acceptodds
Under review as a conference paper at ICLR 2027

Optimal Transport Dropout for Structured Predictive Uncertainty

Abstract

Deterministic neural networks and neural operators provide point predictions with no intrinsic measure of reliability. Yet, predictive uncertainty may stem from irreducible outcome variability, finite data, or limitations of the chosen model class. Monte Carlo dropout offers a computationally convenient way to construct a predictive distribution through stochastic feature masking, without training multiple independent networks or explicitly inferring a posterior over model parameters. However, its perturbation law is largely prescribed a priori and typically factorised across latent coordinates. We introduce Optimal Transport Dropout (OTD), which instead learns the predictive mapping and the law of its latent perturbations jointly. Starting from a simple independent reference distribution, OTD transports latent perturbations through a learnable flow and propagates them through the predictive neural network, thereby inducing a structured predictive law. Training uses the strictly proper Energy Score, while a kinetic-action term geometrically regularises the transport. Synthetic benchmarks show that OTD captures multimodal predictive distributions, generates meaningful dispersion when the model is misspecified, and exhibits contracting dispersion as more training data or greater model capacity are provided. For a field-valued partial differential equation surrogate, predictive dispersion strongly aligns with the spatial pattern of prediction errors. On this task, compared with Monte Carlo dropout, OTD yields more accurate predictions and better-calibrated, substantially narrower intervals. On real-world regression benchmarks, it further shows competitive accuracy and better probabilistic predictions compared to several established baselines. OTD therefore offers a way to learn structured predictive uncertainty without explicit posterior inference or ensembles of independently trained predictors.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Uncertainty quantification, predictive uncertainty, Monte Carlo dropout, optimal transport, surrogate modeling

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_EzNWOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes Optimal Transport Dropout (OTD) to quantify uncertainty in neural networks as an alternative to Monte Carlo Dropout. Relaxed Bernoulli (Concrete) dropout masks pass through a neural ODE in logit space and then multiply the hidden activations, so the mask law is learned instead of being fixed and factorized. The method is validated on several 1d regression problems and 11 OpenML regression datasets.

Critical strengths
  1. The method is quite simple and practical. It uses one network, a few integration steps, and adds little wall-clock cost.
  2. Training uses a strictly proper, sample-based scoring rule and needs no likelihood or variational posterior.
  3. The ablation in Table 3 separates the scoring rule from the transport.
  4. The limitations section is candid, and code is provided for reproducibility.
Critical weaknesses

(1) Several baselines are missing: deep ensembles, Concrete dropout with learned p (the natural diagonal-transport ablation), engression with input noise, multiplicative normalizing flows, GFlowOut, and a GP or PCA-GP

(2) The statistical support is insufficient. Table 2 reports no seeds or uncertainties. Table 3 only reports 3 seeds, and support within statistical variation is partly thin. 10 seeds might give a clearer picture.

Questions for authors

How do performance metrics compare across all tests for other baselines? (deep ensembles, Concrete dropout with learned p (the natural diagonal-transport ablation), engression with input noise, multiplicative normalizing flows, GFlowOut, and a GP)

3 comments

We thank the reviewer for the positive assessment and constructive suggestions. We have addressed the two principal concerns by substantially expanding the probabilistic baseline comparisons and strengthening statistical reliability. The revised manuscript additionally reports predictive accuracy, distributional scores, calibration diagnostics, model complexity, and computational costs, providing a more comprehensive assessment of OTD. We appreciate the reviewer's contribution to the experimental design; the resulting additions are detailed in Section 4.2 and Appendices D.1-D.5.

Critical Weaknesses

  1. We have implemented the requested families of probabilistic baselines, together with the implicit generative approaches of Pacchiardi et al. and Kelen et al. GP and PCA-GP are evaluated on the UCI/OpenML benchmarks. For Ginzburg-Landau, the stochastic models generate complete-field realisations, allowing comparisons through field-level Energy Scores and functional diagnostics. We report predictive metrics, parameter counts, hyperparameters, and training times. The synthetic experiments retain MC Dropout as the main comparator because they are designed to isolate specific properties of transported masking rather than provide comprehensive method rankings. We thank the reviewer for prompting these broader tests, which have strengthened the empirical comparison in Section 4.2, Appendix D.4 (Tables 11 and 12), and Appendix D.5 (Tables 16-19).

