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Under review as a conference paper at ICLR 2027

Zero Flux: Flow-Based Comparison of High-Dimensional Discrete Distributions

Abstract

Comparing two high-dimensional discrete distributions has always been a challenging task due to the exponentially growing state space and complex changes in interactions. A recent work suggests comparing distributions through a vector field trained using flow matching between two continuos distributions. The resulting vector field at mid-point vanishes if and only if two distributions identical. However, such a flow-based criterion does not naturally apply to discrete distributions. We extend this principle to the discrete domain and introduce the Zero Flux criterion, a discrepancy based on local probability fluxes. Under independent coupling, we show that all local probability fluxes vanish at the midpoint if and only if two distributions are the same. This discrepancy decomposes the joint distributional difference into smaller, local contributions and can be efficiently estimated from samples. We establish finite sample error bounds for our estimator. Experiments on synthetic and real categorical data demonstrate reliable recovery of sparse dependence signals and stable tracking of distribution shifts in high dimensions.

Primary area:
generative models
Keywords:
Discrete Distribution Comparison, Discrete Flow Matching

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_5aaPOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes the "Zero Flux" criterion/discrepancy that quantifies the "difference" between two (potentially) high-dimensional discrete distributions. The paper's main contribution is an extension of the recent "Zero Flow" Criterion using theory from discrete flow matching resulting in the Zero Flux criterion. The paper then defines a sample-based discrepancy from this criterion and shows that the discrepancy is invariant to independent irrelevant variables. Another theoretical contribution of the paper is a theoretical analysis of the Zero Flux discrepancy with regards to its error and how large the empirical discrepancy can be when the two distributions are the same. The empirical experiments of the paper also corroborates Zero Flux's invariance to independent irrelevant variables and shows that, under certain conditions, Zero Flux discrepancy is able to track distribution shifts better than other approaches. Lastly, the paper ends with a small case study by tracing the partisan separation of the U.S. over time to showcase a practical usecase of the Zero Flux discrepancy.

Critical strengths

The paper nicely links the recent Zero Flow Criterion with Discrete Flow Matching resulting in a discrete analogue of the Zero Flow Criterion (which they call the Zero Flux Criterion) in Theorem 3.4. Also, as far as I can tell, the proofs for the theory needed for the construction of the Zero Flux Criterion and Discrepancy (Propositions 3.2, 3.3, 4.1, 4.2 and Theorem 3.4) don't contain any obvious errors as well, so the theoretical contributions of the paper is motivated and situated well within the existing literature and is sound; thus making these contributions an interesting result for researchers familiar with the prior work.

Furthermore, the some of the experiments in the paper are well motivated as well. In particular, the experiment in Section 7.1 empirically demonstrates the result in Proposition 4.2 that shows that Zero Flux in invariant to independent irrelevant features/coordinates, a property that is vital when dealing with high-dimensional distributions in general. Furthermore, the experiments in Section 7.4 provides a nice casestudy into situations where having a discrepancy with properties like Zero Flux can be useful.

Critical weaknesses

The main weakness of the paper is that the main text lack discussions as to the method's limitations or situations where the method might not perform as well as other methods. For instance, in Table 1, we can see that Zero Flux is outperformed by 3 other methods (in terms of AUROC) for the Markov 8d dataset, but there doesn't seem to be any discussion about that. Furthermore, the only experiment that tests how Zero Flux responds when the order of the shifting dependence relation increases is relegated to Appendix F.1 and in this experiment Zero Flux seems to lose power when the dependence order increases. It would be nice if such a crucial limitation be mentioned somewhere in the main text or even just in the conclusion. Overall, the paper should be more forthcoming about its limitations.

Questions for authors

Section 7.2 compares Zero Flux's ability to detect distribution shifts against other methods, but without directly defining a threshold τ\tau to use. This is somewhat fine for the experiment since it showcases compares detection ability in the average or best case. But how would someone who would like to use the Zero Flux discrepancy for distribution shift detection set the threshold in practice? I mean eq 20 might be a good start, but that bound contains the E^\hat{\mathcal{E}} terms which involves a KL divergence with the exact posteriors.

