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Under review as a conference paper at ICLR 2027

Learning While Searching: Inverse Design through Online Refinement and Offline Replay

Abstract

Predicting a physical system's response from its parameters is a well-established forward problem. Inverse design is harder when the mapping is nonlinear or non-unique and each simulation is expensive. We introduce ORO (Online Refinement, Offline Reuse), a framework that learns while it searches by coupling a forward surrogate with an inverse design network. Online, the inverse network proposes a candidate for a target whose design is unknown; the simulated response corrects the surrogate, and gradients through the corrected surrogate move the inverse network toward the target, with neither simulator derivatives nor an acquisition function. Offline, the accumulated design–response pairs retrain both networks, with achieved responses serving as inverse-training targets whose designs are known, so unsuccessful proposals continue to inform learning at no extra simulation cost. On three synthetic simulators that separate non-uniqueness from ill-conditioning, at a matched budget of 2,000 simulator calls per target including initialization, ORO attains lower mean and median error than genetic search on the true simulator, Bayesian optimization, and genetic search on an offline-trained surrogate, with median errors 5.5, 51.4 and 1.4 times lower than direct genetic search. Removing offline reuse causes learning to stall. Carrying its dataset across twenty targets, ORO matches the accuracy of a 30,000-sample offline surrogate using under 10% of that budget on two of the benchmarks. On a band-pass filter designed with a commercial full-wave solver, it reaches a compliant design in about 1,200 simulations, against 16,300 for a surrogate-based genetic approach.

Primary area:
optimization
Keywords:
Inverse design, simulation-in-the-loop learning, sample-efficient learning, surrogate models, active learning

Reviews

Among:
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1234this paper, Bottom 2%
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_nKEsOpenReview ↗
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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:

  • 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.

  • 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:

  • 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.

  • 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?

Reviewer_69MdOpenReview ↗
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Paper summary

The paper studies black-box inverse design problems, where simulator derivatives are unavailable and mappings may be non-unique and ill-conditioned. The authors proposed ORO, which involves training a forward neural surrogate S with an inverse design network D. For the online phase, D generates a design proposal and the black-box simulator runs. The local surrogate S then takes a gradient step on the outcome, before S gets frozen and D takes a gradient step. For the offline phase, both networks are trained on all accumulated pairs using tandem loss. The method was empirically tested over 3 15d synthetic benchmarks and a mmWave bandpass filter in CST.

Critical strengths
  • The proposed approach of adapting hindsight replay to this setting is sound, preventing issues related to averaging conflicting supervision signals.
  • The synthetic benchmarks systematically studies non-uniqueness and ill-conditioning separately, and in general key experimental details are well accounted for, e.g. simulator calls.
Critical weaknesses
  • The online phase design of alternating gradient steps between the two networks does not seem robust and is not theoretically principled. In practice, it risks surrogate hallucination and catastrophic forgetting among other problems. Sec 3.4 shows how removing offline batch retraining degrades ORO performance significantly, underscoring how the offline batch training is critical.
  • This makes the issue of the ORO warm-up phase potentially problematic. While not technically part of the ORO method, the main experiments specifically uses a target-directed genetic algorithm method as warm-up for the ORO. It is uncertain whether ORO is just performing as a local optimizer reliant on existing heuristic global search methods.
  • Removing acquisition functions essentially reduces balanced search exploration to greedy deterministic exploitation. This risks surrogate misleading D, which can be seen in the empirical result's large upper error tail and poorer results on the Rational benchmark. The work should be positioned against related works, such as [1] AutoTandemML that involves tandem networks with active learning which is mentioned only briefly as 'target-agnostic' and not benchmarked against, [2] PIED that similarly addresses nested acquisition optimization but taps on unrolled PINN dynamics for physics-informed settings and contrasting ORO's blackbox greedy search with physics-informed experimental design is useful, [3] cINNs resolving non-uniqueness by capturing preimage distributions.
  • Results on realistic Rational benchmark seems to not be conclusive, underperforming CMA-ES and BO. Sequential data accumulation also seems to increase failure rates.

