acceptodds
Withdrawn from ICLR 2027

FluidTopoBench: A Benchmark for Learning-Based Fluid Topology Optimization

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Learning-based methods are increasingly used in fluid topology optimization to generate channel layouts, predict flow responses, and initialize numerical solvers. However, these capabilities are typically evaluated in isolation, making it difficult to assess how learned outputs translate into physical design quality and downstream optimization performance. We introduce FluidTopoBench, a benchmark of 40,500 steady two-dimensional incompressible Navier–Stokes–Brinkman problems spanning diverse channel layouts, flow regimes, and obstacle configurations. Each instance pairs operating conditions and the response of a uniform initial design with a binary reference topology, its finite-element response and dissipation, and numerical records for downstream evaluation. FluidTopoBench supports topology generation, response prediction, candidate selection, and warm-start optimization under a shared physical evaluation protocol. We evaluate six generators and six predictors using geometric, physical, and downstream metrics across multiple physical and geometric variants. Initial-response conditioning lowers mean dissipation error under unseen boundary layouts, while frozen response predictors provide useful signals for finite-element-verified candidate selection. Generated candidate sets can contain designs with lower dissipation than the numerical reference, and suitable initialization processing improves optimization endpoints. Finally, FluidTopoBench provides a unified framework for evaluating learned geometries and responses by their verified design and optimization outcomes.

Primary area:
datasets and benchmarks
Keywords:
Fluid topology optimization, scientific machine learning, generative design, neural operators, physics-aware evaluation

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.
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Paper summary

FluidTopoBench provides 40,500 two-dimensional steady Navier–Stokes–Brinkman design problems. It connects topology generation, flow-response prediction, candidate selection, and numerical warm-start optimization through shared finite-element evaluation. Six generators and six predictors are evaluated under changes in boundary conditions, obstacles, flow regimes, and resolution.

The paired dataset and downstream evaluation protocol are useful contributions. However, the evidence remains confined to a synthetic 2D numerical setting, and the practical significance of the downstream gains is not sufficiently established. The absence of validation beyond the shared Brinkman model, together with numerical sensitivity and incomplete end-to-end timing, leaves me unconvinced that the current benchmark provides sufficiently reliable guidance for practical fluid design. I therefore lean toward rejection.

Critical strengths
  1. The evaluation connects learning metrics to design outcomes. Geometric overlap and field reconstruction error do not necessarily reflect dissipation or candidate-selection quality. The shared physical evaluation and fixed candidate pools provide a useful way to distinguish generation failures from selection errors.

  2. The numerical validation is reasonably thorough within the chosen model. Multi-start comparisons, mesh refinement, an independently assembled finite-element formulation, and explicit accounting for failed downstream attempts strengthen the benchmark.

Critical weaknesses
  1. The practical relevance remains insufficiently validated. All instances are synthetic, two-dimensional steady-flow problems within a limited set of channel families. There are no 3D cases, measured flow data, or reported COMSOL/ANSYS comparisons. These omissions are not individually disqualifying, but together they leave the benchmark’s relevance beyond its numerical setting unclear. The independent finite-element check uses the same Brinkman model and therefore does not establish transfer to a distinct physical modeling approach or real devices.

  2. The demonstrated downstream benefits are modest or incompletely characterized. CNO increases default-band passing from 89.45% to 91.95% over maximum-volume selection. For initialization, simple global relaxation already captures much of the improvement, while several comparisons rely on small objective differences. Their reliability should be assessed against the numerical and material-model sensitivities reported in Appendix A.4. The reported solver-stage time reduction also excludes initial-response acquisition and generator inference, so a practical end-to-end speed advantage has not been established.

Questions for authors
  1. What evidence supports transferring the benchmark’s conclusions beyond the specified 2D Brinkman setting? An independent CFD validation using explicit solid boundaries would be particularly informative.

  2. Do candidate rankings and reference-improvement rates remain stable under mesh refinement and increased solid resistance, especially at the 0.1%–1% improvement thresholds?

  3. What is the complete runtime relative to cold-start optimization, including initial-response computation, generation, prediction, verification, and refinement?

  4. How much advantage does SP-CPR retain over global relaxation when both interfaces are tuned for the same endpoint-quality criterion?

