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Under review as a conference paper at ICLR 2027

FLOATBench: A Tabular Dataset and Benchmark for Fatigue Prediction on Floating Offshore Wind Turbine Towers

Abstract

Tabular surrogates are commonly ranked on random validation splits. Yet a surrogate is used to predict wherever no simulation exists, both between training points (interpolation) and beyond the training domain (extrapolation), and random splits cannot tell the two apart, so the selected model may fail where it extrapolates. We introduce FLOATBench, a tabular dataset and benchmark for fatigue prediction on floating offshore wind turbine towers that tests whether model selection stays valid as predictions move from interpolation to extrapolation. It provides 582,120 per-section fatigue-damage labels from 19,404 OpenFAST simulations of three 22 MW tower geometries over 1,078 wind–wave operating conditions. FLOATBench is distinguished by a regime-aware partition that places each test point relative to the training domain as in-train, interpolation, or extrapolation, so extrapolation depth is controlled by construction, and by cross-tower transfer with condition-level bootstrap intervals. Across 735 trained surrogates and seven standalone baselines on three towers, the global rank-1 model falls to ranks 23, 11, and 11 in joint wind-and-wave extrapolation, where a network ranked 69th–79th globally wins (a rank reversal), and validation-based selection leaves 1.5–1.9× the best available extrapolation error. In cross-tower transfer, the relative L2 error is 0.067–0.098 when the reference tower is in training versus 0.423 when it is held out. The rank reversal holds across all 15 tested partition settings and after retraining on two alternative training grids (REF). Limitations: one 22 MW design family and aligned power-production conditions. Resources: dataset and code at https://anonymous.4open.science/w/FLOATBench-115C/index.html.

Primary area:
datasets and benchmarks
Keywords:
benchmark dataset, extrapolation, model selection, tabular regression, surrogate modeling, scientific machine learning, floating offshore wind turbine, structural fatigue

Reviews

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1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_HLG2OpenReview ↗
Rating
1
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4
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1
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Paper summary

This work presents a benchmark dataset for wind turbine tower fatigue prediction, the FLOATBench, and applied a number of machine learning based methods, such as trees based and neural network based, to conduct modeling and perform the prediction. Numerical results are reported.

Critical strengths

I have critical concerns rather than seeing strength regarding this work.

Critical weaknesses

The critical weakness is that the dataset is generated from a simulation software rather than field data collected by various sensors mounted on a real 22-MW wind turbine. If it is a field dataset, I would do a full support. However, we do know the issues of the simulated dataset and its value is limited on conducting data-driven modeling. I have seen people repeating this error for decades. The simulated software in its nature is a set of mathematical equations, e.g., PDEs. Hence, machine learning methods applied into modeling based on such data are eventually approximating this set of math equations rather than the true dynamics of a wind turbine. The only benefit is that you might leverage the surrogate models to speed up the simulation experiments by OpenFAST and other tools, such as Blades.

Questions for authors

I have no questions for authors. I only concern the value of such a dataset and its benchmarking results in the real wind turbine tower fatigue modeling.

6 comments
AuthorsOpenReview ↗

Physical Validation, Real-World Relevance, and Benchmark Value

We thank the reviewer for finding the paper clear and easy to follow. We agree that engineering datasets should be grounded in real measurements. We'd like to clarify that FLOATBench already reflects this principle: our inputs are drawn from a real site, as outlined in Sec. 3. However, fatigue data isn't feasible because no such site has ever been constructed. The purpose of this data is to support design decisions, not to reflect maintenance conditions.

Assessing fatigue for a single tower requires thousands of simulations, which limits how many candidate designs engineers can evaluate. Reliable ML surrogates could reduce this cost, and FLOATBench tests whether they stay reliable under unseen conditions. We address the concern in seven points: where the data come from and why simulation is needed (1-3), how OpenFAST has been validated (4), what the benchmark adds (5-6), and where field data fit (7).

1. The inputs come from a real site. The wind and wave conditions come from 22 years of ERA5 data west of the Isle of Barra (Papi et al., 2022): 1,078 conditions with 6 seeds each, following DLC 1.2 and DNV-RP-C203.