  2. We have extended the component ablation and the Ginzburg-Landau experiments to ten independent seeds (0-9), reporting means and standard deviations (Table 5). We have also done so for the bimodal, misspecification, model-capacity, integration-depth, temperature-sensitivity, and timing analyses, where corresponding results are reported. The revised ablation study considers eight configurations and more clearly separates the contributions of the Energy Score, learned transport, kinetic regularisation, and model capacity. For UCI/OpenML, we retain the five-fold cross-validation protocol and report fold-wise variability separately from the ten-seed experiments; we do not present those folds as ten independent runs. We thank the reviewer for stressing statistical robustness, which motivated the updated tables in Section 4.1 (Tables 1,2), Appendix D.3 (Table 9), Section 4.2 (Table 3), Appendix D, and Appendix F.

AuthorsOpenReview ↗

Response to question

  • We now provide comprehensive numerical comparisons in the revised appendix. On Ginzburg-Landau, OTD achieves lower RMSE and field-level Energy Score than the evaluated probabilistic baselines, including Kelen et al., Pacchiardi et al., and Deep Ensembles. Calibration performance is more heterogeneous, and different methods perform best on different diagnostics. For UCI/OpenML, we have replaced the original NLL comparison with the Energy Score and restricted numerical comparisons to independently evaluated methods following common data splits and predictive sampling. OTD remains competitive across heterogeneous regression tasks, although its relative performance depends on the dataset and evaluation metric, with GP-based approaches particularly strong in some settings. The revised figure and tables report distributional accuracy, marginal calibration, model size, and computational costs, allowing a more balanced assessment. We thank the reviewer for requesting numerical detail beyond aggregate plots; the extended results are provided in Appendix D.4 and Appendix D.5, with the UCI visual summary in Section 4.3, Figure 5.

I appreciate the response and the changes made by the authors, and I will adjust my score accordingly.

Reviewer_bJ7aOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes Optimal Transport Dropout (OTD), which uses flow matching to learn dropout masks beyond the Bernoulli distribution that allow for more expressive predictive distributions. Using the energy score as an objective leads to an end-to-end trainable network that learns the best projection onto the true distribution (in terms of the energy distance). I liked the general idea of the method, as well as the controlled experiments regarding what types of uncertainty are actually learned by the method. Further, the authors show good performance on selected tasks. However, in my opinion several weaknesses outweigh the strengths. In particular, the motivation is not really clear, as the paper sits weirdly between a generally novel predictive method and the setting of surrogate models. The latter are strongly motived but play only a small part in the experiments and do not really fit to the rest of the paper. In addition, no real baselines are provided here; for the regression tasks the benchmark selection is questionable and should at least be further backed by references. Together with missing ablations on the runtime and (possibly) higher parameter count of OTD, as well as part of the contribution (the kinematic regularization) being insignificant in the provided experiments I suggest a weak reject. I encourage the authors to further improve the paper, as the method is very promising, although this might require a major rewrite of the paper in terms of the contribution and motivation (following my weakness 1), which might extend the scope of a rebuttal.

Critical strengths

I like the proposed method (OTD) as a fairly simple but yet sophisticated way to improve neural samplers beyond regular MCDropout. It provides a way to transform the (relaxed) Bernoulli masks into any flexible distribution that can represent the uncertainty in the neural network better and estimates the true distribution more closely (in terms of the energy distance). I also appreciate the interpretation and the synthetic experiments regarding the different types of uncertainty and the verification that OTD is able to represent mainly predictive uncertainty, which, based on the data-generating process, could either be aleatoric, based on estimation error or a combination of the two. The corresponding controlled experiments highlight that OTD behaves as desired.