3 comments

We thank the reviewer for recognizing that the evaluation links learning metrics to design outcomes and that the numerical validation is thorough. We ran a new experiment for each question. This comment answers the two validation questions (W1/Q1 and Q2); the second covers the size of the downstream gains (W2.1, Q4) and runtime (Q3).

W1 / Q1 — Evidence beyond the 2D Brinkman setting

We ran the requested independent CFD validation with explicit solid boundaries on 96 pre-registered problems across all six splits. The OpenFOAM finite-volume solver has no Brinkman term; meshes are built directly from each binary design, with only fluid pixels meshed (refined r×rr\times r, r=2,4,8r=2,4,8) and every fluid–solid face a no-slip wall.

Table C1. Benchmark decisions re-checked in explicit-wall CFD.

DecisionAgreement
Pairwise candidate order within pools432/448 (96.4%)
Best candidate of complete pools40/43 (93.0%)
≥0.1% / ≥1% reference improvements retained101/104 (97.1%) / 33/36 (91.7%)
Median abs. gain difference, CFD vs FE0.098 pp

The check changes the physical model (explicit walls vs Brinkman), the discretization (finite volume vs stabilized Q1Q_1–Q1Q_1 FE), and the mesh, while the unsmoothed pixel boundary keeps the geometry exactly fixed. It therefore tests precisely the requested transfer. The solver reproduces an analytical channel flow within 0.022% (velocity) and 0.12% (dissipation). Measured data and 3D devices remain outside the current scope; our claim concerns design decisions for the canonical 2D steady problem class, and it now holds beyond the Brinkman model.

In the revised manuscript, we present the explicit-wall CFD setup and per-split results in a new App. A.5 (Table 9) and summarize the cross-model transfer and scope in Secs. 3.2, 4.4 (Table 4b), and 5.

W2.2 / Q2 — Reliability of small differences under mesh refinement and solid resistance

Yes: candidate rankings and reference-improvement rates remain stable at the 0.1%–1% thresholds. Tenfold solid resistance shifts the reference objective itself by a median of 7.3%, but such shifts largely cancel between two designs compared under a common model, so paired decisions are robust.

Table C2. Share of FE-verified reference improvements retained after each change.

Change≥0.1% retained≥1% retainedMedian paired change
Grid 64×96 → 128×192266/270 (98.5%)120/121 (99.2%)0.026 pp
Solid resistance ×10259/270 (95.9%)119/121 (98.3%)0.129 pp
Explicit-wall CFD101/104 (97.1%)33/36 (91.7%)0.098 pp

The lower 95% bootstrap bound is at least 93.3% in every FE check. Rankings are equally stable: CFD preserves 96.4% of within-pool orderings (Table C1), and the gain changes by a median of only 0.0095 pp between the two finest CFD meshes. Typical numerical perturbations are thus well below the smallest margin used in the paper (0.1 pp).

We summarize decision retention across mesh refinement, solid resistance, and explicit-wall CFD in Sec. 4.4 (Table 4b), with bootstrap confidence intervals in App. A.4 and solver-level comparisons in App. A.5.

W2.1 — Magnitude of the selection gain

The +2.50 pp looks modest because the default band is nearly saturated: exhaustive FE screening of the same pools reaches only 92.56%, 3.1 pp above maximum volume. Against this attainable headroom, CNO recovers 80.3%, and where the headroom is larger, at strict reference-improvement targets, physical scoring adds more.

Table C3. Selection on the same 15,000 five-candidate pools (macro %; Scalar CNN is a new direct objective regressor, three seeds).

TargetMax. volumeScalar CNNCNOFE ceiling
Default band89.4591.15±0.0491.9592.56
≥0.1% better than reference24.2020.57±0.5425.0126.76
≥1% better than reference9.829.52±0.2311.4312.01
Conditional regret1.931.54±0.060.830

The gain is not trivial to obtain: the scalar regressor falls below maximum volume on reference improvement, while CNO exceeds both and reaches 95.2% of the FE ceiling at the 1% target. Its gain is positive in all nine tested quality bands (+0.52 to +3.91 pp). With a larger proposal budget, RF16+CNO beats the numerical reference by ≥0.1% in 59.2% of 3,750 problems.