2. No public field data exist for floating towers at this scale. To our knowledge, no field measurements of a floating turbine tower of 20 MW or more are publicly available. Data from smaller floating turbines cannot simply be scaled to 22 MW: geometry, natural frequencies, loading and platform dynamics change the fatigue response. Field data also cover few sensors and only the conditions experienced, and need calibration.

3. Real turbines are designed with simulations. Fatigue must be assessed before a turbine is built (IEC TS 61400-3-2). Loads are measured later, on a prototype (IEC 61400-13): measurements validate the simulator; simulations design what does not yet exist.

4. OpenFAST has been checked against measurements: Hywind Demo (Driscoll et al., 2016), alpha ventus (Popko et al., 2021) and TetraSpar, where an OpenFAST digital twin estimated tower fatigue DELs with errors of 10–15% on average (Branlard et al., 2024). Known limits are documented as well: in scale-model wave-tank tests, tower loads are somewhat underestimated (Robertson et al., 2017), mainly through low-frequency hydrodynamic loads (Robertson et al., 2020), and no validation exists yet at 22 MW.

5. Speed is not the only benefit. A faster surrogate helps only if it can be trusted. Random validation selects a model with 1.4–1.6× the extrapolation error of the best network. With it, 38–59% of the joint-extrapolation damage lies in predictions more than 10% too low, against 6–19% with the network, so a design could look safer than its simulation reference.

6. It also serves ML research. 582,120 section-resolved labels and 735 fitted models give a testbed for building tabular models, including foundation models such as TabPFN, that extrapolate reliably; physics data are rare in tabular benchmarks (at most 3 of 51 TabArena datasets). The global rank-1 model falls to ranks 21/11/13 under joint extrapolation, while a network ranked 69th–79th becomes the best, across grids, partitions and five seeds, and TabPFN-2.5 does not beat it. PDEBench and The Well are similar simulation-based testbeds.

7. Field data would extend, not invalidate, the benchmark. Measurements from a large floating turbine could be added as a test set with the same inputs (wind and wave conditions) and labels (damage at gauge heights). Models trained on FLOATBench could then be tested and fine-tuned on real data, measuring the simulation-to-reality gap, and the regime partition would show which measured conditions fall outside the simulated envelope.

In summary, FLOATBench serves the design stage, where fatigue is assessed with simulations before a turbine is built. Its inputs come from a real site, and no public fatigue measurements exist for a floating turbine of this size. FLOATBench provides a public dataset and a reproducible benchmark for developing reliable surrogates that support these design decisions, and for ML generalization research. We thank the reviewer for raising this concern, and we hope these clarifications and revisions warrant a reconsideration of the overall assessment.

References (added to the revised paper):

  • Driscoll et al. (2016), Hywind Demo, Energy Procedia 94. doi:10.1016/j.egypro.2016.09.181
  • Popko et al. (2021), alpha ventus, J. Offshore Mech. Arct. Eng. 143. doi:10.1115/1.4047378
  • Branlard et al. (2024), TetraSpar digital twin, Wind Energy Science 9. doi:10.5194/wes-9-1-2024
  • Robertson et al. (2017), OC5 Phase II, Energy Procedia 137. doi:10.1016/j.egypro.2017.10.333
  • Robertson et al. (2020), OC6 Phase I, J. Phys. Conf. Ser. 1618. doi:10.1088/1742-6596/1618/3/032033
  • Papi et al. (2022), met-ocean conditions, J. Phys. Conf. Ser. 2385. doi:10.1088/1742-6596/2385/1/012117
Reviewer_HLG2OpenReview ↗

Response to authors' feedback

Thank you very much for the constructive feedback.

Please allow me to again present my stand. I agree with you that maybe, so far, so publicly accessible wind turbine datasets for evaluating latest 20MW above offshore wind turbine tower fatigue. Yet, this does not address the critical point that the presented dataset value is not as meaningful as imagined by you to people who worked on wind turbine system modeling with data-driven methods. The core issue have been clearly explained in my previous points, data generated from simulators are distant from reality and people who use these simulated data can only obtain a surrogate of the equations behind the simulator. Therefore, if a score collaborated with a wind turbine design and research laboratory, once get the inputs, can generate simulated data very well. However, the real tower fatigue of offshore wind turbine in reality can be much more than that. And the data-driven models obtained based on such a dataset cannot draw more reliable conclusions beyond the simulator can tell. Then, the scientific aspect value of the dataset become very slim. Studies based on this dataset will be rejected by journals as editors will ask why not directly work with simulation tools?