[1] Grbcic et al., AutoTandemML: Active learning enhanced tandem neural networks for inverse design problems, Applied Soft Computing, 2025. [2] Hemachandra et al., PIED: Physics-Informed Experimental Design for Inverse Problems, ICLR 2025 [3] Ardizzone et al., Analyzing Inverse Problems with Invertible Neural Networks, ICLR 2019.

Questions for authors
  • What is the ORO performance if instead of a target-directed GA, 400 task-agnostic uniform random, space-filling methods such as Latin Hypercube samples are used instead for warm-up?
  • Why was the BO baseline restricted to using random subsamples of 300 evaluations, rather than using scalable trust-region BO designed for large budget such as TuRBO [4]?
  • Why does carrying forward data and network across sequential targets increases failures on the Rational benchmark, and how can it be mitigated?

[4] Eriksson et al., Scalable Global Optimization via Local Bayesian Optimization (TuRBO), NeurIPS 2019.

2 comments
AuthorsOpenReview ↗

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.

Thank you for the response. It helped provided clarity, but confirmed my main concerns regarding the method's and empirical results' robustness as the authors have also pointed out. Hence, I maintain my rating.

Reviewer_JEvsOpenReview ↗
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Paper summary

This paper proposes Online Refinement, Offline Reuse (ORO), a framework for inverse design with expensive black-box simulators. The method combines a differentiable forward surrogate with a target-conditioned inverse design network and alternates between online refinement and offline learning from previously collected simulator evaluations. During online refinement, the inverse network proposes candidate designs, the simulator provides their actual responses, and the corrected surrogate supplies gradients for improving subsequent proposals. During offline reuse, the method treats previously achieved responses as valid training targets, allowing both networks to learn from simulations without additional simulator calls. The authors evaluate ORO on three synthetic benchmarks covering non-uniqueness and ill-conditioning, a sequential multi-target design setting, and a millimeter-wave band-pass filter designed using a commercial full-wave simulator. ORO achieves lower median response error than the reported baselines at a budget of 2,000 simulations per target and demonstrates substantial simulation savings in the filter-design example. Overall, I find the approach practical and the experimental results encouraging. However, I have concerns about whether the experiments sufficiently isolate the benefit of the proposed learning mechanism, the competitiveness of the baselines, and the computational cost and generalizability of the approach.

Critical strengths
  • Well-motivated approach to expensive inverse design. Simulator evaluations are expensive and gradients are often unavailable in scientific and engineering design. Learning a differentiable forward surrogate while optimizing an inverse network is a reasonable response. Defining the objectives in response space suits problems with multiple valid solutions.

  • A useful combination of online refinement and offline reuse. The paper separates improving the design for the current target from learning from responses the simulator has already produced. Reusing unsuccessful proposals as valid training targets is an intuitive way to extract more information from expensive evaluations. The target-conditioned inverse network also offers an alternative to explicitly optimizing an acquisition function.

  • Strong results under matched simulator budgets. At 2,000 calls per target, ORO has the lowest median error on all three synthetic benchmarks (Section 3.3). Its gains over genetic search on the true simulator are about 5.5×, 51.4× and 1.4× on resonance, Rosenbrock and rational. Paired win rates and sign tests are reported alongside averages. The paper also discusses the crossover budgets below which genetic search remains better, which makes the evaluation more balanced.

  • Benchmark design and ablation. The three synthetic simulators separate non-uniqueness from ill-conditioning. Resonance and rational contain equivalent solutions, while Rosenbrock is a uniquely solvable control. The no-offline-reuse ablation shows that removing offline learning substantially worsens performance at the same simulator budget. The appendices give the formulation and implementation in useful detail.

Critical weaknesses
  • The contribution of the online–offline mechanism is not isolated.