We now quantify headroom recovery and include the Scalar CNN selector in Sec. 4.4 (Table 4a), with complete multi-threshold selection profiles in App. G (Tables 24–25).

W2.2 / Q4 — SP-CPR vs Global-relaxation under same-target tuning

With both interfaces tuned on 32 validation instances for the same endpoint target, SP-CPR keeps a clear advantage at the strict target: 31/96 vs 23/96, with 8 vs 0 exclusive successes. At the relaxed target the two are on par, as the paper reports.

Table C4. Same-target tuning on 96 test instances (strict: ≥0.1% better than matched cold start; relaxed: ≤0.1% excess).

InterfaceStrictRelaxed
Raw931
Projection-only1147
Global-relaxation2386
SP-CPR3185

This agrees with the large cohort (27,000 attempts per interface), where SP-CPR's strict-target gain over Global-relaxation is positive in all six splits (+3.6 to +8.1 pp, paired 95% intervals above zero). With a 100× tighter optimizer tolerance and 4× budget, the cold endpoint also improves and both interfaces reach 5/96; an interface's value is therefore defined at a fixed optimization budget, which the benchmark holds constant.

The revised paper summarizes the same-target tuning comparison in Sec. 4.5 and reports full results under both the original and strict optimizer settings in a new App. H.3 (Table 27).

W2.3 / Q3 — Complete runtime relative to cold-start optimization

We now time every stage and a fully serialized end-to-end run. The learned stages are cheap and the solver stage is roughly halved, but a serialized single-instance pipeline is not faster in wall clock than a cold start. SP-CPR contributes endpoint quality at a fixed budget, not end-to-end speedup, and the benchmark reports the two separately.

Table C5. Measured wall-clock cost (medians per instance).

StageCoverageCost
Initial-response acquisition483.19 s
Five RF candidates + CNO scoring482.98 s + 0.025 s
FE verification: selected only vs all five482.78 s vs 19.50 s
Optimizer: SP-CPR warm vs matched cold41 pairs38.3 s vs 76.9 s (0.52×)
Serialized pipeline vs cold-start process22 of 24145.5 s vs 87.2 s (1.59×)

At selection, 25 ms of physical scoring replaces FE verification of four of five candidates. The serialized run launches each stage as a fresh process with model loading and shared-GPU admission (1.42× without recorded queueing); 7 of its 24 endpoints are ≥0.1% better than cold start and 22 lie within 0.1%.

We have added the stage-wise and serialized runtime measurements in App. H.4 (Table 28) and explicitly state the scope of the warm-start runtime claim in Sec. 4.5.

I agree with the other reviewer's concern, and I don't think the paper should be published without any 3D validation. So, I adjust my score to 1

Reviewer_EinXOpenReview ↗
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Paper summary

The authors proposed FluidTopoBench, which contains over 40k 2D designs, and use it to benchmark four tasks in the topology optimization loop. I found the work has quite a large overlap with the paper “On the Generalization in Topology Optimization via Sensitivity-Conditioned Bernoulli Flow Matching” (ICML 2026), which also provides a benchmark test on very similar problems, and more importantly, provides a more insightful explanation of the conditioning mechanism that overrides this paper’s third contribution. As for the dataset and benchmark test itself, I also have concerns about the quality of the reference (see W2) and the lack of strong baselines.

Critical strengths

Method and results are well presented.

Critical weaknesses
  1. Overlapped contribution as an ICML 2026 paper and without citation to it. Given that the ICML 2026 paper already provides stronger guidance on selecting a conditioning signal, the paper's contribution is primarily limited to benchmarking.
  2. The reference results in the dataset are weak. (1) The paper didn’t provide the full parameter setup for the solver-based topology optimization. It didn’t provide either the intuitive optimization trajectories / final loss distributions / etc., that would help tell whether the reference results have converged. (2) The validation is not sufficient for fluid topology optimization. As reported in the paper, the validation was performed using the same Brinkman model but on a finer grid. To my understanding, the fluid-solid boundary captured by this model is much less accurate than the wall-fitted mesh simulation results. As a benchmark dataset aimed at downstream applications, I expect the author to perform at least one or two validations using a wall-fitted mesh regenerated from the optimal topology binary field and compare the results. (3) There are quite a few 2d topo opt networks that should've been benchmarked.
Questions for authors
  1. How do you compare your work with the ICML 2026 paper?
  2. I would recommend including optimization trajectories and wall-fitted mesh simulations to further validate the dataset.
3 comments

We thank the reviewer for the careful reading and for pointing us to SBFM. We added three studies: SBFM's TopoTransformer and other recent baselines with three seeds, an independent explicit-wall CFD validation, and a strict re-optimization of the references. This comment answers the relation to SBFM and the wall-fitted validation; the second covers reference convergence and baselines.