Meanwhile, as a scholar who has worked in this field for a long while, I can tell you that I have visited the real laboratory for offshore wind turbines with capacity higher than 20 MW. People have installed sample machines for degradation studies and fatigue studies with collecting real data. They also have testing facilities to accelerate the fatigue testing of the tower under different conditions. I hence encourage authors to reach out more and explore more. One primary assumption that engineering field can accept the data-driven study is that we believe data serve as the digital copy of the real world and data-driven methods help us approximate this real world dynamics or other complicated relations that classical explicit math expressions cannot do. Yet, if you report only the simulated data, this principle got violated. Meanwhile, I use simulators can explore much more design or operating scenarios that this dataset can tell.

Hope my feedback can further help authors in the future identify and report real and more valuable dataset and benchmarking studies.

AuthorsOpenReview ↗

Physical Grounding and the Scientific Value of FLOATBench

FLOATBench is grounded in real offshore operating conditions and established wind-turbine engineering practice. Its wind–wave operating envelope is informed by 22 years of ERA5 reanalysis for a real offshore site; its labels are generated through OpenFAST, which has undergone experimental validation in other turbine configurations; and its fatigue assessment follows established engineering procedures. We therefore disagree with the characterization that the data’s simulated origin makes it detached from reality or scientifically uninformative.

The research question arises directly from this engineering workflow: when expensive simulations are approximated by ML surrogates, do their predictions remain accurate under unseen operating conditions, and can standard validation identify the models that do so? FLOATBench demonstrates that strong aggregate performance can conceal substantial extrapolation errors and misleading model rankings. Knowing the simulator’s equations does not determine these properties of the learning algorithms.

Where matching field measurements are not publicly accessible, why should their availability be a prerequisite for publishing reproducible evidence of these ML failures? A physically grounded, openly available simulation benchmark enables the community to investigate them now.

The simulator can certainly generate further scenarios. Releasing a common dataset and controlled evaluation protocol allows researchers to compare methods without independently repeating an expensive simulation campaign. This is the contribution of a shared benchmark.

Experimental measurements would complement this work by enabling direct validation of the particular 22 MW configuration. That additional validation question does not negate the dataset’s existing physical grounding or the relevance of the surrogate-learning failures it reveals. We will acknowledge this in the paper. We ask that the submission be assessed on those contributions and its explicitly stated scope.

Reviewer_3D6QOpenReview ↗
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3
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Informativeness
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Paper summary

This is a dataset and benchmark paper. The authors release approximately 582,000 section-level fatigue-damage labels from 19,400 OpenFAST simulations of three 22 MW floating tower geometries: the IEA-22 reference tower (REF) and two fatigue-aware redesigns (OPT1 and OPT2). The simulations cover a 22 × 7 × 7 wind–wave grid, with six seeds and 30 tower sections.

The main contribution is the evaluation protocol rather than the dataset size alone. An alpha-shape partition classifies test points as in-train, interpolation, or extrapolation in the wind and wave subspaces. The benchmark also includes leave-one-tower-out transfer. Its central finding is a rank reversal: strong aggregate performance does not imply strong performance in the joint extrapolation cell, EX_EX. In-distribution validation fails to identify the best extrapolator, leaving approximately 1.5–1.9 times the best available EX_EX error.

Critical strengths

The paper provides a substantial and costly engineering artifact. To my knowledge, there is no comparable public 22 MW floating-tower fatigue dataset with section-resolved labels. Table 1 makes a convincing case for the gap relative to existing releases.

The documentation and reproducibility provisions are strong: dataset and code licenses, a datasheet, condition-level bootstrap analysis, metadata provisions, and a 147-simulation raw audit subset that reportedly reproduces the labels to machine precision. These are useful components of a benchmark release.

The central message—that random splits can hide extrapolation failures and produce misleading deployment rankings—is demonstrated carefully. Appendix H is particularly strong. Its partition sensitivity tests, alternative training grids, extrapolation-depth analysis, and degenerate-alpha check substantially address the concern that the result is an artifact of one partition.

