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Under review as a conference paper at ICLR 2027

Hyperbolic Live-Manifold Learning for Generalizable Face Anti-Spoofing

Abstract

Generalizable face anti-spoofing (FAS) aims to learn liveness representations that remain discriminative across unseen domains. Most methods optimize live and spoof samples symmetrically in Euclidean space, overlooking their structural asymmetry: live samples tend to share coherent liveness properties, whereas spoof samples vary substantially across attack types and domains. Such symmetric modeling makes it difficult to preserve a stable live structure while accommodating diverse spoof patterns. To address this issue, we propose HypLive-FAS, which organizes live representations into a compact manifold in hyperbolic space and identifies spoof samples through their deviations from this manifold. The expanding capacity of hyperbolic space away from the live region allows heterogeneous spoof patterns to be accommodated without forcing them into a unified cluster. Specifically, Hyperbolic Live-Manifold Learning (HLM) constructs a live-centered manifold primarily from live samples while encouraging spoof samples to remain separated from it, thereby reducing their interference with the intrinsic live structure. While HLM captures this asymmetric class structure, the learned manifold may still drift under domain-specific appearance variations. We therefore introduce Liveness-Preserving Augmentation (LPA), which perturbs domain-dependent appearance while enforcing representation- and prediction-level consistency between original and augmented samples, improving the stability of the learned liveness structure. Extensive experiments on multiple benchmarks demonstrate that HypLive-FAS achieves competitive cross-domain generalization and consistently outperforms existing methods.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
face anti-spoofing, domain generalization, hyperbolic learning, manifold learning, vision-language models

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 2 reviews, above 85% of the others.
Reviewer_amWgOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper is motivated by the observed asymmetry between bona-fide and spoof face samples in terms of their class distributions and feature representations. Based on this observation, the paper proposes HypLive-FAS, a hyperbolic live-manifold learning framework that models bona-fide representations using a PCA-anchored nonlinear manifold and identifies spoof samples through Jacobian-guided deviations from the learned manifold. Moreover, a liveness-preserving augmentation strategy further improve generalization capability. The experiments on commonly-used FAS datasets demonstrate competitive performance against existing methods.

Critical strengths

The experiment results show competitive performance against existing methods under cross-domain protocols, and the ablation studies provide empirical evidence for the effectiveness of the proposed components.

Critical weaknesses
  1. The motivation that bona-fide faces exhibit compact and consistent representations while spoof samples are heterogeneous has been extensively explored in prior FAS studies. Both one-class asymmetric representation and hyperbolic manifold-based learning have been extensively explored in recent studies. However, this paper proposed insufficiently novel contributions to the FAS community.
  2. Although the paper introduces a PCA-anchored nonlinear manifold and Jacobian-guided deviation scoring, their fundamental differences and advantages over existing approaches are not sufficiently established. Consequently, the methodological contribution appears incremental.
Questions for authors

What is the specific motivation of adopting PCA-anchored nonlinear manifold and Jacobian-guided deviation scoring, or why the authors use these two methods as the implementation scheme. If additional ablation study can demonstrate the effectness these two desgins over simpler alternatives.

5 comments
AuthorsOpenReview ↗

Response to W1

Thank you for the comment. We agree that live compactness, spoof heterogeneity, class asymmetry, and hyperbolic representation learning themselves are not concepts introduced for the first time in this paper. The contribution of this work lies in translating these priors into a concrete mechanism for live-structure modeling and attack discrimination.

Existing asymmetric FAS methods shape class distributions at different levels. SSDG aggregates live samples and disperses spoofs using domain relationships, but domain labels do not directly describe the structure of live samples themselves. DiVT enhances class compactness through live concentration and spoof separation, but a global concentration constraint is not well suited to representing legitimate intra-class variation caused by identity, pose, and illumination. TACL adjusts local representations through sample relationships and token-level contrastive learning, but it does not explicitly construct a reconstructable live manifold or structurally decompose local residuals.

In contrast, HypLive-FAS learns a PCA-anchored nonlinear manifold from source-domain live samples and uses a sample-dependent Jacobian to fit local live variation. It then uses the remaining regularized deviation for attack discrimination. Thus, the distinction of this paper does not lie in proposing class asymmetry again, but in realizing it as a unified mechanism of live-structure learning, local-variation explanation, and deviation scoring.