Critical weaknesses

1. Paper framing: The contribution sits a bit awkwardly between a general purpose uncertainty method and applications to surrogate models. For example, the abstract directly mentions neural operator, although they are never used. Similarly, a whole paragraph of the introduction concerns surrogate modeling, although it is later only one specific dataset/experiment. Section 3.2 on the energy score is also overly complicated for general spaces and metrics, probably to accommodate a possible function space setting. However, it could be much simplified to the reader by just using dY=∥⋅∥2d_{\mathcal{Y}} = \|\cdot\|_{2}, since ultimately all used models operate on Rd\mathbb{R}^d (the functional setting uses an MLP as well, to my understanding).

I would either claim the method to either be

  1. A general-purpose method (which I think it is) that can be combined with almost any architecture and is a simple way to improve MCDropout to accommodate more complex distributions. This goes in line with the controlled experiments and the regression benchmarks. The functional uncertainty should then be claimed and seen as a possible extension or just as another benchmark
  2. A method for surrogate modeling, which would at the moment raise the question why most of the paper focuses on the multivariate setting and provides only a single PDE experiment.

At the moment the motivation is not really clear and it reads like the surrogate part was somehow forced into the paper. This diminishes the contribution and makes the paper sit awkardly between two almost adjacent parts that are not sufficient on their own. I encourage the authors sharpen the contribution, which (together with addressing the following points) can lead to a great paper with an interesting uncertainty representation method.

2. Experiments, baselines and dataset selection: I believe that the experimental section requires a major update in order to properly assess the performance of OTD. I like the controlled experiments here and in this case comparing only to MCDropout is generally sufficient. However, here it would be a good place to state more clearly the runtime/compute differences of the method and the performance with respect to the amount of parameters (compare question 6).

However, the real-world data experiments are in my view not sufficient in their current state. The Ginzburg-Landau experiment compares only to the deterministic method and the MCDropout and can only verify improvements against the latter, which are expected since OTD adds extra compute/parameters to provide a more flexible dropout distribution. Instead it would be much more interesting to compare to other (functional) uncertainty estimation approaches, for example those mentioned by the authors themselves or for example from Magnani et al. [1] or Diaconu et al. [2]. For this task the current baseline selection is not sufficient to assess the performance of OTD with respect to functional uncertainty estimation.

The regression benchmarks are claimed to be "established in the literature" (l. 453), but only cite an arXiv preprint. I would at least add corresponding citations for the UCI datasets and any published benchmarks. Similarly, the corresponding baselines are not described and not referenced so there is no information which category the corresponding baselines fall into and what method they are based on. At the same time, reasonable baselines that are cited by the authors themselves are not compared, for example Pacchiardi et al. [3]. Further baselines that go into the same direction and might be interesting to add could be Kelen et al. [4] or Han et al. [5]. As you already provide many baselines, I suggest to strengthen the benchmark claim, explain the methods in more detail and provide more detailed results, for example providing tables similar to Table 14 for all metrics (same for Figure 5). Together with addressing the fair parameter count (compare question 6) and addressing the additional runtime for OTD this could significantly strengthen the regression benchmark setting.

3. Kinetic regularization: I understand and like the idea of applying the kinetic regularization, especially with the motivation of the smooth and rough paths in Appendix E. However, the impact, at least in the ablation, seems overstated. While the authors acknowledge that the kinetic regularization has a smaller effect, Table 3 shows that there is actually no significant (in terms of seed standard deviation) effect of setting λkin=0\lambda_{\mathrm{kin}}=0. The only significant improvement is in MACE where however both OTD variants are within the same standard deviation of MCDropout. This raises the question whether the regularization is needed in practice at all and leads to any improvement gains. A the same time, the selection of λkin\lambda_{\mathrm{kin}} seems not clear, l. 1808 claims selection so that it "remains small relative to the Energy Score", which does not offer clear selection guidance. I would suggest the authors to

  1. More thoroughly analyze the effect of the kinetic regularization and its effect on the quantitative performance across all studied datasets. This would show whether λkin>0\lambda_{\mathrm{kin}}>0 is required in general, for some specific tasks, or not at all.
  2. At the same time, provide a clear way to select λkin\lambda_{\mathrm{kin}}, for example based on hyperparameter tuning or some heuristic and analyze its interplay with the resulting performance of the regularized OTD.