Lines 417-418 (and later in line 1619 in the appendix) say that MNIST is binarised to {0,1}784\{0,1\}^{784}, but how exactly was it binarized? And why not discretizing the MNIST pixel values into more levels than just binary?

Also in the set of methods being compared against in Section 7.2 and 7.3 seem to be different. Most notably is the absence of Zero Flow since the one-hot construction in Section 7.1 seems to be extendable to any alphabet. Is there a reason why Zero Flow was left out in Section 7.3?

In Table 1 and Figure 7 in the Appendix, the AUROC of a couple of methods like Classifier-JS, VAE-ELBO, and VAE-IWAE seem to decrease as the contamination levels increases, especially on the Markov d=128 dataset. This seems somewhat un-intuitive for me since, I would expect that the problem of detecting distributional shift becomes easier as the second distribution Da(ϵ)D_a(\epsilon) contains less and less samples from the "null" distribution Db(0)D_b(0). So despite the problem (in principle) becoming easier as ϵ\epsilon increases, the AUROC decreases for these methods. Do you know the reason for this counterintuitive result?

Minor Comments

  • line 068: maybe state what is dd here.
  • eq 1: maybe define t here as well instead of just in eq 3
  • Line 114: "Since..." did you mean assume here? I might be misunderstanding this line .
  • line 264: maybe state where the mm evaluation midpoints come from.
  • Figure 3: seems vertically squished
4 comments
AuthorsOpenReview ↗

We Have Added a Limitations Discussion, Permutation-testing for Threshold Selection, and Expanded the Experimental Evaluation

We thank the reviewer for the constructive comments.

Weakness 1. Discussion of limitations

We have added a discussion of the limitations and dependence-sensitive behavior of Zero Flux in Sections 7.2 and 8, including the results of the higher-order interaction experiment in Appendix F.1.

There doesn't seem to be any discussion about Zero Flux being outperformed by three other methods (in terms of AUROC) on the Markov 8d dataset.

We have expanded the discussion of Table 1 in Section 7.2. On Markov 8d, LRD (0.982), Classifier-JS (0.977), and Zero Flow (0.958) all achieve higher AUROC than Zero Flux (0.874). LRD fits a first-order Markov likelihood that directly captures the change in transition probabilities between the reference and contaminating chains. Classifier-JS and Zero Flow also perform well on these short sequences without specifying a transition model.

On higher dimensional data like Markov 128d, however, Zero Flux achieves the highest AUROC among all methods except LRD (0.920 for Zero Flux and 1.000 for LRD). Zero Flux outperforms both Zero Flow (0.861) and Classifier-JS (0.424), demonstrating its ability to detect high-dimensional distributional differences directly from samples without specifying a Markov transition model or estimating the joint likelihood.

Sensitivity to higher-order interactions

The higher-order interaction experiment in Appendix F.1 characterizes the dependency-sensitive inductive geometry of Zero Flux. As the interaction order increases, the population discrepancy can decrease even when total variation and KL divergence remain fixed. This reflects the intrinsic sensitivity of Zero Flux to different dependency structures, while preserving population identifiability. A practical implication is that, as the population signal becomes smaller at higher interaction orders, its estimation can become more susceptible to posterior estimation errors and optimization noise, as discussed in Section 8.

Question 1. Practical threshold selection

In practice, the detection threshold for Zero Flux can be determined using a permutation test, a standard nonparametric approach under exchangeability [1, 2]. Given two independently sampled datasets from P0P_0 and P1P_1, we first compute the observed Zero Flux discrepancy. We then pool the observations and randomly permute their group labels while preserving the original sample sizes. For each permutation, we reinitialize and fully retrain the posterior networks to obtain a null statistic.

The detection threshold is then selected from the resulting permutation null distribution according to a prespecified significance level α\alpha. Specifically, we reject the null hypothesis when the observed discrepancy exceeds the corresponding threshold, or equivalently, when the permutation pp-value satisfies p≤αp\leq\alpha. This allows the threshold to be determined directly from the observed data without requiring knowledge of the exact posterior distributions or their approximation errors.