W1 / Q1 — Relation to the ICML 2026 SBFM paper

We now cite, discuss, and benchmark SBFM. The two works are complementary. SBFM is a method paper: it proposes a generator and explains why sensitivity-like fields are effective conditioning signals. FluidTopoBench is a benchmark: it scores generation, response prediction, candidate selection, and warm-start optimization by FE-verified design outcomes. Conditioning is only one of its findings; the others lie outside SBFM's scope.

Table A1. Findings that require the benchmark's paired protocol.

FindingKey result
Field accuracy ≠ objective accuracy (7 predictors × 3 seeds)Test ranking disagreement EuE_u–EJE_J 35.9±2.1% vs EuE_u–ηρ\eta_\rho 9.6±0.8%
Equal geometry ≠ equal physics (edits matched in volume and IoU)Cross-stream +1.26 pp vs two-site −0.84 pp (95% CIs exclude 0)
Physical scoring adds selection value≥0.1% reference improvement: CNO 25.0% vs scalar regressor 20.6%
Generation + selection beats the optimizerRF16+CNO beats the reference by ≥0.1% in 59.2% of 3,750 problems
Initialization changes the optimizer endpointStrict-improvement rate: SP-CPR 32.1% vs Raw 13.5%

The first finding has an explicit mechanism, now Eq. (7). With residual r=u^−u\mathbf r=\widehat{\mathbf u}-\mathbf u and Φ(v)=12aρ,h(v,v)\Phi(\mathbf v)=\tfrac12 a_{\rho,h}(\mathbf v,\mathbf v),

Φ(u^)−Φ(u)Φ(u)=ηρ2+2 aρ,h(u,r)aρ,h(u,u),\frac{\Phi(\widehat{\mathbf u})-\Phi(\mathbf u)}{\Phi(\mathbf u)}=\eta_\rho^2+\frac{2\,a_{\rho,h}(\mathbf u,\mathbf r)}{a_{\rho,h}(\mathbf u,\mathbf u)},

so the objective error depends on the residual's signed alignment with the true flow, not only on its size.

On conditioning, our initial response is the forward flow of the uniform design and needs no adjoint solve; its velocity-magnitude channel is a forward analogue of SBFM's pseudo-sensitivities. It lowers OOD-BC mean DPE for all six generator families (paired 95% intervals above zero, +8.7 to +80.5 pp), which we now present as cross-architecture evidence consistent with SBFM. Benchmarked under the same interface, TopoTransformer matches RF on Test but has nearly twice its OOD-BC DPE (W2-(3)).

In the revised manuscript, we discuss SBFM in Sec. 2, frame initial-response conditioning alongside it in Secs. 1 and 4.2, formalize the dissipation-error decomposition as Eq. (7) in Sec. 4.3, and report the TopoTransformer baseline in Table 3 and Apps. B.1 and D.

W2-(2) / Q2 — Validation with explicit-wall CFD

We ran this validation on 96 pre-registered problems across all six splits, with an independent OpenFOAM finite-volume solver and no Brinkman term. Meshes are built directly from each binary design: only fluid pixels are meshed (refined r×rr\times r, r=2,4,8r=2,4,8), and every fluid–solid face is a no-slip wall. The pixel boundary is kept unsmoothed, so the scored geometry is fixed and only the treatment of the solid changes.

Table A2. Benchmark decisions re-checked in explicit-wall CFD.