4. Minor points and style

  • GθG_{\theta} is never properly defined.
  • ρ0,l\rho_{0,l} not properly defined, maybe just include the space it lives on and a symbol for the used distribution? I assume that ll denotes the index of the hidden representation/unit?
  • The table in l. 396 is not a proper table with title etc.
  • Table 2: The width highlighting is misleading as a very small width is not better if the corresponding PICP is far away from α\alpha. Otherwise, any deterministic baseline would be best with=0. I suggest to remove the width highlighting overall and only supply it as an addition to PICP to check width in well-calibrated cases.
  • Figure 1: Maybe the two right plots could be scaled to the same size as the left one to improve visibility? Also in the left panel PP denotes the KDE estimate, so since it is a density it should probably be written as small pp with a corresponding definition before.
  • Z1Z_{1} in l. 155 should use a definition symbol
  • l. 230 & l. 237. P∗P^* is never actually defined, I assume you mean Px∗P_{x}^* ?
  • The papers [1,2] mentioned earlier with regards to baselines, would also be a good addition to the related work on uncertainty in functional surrogates.

References

[1] Magnani, E. et al. Linearization Turns Neural Operators into Function-Valued Gaussian Processes. ICML 2025.

[2] Diaconu, C. et al. Probabilistic retrofitting of learned simulators. ICML 2026.

[3] Pacchiardi, L. et al. Probabilistic Forecasting with Generative Networks via Scoring Rule Minimization. JMLR, 2024.

[4] Kelen, D. et al. Distribution-Free Data Uncertainty for Neural Network Regression. ICLR 2025.

[5] Han, X. et al. CARD: Classification and Regression Diffusion Models. NeurIPS, 2022.

Questions for authors
  1. l. 409 The term "Concrete distribution" is never used elsewhere. Does this refer to the Concrete distribution from literature, so it coincides with their relaxation? In that case it should be named and cited
  2. Table 14 reports a KDE estimate for OTD. Is the same estimate used for the other baselines? Since KDE smoothes the distribution one should probably also sample and estimate KDE for the other baselines as well to make the comparison fair (maybe there is not a difference). Also it would be great to include the same table for the RMSE and energy score.
  3. In section 3.3 the authors state that the population risk minimizer defines a best-in-class predictive model. For completeness, I would add that this minimizer is not necessarily unique and could imply multiple best-in-class models.
  4. 3.3 Best in class sounds a bit weird to me and hides the fact that this might not be a unique minimizer. Maybe rather describe it as the projection in energy distance
  5. How were the samples in Table 8 and Table 10 chosen? I understand the motivation of the sample-level analysis but I would suggest to provide only one or two specific samples with the corresponding visualizations (and explanation how they were chosen, i.e. randomly or selected). The way it is presented currently, does not lead to any additional insights beyond the aggregated rank correlations and raises the questions whether the samples have been cherry-picked.
  6. If all methods use the same backbone (l. 452) you should think about providing an ablation with respect to the additional parameter count imposed by your method. For example with the same backbone MCDropout would have overall less parameter in the network as OTD with the same backbone if I understood correctly.
  7. What purpose does Table 15 serve (except for the MACE)? The datasets are all on different scales and it is hard to tell whether any of these number imply a good prediction. I suggest to provide tables or plots similar to Table 14 or Figure 5 for the RMSE/MAE, energy score and MACE, as well.
5 comments

We thank the reviewer for the detailed and constructive criticism. We have revised the positioning of OTD, substantially strengthened the experimental comparisons, and clarified the role of kinetic regularisation. The revised manuscript presents OTD as a general-purpose predictive uncertainty method, with scientific surrogates as an application. We have added probabilistic baselines, capacity controls, computational measurements, and functional calibration diagnostics, while extending the controlled and Ginzburg-Landau statistical evaluation to ten independent runs. We have also improved the mathematical definitions, benchmark documentation, and presentation. We appreciate the breadth of the reviewer's recommendations, which materially improved the Introduction, Sections 3-4, and Appendices A, C, D, and E.