We have added this threshold selection procedure and its empirical evaluation in Appendix F.2. On MM128, using 100 permutations per trial across 50 independent trials at α=0.05\alpha=0.05, the selected thresholds successfully detect distributional differences in 98% and 100% of trials at ε=0.05\varepsilon=0.05 and ε=0.1\varepsilon=0.1, respectively (Table 5).

Question 2. MNIST preprocessing

We clarified the binarization procedure in Appendix E.2. MNIST images primarily consist of digit strokes against a background, making a binary foreground-background representation a natural choice. Moreover, binarized MNIST is an established benchmark in discrete generative modeling, as demonstrated by recent works [3, 4]. We therefore follow this commonly adopted setting, using a threshold of 0.5 after rescaling pixel intensities to [0,1].

Question 3. Additional UCI baseline

Response. We have added Zero Flow to the UCI comparison in Section 7.3 (Table 2). Zero Flux achieves a C-index of 0.994 and a Pearson correlation of 0.953, improving upon Zero Flow in both metrics.

Minor Comments

All minor comments have been addressed in the revised manuscript.

We thank the reviewer again for the helpful suggestions.

References

[1] Jesse Hemerik and Jelle Goeman. Exact testing with random permutations. TEST, 27(4):811–825, 2018.

[2] Markus Ojala and Gemma C. Garriga. Permutation Tests for Studying Classifier Performance. Journal of Machine Learning Research, 11(62):1833–1863, 2010.

[3] Mingue Park, Jisung Hwang, Seungwoo Yoo, Kyeongmin Yeo, and Minhyuk Sung. PairFlow: Closed-Form Source-Target Coupling for Few-Step Generation in Discrete Flow Models. ICLR 2026.

[4] Zijing Ou, Chinmay Pani and Yingzhen Li. Test-Time Alignment of Discrete Diffusion Models with Sequential Monte Carlo. ICLR 2026.

AuthorsOpenReview ↗

Question 4. Analysis of the counter intuitive AUROC behavior of Classifier-JS and VAE methods

We thank the reviewer for pointing out this interesting observation. We have added training trajectories, retrospective checkpoint comparisons, and a likelihood approximation error analysis in Appendix F.6 (Figures 13–14 and Tables 7–8).

Classifier-JS: Overfitting and early stopping

For Classifier-JS, the training trajectories indicate that continued optimization can lead to in-sample overfitting and deteriorating AUROC, while earlier checkpoints can achieve substantially stronger discrimination. Even with retrospectively AUROC-optimal checkpoints, Classifier-JS achieves AUROCs of 0.7028 and 0.9928 at ε=0.1\varepsilon=0.1 and ε=0.2\varepsilon=0.2, respectively, compared with 1.0000 for Zero Flux at both levels using its standard checkpoint (Table 7).

In our experiments, early stopping is based on the convergence of the respective training objectives, using training cross-entropy for Classifier-JS and ELBO-based likelihood estimates for VAE methods. However, there is no universal early-stopping criterion across different discrepancy estimators, as their estimation objectives and convergence behaviors differ. In particular, AUROC is a downstream evaluation metric that measures discrimination between null and alternative distributions rather than the convergence of the estimated discrepancy, and therefore should not serve as a common early-stopping criterion.

VAE-ELBO and VAE-IWAE: Relative likelihood approximation errors

For VAE-based methods, we train three VAEs: two separately on PP and QQ, and one on their mixture M=(P+Q)/2M=(P+Q)/2. The discrepancy is estimated through their ELBO or IWAE likelihood estimates:

D^VAE=E^P[ℓ^P(X)−ℓ^M(X)]+E^Q[ℓ^Q(X)−ℓ^M(X)]=S^+2G^M−G^P−G^Q,\widehat{D}_{\mathrm{VAE}} = \widehat{\mathbb{E}}_P[\widehat{\ell}_P(X)-\widehat{\ell}_M(X)] + \widehat{\mathbb{E}}_Q[\widehat{\ell}_Q(X)-\widehat{\ell}_M(X)] = \widehat{S}+2\widehat{G}_M-\widehat{G}_P-\widehat{G}_Q,

where S^\widehat{S} is the empirical discrepancy computed using the exact likelihoods, and G^P\widehat{G}_P, G^Q\widehat{G}_Q, and G^M\widehat{G}_M are the corresponding likelihood approximation errors.