The standalone baselines in Appendix I are useful. Including response surfaces, polynomial chaos, Gaussian processes, TabPFN, and constrained XGBoost helps establish that the observed trade-off is not specific to AutoGluon.

Critical weaknesses

The scope is narrow, as the authors acknowledge. All three towers belong to one design family, so cross-tower transfer remains within-family transfer. The difficult held-out-reference result shows that transfer to the dynamically distinct reference geometry is challenging, but there is only one such case. Combined with the restriction to aligned wind–wave conditions under DLC 1.2, this means the benchmark’s broader value rests mainly on operating-envelope generalization rather than geometric diversity.

The task is low-dimensional. The nominal operating grid has three coordinates, with realized wind statistics and local geometry descriptors supplying the model inputs. More importantly, the results show that wind extrapolation drives most of the deterioration, while wave extrapolation contributes comparatively little. The joint wind–wave framing should make this imbalance more explicit.

The emphasis on “735 trained surrogates” overstates the breadth of the modeling study. Most entries are AutoGluon portfolio configurations trained under fixed time budgets, rather than separately designed approaches. The paper should distinguish the number of fitted configurations from the number of substantively different modeling approaches.

Similarly, the 582,000 labels should not be read as independent observations. The count includes strongly dependent sections within simulations and repeated realizations of the same operating conditions. Reporting the count is appropriate, but the framing should consistently distinguish labels, simulations, and operating states.

The central ML finding is useful but largely confirmatory. Trees’ restricted extrapolation behavior, the limitations of random-split evaluation, and the difficulty of selecting models for distribution shift are established concerns, which the paper itself acknowledges. The contribution is making these effects measurable in this engineering domain, rather than discovering a new general phenomenon.

The study diagnoses a practical problem without providing a reliable selection strategy. The best extrapolators belong to a variable neural-network family whose weakest members also extrapolate poorly, and none of the tested selection rules reliably identifies the good configurations. This is an honest and useful benchmark outcome, but it limits the immediate guidance available to practitioners.

Some ranking statements need stronger qualification. The reference-tower aggregate winner is statistically tied with the runner-up, and many adjacent aggregate rankings overlap. The substantial EX_EX rank changes remain interesting, but statements such as “falls to rank 23” should be interpreted alongside uncertainty in the relevant performance differences.

Questions for authors

How sensitive is the rank reversal to the cube-root damage target? Would the conclusion persist if models were trained on raw damage or log-damage?

Have you tested uncertainty-based model-selection rules, such as ensemble disagreement or predictive uncertainty, rather than validation scores and diagnostic cell-based selection alone? Testing an explicitly defined rule would strengthen the discussion of the remaining selection problem.

Given that wind extrapolation drives most of the error, how much additional diagnostic value does the joint wind–wave stratification provide over wind-only stratification?

How many of the 735 fitted configurations represent substantively different predictors, and how many are closely related portfolio variants or ensembles?

1 comment
AuthorsOpenReview ↗

Target Sensitivity, Model Selection, and Benchmark Scope

We thank the reviewer for recognizing a dataset with no public equivalent, strong reproducibility and a carefully demonstrated reversal.

In brief, the reversal persists under log and raw targets, uncertainty-based selection does not close the gap, wind drives the result, and the 735 models come from 54 base configurations.

Q1. Target transform: the reversal persists under all three targets (cube root, log and raw damage). On each tower we retrained only the network and the ensemble's three members on log and raw damage and refit the ensemble weights, with the configurations chosen on the cube-root target. With every target and tower, the ensemble still wins overall and the network at EX_EX (EX_EX Rel L2, network / ensemble; Table 22):

TargetREFOPT1OPT2
Cube root0.054 / 0.0870.069 / 0.1070.065 / 0.110
Log damage0.058 / 0.0900.072 / 0.1040.076 / 0.107
Raw damage0.088 / 0.0950.103 / 0.1210.111 / 0.122

The gap narrows with log and raw damage. The cube root matches engineering practice: it is proportional to the damage-equivalent load. (Changed in the paper: Appendix H.7.)