DecisionAgreement
Pairwise candidate order within pools432/448 (96.4%)
Best candidate of complete pools40/43 (93.0%)
≥0.1% / ≥1% reference improvements retained101/104 (97.1%) / 33/36 (91.7%)
Median abs. gain difference, CFD vs FE0.098 pp

Every benchmark comparison is a relative judgment between designs under one model, and these judgments transfer; the typical deviation is below our smallest margin (0.1%). The solver reproduces an analytical channel flow within 0.022% (velocity) and 0.12% (dissipation).

We detail the explicit-wall CFD setup and per-split results in a new App. A.5 (Table 9) and summarize the cross-solver transfer in Secs. 3.2, 4.4 (Table 4b), and 5.

W2-(1) / Q2 — Reference convergence and solver setup

The references are converged with respect to the optimizer. The full configuration is now in App. A.2 (Table 5, Eq. 14): four-stage qαq_\alpha continuation; optimality-criteria updates with move limit 0.2 and damping 1/3; stopping at relative objective change ≤ 10−310^{-3} for 5 updates or 50 updates per stage; Newton residual 10−610^{-6}; no filters. Beyond trajectories, which show only where an optimizer stops, we tested directly whether further optimization still pays off:

Table A3. Convergence and competitiveness of the references.

CheckCoverageResult
Strict replay: tolerance 10−3→10−510^{-3}\to10^{-5}, 4× budget87 verified pairsMedian extra reduction 0.20%; 86.2% ≤ 1%
Five-start competition at matched volume4,150 problemsMedian extra reduction 0.028%; 93.4% ≤ 1%
Replay of the original protocol96/960 mismatched pixels
Residual of stored FE states40,500/40,500All < 10−610^{-6}

A 100× tighter tolerance costs 3.7× more optimization time for a 0.20% median gain, so the original rule already operates at diminishing returns, and the references reproduce exactly from the released protocol.

We now document the complete reference-optimizer configuration in App. A.2 (Eq. 14 and Table 5) and report the strict-tolerance and exact-replay checks in App. A.4 (Table 7).

W2-(3) — Additional 2D topology-optimization networks

The suite already covers the main 2D TO families: CNN/U-Net, conditional GAN (cf. TopologyGAN), diffusion (DDPM, EDM, PhysToken; cf. TopoDiff), and flow matching (RF). We added the latest model for each learned task, trained with three seeds on all six splits: TopoTransformer (SBFM, ICML 2026) for generation and PDE-Transformer (ICML 2025) for prediction.

Table A4. Three-seed generation on a common cohort (DPE and VFE in %; P95 over instances).

GeneratorTest DPETest IoUOOD-BC DPEOOD-BC VFEOOD-BC P95 DPE
CNN1.10±0.780.9612.51±0.271.44±0.1211.3±0.6
RF0.66±0.710.9511.86±0.371.29±0.178.6±1.5
TopoTransformer0.66±0.500.9513.56±0.953.22±0.2421.2±2.6

RF and TopoTransformer match on Test DPE and IoU, yet separate clearly under unseen boundaries. Likewise, PDE-Transformer has the best Test velocity error (0.0121±0.0002), while CNO stays best on all OOD-BC metrics. TopoTransformer keeps its official architecture and training recipe but uses RF's seven-channel conditioning, so this is a controlled comparison, not a verdict on SBFM with its own sensitivity inputs. We would be glad to add networks the reviewer suggests.

The revised paper integrates the three-seed TopoTransformer and PDE-Transformer results in Secs. 4.1–4.3 (Table 3), records their architectures and training schedules in Apps. B.1–B.2 (Tables 11–12), and provides split-wise evaluations in App. D (Table 16) and App. F.1 (Tables 21–22).

I thank the authors for their response to my comments and for their efforts to clarify the paper’s goal and provide more evidence. However, I would prefer to keep my current score (=1) for the reasons below:

  1. Although the authors proposed 5 new findings from their benchmark test, I found that most of them are either common knowledge (e.g., Field accuracy ≠ objective accuracy) or too case-dependent. It looks more like a broad summary than in-depth research on maybe one or two issues that would bring new insight to the community.
  2. As a benchmark dataset paper, I still didn’t find enough evidence to persuade me of the dataset’s quality. The authors added an explicit wall simulation, but it’s still a Cartesian grid and I actually asked for a “wall-fitted” simulation. As far as I know, fluid simulation is highly sensitive to boundary treatment, and a jagged boundary, especially at this low resolution, would be inaccurate. In addition, a 2D dataset is not particularly valuable, as other reviewers have noted.
  3. The benchmarking baseline models are still limited.
Reviewer_H9VvOpenReview ↗
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Paper summary

The paper introduces a new benchmark for 4 tasks in ML for Fluid Dynamics: Topology, Response, Selection and Refinement. It consists of 40k 2D instances, including a dedicated OOD split and evaluates a range of learning based fluid dynamics methods empirically under the proposed protocol.

