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Paper summary
The paper introduces Online Refinement Offline Reuse (ORO), an inverse-design framework that learns while running an expensive black-box simulator. It combines online correction of a forward surrogate with target-directed updates of an inverse network, then reuses every simulated design-response pair for global offline training. Under matched simulation budgets, ORO outperforms genetic search, Bayesian optimization, and offline-surrogate methods on three synthetic benchmarks, with additional validation on a full-wave filter-design task.
Critical strengths
Strengths:
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The authors propose Online Refinement Offline Reuse (ORO), an inverse-design framework that updates both a forward surrogate of a black-box simulator and an inverse network during online refinement, then reuses accumulated simulations offline to learn from stored samples without additional simulator calls.
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Under matched budgets of 2K simulator calls, ORO achieves lower median error than direct genetic search across three benchmarks. On a full-wave filter-design task, it reaches a compliant design in approximately 1.2K simulations versus 16.3K for the baseline approach.
Critical weaknesses
Weaknesses:
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The comparisons omit closely related adaptive surrogate-based methods, such as AutoTandemML, and stronger Bayesian optimization baselines, such as TuRBO. This leaves unclear whether ORO’s proposed training procedure offers an advantage over existing adaptive approaches, rather than primarily over fixed-surrogate search and the selected optimizers.
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The offline-replay ablation removes both surrogate retraining and inverse-network training on achieved responses, while also reducing training compute. It therefore shows that offline training matters, but does not establish whether achieved-response reuse provides benefits beyond maintaining a more accurate surrogate, leaving a central contribution insufficiently validated.
Questions for authors
Q1: The authors discuss in the introduction AutoTandemML, but the experiments do not include it. The argument that ORO avoids a separate acquisition function explains a methodological difference, not why an empirical comparison is unnecessary. Such a comparison would test whether that difference improves simulation efficiency or solution quality. Could you compare ORO against AutoTandemML or another closely related adaptive surrogate-based inverse-design method under matched simulator budgets, to establish the benefit of the proposed refinement and replay procedure?
Q2: The evaluation counts simulator calls but does not report the cost of pretraining and repeatedly updating the forward and inverse networks. Could you report end-to-end wall-clock time, separating simulation, pretraining, and online/offline training costs, for ORO and the baselines? In particular, does the reduction in simulator calls translate into lower total runtime on the full-wave filter-design task?
Q3: Concerning the full-wave results, what numerical criterion defines a compliant design, and how variable is the simulation count across repeated runs?
Q4: Do all methods search the same parameter bounds? Appendix C.1 gives the inverse network an output range wider than the sampling box, while Appendix C.3 says genetic-search offspring are clipped to the admissible box. Could you clarify the exact bounds used by each method?
Response to Reviewer 69Md
Thank you for a thoughtful review. Your concerns about the online phase, the warm-up and exploration shaped several of the main changes.
W1. Robustness of the online phase. We agree that the online alternating updates alone are not a reliable learning signal, and the revision now shows it directly (Section 3.4, Appendix F). Without offline retraining, the surrogate's gradient is a descent direction for the true error on only 47% of probes, which is chance, with cosine near zero. With it, the figures are 92% on resonance and 79% on the pole–zero benchmark. In ORO the online updates are small corrections between offline retrainings on all data, at a lower learning rate for the surrogate (7×10⁻⁵ online against 8×10⁻⁴ offline). A single point thus refines, rather than overwrites, what offline training learned, and each offline phase corrects drift and forgetting. Section 4 states that the alternating updates carry no convergence guarantee.
W2 / Q1. Reliance on the GA warm-up. Two pieces of evidence now address this. First, in the main comparison ORO starts from the GA's first 400 calls, whose median error at that point is well above TuRBO's on every benchmark. ORO keeps improving until its median overtakes TuRBO's, after about 500, 1,100 and 1,600 calls, so its advantage is not inherited from the warm-up. Second, two experiments start ORO from a task-agnostic Latin-hypercube warm-up of 400 designs. In the direct-design comparison, ORO beats direct optimization on 28/30 resonance targets. In the sequential experiment, ORO has the lowest median error on both benchmarks, 20× below TuRBO on resonance. We did not rerun the main table with a Latin-hypercube warm-up within the rebuttal period.
W3. No acquisition function, the upper tail, and positioning. We agree that removing the acquisition function removes explicit exploration. ORO now adds a scheduled exploration (Section 2.5): a decreasing fraction of calls resample one parameter of the best design found so far. This is a mutation operator, not an acquisition criterion. Its effect is largest on the pole–zero benchmark, where the median error plateaus near 1.0×10⁻² without it and reaches 2.8 to 4.6×10⁻³ with it. Mutation alone does not explain ORO's results: GA, a mutation-based search, loses to ORO on at least 28 of 30 targets on every benchmark, and on resonance most improvements come from ORO's own proposals (29 to 36 per target, against 14 to 17 from exploration). On the upper tail you are right, and the paper now says so: TuRBO has lower mean error on both non-unique benchmarks. On the bijective Rosenbrock control, ORO's mean equals its median, which points to structural traps in non-unique landscapes as the cause. On positioning, AutoTandemML is now benchmarked (ORO is better on 29 or 30 of 30 targets on every benchmark), and Section 1 discusses PIED and conditional invertible networks: both assume either a known governing equation or a fixed training set, rather than a black-box simulator queried during the search.
W4. Results on the pole–zero benchmark. One factual correction, respectfully: the submission did not include CMA-ES, and ORO was better than BO on this benchmark on 23/30 targets (p = 5.2×10⁻³, Table 2 of the submission). In the revision, ORO is better than CMA-ES on 25/30 targets (p = 3.2×10⁻⁴) and than BO on 29/30 (p = 5.8×10⁻⁸). You are right that this is the hardest benchmark: against TuRBO the paired comparison is even (16/30), as the abstract and limitations now state.
Q2. The 300-point BO subset. The random subset bounds the cubic cost of exact GP inference over thousands of evaluations; a random rather than best-only subset keeps information about poor regions. We agree that TuRBO is the scalable alternative, and it is now included (Appendix C.4: TuRBO-1 with a Matérn-5/2 ARD kernel, fitted to the 400 designs nearest the trust-region centre, with Thompson sampling). It is our strongest baseline.
Q3. Sequential failures on the pole–zero benchmark. We identified two likely causes: networks warm-started from earlier targets lose plasticity (Ash & Adams, 2020; Dohare et al., 2024), and uniform replay of a growing history dilutes the data relevant to the current target. The revised scheme (Section 2.7) re-initialises both networks between targets, pre-trains them on the whole history, and trains each target's offline phases on the designs with the lowest error for that target. Over 30 targets with 1,000 calls each, ORO now has the lowest median error on this benchmark (3.2×10⁻³ against 4.9×10⁻³ for TuRBO). It beats GA on 26/30 targets and CMA-ES, BO and AutoTandemML on 30/30, and is level with TuRBO (18/30). Later targets do not become measurably cheaper on this benchmark, which the paper states; on resonance they start from significantly lower error.
We hope the revision addresses your concerns, and we would be glad to clarify anything further.