Can the authors compare against task-conditioned adaptations of closely related offline-MOO generative methods? This would help isolate the benefit of the proposed archive-supported refinement design.
- What is the exact aggregation procedure used for Table 2? Appendix C.2 appears to rank methods separately for each seed and task parameter, whereas Appendix J describes ranking seed-averaged hyper volumes. Since these procedures are not generally equivalent, can the authors clarify the implementation and report seed- or problem-level confidence intervals for the main comparisons?
Dear Area Chairs,
Thank you very much for your time and effort in handling our submission (#36525). As the discussion period concludes, we would like to briefly note the discussion status and summarize our revisions and core contributions to assist your meta-review.
Following our rebuttal, only Reviewer t6aD participated in the discussion, confirming that our new experiments resolved their evaluation concerns and raising Soundness from 2 to 3. Reviewers bLeh and ZFfg did not respond during the discussion phase. Because their primary critiques focused on concrete experimental and statistical requests that are now fully addressed in the revised manuscript, we respectfully hope you will take these updates into account when assessing our paper's contributions.
Summary of Key Revisions
Generative baselines and inverse-model comparisons (Reviewers bLeh, t6aD, ZFfg): We added five task-conditioned generative MOO baselines—ParetoFlow, DEMO (design editing), PGD-MOO, PCD, and Wei et al. (2025)—under an equal budget of K=100 across all 24 deterministic settings (Table 3, Appendix F.5, Table 52). PSD and PPFM outperform all five generative baselines on 22/24 to 24/24 settings (pHolm≤1.79×10−4) and beat the per-setting best-external-mean envelope on 19/24 and 21/24 settings. We also added a matched 9-setting comparison between Concat PSL and the HN-LoRA inverse map (Appendix H.2, Table 21).
Unified candidate budget and inference-cost evaluation (Reviewers t6aD, ZFfg): We recomputed all 16 methods at a matched budget of K≤100 across 5 archive replicates and 16 unseen conditions per setting (Table 2, Appendix J.1), where PPFM ranks 1st overall and PSD ranks 4th (ranking 1st and 2nd on Synthetic in HV, IGD+, and IGD, and top two on REAL). We also added wall-clock latency and evaluation-count caps over 960 serial runs (Table 4b, Figure 2, Appendix I): under a 0.50 s cap, PPFM leads on DF4, DF10, and Solar, whereas running NSGA-II longer degrades true EHV on DF10 (0.6189→0.4023) and Solar (0.7697→0.7094) due to surrogate exploitation.
Statistical rigor, aggregation clarity, and metric sensitivity (Reviewers bLeh, t6aD, ZFfg): Using the 5 archives as paired resampling units, we added archive-level SDs, bootstrap rank CIs, and paired CIs with exact tests across all 432 contrasts, alongside Holm-corrected benchmark sign tests (Tables 2, 44–51, 57–66). We reported both rank aggregation rules (PPFM ranks 1st under both; Table 51) and audited 8 normalization and reference-point schemes on REAL, where 38/40 external comparisons and 100% of control comparisons retain their signs (Appendix G.7).
Problem positioning, theory, and expanded ablations (Reviewers bLeh, t6aD): We explicitly formulated Offline PMOO as conditional offline MOO evaluated on unseen operating conditions (citing Off-MOO-Bench; Sections 1–3, Appendix A), tightened Theorem 1 and Proposition 1 (Appendix B), and expanded component ablations to 8 settings alongside 24-setting paired controls (Generator-removed, Selected nongenerative, and Same-guide NSGA-II; Table 4a, Appendix H.4, Tables 53–56).
Core Contributions and Methodological Takeaway
Regarding Reviewer t6aD’s remaining hesitation on novelty and RE-suite gains: our work provides a zero-query unseen-condition evaluation protocol, a 24-setting benchmark, and a systematic study of conditional surrogates, inverse maps, and warm-started generative refinement. Beyond substantially outperforming standalone generative editing (DEMO) and four other generative MOO methods, PPFM improves over its exact generator-removed control on 21/24 settings. Crucially, our study characterizes when direct surrogate search suffices versus when generative refinement is essential: on low-dimensional, smooth engineering surfaces (the 2–6 variable RE tasks), surrogate error stays small away from the archive (RMSE 0.0065–0.0133) so direct NSGA-II excels; on higher-dimensional or sharply deforming landscapes (Synthetic and REAL), unconstrained search exploits model errors while archive-anchored refinement prevents degradation.
Thank you again for your time and consideration.
Best regards,
The Authors of Submission 36525