AuthorsOpenReview ↗

Critical weaknesses

Critical Weaknesses

  1. We agree and have revised the Abstract, Introduction, and experimental narrative accordingly. OTD is now presented as a general-purpose method that jointly learns the predictive mapping and the distribution of stochastic feature perturbations. Scientific surrogate modelling is introduced as a relevant application, rather than the defining setting. We have also simplified the Energy Score formulation by adopting Euclidean distances in ℝ 𝑑𝑦 , while retaining its extension to metrics of strong negative type. This clarifies the central contribution without restricting its applicability. We thank the reviewer for drawing attention to this framing, now reflected in the Abstract, Introduction (Section 1), and the Energy Score formulation in Section 3.2 (Learning objective).

  2. We agree that stronger experimental comparisons are necessary. We have substantially expanded the Ginzburg-Landau evaluation to include Concrete Dropout, Deep Ensembles, Engression, MNF, GFlowOut, and the implicit generators of Pacchiardi et al. and Kelen et al. We now report predictive accuracy, complete-field Energy Scores, functional calibration, parameter counts, and training times over ten independent seeds. We also introduce width-matched and approximately parameter-count-matched dropout configurations, allowing us to distinguish the contribution of learned transport from increased model capacity in the component ablation. We thank the reviewer for highlighting Magnani et al. and Diaconu et al., which we have incorporated into the related work. We do not reproduce these methods numerically because they are designed around neural operators or pretrained simulators, whereas our benchmark employs a coordinate-based neural-field predictor; adapting them directly would require architectural changes beyond this comparison. For UCI/OpenML, we have added dataset citations, benchmark references, and descriptions of the baseline methods. We have independently implemented Pacchiardi et al., Kelen et al., and several additional probabilistic baselines. CARD is acknowledged as a relevant diffusion-based alternative but is not reproduced numerically. Crucially, we have replaced the original NLL comparison with the Energy Score, avoiding heterogeneous density-estimation procedures and restricting numerical comparisons to methods evaluated under our shared protocol. We are grateful for this suggestion, which prompted a substantially fairer and more informative evaluation: the related work is expanded in Section 2; the Ginzburg-Landau comparison and capacity controls appear in Section 4.2 and Appendix D.4; the regression comparison appears in Section 4.3 (Figure 5) and Appendix D.5.

  3. We have extended the Ginzburg-Landau ablation to ten independent runs, observing improvements in RMSE and Energy Score with kinetic regularisation. However, its primary motivation is geometric and computational: it favours low-action transport trajectories in latent space, potentially facilitating numerical integration with fewer time steps and, consequently, fewer velocity-network evaluations. We do not claim that kinetic regularisation is universally necessary or improves every metric; indeed, the unregularised variant obtains a slightly better Variogram Score. The coefficient 𝜆 kin is chosen heuristically to keep the regularisation term small relative to the Energy Score, so as not to suppress the learned transport. We have not conducted a systematic cross-dataset analysis or hyperparameter optimisation of this coefficient and therefore cannot establish a universally optimal selection rule. The integration-depth sweep varies the number of steps, not the regularisation strength, and does not by itself prove a computational gain attributable to the penalty. We thank the reviewer for prompting a more precise and appropriately limited interpretation: the empirical comparison appears in Section 4.2, the geometric motivation and heuristic in Appendix E, and the integration-depth sensitivity in Appendix D.4.

  4. Thank you for the pertinent and precise suggestions on clarity and presentation. We have revised the notation of the predictive map and transport construction, made the Binary Concrete sampling mechanism explicit, and separated marginal from functional calibration in the diagnostic definitions. These changes reduce ambiguities in the mathematical formulation and reporting. We are grateful for the reviewer's attention to presentation, which has improved Sections 3.1-3.3 and Appendices A (Diagnostic metrics) and C (OTD Implementation Details).

AuthorsOpenReview ↗

Responses to questions

  1. Yes. We have explicitly identified the reference mask law as the Binary Concrete distribution, cited Maddison et al., and provided its complete sampling construction, including the retention probability and temperature. We thank the reviewer for prompting this clarification, now incorporated in Appendix C, paragraph 'Relaxed mask sampling'.