    • The individual components have close precedents: neural-adjoint methods (Ren et al., 2020); AutoTandemML (Grbcic et al., 2025): active learning + tandem networks for inverse; hindsight experience replay (Andrychowicz et al., 2017); goal babbling (Rolf et al., 2010) runs a goal-conditioned inverse model toward requested goals. This is the closest uncited precedent. aken together, the method reads as a useful combination of known ideas for inverse design.
    • The particular integration, with one inverse network serving as both design model and query rule, is a plausible contribution. The experiments do not show which part of it produces the gains.
    • The no-offline-reuse ablation removes all offline updates. It therefore cannot separate the benefit of achieved-response training from that of repeatedly refitting the surrogate on accumulated data, or of simply taking more optimization steps.
    • A controlled comparison that keeps dataset replay and model capacity fixed but changes the inverse-network update would clarify the main contribution. A natural reference is an online-adapted neural-adjoint method that optimizes the design variables directly through the same corrected surrogate.
  • The baselines do not establish superiority over stronger adaptive optimizers.

    • The offline-surrogate baseline uses a fixed dataset and cannot correct its model for the current target, which is exactly the limitation ORO is designed to overcome. Its poor performance therefore says little about other online surrogate-assisted methods.
    • As discussed above, AutoTandemML is directly relevant.
    • The Bayesian optimization baseline uses a global Gaussian process fitted to a random subset of 300 observations once the data exceed that size.
  • Total computational efficiency unclear.

    • Counting simulator calls is appropriate when simulations dominate cost, but network training is not counted.
    • The budget-matched experiments run 15 offline epochs per network after every three online calls (Appendix C.2), which adds up to many training cycles over a 2,000-call run.
    • Wall-clock times, split into simulator, surrogate-training and inverse-network-training costs, would show whether the savings in simulator calls translate into practical efficiency across different simulator-cost regimes.
  • The generality and reliability of the results are limited.

    • All three synthetic benchmarks use 15 design parameters and 200-point responses, with targets generated from feasible designs. The paper frames the problem as allowing unattainable specifications, but none is tested. Higher-dimensional geometries and noisy simulators are not tested either.
    • The margin is small on the hardest benchmark. On rational, ORO improves the median error over direct genetic search by about 1.4× (Table 2) and the mean error by about 1.2× (Table 6). The paired comparison supports a real advantage, but the practical margin is modest.
    • More importantly, Section 3.5 reports no measurable benefit from accumulation on rational. The accumulating variant misses the reference accuracy on 8 of 60 instances, against 3 of 60 for the reset variant.

References

  • Andrychowicz, M., et al. (2017). Hindsight experience replay. NeurIPS 2017.
  • Eriksson, D., Pearce, M., Gardner, J., Turner, R. D., and Poloczek, M. (2019). Scalable global optimization via local Bayesian optimization. NeurIPS 2019.
  • Grbcic, L., Müller, J., and de Jong, W. A. (2025). AutoTandemML: Active learning enhanced tandem neural networks for inverse design problems. Applied Soft Computing, 184, 113828.
  • Ren, S., Padilla, W., and Malof, J. (2020). Benchmarking deep inverse models over time, and the neural-adjoint method. NeurIPS 2020.
  • Rolf, M., Steil, J. J., and Gienger, M. (2010). Goal babbling permits direct learning of inverse kinematics. IEEE Transactions on Autonomous Mental Development, 2(3), 216–229.
Questions for authors
  1. What does optimizing a target-conditioned inverse network add over optimizing the design directly through the updated surrogate? Could the authors compare ORO with an online-adapted neural-adjoint baseline that uses the same surrogate, simulator observations and replay schedule but updates the design variables directly?

  2. How much of the improvement comes from achieved-response reuse? Could the authors add separate ablations that keep offline surrogate training but remove inverse-network training on achieved responses, and vice versa?

  3. How reliable are the gradients from the online-corrected surrogate? Correcting the surrogate at one design does not guarantee accurate local gradients. Since the synthetic simulators are differentiable, could the authors report the alignment between surrogate and true gradients as a diagnostic, without using the true gradients for optimization?

  4. How does ORO compare with stronger adaptive search baselines, such as TuRBO or CMA-ES, under the same simulator budget?

2 comments
AuthorsOpenReview ↗

Response to Reviewer JEvs Part 1 of 2

Thank you for a detailed and generous review. Your questions were specific enough to act on directly, and each is answered by a new analysis in the revision.