Q2. Uncertainty-based selection: we tested both rules, and both pick worse models than validation. Both rules use only test-condition predictions, never the simulated damage. Ensemble disagreement picks the model closest to the pool's median prediction. Predictive uncertainty picks the model whose 8 fold-trained versions agree most at EX_EX. EX_EX error of the chosen model over the best (Table 28):

RuleREFOPT1OPT2
Validation1.611.561.69
Validation, 5-seed mean1.401.531.64
Ensemble disagreement1.731.751.99
Predictive uncertainty1.761.751.99

Agreement is no guide: models whose versions disagree more extrapolate better (Spearman -0.17 to -0.42). (Changed in the paper: Appendix J.3.)

Q3 / W2. Joint vs wind-only stratification: a little; wind-only already shows the reversal, and the joint cell has the highest error. Where the wind extrapolates, whatever the waves, the validation-selected ensemble already loses rank 1. When the waves also extrapolate, the ensemble's error rises only slightly (2-6%), so we keep EX_EX, the highest-error cell, as the main cell. Ensemble on REF / OPT1 / OPT2 (Table 30; standardized partition; rank 23 / 11 / 11 before):

CellRankError over the best
Wind EX, any wave22 / 10 / 121.63 / 1.53 / 1.62
EX_EX21 / 11 / 131.61 / 1.56 / 1.69

(Changed in the paper: Sec. 5.2, Appendix K.4.)

Q4 / W3. Distinct models: 54 of the 735, in 8 families; the rest are retrainings and combinations of them. We trained one AutoGluon portfolio 9 times: per tower in E1 and E2, per fold in E3 (Table 10).

XGBLGBMCBNN-FNN-TTabMETRFWETotal
Models751541571028951473327735
Distinct configurations6111286632-54

(Changed in the paper: abstract; Appendix F.4.)

W4. Dependent labels: yes, so the confidence intervals resample operating conditions, not labels. The 582,120 labels come from 19,404 simulations of 30 sections each, and each tower has 1,078 operating conditions with 6 seeds. Sections of a simulation and seeds of a condition are strongly related. (Sec. 3 now marks rows as dependent.)

W7. Ranking statements: now qualified, and the swap holds despite the ties. In the overall ranking (Table 13), the top five on REF are statistically tied, while on OPT1 and OPT2 the ensemble is significantly first (Appendix G.4, Table 15). At EX_EX, instead of a single rank, we count the models significantly better: at least 11 for each of the five tied REF leaders, 7 for the ensemble on OPT1 and 10 on OPT2 (Table 13 caption). Whichever tied model is called rank 1, the swap holds.

W1, W5, W6. Scope follows the design task; the dataset and the measured cost are new; the guidance is to report EX_EX. W1 (one family): we focus on new operating conditions, the design task: a tower's surrogate learns from some simulated conditions and must predict the rest. The partition needs only the inputs, so the benchmark can grow to new families and load cases; DLC 1.2 usually dominates tower fatigue (Sec. 6). W5 (known effects): what is new is the dataset and the measured cost of these effects: the validation-selected model leaves 38-59% of the EX_EX damage in predictions over 10% too low (6-19% for the network; Table 32). W6 (no selection rule): network results vary widely, so the advice is not "use networks" but "do not trust the global rank".

Summary. The gap holds across targets and comes from wind extrapolation; label-free selection rules do not close it, so model selection is the open challenge of the benchmark. We hope these answers support a reconsideration of your overall assessment.

Reviewer_oCQCOpenReview ↗
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Paper summary

This paper introduces FLOATBench, a dataset and benchmark for fatigue prediction on floating offshore wind turbine towers. The dataset contains 582,120 section-level damage labels derived from OpenFAST simulations across three tower geometries, 1,078 operating conditions, and six turbulence seeds. The benchmark distinguishes interpolation from extrapolation in wind and wave subspaces and evaluates both within-tower prediction and cross-tower transfer. Its main empirical finding is that models with the best aggregate performance can be substantially worse in extrapolation regions, while conventional validation-based selection fails to identify the strongest extrapolators.

Critical strengths

The paper addresses a meaningful problem in scientific machine learning. High simulation costs make surrogate modeling useful, and evaluating performance near and beyond the sampled operating envelope is practically relevant. The combination of matched operating conditions, multiple geometries, and section-level fatigue labels gives the dataset clear potential value. The empirical evaluation is reasonably extensive. Beyond the AutoGluon model portfolios, the paper includes standalone modern and classical baselines, partition-sensitivity analyses, retraining on alternative grids, and a condition-grouped random-split control. These experiments address several plausible alternative explanations for the observed rank reversal. The use of condition-level bootstrap resampling is also appropriate given the dependence among section-level observations.