  2. We agree that a fair likelihood comparison would require a consistent density-estimation procedure across all methods. However, the original comparison combined published NLL values obtained from explicit density estimates with KDE-based estimates from predictive samples. We have therefore removed NLL as a cross-method evaluation criterion and replaced it with the strictly proper Energy Score, which directly evaluates predictive distributions without requiring density estimation. All methods in the revised numerical comparison are independently evaluated using common folds and sample-based evaluation. We additionally report RMSE, sharpness, MACE, and training time. We thank the reviewer for identifying the methodological mismatch; the revised comparison appears in Section 4.3 (Figure 5) and Appendix D.5 (paragraph 'Evaluation metrics' and Tables 16-19), with the score defined in Appendix A.

  3. We agree. We have clarified that population-risk minimisers need not be unique: different parameters or transport maps may induce identical predictive laws or attain the same minimum risk. We now formulate the result in terms of a restricted energy-distance approximation. Kinetic regularisation favours lower-action representations but does not necessarily resolve non-uniqueness. We thank the reviewer for this mathematical clarification, now stated in Section 3.3 (Misspecified predictive models).

  4. The original cases were selected deterministically using approximately equally spaced indices across the ordered test set, independently of predictive performance. To address the concern more directly, we have supplemented these selected-field illustrations with graphical analyses covering all 52 test fields, including per-field predictive metrics and associations of realisation-wise and mean-prediction errors with predictive dispersion and standard deviation. This permits inspection of atypical cases without relying on selected examples; the illustrative field maps remain in the paper. We thank the reviewer for suggesting this stronger reporting, now implemented in Appendix D.4 (paragraph 'Results'; Figures 9-10).

  5. We have introduced width-256 and approximately parameter-count-matched MC Dropout configurations, alongside learned Concrete Dropout. The revised ablation shows that increasing capacity alone does not reproduce the predictive performance of transported masking in this controlled setting. We additionally report parameter counts and training times for the broader baseline comparisons; this is not a claim of equal wall-clock budgets. We thank the reviewer for insisting on capacity-aware evaluation, which motivated the revised component ablation in Section 4.2 and the model-size and training-time comparison in Appendix D.4.

  6. We agree. We now interpret sharpness jointly with coverage and have clarified that narrow intervals are not necessarily better. The revised diagnostic appendix also explains why MACE is a marginal measure and can be misleading for deterministic conditional laws: even an exact degenerate predictive distribution can yield non-zero nominal coverage error under closed empirical intervals. We thank the reviewer for motivating this important qualification, now stated in Appendix A (paragraphs 'Sharpness', 'Mean Absolute Coverage Error', and 'Joint calibration of functional predictions') and reflected in the Ginzburg-Landau discussion in Section 4.2.

  7. We agree that absolute metric values are difficult to interpret across datasets with different target scales. We have therefore replaced the original NLL-based Figure 5 with an Energy Score comparison and expanded the appendix with per-dataset results for all independently evaluated methods. The table reports RMSE, Energy Score, sharpness, MACE, and training time, enabling direct within-dataset comparisons under a common data protocol; parameter counts are reported separately. We interpret these results relative to competing methods on each dataset rather than comparing absolute scores across datasets. We thank the reviewer for suggesting a more interpretable presentation, now realised in Section 4.3 (Figure 5) and Appendix D.5.

Reviewer_fVPCOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The method learns a distribution over dropout masks. A neural flow introduces correlations before those masks reach the predictor. Training combines the Energy Score with a kinetic transport penalty. The resulting network can produce input-dependent predictive distributions, including bimodal ones. I see useful flexibility, but the reliability claims need stronger evidence.

Critical strengths
  • The GL component ablation provides useful evidence. Energy Score falls from 0.0896 for OTD-0 to 0.0455 for the full model. I'm willing to credit that improvement.

  • I like the bimodal toy example. One shared mask distribution generates different conditional shapes across inputs. It makes the model's expressive capability easy to see.

Critical weaknesses
  • I don't yet buy the epistemic interpretation. Better fitting can reduce bias-driven spread without establishing reliable uncertainty on unseen inputs. Repeated training datasets and missing-input-region tests would be more convincing.

