acceptodds
Withdrawn from ICLR 2027

Uncertainty-Aware Distribution-to-Distribution Flow Matching for Scientific Imaging

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Distribution-to-distribution generative models support scientific imaging tasks ranging from modeling cellular perturbation responses to translating medical images across conditions. Trustworthy generation requires reliability, or generalization across labs, devices, and experimental conditions, and accountability, or detecting out-of-distribution cases where predictions may be unreliable. We leverage Stochastic Flow Matching (SFM), a marginal-preserving stochastic extension of flow matching for improved generalization under distribution shift. SFM augments deterministic flows with a diffusion term together with a learned score-based drift correction, retaining the learned transport marginals while modeling conditional variability. Building on this SFM framework, we introduce Bayesian Stochastic Flow Matching (BSFM) as a companion uncertainty quantification mechanism and develop AVUQ (Antithetic Variance-reduction Uncertainty Quantification) to approximately estimate epistemic and aleatoric uncertainty via sample-efficient antithetic sampling with approximate posterior inference. We further use AVUQ to yield anomaly scores for unreliable generation detection. Experiments on cellular imaging (BBBC021, JUMP) and brain fMRI (Theory of Mind) across diverse unseen scenarios show that SFM improves generalization while AVUQ provides effective uncertainty-based anomaly scores under practical sampling budgets.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Trustworthy AI, Virtual Cell Perturbation Modeling

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_KmccOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces a framework for distribution-to-distribution generative modeling of scientific images, with particular emphasis on OOD robustness (different experimental settings) and uncertainty quantification. Stochastic flow matching, where standard flow matching is supplemented with a diffusion component and sinusoidal noise schedule is adopted as the generative model, while the authors derive the decomposition of uncertainties and use MC-Dropout for approximate posterior inference using the trained network. The method is evaluated on 3 benchmark image datasets and compared against several baselines, and appears to work well.

Critical strengths
  • important and general problem in distribution-to-distribution (image) generative modeling
  • the topic is somewhat dense technically, but the authors do a good job in exposing the background material in a didactic manner, with a clear progression of ideas, especially in the intro, related works, and preliminary sections. The setup (section 3) is an especially clear combination of mathematical notations and plain English explanations.
  • the proposed solution seems reasonable, but I am not an expert at all on uncertainty decomposition other than having a conceptual understanding of the problem, so I cannot comment on the validity or novelty of the proposed method. That being said, the sequence of methodology introduced in 4.2-4.4 is again very well motivated and logical, in particular the necessity for AVUQ with the mirrored noise instances (though I also cannot comment on why this should work)
  • empirically, the method seems to work very well compared to baselines, often by a significant amount compared to the next best (e.g., SDEdit)
Critical weaknesses
  • the authors define reliability as specific instances of generalization (across unseen perturbations and experimental setups), and accountability as the ability to report uncertainty under unreliable settings. Is this standard? It makes sense to me but appears somewhat arbitrary, both the definition and the specific desiderata of optimizing these (and not other considerations) in distributional modeling.
  • Table 1 does not report std / uncertainty on performance metrics so it's hard to evaluate how consistent the superior performance is.
  • the experimental evaluation is comprehensive with multiple real data benchmarks and OOD scenarios, but very little space was left to describe and interpret the results. The main table benchmark numbers speak for themselves, but the example generated samples in Figure 3 are not very informative as I’m not sure what features, or differences between methods, are the relevant to focus on. More guidance on interpreting these results (either qualitatively or quantitatively) would be appreciated. In particular, the cell imaging benchmarks seem standard but it's unclear why this particular MRI dataset is included, and what the takeaway is here.
  • it is taken (with cited works) that OOD inputs induces a variance reduction, but this seems to be a critical assumption
Questions for authors
  • could you report variability over multiple seeds / runs in performance for Table 1?
  • could you clarify or provide further context for why reliability and accountability are defined as such, and what aspects the current framework does NOT consider or prioritize in robustness and generalization for image generative modeling?
  • could you explain in more detail the assumption that OOD → variance reduction, scenarios where this would be violated, and how the proposed framework would deal with such cases?
  • could you expand on the qualitative interpretation of the main results on the 3 benchmarks, as well as the justification for the choice of benchmarks? In particular, there are hundreds of cognitive neuroimaging datasets out there, why this particular one and why would one assume low TOM cohort to be OOD in the brain scans? The example images also show anatomical scans without clear indication of neural activity, even though the task is to transform from resting to task activity.
2 comments

We thank the reviewer for the positive assessment and the constructive comments.

W1 / Q2: Are the definitions of reliability and accountability standard? What does the framework not consider?

Thanks for asking. These terms are not standardized for generative models; we use them as operational definitions motivated by deployment in scientific imaging. In standard ML terms:

  • Reliability is robustness to the distribution shifts that occur in practice (new labs, plates, cell lines, perturbations), i.e., generalization under distribution shift.
  • Accountability is failure detection, i.e., flagging inputs whose generations should not be trusted, i.e., unreliable generation detection.

The framework does not address (1) calibration of the uncertainty estimates, which requires paired source–target observations that are unavailable here; (2) shift types beyond those tested; (3) biological validation beyond the MoA classifier (Table 11). We have added these points to the Limitations (Sec. 6).