Critical weaknesses
  1. Section 4.1 and Algorithm 1 derive the boundary tolerance from training-point spacing in standardized coordinates, but compare it against boundary distances in original coordinates. This makes the interpretation of the tolerance unclear and may make the resulting labels sensitive to coordinate scaling or units. Appendix H provides useful parameter-sensitivity results, so this concern does not by itself invalidate the reported rank reversal. However, because the partition is a central contribution, the paper should justify this choice or verify that the principal findings persist when the hull, distances, and tolerance are defined in a common dimensionless space.

  2. Relative L2 error on cube-root damage is a reasonable benchmark metric, and the additional damage-domain R² and bias analyses are valuable. Nevertheless, better performance on these metrics does not necessarily imply more accurate lifetime damage estimates or fewer non-conservative fatigue assessments. Since engineering reliability is a major motivation, a targeted evaluation of lifetime-weighted damage error or critical-section underestimation would strengthen the practical significance of the findings. Alternatively, the paper could narrow its claims to predictive accuracy under distribution shift.

3.The main EX_EX comparisons show substantial error gaps, and the condition-level bootstrap is an appropriate improvement over row-level resampling. However, some section-specific winner changes involve much smaller differences—for example, approximately 0.0601 versus 0.0604 at the REF tower base in Table 26. These cases should be supported by paired uncertainty estimates or described as near-ties. In addition, the reported bootstrap does not capture training variability; repeating a small number of representative models would help establish the stability of the main extrapolation advantage. The test-set oracle is useful diagnostically, but should remain clearly distinguished from an actionable model-selection procedure.

Questions for authors

1.Does the principal rank reversal persist when all partitioning operations are performed in a consistent standardized space? 2.What are the paired confidence intervals for the EX_EX error differences between the validation-selected ensemble and the highlighted neural network? 3.Do these improvements translate into lower lifetime-weighted damage error and reduced non-conservative underestimation? 4.Can a boundary-held-out validation split constructed entirely within the training data reduce the reported model-selection regret?

1 comment
AuthorsOpenReview ↗

Standardized Partition, Statistical Robustness, and Fatigue Reliability

We thank the reviewer for recognizing that FLOATBench addresses a meaningful problem in scientific machine learning, that the dataset has clear potential value, and that the evaluation is reasonably extensive.

In brief, the reversal holds under the standardized partition (Q1), and its gap is significant on every tower (Q2). Both models keep the lifetime damage within 3.5%, but the ensemble under-predicts far more often (Q3). Boundary-held-out validation does not give a better final model (Q4).

Q1 / W1. Fully standardized partition: yes, the reversal persists, and the revised paper now uses it. Following your suggestion, the hull, the distances and the tolerance are now all in standardized units. Only 98 of the 4,740 test simulations get a new label, all from wind extrapolation to interpolation or in-train. We updated the code, released the new labels and recomputed every regime-dependent result. The reversal still holds in all 48 tower-partition pairs of the sweep. The model ranked first overall drops to rank 21 / 11 / 13 at EX_EX (23 / 11 / 11 before). A FastAI network is always first there, the same one in 45 of 48. (Changed in the paper: Sec. 4, Algorithm 1, Appendix H and all regime-dependent results.)

Q2 / W3. Paired intervals of the EX_EX gap: significant on every tower. Small section-level differences: near-ties. We compared the two released models with a paired bootstrap over operating conditions (2,000 resamples). The ensemble's EX_EX error exceeds the network's by 0.033 [0.026, 0.043] on REF, 0.039 [0.025, 0.057] on OPT1 and 0.045 [0.032, 0.063] on OPT2. No interval includes zero (Table 21). For the small section-level differences you point to, Tables 33-34 now give paired intervals too. At the tower base they are near-ties, as in your example (0.0601 against 0.0604 on REF, interval [-0.0003, 0.0008]). At the top, the ensemble loses to the section winner significantly on REF and OPT2, and it is a near-tie on OPT1. Sec. 5.2 now says both.