Our analysis shows that the relative likelihood approximation errors among the three VAEs can dominate the underlying distributional separation, distorting the estimated discrepancy. For example, at ε=0.2\varepsilon=0.2, the empirical separation relative to the null is +0.149+0.149, while the relative approximation-error correction changes by −0.843-0.843 for VAE-ELBO, reversing the ordering of the estimated discrepancies. This explains the observed AUROC degradation, as further supported by the training trajectories and checkpoint comparisons in Appendix F.6.

We thank the reviewer again for motivating this additional analysis.

Due to the detailed response by the authors, especially regarding the addition of the discussion on the dependence-sensitive behavior of Zero Flux and its limitations, as well as a procedure for threshold selection, I will raise my rating from 3 to 4.

Thank you for your time and careful consideration of our responses. We remain available should you have any further questions or concerns.

Reviewer_B9vpOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The paper proposes Zero Flux, based on flow matching, to compare high-dimensional discrete distributions. In the proposed method, the authors use a local probability-flux criterion with additional theoretical guarantees. Moreover, they showcase its limitations on synthetic and real-world datasets. I find the formulation and theoretical analysis strong.

Critical strengths

Strengths:

  1. The overall idea and theoretical analysis are interesting to me.
  2. Decomposition through coordinates provides a useful way to spot divergence.
  3. The experimental evaluation is well conducted, involving multiple datasets and real-world data.
Critical weaknesses

Weakness:

  1. A clear discussion is needed regarding Zero Flux's performance in Table 1.
  2. The authors did perform a first-order Markov likelihood baseline comparison. However, a more flexible likelihood baseline may be interesting. I am fine with a discussion in this direction but keen to see something regarding this.
  3. A computational efficiency chart is needed; the authors should provide this information in the paper.
Questions for authors

Questions for rebuttal:

  1. Regarding Weakness 1, a clear discussion of Table 1 is needed.
  2. Regarding Weakness 2, I am keen to discuss this further and would appreciate some supporting evidence from the authors.
  3. Regarding Weakness 3, I am convinced that training neural posterior estimators might be attractive. However, I need some information about their efficiency.
3 comments
AuthorsOpenReview ↗

We Expanded Baseline Comparisons and Added Computational Efficiency

Weaknesses 1 Discussion of Table 1

We have expanded the discussion of Table 1 in Section 7.2 to clarify the performance of Zero Flux across different dependence structures and dimensions. The revised discussion highlights the advantage of structure-specific baselines on low-dimensional Markov data, while showing that Zero Flux improves over Zero Flow on Markov 128d and achieves competitive performance on HMM 128d and binarized MNIST. This clarifies the complementary role of Zero Flux as a high-dimensional discrete distribution comparison method without a prespecified parametric transition model.

Weaknesses 2 More flexible likelihood baselines

We would like to clarify that the original manuscript already included several likelihood-based approaches. Specifically, LRD uses fitted first-order Markov models on the Markov and HMM benchmarks, with likelihoods computed from the corresponding transition probabilities. On binarized MNIST, we use an autoregressive Transformer that factorizes the joint likelihood over tokens into a product of conditional probabilities and is trained by maximum likelihood. We also include VAE-ELBO and VAE-IWAE as latent-variable likelihood estimators, which approximate the marginal log-likelihood through variational lower bounds (Section 7.2, Table 1; Appendix E.2).

Following the your suggestion, we further introduced second-order Markov and two-state HMM likelihood models (Appendix F.5, Table 6). On HMM 128d, their mean AUROCs reach 0.857 and 0.930, respectively, compared with 0.522 for the first-order Markov model. These results demonstrate that likelihood-based methods can achieve strong discrimination when the underlying dependence structure is adequately captured by the specified likelihood family.

However, we would like to emphasize that the effectiveness of likelihood-based comparison relies on having a tractable likelihood or accurately estimating it. When the underlying likelihood is unknown, particularly for complex high-dimensional distributions, learning an accurate likelihood model can itself be challenging. This distinction is reflected in our experiments: while LRD performs strongly when the Markov likelihood structure is available, autoregressive and variational likelihood estimation on MNIST does not provide comparably effective distributional discrimination.