*W2 / Q1: Could you report variability over multiple seeds / runs for Table 1?

We agree that Table 1 should report variability across runs. Given the time constraints of the rebuttal period, we could not complete multiple training seeds for every baseline. We will report the corresponding multi-seed results (mean ± std) in the final revision.

W3 / Q4: Interpretation of the results; choice of benchmarks; why this fMRI dataset, why low-ToM is OOD, and why the images look anatomical.

  • Quantitative interpretation. FID and KID measure distributional similarity; whether generated cells carry the right biology is measured quantitatively by classifying the MoA of the generated images (Table 11).

  • Fig. 3. The relevant features are the compound-induced changes in cell and nuclear morphology and in the cytoskeleton. In the BBBC021 columns, the targets show enlarged, spread cells with a large nucleus (blue) and actin concentrated at the cell periphery (red). Under both the intensity shift and the combined shift, SFM generates this morphology, whereas SDEdit and UNSB largely keep the crowded layout of the source and CellFlux shows color artifacts. On JUMP Unseen Cell Lines, SFM preserves the sparse cell layout of the targets, whereas SDEdit and CellFlux generate densely packed cells; on JUMP Unseen Plates, the mildest shift, all methods produce plausible images. Under the intensity shift, both source and target test images are rescaled, so the question is whether the compound's morphology is still generated from inputs with unfamiliar intensities.

  • Benchmarks. BBBC021 and JUMP are standard benchmarks for perturbation-response generation (CellFlux, IMPA). We include fMRI to test whether the approach carries over to a second imaging modality with a subject-level cohort shift.

  • Why ds000228. It provides three properties this test requires: (i) source and target states within the same scan (an annotated baseline period and annotated ToM events), so source and target come from the same subject, analogous to control and perturbed cells; (ii) an independent behavioral measure (false-belief task performance) that defines the cohorts, so the shift is set by a non-imaging variable rather than by acquisition; and (iii) a movie-viewing paradigm suitable for young children, so the OOD cohort is also younger, an age range over which ToM-network responses become increasingly specialized (Richardson et al., 2018). Many cohort-shift datasets in medical imaging provide a single image type per subject and therefore do not define a source-to-target task.

  • Why low-ToM is OOD. The INC+FAIL children are younger (4.7 vs. 7.6 years) and have lower ToM scores (0.54 vs. 0.88). A model trained on PASS children therefore faces a population shift defined by an external, non-imaging variable rather than by image statistics.

  • Anatomical appearance. The images are single-TR BOLD slices. BOLD contrast is dominated by static tissue contrast, and task-evoked changes are only a few percent of the signal, so rest and ToM frames look similar by eye.

We have added this interpretation to Sec. 5.3 and the fMRI motivation to Appendix B.

W4 / Q3: The assumption that OOD inputs induce a variance reduction: when is it violated, and how does the framework deal with it?

This is an empirical observation, not an assumption of the method: the estimators (Eqs. 14–20) do not depend on it; only the sign of the scalar anomaly score does (Sec. 4.4). It can be violated when a shift induces genuine posterior disagreement. To handle both directions without assuming either, we added a two-sided, label-free score, fixed in advance: each component's log-trace is standardized by the mean and standard deviation of the ID inputs, and an input is scored by its absolute z-score, so it is flagged when its uncertainty is unusual in either direction. No OOD input, label or direction is used. AUROC / AUPR:

MethodBBBC021 Unseen Pert.BBBC021 IntensityJUMP Unseen Cell LinesJUMP Intensity
MAP Aleatoric0.532 / 0.3630.552 / 0.5470.526 / 0.5340.581 / 0.505
SWAG Aleatoric0.639 / 0.5170.681 / 0.7110.534 / 0.5400.636 / 0.576
SWAG Epistemic0.639 / 0.5020.677 / 0.7010.532 / 0.5390.624 / 0.566
LA Aleatoric0.620 / 0.5030.679 / 0.7060.531 / 0.5470.612 / 0.569
LA Epistemic0.583 / 0.4000.651 / 0.6320.520 / 0.5200.356 / 0.396
MCD Aleatoric0.581 / 0.3910.602 / 0.5720.568 / 0.5700.457 / 0.436
MCD Epistemic0.556 / 0.3710.576 / 0.5490.553 / 0.5540.446 / 0.429
AVUQ Aleatoric0.554 / 0.3810.585 / 0.5690.581 / 0.5790.592 / 0.512
AVUQ Epistemic0.684 / 0.6070.689 / 0.7240.545 / 0.5430.667 / 0.586

Same per-input scores, inputs and labels as Table 5. As expected, not assuming a direction reduces power relative to the one-sided score (e.g., AVUQ Epistemic 0.764 → 0.684 on BBBC021 Unseen Pert.), but AVUQ remains the best detector in all four cohorts, with the same component as under the one-sided score: Epistemic on BBBC021 Unseen Pert., BBBC021 Intensity and JUMP Intensity (AUROC 0.684 / 0.689 / 0.667), and Aleatoric on JUMP Unseen Cell Lines (AUROC 0.581).

We will discuss this explicitly in the paper, and we thank the reviewer again for the helpful suggestions.