  • The field study evaluates scalar coordinate predictions. Marginal Energy Scores don't identify the joint distribution of complete fields. I'd want spatial-dependence and field-level calibration tests.

  • The efficiency case is incomplete. Appendix F times OTD variants without a matched dropout or ensemble benchmark. That leaves the practical cost unclear.

Questions for authors
  • Why do favorable NLL results coexist with MACE above 0.6? Are KDE likelihoods and empirical intervals evaluating different predictive laws? Please evaluate likelihood and coverage for the same law.

  • Do the GL gains survive equal parameter and wall-clock budgets? Please include width-256 dropout and a plain learned-mask generator. Comparisons with Concrete Dropout or GFlowOut would also affect my assessment.

  • How well does spread predict ensemble-mean error across all 52 test fields? Use that error directly rather than ϵF\epsilon_F. Per-field results across multiple data splits would help.

  • Were the Table 14 baselines rerun on identical folds and target transformations? Comparative Energy Scores and calibration metrics are needed too. KDE-based NLL alone doesn't establish better predictive uncertainty.

2 comments

We thank the reviewer for the careful assessment and constructive suggestions. We have substantially strengthened the manuscript in four directions: (i) clarifying the interpretation and limitations of predictive uncertainty; (ii) extending functional evaluation beyond marginal calibration; (iii) introducing stronger probabilistic baselines and capacity-controlled comparisons, with explicit computational costs; and (iv) improving statistical reliability through ten independent runs for the controlled and Ginzburg-Landau experiments. Importantly, we have replaced the original likelihood-based benchmark comparison with Energy Score evaluations of independently implemented baselines under a common data-splitting and evaluation protocol, complemented by predictive accuracy and calibration diagnostics. We are grateful for the reviewer's guidance, which has made the scope, evidence, and limitations substantially clearer in the whole manuscript.

Critical Weaknesses

  • We agree that a reduction in predictive dispersion as the model fit improves does not, by itself, establish reliable epistemic uncertainty quantification. However, our objective is not to estimate a specific source of uncertainty, but rather to learn a predictive distribution whose dispersion can reflect the combined effects of irreducible variability, limited training data, and model-class limitations. We do not aim to disentangle these contributions or to recover a Bayesian posterior. Instead, our goal is to obtain predictions accompanied by an informative indication of their reliability. Our experiments assess this property through predictive accuracy, calibration, error-dispersion alignment, and the response of predictive dispersion to changes in data availability and model capacity. Regarding unexplored input regions, we acknowledge that OTD is not designed to guarantee reliable uncertainty estimates in large regions of the input space that are absent from the training data. In such regions, the training objective does not directly constrain the predictive distribution, and reliable uncertainty quantification necessarily depends on additional inductive assumptions, such as explicit priors in a Bayesian framework. This setting is not addressed by the proposed method. We thank the reviewer for prompting us to state this distinction explicitly; it is now reflected mainly in Section 5 (Discussion and limitations).

  • We agree and have substantially extended the evaluation. The Ginzburg-Landau Energy Score is explicitly computed on complete fields using the normalised Euclidean distance. We additionally introduce functional-rank calibration, projection-based PIT diagnostics across spatial frequencies, and the Variogram Score. These complementary diagnostics assess field-level predictive behaviour and spatial dependence beyond marginal coverage. We also clarify that marginal PICP and MACE do not imply joint calibration, and that no finite collection of the proposed diagnostics establishes complete conditional calibration. We appreciate the reviewer's emphasis on joint rather than marginal uncertainty, which directly motivated the new definitions in Appendix A (Diagnostic metrics) and the functional results in Section 4.2 and Appendix D.4, especially Table 12 and 13.

  • We have extended the Ginzburg-Landau and UCI/OpenML evaluations to report wall-clock training times for MC Dropout, Deep Ensembles, and other probabilistic baselines, together with model complexity. In particular, the Ginzburg-Landau comparison reports both parameter counts and times; the UCI/OpenML appendix reports training times and separately specifies parameter counts. These comparisons quantify the additional computational cost incurred by OTD in exchange for its predictive performance; they do not establish superiority under a strictly matched computational budget. We thank the reviewer for highlighting this practical consideration, now addressed in Appendix D.4, Appendix D.5. Also, Appendix F nos times OTD variants with a matched dropout benchmark, Table 20.