We further analyze the VAE results in Appendix F.6 (Figure 14 and Table 8). Exploiting the tractable likelihood of MM128, we decompose the empirical VAE discrepancy into the exact empirical likelihood-ratio separation and a correction arising from differences in likelihood approximation errors among three VAE models: two trained separately on the respective endpoint datasets and one trained on the combined samples from both datasets. The results show that this correction can dominate the genuine distributional separation, explaining the poor discrimination of VAE-based methods.

In contrast, Zero Flux does not require specifying or accurately estimating the joint likelihood. It directly estimates endpoint-coordinate posteriors and provides competitive detection performance across different settings, including MM128, HMM128, and binarized MNIST, while additionally providing coordinate-wise contributions and local probability fluxes. Thus, Zero Flux provides a general framework for comparing high-dimensional discrete distributions directly from samples, without requiring a model or estimate of the joint likelihood.

Weakness 3. Computational efficiency

We have added this analysis in Appendix F.4 (Figure 10). On MM128, Zero Flux takes longer per comparison than training-free MMD (19.15 seconds versus 0.033 seconds on an NVIDIA A100), but achieves a higher AUROC (1.000 versus 0.806). The same trained posterior networks also show which coordinates contribute most to the global discrepancy and the direction of probability flux along individual transitions. Thus, the additional computation yields both stronger detection on MM128 and a way to localize the detected differences without further training.

We thank you again for these helpful suggestions.

Thanks for the clarification. I am happy with the effort put. I will raise my scores.

Thank you for taking the time to review our revisions. We’re glad the clarifications addressed your concerns, and we appreciate your feedback, which helped us improve the manuscript.

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

This authors extend the Zero Flow two-sample test, in which the midpoint velocity of a flow-matching bridge vanishes iff the endpoint distributions are identical, to high-dimensional discrete distributions. The key contributions are:

  • A discrete Zero Flow-like ("Zero Flux") criterion: on the discrete flow-matching bridge between independently coupled endpoints, the velocity is replaced with a local probability flux, i.e., the net probability flow along edges that flip a single coordinate. The authors prove that all midpoint fluxes vanish iff the two joint distributions are identical.
  • A sample-based discrepancy D∗∈[0,4⋅dim]D^* \in [0, 4 \cdot dim] that is identifiable, symmetric, and decomposes into interpretable per-coordinate contributions (thus also provably ignoring irrelevant independent coordinates).
  • A neural estimator (via two categorical posterior heads trained by cross-entropy) with a finite-sample error bound separating sampling error from posterior estimation error. The experiments show accurate recovery of sparse dependence changes up to dimension 256256, reliable tracking of distribution shifts (Markov/HMM/binarized MNIST), and an interpretable decomposition of partisan separation in the Nationscape survey.
Critical strengths
  1. The theory is thorough. The authors provide a complete identifiability result, a proved discrete continuity equation, an invariance-to-irrelevant-coordinates guarantee, and a full finite-sample error decomposition with an exact null bound.
  2. The experiments are rather diverse: dependence changes with matched univariate marginals (sparse recovery, UCI degradation), contamination/shift detection (Markov, HMM, binarized MNIST), and a real-world application (Nationscape). In the sparse-recovery setup, Zero Flux keeps sign agreement at 1.0001.000 as dimension grows to 256256, while the coordinate-wise baselines collapse to near random guess.
  3. The discrepancy appears to be interpretable. For instance, the authors argue that the signed, context-dependent flux localizes both where and in which direction the two distributions differ, and the per-coordinate decomposition attributes the total to individual coordinates.
Critical weaknesses
  1. The proposed object is not a test in the statistical sense: there is no null distribution, no type-I error control, and no pp-value procedure (the paper gives an almost-sure exact-null bound (Cor. 5.2) but it is an upper bound depending on the uncontrolled posterior error). There is also no separation analysis: no lower bound on D∗D^* under fixed alternatives, no minimax rate, and no analysis of how detectability scales with the perturbation size (η,ε)(\eta, \varepsilon). The empirical AUROC/FPR protocol is a reasonable practical substitute but is not backed by theory.