Reviewer_mu2QOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies distribution-to-distribution generation for scientific imaging, aiming to improve generation under distribution shifts and identify unreliable outputs. It uses continuous-time stochastic flow matching with perturbed training paths and a score-based drift correction, approximates parameter uncertainty with MC-dropout, and estimates within-model and between-model variance through nested sampling. AVUQ uses antithetic noise pairs to reduce the Monte Carlo variance of conditional-mean estimates and derives anomaly scores from the resulting variance statistics. Experiments cover cellular imaging and fMRI.

Critical strengths

Whether scientific image generation remains useful under distribution shift, and when its outputs should not be trusted, are worthwhile questions. The paper also provides a useful mechanism-level experiment: Table 8 reports a 1.82–4.29-fold reduction in conditional-mean estimator variance at the same 16-sample budget. This supports the computational value of antithetic sampling in the tested settings.

Critical weaknesses

1. The continuous-time construction is inconsistent, undermining the central marginal-preservation claim

This is a continuous-time, continuous-state ODE/SDE construction. Discrete numerical solver steps do not change the equations that its underlying continuous model must satisfy.

For the standard linear path Xt=(1−t)X0+tX1X_t=(1-t)X_0+tX_1, endpoint-difference regression learns the marginal velocity

vt∗(x,c)=E[X1−X0∣Xt=x,c].v_t^*(x,c)=\mathbb E[X_1-X_0\mid X_t=x,c].

If its ODE marginals satisfy the continuity equation, adding isotropic diffusion while preserving those marginals requires the forward drift

vt∗+σt22∇log⁡pt.v_t^*+\frac{\sigma_t^2}{2}\nabla\log p_t.

Equations (8)/(11) instead use a minus sign. Equation (4) explicitly generates forward from t=0t=0 to t=1t=1, so a reverse-time convention does not explain this. Substitution into the forward Fokker–Planck equation gives

∂tpt=−∇⋅(vt∗pt)+σt2Δpt,\partial_t p_t=-\nabla\cdot(v_t^*p_t)+\sigma_t^2\Delta p_t,

leaving an additional diffusion term rather than cancelling it. Even with v=0v=0 and a standard Gaussian initial distribution, the proposed SDE increases the variance, whereas the ODE preserves that distribution.

There is a separate inconsistency in the training path. Equation (9) introduces

Xt=(1−t)X0+tX1+γtZ,X_t=(1-t)X_0+tX_1+\gamma_t Z,

whose probability-flow velocity is

bt(x,c)=E[X1−X0+γ˙tZ∣Xt=x,c].b_t(x,c)=\mathbb E[X_1-X_0+\dot\gamma_t Z\mid X_t=x,c].

Equation (10) still regresses only X1−X0X_1-X_0. Writing the resulting field as utu_t, a consistent forward sampling drift would require

ut+(σt22−γtγ˙t)st.u_t+\left(\frac{\sigma_t^2}{2}-\gamma_t\dot\gamma_t\right)s_t.

This correction is absent from Eq. (11). Changing the score sign alone would therefore not make the training and sampler consistent. These relations also follow from the stochastic-interpolant framework cited by the paper; see Eqs. (2.10) and (2.21) in Albergo et al..

These are inconsistencies in the continuous-time construction, and a more accurate solver cannot resolve them. The implementation could differ from the manuscript, but no consistent derivation or accessible code establishes that it does. The reported generation results therefore do not currently substantiate the claimed marginal-preserving method.

2. The experiments support sampling efficiency and anomaly ranking more directly than the claimed scientific uncertainty interpretation

I agree that antithetic sampling can stabilize conditional-mean estimation, and Table 8 provides evidence for that. Reducing Monte Carlo error does not, by itself, establish accurate epistemic and aleatoric uncertainty for the scientific task. With unpaired source and target observations, the chosen SDE defines a stochastic coupling; the paper does not establish why conditional variance induced by its adjustable noise mechanism corresponds to biological variability. The finite-budget estimator in Eq. (19) still contains residual Monte Carlo variation, while sample variance from raw antithetic trajectories is affected by their dependence. The manuscript acknowledges that the latter is used primarily as a ranking statistic, and the interpretation of these quantities should reflect that limitation.

The Lipschitz/Laplace bound in Appendix A is broadly valid under its assumptions, but it assumes a concentrated Gaussian posterior and yields LϵdL\epsilon\sqrt d, without controlling these quantities for the actual model. The main method uses MC-dropout. This bound does not establish calibration of the implemented estimator, reliability under distribution shift, or a relationship between the anomaly score and generation error.

The reliability evaluation also raises a substantive concern. Appendix C defines error using distances between predictions and randomly paired treatment images, then removes high-error ID samples and low-error OOD samples. Without paired ground truth, this distance can reflect both normal biological variation and prediction error; it is not directly a ground-truth label for failure on an individual input. The unfiltered results in Table 5 are useful, but primarily evaluate scenario provenance rather than whether the model identifies genuinely failed outputs across all inputs.

The additional MoA evaluation is more persuasive than FID alone. However, under combined intensity shift and unseen perturbations, SFM reaches only 12.89% MoA accuracy, compared with 43.23% for real target images, with an interval overlapping the closest baseline. Together with the label-construction issue, this leaves the broader claim of trustworthy scientific generation insufficiently supported.