W1. Precedents and the contribution. We agree, and Section 1 now names each precedent with its citation: the neural adjoint (Ren et al., 2020), AutoTandemML (Grbcic et al., 2025), hindsight experience replay (Andrychowicz et al., 2017), goal babbling (Rolf et al., 2010), and training an inverse model through a learned forward model (Jordan & Rumelhart, 1992). We describe goal babbling as the closest: it also runs a goal-conditioned inverse model toward requested goals and learns from the outcomes it reaches, but fits the inverse model directly to those outcomes, weighting samples to resolve redundancy, where trials are cheap. ORO instead learns through a differentiable forward surrogate, which supplies a gradient toward a target not yet reached, under a fixed budget of expensive simulations. We now present the contribution as this integration, with one target-conditioned network as both design model and query rule, together with an analysis of which part produces the gains.

Q2. Achieved-response reuse versus surrogate refitting versus more steps. An offline-objective study gives every variant the same number of offline updates (Section 3.4, Appendix D). Training on the requested target matches or beats achieved-response training: on resonance with exploration it is better on 27/30 targets, with a per-target median error 7.7× lower; on the pole–zero benchmark the difference is not significant. Achieved-response reuse is therefore not the source of the gains, and we have revised the central claim accordingly. The component ablation (Appendix E) keeps offline surrogate training but removes offline inverse training, which raises the final median error about 14× on resonance. The converse, offline inverse training without offline surrogate retraining, was not run. Its surrogate would be trained only by single-point online corrections, the regime in which the gradient diagnostics below find gradients no better than chance; Appendix E says this.

Q1. An online neural adjoint. We implemented exactly this (Section 3.4, Appendix G): the same surrogate, online correction, offline retraining, learning rates and schedule, but a single design vector optimized through the corrected surrogate. From the same Latin-hypercube warm-up, the inverse network is better on 28/30 resonance targets after 1,000 calls (median 2.1×10⁻³ against 1.0×10⁻², p = 8.7×10⁻⁷). On the pole–zero benchmark it is ahead in median but not significantly (18/30, p = 0.36).

Q3. Reliability of the online-corrected gradients. Following your suggestion, Appendix F compares surrogate and true gradients at 160 probes on each of 10 targets, using true gradients only for the measurement. With offline retraining, the median cosine is 0.77 on resonance and 0.43 on the pole–zero benchmark, and the surrogate gradient is a descent direction on 92% and 79% of probes. Without offline retraining, the cosine is −0.02 and descent occurs on 47% of probes, which is chance. The online correction itself helps modestly (from 90% to 92%, and from 77% to 79%).

AuthorsOpenReview ↗

Response to Reviewer JEvs (part 2 of 2)

(Continued from the previous comment.)

W2 / Q4. Stronger baselines. We agree that the offline-surrogate GA says little about adaptive methods, and it is omitted. TuRBO, CMA-ES with increasing-population restarts and AutoTandemML are added under matched budgets (Table 1). ORO has the lowest median error on all three benchmarks: 45× below TuRBO on resonance (26/30), 10× below CMA-ES on Rosenbrock (25/30), and level with TuRBO on the pole–zero benchmark (16/30), where it beats CMA-ES on 25/30 targets. TuRBO leads at small budgets. BO's 300-point random subset bounds the cubic cost of exact GP inference, and TuRBO is its scalable alternative.

W3. Computational efficiency. Table 11 splits wall-clock time per target into simulator, offline surrogate and offline inverse-network training. ORO takes 336 to 425 s of GPU time, about 98% of it offline, so on cheap simulators GA and CMA-ES are far faster. With CST, at about 5 minutes per simulation of our filter, 2,800 calls take 233 hours against ORO's 6 to 7 minutes. ORO's extra overhead over TuRBO, at most 291 s, is less than one simulation, so wherever ORO needs fewer calls it is also faster end to end. On resonance it reaches TuRBO's final median error after about 1,250 calls, saving about 130 hours per target.