    Moreover, even the provided bound is written in terms of E^r\widehat{\mathcal{E}}_r, for which no approximation or estimation rate is given.

  2. Baseline coverage is uneven. The strongest competitors (LRD, classifier-JS, Deep MMD, VAE-ELBO/IWAE) appear only in the contamination study (Sec. 7.2, Table 1); the UCI study (Sec. 7.3) compares only against MMD, MMD-FUSE, and Cramer's V, and the Nationscape study (Sec. 7.4) only against MMD variants. The evidence that Zero Flux beats the best available methods is thus concentrated in one of the four regimes.

    The method also trains a large network (two categorical heads, one per endpoint, each with per-coordinate outputs; up to 80k steps / 1000 epochs), with no compute-vs-accuracy comparison against near-free kernel methods, leaving the practical cost of the interpretability gain open.

  3. The range of D∗D^*, [0,4d][0, 4d], and the concentration term both scale with dd; the authors normalize by dd ad hoc in some experiments (e.g., Nationscape, UCI) but offer no principled dimension-free scale, so absolute D∗D^* values are not comparable across dimensions.

Questions for authors
  1. In Appendix C.2 you show the independent-coupling assumption is essential. Have you explored whether there exist other couplings that also admit a provable Zero Flux-type characterization?
3 comments
AuthorsOpenReview ↗

We have added a quantitative separation analysis, a permutation testing procedure and expanded the experimental comparisons.

Weakness 1. Statistical testing and theoretical guarantees

The proposed object is not a test in the statistical sense: there is no null distribution, no type-I error control, and no p-value procedure.

We thank the you for pointing out this interesting extension. Following this suggestion, we study Zero Flux under a permutation-based two-sample testing framework (Appendix F.2). Under the null hypothesis, exchangeability provides finite-sample Type-I error control through permutation calibration, while the resulting permutation distribution provides a practical procedure for selecting the detection threshold at a prespecified significance level. We reinitialize and fully retrain the posterior networks for each permutation. On MM128, using 100 permutations per trial across 50 independent trials, the empirical Type-I error is 2%, while the statistical power reaches 98%,and 100% at ε=0.05\varepsilon=0.05 and 0.10.1, respectively (Table 5).

No lower bound under fixed alternatives and no analysis of how detectability scales with the perturbation size.

We have established a quantitative separation result (Proposition D.6, Appendix D.2.1). For the contamination model Qε=(1−ε)P+εRQ_\varepsilon=(1-\varepsilon)P+\varepsilon R with P≠RP\ne R, we prove that the population discrepancy D∗(P,Qε)D^*(P,Q_\varepsilon) is strictly increasing in ε\varepsilon and satisfies the quadratic lower bound

D∗(P,Qε)≥c(P,R)ε2,D^*(P,Q_\varepsilon)\geq c(P,R)\varepsilon^2,

where c(P,R)>0c(P,R)>0 depends only on PP and RR. Under a full-support condition, we further show that the population discrepancy is approximately proportional to the square of the contamination level near the null Q0=PQ_0=P.

No approximation or estimation rate is given.

We clarify that Theorem 5.1 provides an oracle-to-estimator error decomposition rather than an architecture-specific posterior learning rate. Our focus is on introducing Zero Flux as a distributional discrepancy and establishing its theoretical properties and finite-sample estimation guarantees.

Specifically, Theorem 5.1 establishes a high-probability error bound separating endpoint and midpoint sampling fluctuations from posterior approximation errors, quantified through empirical excess cross-entropies E^0\widehat{\mathcal{E}}_0 and E^1\widehat{\mathcal{E}}_1. This guarantee holds for arbitrary categorical posterior networks with finite empirical excess cross-entropy, including networks trained and evaluated on the same samples. We leave posterior estimation convergence rates for specific neural architectures, as well as minimax-optimal testing rates, for future work. We thank you for pointing out these interesting research directions.

Weakness 2. Baseline coverage and computational efficiency

Baseline coverage is uneven, particularly in the UCI and Nationscape experiments.