Questions for authors
  1. What drift and velocity-regression target were actually used in the experiments? Do they match Eqs. (10)/(11)? Please provide a derivation and implementation consistent with the time direction, score sign, and γ˙tZ\dot\gamma_t Z term, and clarify whether correcting these issues requires rerunning the principal experiments.

  2. How much residual Monte Carlo contamination remains in Eq. (19) at the small sampling budgets used here? Why is there no equal-budget comparison with the i.i.d. estimator corrected by subtracting A^/K\hat A/K, which the paper itself discusses? Do the results support more accurate variance decomposition or primarily better anomaly ranking?

  3. Why should distance to a randomly paired treatment image provide a valid label for generation error on an individual input? When high-error ID and low-error OOD examples are retained, can the method be evaluated directly on actual generation failures rather than scenario provenance?

  4. How are the negative score direction and the choice of epistemic versus aleatoric component determined without inspecting labels from a new scenario? Can this rule be fixed before evaluating all test scenarios?

4 comments

We thank the reviewer for the precise analysis. The reviewer is correct about the equations in the manuscript.

W1 / Q1: The continuous-time construction is inconsistent. What drift and velocity-regression target were actually used? Do they match Eqs. (10)/(11)? Does correcting these issues require rerunning the principal experiments?

Summary. As written, Eqs. (8), (10) and (11) have the issue on both points the reviewer identifies: the score term must enter the forward drift with a plus sign, and the velocity target is missing tz. The implementation used for all reported experiments is correct and does not have the errors that appeared in the typed equations. It regresses the velocity onto x1-x0+tz and integrates forward in time with the drift vθ+12σt2sϕv_\theta+\tfrac12\sigma_t^2 s_\phi, which is the consistent construction the reviewer derives. The errors are in the write-up, and the code implementation included in the supplementary material is correct, so the reported results do not change and no rerun is needed. We are very grateful for pointing out this issue in our methods description.

Corrected equations.

xt=(1−t)x~0+tx1+γtz,Lv=E∥vθ(xt,t,c)−(x1−x~0+γ˙tz)∥2,Lη=E∥ηϕ(xt,t,c)−z∥2x_t=(1-t)\tilde x_0+t x_1+\gamma_t z,\qquad \mathcal L_v=\mathbb E\lVert v_\theta(x_t,t,c)-(x_1-\tilde x_0+\dot\gamma_t z)\rVert^2,\qquad \mathcal L_\eta=\mathbb E\lVert \eta_\phi(x_t,t,c)-z\rVert^2

dxt=(vθ(xt,t,c)+12σt2sϕ(xt,t,c))dt+σtdWt,sϕ=−ηϕ/γt,t:0→1dx_t=\big(v_\theta(x_t,t,c)+\tfrac12\sigma_t^2 s_\phi(x_t,t,c)\big)dt+\sigma_t dW_t,\qquad s_\phi=-\eta_\phi/\gamma_t,\qquad t: 0\to 1

Eq. (8) correspondingly becomes dxt=(v+12σt2∇log⁡pt)dt+σtdWtdx_t=\big(v+\tfrac12\sigma_t^2\nabla\log p_t\big)dt+\sigma_t dW_t.

Derivation. The minimizer v⋆(x,t)=E[x1−x~0+γ˙tz∣xt=x]v^\star(x,t)=\mathbb E[x_1-\tilde x_0+\dot\gamma_t z\mid x_t=x] is the probability-flow velocity of the interpolant, so tpt=-(vpt) (Albergo et al., Eq. 2.10). With η⋆=E[z∣xt]\eta^\star=\mathbb E[z\mid x_t] and pt=-/t (Eq. 2.21), take the drift b=v⋆+12σt2∇log⁡ptb=v^\star+\tfrac12\sigma_t^2\nabla\log p_t. Using ptpt=pt, its Fokker–Planck right-hand side is

−∇⋅(bpt)+12σt2Δpt=−∇⋅(v⋆pt)−12σt2Δpt+12σt2Δpt=∂tpt,-\nabla\cdot(b p_t)+\tfrac12\sigma_t^2\Delta p_t=-\nabla\cdot(v^\star p_t)-\tfrac12\sigma_t^2\Delta p_t+\tfrac12\sigma_t^2\Delta p_t=\partial_t p_t ,

so the marginals are preserved for any t; this is the reviewer's drift. Since E[γ˙tz∣xt]=−γtγ˙t∇log⁡pt\mathbb E[\dot\gamma_t z\mid x_t]=-\gamma_t\dot\gamma_t\nabla\log p_t, we have v=u-ttpt with u=E[x1−x~0∣xt]u=\mathbb E[x_1-\tilde x_0\mid x_t], hence b=u+(12σt2−γtγ˙t)∇log⁡ptb=u+(\tfrac12\sigma_t^2-\gamma_t\dot\gamma_t)\nabla\log p_t.

We have corrected Eqs. (8)–(11) and Fig. 2 accordingly (Sec. 4.1) and added this derivation, together with the implementation details (source perturbation, t and t schedules), to Appendix G.

W2: Conditional variance induced by an adjustable noise mechanism vs. biological variability; dependence of raw antithetic trajectories; the Appendix A bound; MC-Dropout.

