- Rating
- 3
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
Read review
Paper summary
This paper proposes an anomaly detection framework built on conditional flow matching. The core idea is to learn an invertible transport map that projects the reference distribution onto a standard Gaussian distribution. Under an ideal transport, the squared norm of transformed normal samples follows a chi-squared distribution, which enables analytically calibrated thresholds with explicit Type I error guarantees.
Critical strengths
- This work establishes a rigorous theoretical chain from model training loss to statistical detection guarantees, which is a contribution to deep learning-based anomaly detection.
- The paper creatively combines flow matching with classical statistical hypothesis testing for anomaly detection.
Critical weaknesses
- Theoretical bounds lack tightness and are misaligned with the practical pipeline. The derived upper bounds include the exponential Lipschitz constant, which can be extremely large in high-dimensional settings such as images. This makes the bounds too loose for quantitative practical guidance, and they function more as existence guarantees than usable error estimates.
- The paper acknowledges that independent coupling introduces an irreducible variance D that prevents loss from converging to zero, and proposes Reflow to mitigate this issue. However, the theoretical bounds are not extended to the Reflow setting, creating a gap between the theoretical analysis and the actual algorithm used in experiments.
- Limited competitiveness on mainstream vision OOD benchmarks. While the method ranks first among methods trained exclusively on in-distribution data, it lags significantly behind pretrained-backbone methods on image OOD tasks. Although the authors correctly note that pretrained methods do not transfer to non-image domains, the paper omits comparisons with more recent non-pretrained flow matching/diffusion OOD methods, making it hard to assess the relative advantage of this framework within the same method category.
- The paper's central selling point is explicit Type I error control. However, empirical validation of false alarm alignment is only conducted on synthetic K-distributed data. No corresponding experiments verify how closely the actual false alarm rate matches the nominal level when using the analytic chi-squared threshold on image or biological data. This weakens the theory-practice connection for real-world high-dimensional applications.
- The related work section only briefly mentions a small number of flow matching detection works. No direct experimental comparison is performed with these methods, so it remains unclear what specific advantages the proposed calibrated-test framework offers over other flow-based anomaly detection approaches.
Questions for authors
Please see Weaknesses.
2 comments
Thanks for your reponnse.
We thank the reviewer for the careful and constructive review. Tables R1–R8 are in the common comment.
W1: the theoretical bounds lack tightness, with an exponential Lipschitz constant.
We agree that the exponential Lipschitz constant is a worst case. In the revision, instead of bounding how fast two trajectories can drift apart anywhere in space (via Grönwall), we write the error exactly as the velocity error along the true trajectory, carried back to t=0 by the Jacobian of the learned flow (the classical Alekseev–Gröbner formula). The constant is then the size of this Jacobian where the data lie, which we measure by automatic differentiation. The bound, however, can be evaluated numerically only when the true transport is known (Gaussian and spherical distributions), since LFM requires the true velocity field.
On Gaussian references (d=4,8), the bound of Lemma 1 is within a factor of 9 to 12 of the measured transport error (Table R8). We have no such evidence in high dimension: the bound cannot be evaluated on images. The bounds have a supporting role and are not meant to certify a level numerically; the revised title, introduction and conclusion no longer speak of guarantees.
W2: the theoretical bounds are not extended to the Reflow setting.
We now state explicitly that Lemma 1 controls the transport towards the distribution a model is trained on: PH0 for the first round, the samples of the previous model afterwards. A bound with respect to PH0 across rounds remains open. Proposition 2, however, depends only on the transport error of the deployed map, so it also applies to reflowed models.
Besides, Reflow is not needed for the bound to vanish. D does not depend on the model, and our proof already bounded the transport error by the excess loss LFM=LCFM−D (Eq. 26). Only the statement used LCFM, because it can be computed, which is why the bound had a floor. We made two changes:
Empirically, Reflow is not uniformly beneficial: at a 1% type-I error with SVHN as ID, the model without Reflow detects more (Table R5).
W3, W5: limited competitiveness on vision OOD benchmarks; no comparison with recent flow matching/diffusion detection methods.
The revision removes the "Avg" column and presents this scenario as a limitation, whose cause is discussed in our response to Reviewer uus6 (W2): our statistic is the flow's likelihood without its volume term and partly inherits the failure of likelihood-based detection (Nalisnick et al., 2019). The detection requires the shift of ∣∣z∣∣2 between the 2 hypotheses to exceed the spread of its χ2 distribution (2d, d=3072 for image OOD scenario); otherwise the score distributions overlap. Future work can mitigate this limitation by feature extraction: in preliminary results, Table R1, our method ranks first or tied for first as well from Table R4 in three of the six OOD scenarios among pretrained-backbone methods
Regarding methods of the same category, Table 1 already included DDPM-OOD (Graham et al., 2023), a diffusion model trained on ID data only; we could not add further non-pretrained image baselines during the rebuttal. We added TCCM (Li et al., 2025), a flow-matching baseline designed for anomaly detection, on ADBench, where our method obtains the best AUROC on six of seven datasets (Tables R2 and R7). The other flow matching works address different problems: failure detection for robot policies (Sun et al., 2026; Xu et al., 2025) and generalization of conditional flow matching to unseen conditions (Pham, 2026). To our knowledge, none of these works provides a test statistic with a known distribution under H0, nor do they address radar detection.
W4: false alarm alignment is only validated on synthetic data, not on image or biological data.
We concede this point: the agreement between the realised and nominal false-alarm rates is only verified on synthetic data. As stated in our response to Reviewer uus6 (Q2), the analytic threshold is not yet reliable on images, and we have not evaluated it on the biological data. However, first, K-distributed clutter is a standard model of heavy-tailed clutter in radar detection. Second, the study added for Reviewer uus6 (Table R6) shows when this threshold is useful in practice: at the false-alarm rates used in radar (α=10−5), an empirical threshold needs about 107 samples, and none can even be computed from our 5×104 training samples, whereas the analytic threshold gives a realised rate on Gaussian data (d=4,8).