Critical strengths
  • The proposed task selection and evaluation procedures are sound
  • The dataset contains an explicit OOD split across multiple categories, including topologies never seen during training
  • the paper evaluates the tasks on a wide range of (physical) metrics
Critical weaknesses
  • Amonst the compared baselines there are few recently proposed methods (most recent one from 2024), which makes it hard to assess the quality of the benchmark to precisely assess and advance progress of the field. This missing context makes it hard to justify what advances can be measured with the proposed new benchmark and is my main concern.
  • It would be good to include additional non learning based baselines (or simple ml predictors for ie selection), to put the advantages and progress of learning-based methods into proper context. This might require an additional quality/speed/resource tradeoff analysis
  • models are only evaluated under a single seed setting, there is little discussion on the training and inference compute requirements
  • scope is limited to 2D fluid dynamics
Questions for authors

See mostly weaknesses.

Additionally, how were important hyperparameters determined for the trained models?

2 comments

We thank the reviewer for finding the task selection and evaluation procedures sound. We added recent baselines, three training seeds, a simple learned selector, and stage-wise costs. This comment answers the main concern (recent baselines) and seeds; the second covers simple baselines, hyperparameters, and scope.

W1 — Recent baselines and what advances the benchmark can measure

We added the latest model for each learned task, both trained with three seeds on all six splits: TopoTransformer (ICML 2026) for generation and PDE-Transformer (ICML 2025) for prediction. Their results show what FluidTopoBench measures: progress under physical shift, and in physical rather than geometric quality.

Table B1. Three-seed generation on a common cohort (DPE in %; P95 over instances).

GeneratorTest DPETest IoUOOD-BC DPEOOD-BC P95 DPE
CNN1.10±0.780.9612.51±0.2711.3±0.6
RF0.66±0.710.9511.86±0.378.6±1.5
TopoTransformer0.66±0.500.9513.56±0.9521.2±2.6

Table B2. Predictor with the lowest three-seed mean error on each split.

SplitEuE_uηρ\eta_\rhoEJE_J
TestPDE-TransformerPDE-TransformerPINO
OOD-BCCNOCNOCNO
Low-ReU-FNOU-FNOPINO
Dual / LargeCNOPDE-TransformerCNO
NotchPDE-TransformerPDE-TransformerPDE-Transformer

The benchmark resolves three kinds of progress:

  • Generation under shift: TopoTransformer matches RF on Test DPE and IoU, yet on unseen boundaries its mean DPE is nearly twice RF's and its P95 tail about 2.5×.
  • Prediction under shift: PDE-Transformer is most accurate in distribution, but CNO leads every metric under boundary shift.
  • Objective-level accuracy: velocity-error and objective-error rankings disagree on 35.9±2.1% of Test predictor pairs (vs 9.6±0.8% for velocity vs energy norm), because the objective error contains a signed cross term (Eq. 7). Field accuracy alone does not certify a predictor for design use.

No single model dominates, leaving measurable room for new methods.

In the revised manuscript, we present the new baselines and the dissipation-error decomposition in Secs. 4.1–4.3 (Table 3 and Eq. 7), document model configurations in Apps. B.1–B.2 (Tables 11–12), and report full split-wise results in App. D (Table 16) and App. F.1 (Tables 21–22).

W3 — Training seeds and compute

CNN, RF, TopoTransformer, and all seven predictors now use three seeds (30 runs, plus 3 Scalar CNN selectors), with near-complete coverage (123,720/123,750 generation FE analyses; 78,750/78,750 reference predictions). Seed SDs are far below the reported effects: OOD-BC DPE for RF vs TopoTransformer is 1.86±0.37% vs 3.56±0.95%, and ≥0.1% reference improvement for CNO vs Scalar CNN is 25.0% vs 20.6±0.5%.