  • Biological variability. We agree. Here, the aleatoric term measures how much generations from a single model vary for a given input, and the epistemic term measures how much the model's average generation moves across plausible parameters under the (approximate) posterior. With unpaired data, p(x1∣x0,c)p(x_1\mid x_0,c) is determined by the stochastic coupling induced by t and t: SFM fixes the marginals but not the conditional spread. A is therefore model-induced conditional variance rather than biological variability, and its scale is set by the injected noise, so we use it only to rank inputs. We have revised Sec. 4.3 accordingly (right after Eq. (14)), present both terms as ranking statistics for unreliable-generation detection, and added this limitation to Sec. 6.

  • Dependence of antithetic trajectories. For K samples formed by pairs with correlation , the sample variance has expectation 2(1-/(K-1)), a 17–26% inflation for K=4 and the values in Table 8. We have added this to Sec. 4.4, with the derivation in Appendix G.3.

  • Appendix A bound. We agree: Proposition A.1 only justifies the MAP plug-in locally, under a Laplace surrogate (Remark A.2), and we have stated this scope explicitly in Remark A.2.

  • MC-Dropout is our scalable posterior approximation for a generator with about 56M parameters. AVUQ does not depend on this choice, and Table 2 reports LA and SWAG under the same nested protocol.

Q2: How much residual Monte Carlo contamination remains in Eq. (19)? Why no equal-budget comparison with the i.i.d. estimator corrected by A/K? Do the results support a more accurate decomposition, or primarily better ranking?

For i.i.d. paths, E[E^]=E+A/K\mathbb E[\hat E]=E+A/K with A=Eθ[Var(x1∣θ)]A=\mathbb E_\theta[\mathrm{Var}(x_1\mid\theta)]. With antithetic pairs of correlation , the residual in Eq. (19) becomes (1+)A/K, i.e., 0.23–0.48 of the i.i.d. residual for the correlations in Table 8, at no extra cost.

Equal-budget comparison. Following the suggestion, we subtracted the estimated residual from each estimator at our budget (M=K=4, 16 SDE solves per input): A/K for i.i.d. sampling, and Apair/J for Eq. (19), where Apair is the variance of the J=K/2 pair means. At this budget the estimated residual is of the same order as E for both designs, so the corrected per-input estimates are dominated by sampling noise: about half are negative, and with the score and unfiltered labels of Table 5 their AUROC is close to chance (0.46–0.48 for both designs in all four cohorts). This is the regime noted in the paper: subtracting A/K is the ideal correction, but it becomes low-variance only for large M and K, which is prohibitive for high-dimensional SDE sampling. AVUQ instead reduces the residual itself at a fixed budget (Table 8). We have added this comparison to Appendix F.2.

Decomposition or ranking. We agree with the reviewer's reading: at the budgets used, the results support lower-variance estimation (Table 8) and better anomaly ranking (Tables 2 and 4–6), not an accurate per-input decomposition. We have stated this next to Eq. (19) (Sec. 4.3) and describe both traces as ranking statistics throughout.

Q3: Why should the distance to a randomly paired treatment image be a valid label? Can the method be evaluated on actual generation failures with all inputs retained?

We thank the reviewer for this question. The filtering serves the purpose of the benchmark, which asks whether uncertainty flags unreliable generations: because SFM generalizes well to some unseen inputs (Table 1), labeling every OOD input as unreliable would be incorrect, so the filter removes the ambiguous cases between clearly good ID generations and clearly poor OOD generations (Appendix C). We agree that, per input, an error computed against a single randomly paired target mixes biological variation with prediction error. We therefore also evaluate without random pairing, using the pretrained MoA classifier of Table 11, which judges each generation without any paired target image (Appendix I).

Label without random pairing. For each input, the classifier scores the model's own four generations (MAP sampling); we average the probability it assigns to the compound's annotated MoA and use one minus this average as the error. We then apply the filtering rule of Table 2 (0.5) to the same cohorts and methods (Appendix I, Table 13). AUROC / AUPR:

MethodBBBC021 Unseen Pert.BBBC021 Intensity Shift
non-nested
MAP Aleatoric0.709 / 0.6330.717 / 0.701
MCD-DFM Epistemic0.679 / 0.5160.674 / 0.609
nested-i.i.d.
SWAG Aleatoric0.706 / 0.6910.694 / 0.738
SWAG Epistemic0.723 / 0.7030.687 / 0.729
LA Aleatoric0.693 / 0.6630.672 / 0.702
LA Epistemic0.692 / 0.6580.698 / 0.728
MCD Aleatoric0.739 / 0.6870.701 / 0.726
MCD Epistemic0.726 / 0.6670.693 / 0.714
nested-antithetic
AVUQ Aleatoric0.717 / 0.6780.713 / 0.737
AVUQ Epistemic0.788 / 0.7860.733 / 0.778

AVUQ Epistemic remains the best detector in all four entries. This label is available only for BBBC021, because JUMP does not provide comparable MoA labels for its perturbations.

Q4: How are the negative score direction and the epistemic vs. aleatoric component chosen without inspecting labels from a new scenario? Can this rule be fixed in advance?