W3. Training seeds: the network wins at EX_EX for every seed, and the oracle is now only a diagnostic. We retrained the network and the ensemble's members with five seeds on each tower. The network wins at EX_EX every time, and the paired interval always excludes zero (Table 21). On REF, the submitted network was the best of the five seeds, so we now report five-seed means: the ensemble's EX_EX error is 1.40 / 1.53 / 1.64 times the network's (1.61 / 1.56 / 1.69 with the released seed). The test-set oracle is now only a diagnostic, not a way to select a model (Appendix J.1). (Changed in the paper: abstract, Sec. 5.2, Appendices H.6, J.1 and K.6.)

Q3 / W2. Lower lifetime damage error: not consistently. Less non-conservative underestimation: yes, clearly. Both models predict lifetime damage within 3.5%. Frequent conditions dominate it; extrapolated ones are a small share of this site's operating time. The difference is in the direction of the error: at EX_EX the ensemble predicts too little damage on every tower, while the network errs on the high side on average, the safe side for a fatigue check. Values for REF / OPT1 / OPT2 (Table 32):

EnsembleNetwork
Lifetime damage error, worst section1.6 / 2.8 / 2.4%3.4 / 0.9 / 1.4%
Mean damage error at EX_EX (negative = too little)-3.0 / -6.8 / -10.0%+4.5 / +3.4 / +4.0%
EX_EX damage in predictions >10% too low38 / 50 / 59%6 / 19 / 17%

(Changed in the paper: abstract, Sec. 5.2, Appendix K.5.)

Q4. Boundary-held-out validation: it ranks the models better, but the final model is not better. On each tower, instead of a random 20% of the training data, we held out the two lowest and the two highest training wind speeds (4.5, 5.5, 22.5 and 23.5 m/s; 22% of the conditions) and retrained all the models on the rest. Boundary validation picks a model close to the best of its own pool (row 2). But without the edges, every model must extrapolate three wind bins instead of one, and all get worse (row 3). Used only to choose among the paper's models, which keep the edges, it picks essentially the same model as random validation (row 4). EX_EX error of the selected model over the best, released seed (regret, Table 28):

SelectionREFOPT1OPT2
Random validation (paper)1.611.561.69
Boundary validation, own pool1.031.151.30
Same model vs. best paper model2.152.372.31
Boundary choice among paper models1.611.621.69

(Changed in the paper: Appendix J.3, Table 28.)

Summary. The reversal holds under the standardized partition and for every training seed, with a significant gap. In practice it changes the side of the error, not the lifetime total: the selected ensemble under-predicts damage where it extrapolates. Boundary-held-out validation did not solve model selection. We hope these analyses address your soundness concerns and warrant reconsidering your overall assessment.

Reviewer_zQXyOpenReview ↗
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Paper summary

This paper proposed a benchmark for FOWT tower fatigue. The data is tabular. Each row contains simulation information and setup and the labels are the cumulative damages. 3 splits are tested for accessing out-of-distribution behaviors of models.

Critical strengths
  • The presentation is overall clear.
  • Both in-distribution and out-of-distribution tests are conducted.
Critical weaknesses
  • It seems that the simulations are generated in a prior paper instead of by this paper, but the text did not mention this.
Questions for authors
  • How does the benchmark compare with "FLOAT: Fatigue-aware design optimization of Floating Offshore Wind Turbine towers." Ocean Engineering (2026)?
  • Are there individual simulation data for the 30 sections or are they interpolations?
  • Does the extrapolation test mean that the models fail to extrapolate from 23.5 to 24.5 m/s? Does the rank reversal mean that the surrogate models can not generalize meaningfully?
  • What would be the use cases for such surrogate models? Is the cross-tower transfer possible (in terms of information)?
  • in Figure 4 (c) , why does the damage profile of REF looks so different from the other two?
1 comment
AuthorsOpenReview ↗

FLOAT Relationship, Section Labels, and Extrapolation

We thank the reviewer for the positive assessment, and for noting that the presentation is clear and that we test both in- and out-of-distribution cases.

In brief, FLOATBench is the dataset and benchmark built with the FLOAT framework, each section has its own damage label, and the models do not fail at 24.5 m/s. The real risk is choosing the wrong model.