Training budgets for every model are listed in App. B. At inference, a predictor forward pass takes 2.2–4.6 ms per geometry, five RF samples about 3 s, and one FE verification about 3 s.

We now report three-seed means and standard deviations in Table 3 and Tables 16 and 21–22, relate seed variability to instance-bootstrap intervals in App. C.2, and summarize training budgets and inference timings in App. B (Tables 10–12).

W2 — Non-learning and simple baselines; quality–speed trade-off

Each stage now has a non-learning anchor: the numerical optimizer for generation, the maximum-volume rule and exhaustive FE screening for selection, and cold start for initialization. We also added the simple ML selector the reviewer suggested: a Scalar CNN that regresses the objective directly (three seeds).

Table B3. Selection on the same 15,000 five-candidate pools (macro %).

SelectorDefault band≥0.1% better than ref.≥1% better than ref.Regret
Maximum volume89.4524.209.821.93
Scalar CNN91.15±0.0420.57±0.549.52±0.231.54±0.06
CNO (full-field)91.9525.0111.430.83
FE screening (all 5)92.5626.7612.010

The scalar regressor helps on the default band but falls below the volume rule at strict targets, while full-field CNO exceeds both: the value comes from field-level physical scoring. On quality vs speed (medians, 48 instances):

  • Selection: CNO scores five candidates in 25 ms, so only one needs FE (2.78 s vs 19.50 s), while recovering 80.3% of the FE-screening headroom.
  • Generation vs optimizer: 16 RF proposals with CNO selection beat the reference by ≥0.1% in 59.2% of 3,750 problems.
  • Refinement: warm starts halve solver time (0.52×), but a serialized single-instance pipeline is not faster in wall clock, so the benchmark reports quality and cost separately.

We have added the Scalar CNN baseline and headroom analysis in Sec. 4.4 (Table 4a) and App. G (Tables 24–25), together with the stage-wise and serialized runtime breakdown in App. H.4 (Table 28).

Q1 — How were important hyperparameters determined?

All settings were fixed in advance or selected on validation data; test-set FE results were never used for tuning or checkpoint selection.

Table B4. Hyperparameter protocol.

ComponentProtocolSelection
Six original generatorsComparable capacity (shared U-Net, 138.5–156.9M parameters); aligned exposure (diffusion/flow: 200 epochs, 50k updates, batch 128); AdamW, lr 10−410^{-4}Own validation objective
PredictorsFixed architecture-specific recipes (mostly lr 5×10−45\times10^{-4}, 300–400 epochs); PDE-Transformer: official PDE-S, 33.2M parametersValidation relative-L2L_2 error
TopoTransformerOfficial recipe (34.3M parameters, 151 epochs, batch 256); shared data and conditioningValidation loss
Scalar CNNTrain-only normalizationValidation loss
Initialization interfacesTuned on 32 validation instances, then frozenSame endpoint target

Matching capacity and exposure makes comparisons reflect the generative formulation and conditioning rather than tuning effort.

The revised paper details the generator capacity-and-exposure protocol and TopoTransformer setup in App. B.1, the predictor schedules in App. B.2 (Table 12), and the validation-based interface tuning in App. H.3.

W4 — Scope limited to 2D

The 2D steady setting is deliberate. It is the canonical problem class in fluid TO, and it lets all 40,500 instances carry an optimization record, FE-verified targets, and downstream multi-start and warm-start evaluations. The conclusions are also not tied to our numerical model: on 96 pre-registered problems, an independent OpenFOAM solver with explicit no-slip walls preserves the benchmark's decisions.

Table B5. Benchmark decisions re-checked in explicit-wall CFD.

DecisionAgreement
Pairwise candidate order within pools432/448 (96.4%)
Best candidate of complete pools40/43 (93.0%)
≥0.1% reference improvements retained101/104 (97.1%)

The protocol (paired physical records, fixed candidate pools, joint completion–quality rates) is dimension-independent and provides a template for 3D extensions.

We report the explicit-wall CFD validation in a new App. A.5 (Table 9) and clarify the 2D scope alongside directions for 3D, unsteady, and experimentally measured extensions in Sec. 5.

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

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