The negative direction is a single convention, applied to both components and all cohorts; it was never tuned per scenario. To remove the direction choice, we added a two-sided, label-free rule, fixed in advance: each component's log-trace is standardized by the mean and standard deviation of the ID inputs, and an input is scored by its absolute z-score, i.e., flagged when its uncertainty is unusual in either direction. ID inputs are scored with cross-fitting, and no OOD input, label or direction is used, so the rule applies unchanged to a new scenario. We have added it to the paper (Sec. 4.4 and Appendix H, Table 12). AUROC / AUPR:

MethodBBBC021 Unseen Pert.BBBC021 IntensityJUMP Unseen Cell LinesJUMP Intensity
MAP Aleatoric0.532 / 0.3630.552 / 0.5470.526 / 0.5340.581 / 0.505
SWAG Aleatoric0.639 / 0.5170.681 / 0.7110.534 / 0.5400.636 / 0.576
SWAG Epistemic0.639 / 0.5020.677 / 0.7010.532 / 0.5390.624 / 0.566
LA Aleatoric0.620 / 0.5030.679 / 0.7060.531 / 0.5470.612 / 0.569
LA Epistemic0.583 / 0.4000.651 / 0.6320.520 / 0.5200.356 / 0.396
MCD Aleatoric0.581 / 0.3910.602 / 0.5720.568 / 0.5700.457 / 0.436
MCD Epistemic0.556 / 0.3710.576 / 0.5490.553 / 0.5540.446 / 0.429
AVUQ Aleatoric0.554 / 0.3810.585 / 0.5690.581 / 0.5790.592 / 0.512
AVUQ Epistemic0.684 / 0.6070.689 / 0.7240.545 / 0.5430.667 / 0.586

Same per-input scores, inputs and labels as Table 5.

  • Direction. As expected for a test that does not use the direction, power is lower than with the one-sided score (e.g., AVUQ Epistemic 0.764 → 0.684 AUROC on BBBC021 Unseen Pert.). Nevertheless, AVUQ remains the most reliable approach: it is the best detector in all four cohorts (AUROC and AUPR), with the same component as under the one-sided score (Table 5): Epistemic on BBBC021 Unseen Pert., BBBC021 Intensity and JUMP Intensity, and Aleatoric on JUMP Unseen Cell Lines.
  • Component. The epistemic trace is the stronger AVUQ component in every cohort except JUMP Unseen Cell Lines, under the one-sided score (Tables 2 and 5) and the two-sided rule alike. We therefore use it as the fixed default, chosen once rather than per scenario.

W2 (MoA): 12.89% vs. 43.23% MoA accuracy under the combined shift, with an interval overlapping the closest baseline.

We agree that under the combined shift (the BBBC021 Unseen Pert. cohort) all generators remain far from real images, and SFM's interval overlaps those of the closest baselines. We have tempered the claim (Sec. 5.3): SFM improves generation under shift but does not by itself make generation trustworthy, which is why unreliable-generation detection is needed. In this cohort, AVUQ Epistemic is the best detector both in Table 2 (0.809 AUROC) and under the pairing-free label of Q3 (0.788).

We thank the reviewer again for the careful reading, which substantially improves the correctness, precision, and clarity of the paper.

Reviewer_C7LtOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

The contributions of the paper are twofold. Firstly, the authors conduct experiments on Stochastic Flow Matching and verify its robustness under distribution shift. Secondly, they propose a new sampling technique for uncertainty quantification of flow matching models. They conduct experiments on cellular imaging and brain fMRI datasets for two tasks: robust generation and unreliable output detection.

Critical strengths

The experiments are conducted on a range of datasets spanning two modalities.

AVUQ shows to be better at unreliable generation detection than other methods.

Critical weaknesses

The first contribution of this paper is not very significant. Firstly, the paper does not show any new methods or applications for Stochastic Flow Matching. The existing method is applied on an existing task to verify its property of robustness. The performance of this method on JUMP and Unseen Plates is not better than two other methods either.

The motivation for nested sampling and antithetic sampling is not clear. If nested sampling is so expensive, we can use non-nested sampling instead. The performance of non-nested MAP Aleatoric is very close to nested-antithetic AVUQ Aleatoric across 3 of 4 settings. Therefore, the use of nested sampling is questionable.

Questions for authors

What is the difference in performance between the same anomaly-scoring method with nested and antithetic sampling? Does antithetic sampling worsen performance?

2 comments

We thank the reviewer for the constructive comments.

W1: The first contribution is not significant: SFM is applied to an existing task, and on JUMP Unseen Plates it is not better than two other methods.

We agree that SFM itself is not new: marginal-preserving stochastic samplers have been used for noise-to-data generation (Song et al., 2020; Karras et al., 2022) and, by Su et al. (2025), to improve in-distribution distribution-to-distribution generation. They have not been used to improve generalization under distribution shift, which is what we study; we clarified this in Sec. 1. Our claims are:

  1. Generalization under scientific distribution shift. Across six unseen scenarios, SFM is best in five (Table 1). This significant demonstration on a challenging real-world problem will hopefully highlight the importance of SFM for improved distribution-shift robustness.
  2. A controlled ablation (Table 7) with the same architecture, data and training budget. Stochastic-interpolant training alone improves the deterministic FM baseline in 3 of 4 cohorts (e.g., FID 103.73 → 36.81 on BBBC021 Unseen Pert.), score-corrected sampling improves on it in all 4, and naive noise injection degrades both backbones.
  3. SFM is the backbone AVUQ needs. Our primary focus is on uncertainty quantification and SFM provides a key component building towards that. The aleatoric term requires a stochastic sampler, and deterministic FM with MC-Dropout (MCD-DFM) is clearly weaker for detection (e.g., 0.621 vs. 0.809 AUROC on BBBC021 Unseen Pert., Table 2).