W4. Generality and reliability.

Unattainable specifications: the new filter experiment designs from an explicit specification mask with no reference design behind it (Section 3.6). Its best design meets the mask only in part, consistently across four runs. That design problem has 30 parameters, against 15 in the synthetic benchmarks. Noisy simulators and higher-dimensional synthetic problems remain untested, and Section 4 says so.

Margin on the pole–zero benchmark: ORO's median is now 5.8× below GA's (29/30) and it beats CMA-ES, BO and AutoTandemML, but it is level with TuRBO, as stated.

Accumulation on the pole–zero benchmark: the sequential scheme now re-initialises the networks between targets and trains on a target-specific buffer (Section 2.7). ORO has the lowest median error over 30 sequential targets on both benchmarks. On the pole–zero benchmark later targets do not become measurably cheaper, which we state; on resonance they start from significantly lower error (rank correlation −0.46, p = 0.011).

We hope the revision addresses your concerns, and we would be glad to clarify anything further.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response

We thank all three reviewers for careful and constructive reviews. They agreed on the motivation, the benchmark design and the budget-matched protocol, and raised three shared concerns: missing adaptive baselines (AutoTandemML, TuRBO, CMA-ES); whether the online–offline mechanism, and achieved-response reuse in particular, is isolated; and computational cost and generality. We have revised the paper substantially. All changed text is in blue.

  1. Stronger baselines, identical bounds, every call counted. The main comparison (Section 3.3, Table 1) now includes GA, CMA-ES with increasing-population restarts, BO, TuRBO and AutoTandemML. All methods search the same box, from which the targets are drawn; every call is counted; each benchmark has 30 targets and 2,800 calls per target, with paired sign tests. ORO has the lowest median error on all three benchmarks: 45× below TuRBO on resonance (26/30 paired wins), 10× below CMA-ES on Rosenbrock (25/30), and level with TuRBO on the pole–zero benchmark (16/30, p = 0.86), where it beats GA, CMA-ES, BO and AutoTandemML on 25 to 29 of 30 targets. We also report where ORO does not lead: TuRBO is stronger at small budgets when each target starts from scratch.

  2. Isolating the mechanism. Section 3.4 adds four analyses: gradient alignment between surrogate and true gradients; a component ablation; an offline-objective study comparing achieved-response, requested-target and alternating training with an identical number of updates; and a comparison with optimizing a design vector directly through the same corrected surrogate, an online neural adjoint. With offline retraining, the surrogate gradient is a descent direction for the true error on 92% (resonance) and 79% (rational) of probes; without it, on 47%, which is chance.

  3. A revised central claim. The offline-objective study changed our understanding. At equal compute, training the inverse network offline on the requested target matches or beats training it on achieved responses (better on 27/30 resonance targets with exploration; no significant difference on the pole–zero benchmark). The benefit of the offline phase therefore comes mainly from retraining the surrogate on all data, which makes its gradients reliable, rather than from achieved-response targets specifically. The paper now states this plainly, and uses achieved-response training for pre-training and for consolidation between targets.

  4. Exploration. Gradient refinement is local. Following Reviewer 69Md, ORO now adds a scheduled mutation of its best design (Section 2.5), which is not an acquisition criterion, and Section 3.4 reports its contribution.

  5. Cost and the sequential setting. ORO's own computation is 6 to 7 minutes of GPU time per target (Appendix I), under 0.1% of the 233 hours that 2,800 five-minute CST simulations take. On resonance, ORO reaches TuRBO's final median error after about 1,250 calls, saving about 130 hours of simulation per target. The sequential experiment (Section 3.5) now starts from a task-agnostic Latin-hypercube warm-up and compares with all baselines over 30 targets: ORO has the lowest median on both benchmarks, 20× below TuRBO on resonance (28/30) and level with it on the pole–zero benchmark.

  6. Filter and related work. Section 3.6 defines the compliance criterion and adds a design from an explicit specification mask, repeated over four runs (Appendix C.5). Section 1 positions ORO against goal babbling, the distal-teacher formulation, PIED and conditional invertible networks.

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