W1/Q1. Relationship to FLOAT (2026): FLOAT is the physics behind the data; FLOATBench is the dataset and ML benchmark built on it. FLOAT (2026) is an open-source framework for the fatigue simulation and design of floating turbine towers, built on OpenFAST and WISDEM. It came with no public dataset and no ML benchmark. The simulations follow the FLOAT methodology, on REF (the IEA 22 MW reference tower) and on the two towers FLOAT redesigned, OPT1 and OPT2. New in FLOATBench are the public data, 582,120 per-section fatigue labels, reproducible splits, a protocol that separates interpolation from extrapolation, and a benchmark of 735 fitted models. The Introduction, Sec. 3 and Appendix N now state this.

Q2. Are the 30 section labels interpolated? No: only the bending moments are interpolated; damage is computed separately for each section. OpenFAST gives the bending moment over time at 11 heights, which we interpolate linearly to the middle of each of the 30 sections. Each section then gets its own stress, from its own diameter and wall thickness, and its own damage, from rainflow counting and Miner's rule. The moments vary smoothly along the height, but the damage is a strongly nonlinear function of both the moment time series and the section properties. Sec. 3 now explains this.

Q3. Does extrapolation from 23.5 to 24.5 m/s fail? Does rank reversal imply poor generalization? No to both: both stay accurate at 24.5 m/s, and the reversal is a model-selection problem. At high wind the turbine is at full power and pitches its blades to limit the load, so the tower load barely changes. The hard side is the low one: 3.5 m/s is below the lowest training speed and close to cut-in (3 m/s), where the load changes quickly. There, the ensemble's tree models stay at their edge value, while the network follows the downward trend (Table 31).

Test region (REF / OPT1 / OPT2)Mean load change vs. training edgeEnsemble Rel L2Network Rel L2
3.5 m/s (edge 4.5)-27 / -34 / -34%0.650 / 0.905 / 0.8900.342 / 0.339 / 0.368
24.5 m/s (edge 23.5)0 / +4 / +3%0.053 / 0.067 / 0.0690.040 / 0.062 / 0.055
EX_EX-0.088 / 0.108 / 0.1110.054 / 0.069 / 0.065
Global-0.063 / 0.069 / 0.0700.079 / 0.085 / 0.081

So the issue is which model gets chosen. A network that ranks only 69th–79th overall is the best at EX_EX (joint wind and wave extrapolation) on all three towers, and is even more accurate there than overall. Yet random validation picks the ensemble. This holds across splits, training sets and five seeds. The wrong choice has a cost: with the ensemble, predictions more than 10% too low carry 38–59% of the EX_EX damage, against 6–19% with the network. There, a tower looks safer than its simulations say. (Changed in the paper: Appendix K.4–K.5, Tables 30–32.)

Q4. Use cases and cross-tower transfer: faster fatigue checks during design; transfer works within this tower family when REF is in training. One fatigue check takes 6,468 OpenFAST runs (~6,500 CPU-hours) per tower. A surrogate trained on 27% of the conditions predicts the rest. For transfer, Sec. 5.3 trains on two towers and predicts the third (rank-1 model):

Trained onPredictedRel L2
REF + OPT1OPT20.067
REF + OPT2OPT10.098
OPT1 + OPT2REF0.423

REF is much harder to predict: it differs most in geometry and damage. It is also a test bed for new tabular models under controlled extrapolation; physics data are rare in tabular benchmarks (at most 3 of 51 TabArena datasets [Erickson et al., 2025]).

Q5. Why is REF different in Fig. 4(c)? It is the starting design, not yet designed for fatigue or for a floating platform. Its lifetime damage is well above 1, where 1 means failure at the end of the design life. OPT1 and OPT2 are FLOAT redesigns for this platform, with new diameter and wall-thickness profiles. They move the tower's first fore-aft frequency away from the blade-passing frequency (~0.35 Hz), so the loads are amplified less:

TowerFore-aft frequencyDamage along the height
REF0.336 Hz4–32
OPT10.573 Hz0.49–1.28
OPT2 (final)0.537 Hz0.78–0.94

The Fig. 4 caption now explains this.

Summary. FLOATBench is the dataset and benchmark built with FLOAT, and every section has its own damage label. The models stay accurate at 24.5 m/s; the risk is selecting one that predicts too little damage under extrapolation. Thank you again; we hope these clarifications and revisions warrant a reconsideration of your overall assessment.

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

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