JUMP Unseen Plates is the mildest shift (Table 3). As a result, multiple approaches suffice, which is to be expected.

W2: The motivation for nested and antithetic sampling is unclear; non-nested MAP Aleatoric is close to AVUQ Aleatoric in 3 of 4 settings.

Why nested. Each non-nested alternative gives only one component: MAP only aleatoric (its parameters are fixed), MCD-DFM only epistemic (its backbone is deterministic). The strongest detector in 3 of 4 cohorts is AVUQ's epistemic trace, which neither alternative provides (Table 2, AUROC):

BBBC021 Unseen Pert.BBBC021 IntensityJUMP Unseen Cell LinesJUMP Intensity
MAP Aleatoric (non-nested)0.6910.7110.7990.276
AVUQ Aleatoric0.7420.7290.8690.309
AVUQ Epistemic0.8090.7850.7940.890

AVUQ Aleatoric is also above MAP Aleatoric in all four cohorts (+0.02 to +0.07 AUROC), but the main benefit of nesting is the epistemic term.

Why antithetic. It makes nesting affordable. At the cost of MAP (4 SDE solves per input), AVUQ with 22 samples (Table 4) gives an epistemic score above MAP in 3 of 4 cohorts (0.752 / 0.785 / 0.826 vs. 0.691 / 0.711 / 0.276); in the fourth, its aleatoric score is above MAP (0.838 vs. 0.799). Without antithetic sampling, many more samples would be needed to keep the epistemic estimate from being dominated by leaked aleatoric Monte Carlo noise (Sec. 4.3).

Q1: What is the difference between the same scoring method with nested i.i.d. and with antithetic sampling? Does antithetic sampling worsen performance?

This comparison is in Table 2. The MCD rows (nested i.i.d.) and the AVUQ rows (nested antithetic) use the same MC-Dropout posterior, the same 44 budget and the same scores; only how the SDE noise is drawn differs: independent paths (MCD) vs. antithetic pairs ,- (AVUQ). AUROC, i.i.d. → antithetic:

BBBC021 Unseen Pert.BBBC021 IntensityJUMP Unseen Cell LinesJUMP Intensity
Aleatoric0.741 → 0.7420.720 → 0.7290.856 → 0.8690.438 → 0.309
Epistemic0.731 → 0.8090.729 → 0.7850.833 → 0.7940.418 → 0.890

Antithetic sampling targets the Monte Carlo variance of our epistemic estimate. As derived in Sec. 4.3 (Eq. 18), the naive nested estimator of epistemic uncertainty contains residual Monte Carlo noise of size A/K, i.e., aleatoric uncertainty leaking into the epistemic estimate; antithetic pairs shrink this term to (1+)A/K at no extra cost (Sec. 4.4). In practice, Table 8 shows a 1.82–4.29× reduction of this Monte Carlo variance at an equal sampling budget. The table shows the consequence for detection. With i.i.d. paths, the epistemic score behaves like the aleatoric one (their AUROCs differ by at most 0.023 in every cohort), as expected when the epistemic estimate is dominated by leaked aleatoric noise. With antithetic pairs, the epistemic score separates and becomes the best detector in Table 2 on BBBC021 Unseen Pert., BBBC021 Intensity and JUMP Intensity (e.g., 0.418 → 0.890). As a result, the better AVUQ component exceeds the better i.i.d. component in every cohort (0.809 / 0.785 / 0.869 / 0.890 vs. 0.741 / 0.729 / 0.856 / 0.438), and the same holds in all five cohorts of Tables 5 and 6. Antithetic sampling therefore improves detection.

We hope these clarifications address the reviewer's concerns and are happy to discuss further.

Reviewer_p7dQOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper presents diffusion models for uncertainty estimation using bayesian stochastic flow matching. It performs experiments on anomaly analysis and prediction, showing improvements over baselines. The labels are computed through prediction errors though.

Critical strengths
  1. Use sfm for uncertainty estimation is sound and reasonable.
  2. It ouperforms several baselines in anomaly detection.
Critical weaknesses
  1. This anomaly benchmark itself has some problematic parts: a. The anomaly labels are constructed using prediction errors b. Comparison against external OOD detectors is limited c. AUPR comparison has another issue: different class distributions
  2. The idea itself lacks novelty. As using bayesian flow matching is widely reported for uncertainty estimation in the literature.
Questions for authors

Please clarify the weakness I mentioned.

2 comments

We thank the reviewer for the constructive comments.

W1a: The anomaly labels are constructed using prediction errors.