We have expanded the baseline comparisons in both experiments. On UCI (Section 7.3, Table 2), we additionally include Deep MMD, Classifier-JS, and Zero Flow. Excluding the task-aligned Cramér's VV reference, Zero Flux achieves the highest C-index (0.994) and a Pearson correlation (0.953) nearly matching the best-performing method (0.955), while maintaining a near-zero NVI (0.002) and improving upon Zero Flow across all three metrics.

For Nationscape (Appendix F.3, Figures 11–12), we additionally compare with Classifier-JS and Zero Flow. Both Zero Flux and Zero Flow capture a pronounced increase in January 2021, while the MMD variants show a decline and Classifier-JS does not capture a comparable increase. Furthermore, the coordinate-wise decomposition of Zero Flux identifies the policy-item contributions underlying its temporal changes.

No compute-vs-accuracy comparison against near-free kernel methods.

We have added a computational efficiency analysis (Appendix F.4, Figure 10). On MM128, MMD achieves an AUROC of 0.806 in 0.033 seconds, whereas Zero Flux reaches an AUROC of 1.000 in 19.15 seconds on an NVIDIA A100. The same posterior networks provide the global discrepancy, coordinate-wise contributions, and local flux field. These results quantify the computational trade-off: Zero Flux incurs additional neural estimation costs compared with training-free MMD, while achieving substantially higher detection AUROC and providing coordinate-wise and local flux information.

AuthorsOpenReview ↗

Weakness 3 Discrepency Normalisation and Question 1 Alternative coupling constructions

Weakness 3. Dimension normalization

The range of D∗D^* and the concentration term both scale with dd, with no principled dimension-free scale.

We clarify that the dimension normalization of Zero Flux is motivated by both its intuitive interpretation and its theoretical estimation guarantees.

First, from an intuitive perspective, Zero Flux is additive over coordinates, $D^* =\sum_{i=1}^d D_i^* $, where each coordinate-wise discrepancy satisfies Di∗∈[0,4]D_i^* \in[0,4]. Therefore, the normalized discrepancy D∗/dD^*/d naturally represents the average coordinate-wise discrepancy, with a uniformly bounded range [0,4][0,4] independent of the dimension.

Second, from a theoretical perspective, applying this normalization to Theorem 5.1 yields

\left|\frac{D^*}{d}-\frac{\widehat D_{n,m}}{d}\right| \leq{}& 4\sqrt{\left(\frac{1}{n}+\frac{1}{2m}\right)\log\frac{2}{\delta}} +4\sqrt{\frac{\widehat D_{n,m}}{d}} \left(\sqrt{\widehat{\mathcal E}_0}+\sqrt{\widehat{\mathcal E}_1}\right) +4\left(\sqrt{\widehat{\mathcal E}_0}+\sqrt{\widehat{\mathcal E}_1}\right)^2. \end{aligned}$$ Importantly, **the right-hand side no longer contains explicit dimension factors**, establishing an estimation bound for the average coordinate-wise discrepancy without explicit dependence on $d$. The posterior estimation errors may still depend implicitly on the dimension. Furthermore, Proposition 4.2 establishes invariance to independent irrelevant coordinates: adding coordinates that are independent of the original variables and identically distributed under both endpoints leaves the original coordinate contributions unchanged and assigns zero discrepancy to the added coordinates. This complements the normalized discrepancy by preserving the ability to identify which coordinates contribute to distributional differences. We thank the reviewer for pointing out the need for a clearer theoretical justification. We have now added a discussion of this normalization in the theoretical analysis section of the revised manuscript. ## Question 1 Existence of Alternative Coupling > whether there exist other couplings that also admit a provable Zero Flux-type characterization We thank you for this interesting question. Our current identifiability theorem relies on the independent-coupling assumption, and replacing it with an arbitrary coupling would fall outside the theorem's assumptions. Indeed, the counterexample in Appendix C.2 demonstrates that an arbitrary coupling can introduce nonzero directional midpoint flux even when the endpoint distributions are identical. Nevertheless, this does not preclude other structured couplings from admitting a provable Zero Flux-type characterization. As a concrete example, we consider an optimal transport coupling under the Hamming ground metric. The resulting coordinate-wise discrete bridge forms a constant-speed Wasserstein-1 geodesic, satisfying $$W_1(P_s,P_t)=(t-s)W_1(P_0,P_1).$$ Using the continuity equation and this geodesic property, we can establish that all midpoint local fluxes vanish if and only if $P_0=P_1$. This provides an alternative midpoint identifiability characterization under optimal transport coupling. The results have been included in Appendix D.2.2. We retain independent coupling in this work because it enables direct sample-based estimation without solving an additional transport problem, while providing the identifiability and finite-sample guarantees established in our analysis. Extending the finite-sample theory to estimated OT couplings and investigating entropically regularized alternatives such as Sinkhorn coupling are interesting directions for future work. We thank you again for these helpful suggestions.