AuthorsOpenReview ↗

Responses to questions

  • We agree that the original discrepancy between NLL and MACE requires clarification. NLL was estimated using a Gaussian KDE fitted to predictive samples, whereas MACE used their empirical quantiles. KDE smoothing may therefore assign probability mass beyond narrow empirical intervals, potentially improving NLL without improving their coverage. Moreover, the original comparison involved published likelihood values computed using different density-estimation procedures. Rather than retain this potentially misleading comparison, we have removed NLL as a cross-method evaluation metric and adopted the strictly proper Energy Score, computed directly from predictive samples without density estimation. We retain MACE as a complementary diagnostic of marginal calibration; this is not a claim that Energy Score alone proves calibration. We thank the reviewer for exposing this comparability issue, which prompted the replacement of the benchmark Figure 5 in Section 4.3, the revised local-results Table 19 in Appendix D.5, and the distinct metric definitions in Appendix A.

  • We have expanded the component ablation to eight configurations, including width-256 MC Dropout, approximately parameter-count-matched MC Dropout, MC Dropout trained with the Energy Score, learned Concrete Dropout, zero-step OTD, and OTD without kinetic regularisation. Over ten independent runs, complete OTD achieves lower RMSE and Energy Score than the considered ablation baselines. These results identify the learned transport as the principal source of improvement in this controlled comparison, rather than increased predictive-network width alone. We have also introduced broader comparisons with Deep Ensembles, Engression, MNF, GFlowOut, and implicit generative models, reporting both model size and computational cost. We are grateful for the request for capacity controls: it led to the expanded ablation in Section 4.2 Table 5 and to the broader comparison in Appendix D.4, involving mainly Tabls 12 and 13.

  • We agree that ensemble-mean error is an important complementary diagnostic. Our primary interest, however, is the reliability of individual predictive realisations. We therefore consider both the expected realisation-wise discrepancy, εF(x)=EY^dY(Y^,y)\varepsilon_F(x)=\mathbb E_{\hat Y}d_{\mathcal Y}(\hat Y,y), and the error of the predictive mean, e(x)=dY(EY^,y)e(x)=d_{\mathcal Y}(\mathbb E\hat Y,y). This distinction is particularly relevant for multimodal laws, where the mean may lie between physically plausible outcomes. Neither measure replaces the other. We have extended the graphical analysis to all 52 test fields, comparing error-dispersion relationships with predictive dispersion and standard deviation. The corresponding Spearman correlations across the 52 fields are 0.917 for (εF,εD)(\varepsilon_F,\varepsilon_D) and 0.856 for (e,εD)(e,\varepsilon_D); using predictive standard deviation instead of dispersion, they are 0.919 and 0.859, respectively. The analysis also identifies severely under-dispersed high-error cases rather than obscuring them through a selected-case summary. We thank the reviewer for suggesting this more complete diagnostic; the resulting per-field plots and correlations are reported in Appendix D.4, paragraph 'Results', Figures 9 and 10.

  • We have clarified the five-fold cross-validation protocol, preprocessing, and target transformations. The published benchmarks are now used as methodological references rather than sources of numerical comparisons, since their evaluation procedures are not directly equivalent to ours. Instead, we independently evaluate MC Dropout, Concrete Dropout, Deep Ensembles, Engression, MNF, GFlowOut, Pacchiardi et al., Kelen et al., and GP/PCA-GP using common folds, preprocessing, and sample-based evaluation. We replace the original NLL comparison with an Energy Score plot and report RMSE, Energy Score, sharpness, MACE, and training times in the appendix, alongside a separate parameter-count table. This provides a more consistent assessment of predictive quality and computational cost. We thank the reviewer for insisting on reproducible, like-for-like comparisons; the revised protocol and model descriptions appear in Appendix D.5, with the new visual comparison in Section 4.3, Figure 5.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.