Our interest is in flagging generated samples that are untrustworthy. To test our ability to do so, we generate a set of labels by comparing generations to real cell images and using error-based filtering to define a set that is close to real cells (class 0) and far from real cells (class 1). We then see if our anomaly score flags the appropriate class 1 generations. Table 5 reports the same comparison without any filtering: its labels are scenario provenance only and involve no prediction errors, and AVUQ remains the best detector in four of five cohorts. The only scenario where AVUQ has poor detection performance without the error-based filtering is on JUMP Unseen Plates, which is the mildest distribution shift and where SFM generalizes well (see Table 1). This is actually a positive result as we would not want to flag generations from a model that is robust to the Unseen Plate scenario as untrustworthy. Instead, the combination of Table 1 and Table 5 results demonstrate that our AVUQ method is flagging bad generations, not just unseen scenarios. We have updated the text in Sec. 5.3 (Unreliable Generation Detection Performance Analysis) to clarify this important point.

We also replaced the random-pair error with one that needs no paired target image: the pretrained MoA classifier of Table 11 judges each input's own 4 generations (MAP sampling), and the error is one minus the probability of the compound's annotated MoA, averaged over these generations. We use the same cohorts, methods and 0.5 rule as Table 2. AUROC / AUPR:

MethodBBBC021 Unseen Pert.BBBC021 Intensity Shift
non-nested
MAP Aleatoric0.709 / 0.6330.717 / 0.701
MCD-DFM Epistemic0.679 / 0.5160.674 / 0.609
nested-i.i.d.
SWAG Aleatoric0.706 / 0.6910.694 / 0.738
SWAG Epistemic0.723 / 0.7030.687 / 0.729
LA Aleatoric0.693 / 0.6630.672 / 0.702
LA Epistemic0.692 / 0.6580.698 / 0.728
MCD Aleatoric0.739 / 0.6870.701 / 0.726
MCD Epistemic0.726 / 0.6670.693 / 0.714
nested-antithetic
AVUQ Aleatoric0.717 / 0.6780.713 / 0.737
AVUQ Epistemic0.788 / 0.7860.733 / 0.778

AVUQ Epistemic is the best detector in all four entries (Appendix I, Table 13). This label is available only for BBBC021, because JUMP does not provide comparable MoA labels for its perturbations.

W1b: Comparison against external OOD detectors is limited.

Appendix F.3 (Table 9) compares against two external, unsupervised detectors fit on in-domain data only: ODEED (probability-flow ODE reconstruction) and PatchCore (patch-feature memory bank). AVUQ gives the best AUROC in all four cohorts. External detectors score whether the input is unusual, whereas we flag unreliable generations for a given source and condition, using only the generative model itself.

W1c: AUPR comparison: different class distributions.

We thank the reviewer for raising this point. Because AUPR depends on the positive rate, it is not comparable across cohorts. Within a cohort, all methods are evaluated with the same labeling rule, so comparisons within a column are valid; AUROC, which does not depend on prevalence, leads to the same conclusions. We now report each cohort's positive rate (the AUPR of a random detector) in Appendix C; for example, in the unfiltered Table 5 it is 50% (35% for BBBC021 Unseen Pert.).

W2: The idea lacks novelty, as Bayesian flow matching is widely reported for uncertainty estimation in the literature.

We thank the reviewer for pushing us to sharpen the novelty; we have revised the introduction (Sec. 1) accordingly. To our knowledge, Bayesian flow matching has not been widely used for uncertainty estimation. The closest methods target noise-to-data generation and estimate a single per-sample uncertainty: post-hoc Laplace approximations for pretrained diffusion or flow-matching models (BayesDiff; Jazbec et al., 2025) and a predicted velocity uncertainty for flow matching (Han et al., 2026). Hyper-Diffusion separates aleatoric and epistemic uncertainty but relies on costly nested sampling. None addresses distribution-to-distribution generation, where reliability must be judged for each source input and condition. We would be grateful for specific references and will gladly discuss them. The key hurdle, which our contributions address, is that a deterministic flow maps each source to a single output and therefore cannot express aleatoric uncertainty; a stochastic flow can, but separating the two terms then requires nested sampling over posterior draws and SDE paths, and at affordable budgets aleatoric Monte Carlo noise leaks into the epistemic estimate (Sec. 4.3, Eq. 18).

  • SFM for generalization under distribution shift. Marginal-preserving stochastic samplers have been used for noise-to-data generation (Song et al., 2020; Karras et al., 2022) and for in-distribution distribution-to-distribution generation (Su et al., 2025). We show that SFM improves generalization to unseen scientific scenarios (best in 5 of 6, Table 1), with a controlled ablation (Table 7).
  • AVUQ. Antithetic sampling reduces the leakage of aleatoric noise into the epistemic estimate by 1.82–4.29× at equal budget (Table 8). This is what makes the epistemic term useful: with the same posterior and budget, nested i.i.d. sampling yields two near-identical scores (MCD rows of Table 2), whereas AVUQ Epistemic is the best detector in 3 of 4 cohorts (e.g., 0.418 → 0.890 AUROC on JUMP Intensity Shift).
  • Unreliable-generation detection under shift. An AVUQ component is the best detector in all four cohorts of Table 2, and AVUQ outperforms external OOD detectors in all four cohorts (Table 9).

We hope these clarifications address the reviewer's concerns and are happy to discuss further.

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

Related papers

Discussion (0)

Sign in to comment.