Thank you for your time and effort for reviewing our work! We would be happy to address any further questions or concerns you may have during the rebuttal discussion period.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of Revisions

Summary of Revisions

We thank the reviewers for their constructive feedback. We have revised the manuscript to include the following theoretical results, experiments, and methodological clarifications.

  1. Separation Lower Bound under Fixed Alternatives and Scaling with Perturbation Size (dKeQ, W1). For the contamination model Qε=(1−ε)P+εRQ_\varepsilon=(1-\varepsilon)P+\varepsilon R in Section 7.2, we prove that the population discrepancy D∗(P,Qε)D^*(P,Q_\varepsilon) is strictly increasing in ε\varepsilon when P≠RP\ne R and satisfies the quadratic lower bound

    D∗(P,Qε)≥c(P,R)ε2,D^*(P,Q_\varepsilon) \geq c(P,R)\varepsilon^2,

    where c(P,R)>0c(P,R)>0 depends only on PP and RR. Under a full-support condition, we also derive a local expansion showing that the discrepancy has exact quadratic order near the null Q0=PQ_0=P (Proposition D.6, Appendix D.2.1). Under a full-support condition, we further show that the population discrepancy is approximately proportional to the square of the contamination level near the null Q0=PQ_0=P (Proposition D.6, Appendix D.2.1).

  2. Permutation-Based Hypothesis Testing and Threshold Selection (dKeQ, W1; 5aaP, Q1). We extended the Zero Flux framework to permutation-based two-sample hypothesis testing, with posterior networks fully retrained for each permutation. This provides a practical procedure for selecting the detection threshold at a prespecified significance level. We report empirical Type-I error and statistical power in Appendix F.2.

  3. Expanded baseline comparisons (dKeQ, W2; B9vp, W2; 5aaP, Q3). We added Deep MMD, Classifier-JS, and Zero Flow to the UCI experiments (Section 7.3, Table 2), and Classifier-JS and Zero Flow to the Nationscape comparisons (Appendix F.3, Figures 11–12). We also added likelihood baselines based on a second-order Markov model and a two-state HMM (Appendix F.5, Table 6).

  4. Computational efficiency analysis (dKeQ, W2; B9vp, W3). We compared AUROC against GPU computation time on the 128-dimensional Markov model (MM128). The comparison includes training-free MMD and Zero Flux evaluated at several optimization checkpoints (Appendix F.4, Figure 10).

  5. Training behavior analysis (5aaP, Q4). We examined why the reported AUROC can decrease as contamination increases on MM128 for Classifier-JS and VAE-based methods. We analyzed the AUROC trajectories of Classifier-JS, VAE-ELBO, and VAE-IWAE over training and compared checkpoints retrospectively (Appendix F.6, Figures 13–14 and Tables 7–8).

  6. Discussion of experimental findings and limitations (B9vp, W1; 5aaP, Critical Weakness). We expanded the discussion of Table 1 and incorporated the higher-order interaction analysis from Appendix F.1 into the main text and conclusion. We clarified how sensitivity to dependence affects the interpretation of Zero Flux and discussed the computational cost of learning the posterior networks (Sections 7.2 and 8).

  7. Methodological and presentation clarifications (5aaP, Minor Comments). We clarified how the midpoints used for evaluation are sampled in Section 4.3, revised the relevant notation and definitions, and updated Figure 3.

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