Existing hyperbolic FAS methods also use hyperbolic space, but their hyperbolic modeling mainly serves instance–prototype relationships, hierarchical prototype modeling, distribution alignment, or hyperbolic classification. For example, HPDR primarily uses hyperbolic space to model relationships among instances, prototypes, and hierarchical prototypes, while HML-FAS combines hyperbolic enhancement, distribution alignment, and a hyperbolic classifier to learn robust cross-domain representations. In contrast, HypLive-FAS further exploits the negative curvature and radial expansion of hyperbolic space to directly construct a compact source-domain live manifold and discriminate attacks through local deviations from this manifold.

We have further clarified these distinctions in the Related Work section of the revised manuscript and added Table 7 to verify the roles of the PCA anchor, nonlinear decoder, and sample-dependent Jacobian.

AuthorsOpenReview ↗

Response to W2 & Q2 (part 1)

Thank you for your question.

The specific motivation for using a PCA-anchored nonlinear manifold is as follows: the centered live tangent-space representation lies in a 512-dimensional space, but its shared authenticity cues are expected to concentrate along a smaller number of principal variation directions. PCA extracts these principal directions from source-domain live samples and provides a stable initialization for subsequent nonlinear manifold learning. Starting from the linear structure initialized by PCA, the nonlinear decoder further learns the local curvature of the live manifold, while the anchoring term prevents this structure from deviating too far from the PCA prior.

This choice is consistent with our modeling assumption about live structure in FAS. The live attributes of a real face arise from its genuine facial structure and direct capture process. Although they are affected by identity, pose, illumination, and imaging conditions, these variations are usually dominated by a limited number of factors. Therefore, the effective variation dimensionality of live features in the 512-dimensional space is expected to be lower than the original feature dimension. PCA extracts the principal directions with the largest variance from source-domain live samples and compresses live information into a low-dimensional subspace. Thus, PCA is not an arbitrary generic dimensionality-reduction operation; it is a structural initialization that matches the FAS assumption that shared live cues concentrate along a small number of principal directions.

The motivation for Jacobian-guided deviation scoring is as follows: the raw reconstruction residual does not necessarily correspond entirely to spoof cues. It may contain normal variation along the live-manifold directions. Some genuine samples may lie at different positions on the live manifold, and their changes in identity, pose, illumination, or imaging conditions may also produce a large reconstruction residual. Although these variations are not fully recovered by the low-dimensional reconstruction, they may still follow local directions of the live manifold and therefore should not simply be treated as spoof cues.

Let

\tilde y=G(a),\qquad r=y-\tilde y.$$ Around the current sample position $a$, the decoder can be represented by the first-order Taylor expansion $$G(a+\Delta a) \approx G(a)+J_G(a)\Delta a,$$ where $$J_G(a)=\frac{\partial G(a)}{\partial a}$$ is the decoder Jacobian at the current sample position. The Jacobian provides the local live-variation directions around the current sample. Through regularized local fitting with a ridge term and a primitive prior, we estimate the variation that can be explained by the current live manifold, $J_G(a)\hat{\Delta a}$, and compute $$r_{\mathrm{unexplained}}=r-J_G(a)\hat{\Delta a}.$$ The local fitting therefore attempts to absorb changes that can be explained by the live manifold, while the remaining regularized deviation is used as the spoofness score. A larger score indicates that the sample is more difficult to explain using live structure and is therefore more likely to be a spoof. This motivation is supported jointly by the Jacobian-related residual ablation in the original manuscript and by the new structured ablations that address the simple alternatives suggested by the reviewer. In the original results, the mean HTER/AUC were **2.73%/99.09%** when using the raw reconstruction residual, **1.82%/99.52%** after adding Jacobian local fitting, and **1.19%/99.64%** after further adding the primitive prior. These results indicate that Jacobian local fitting filters out some variation explainable by live structure, while the primitive prior provides an additional constraint on the local fitting.
AuthorsOpenReview ↗

Response to W2 & Q2 (part 2)

To directly answer the reviewer's question about why we use a PCA-anchored nonlinear manifold and Jacobian-guided deviation scoring, and whether they outperform simpler alternatives, we conducted supplementary comparisons on the four target domains of Protocol 1 with three random seeds. The data splits, training recipe, evaluation method, and checkpoint-selection rule were kept identical:

\hline \text{Variant} & \text{Change relative to the full model} & \text{HTER (\\%)} & \text{AUC (\\%)} \\\\ \hline \text{Full HypLive-FAS} & \begin{array}{l} \text{PCA anchor, nonlinear decoder,} \\\\ \text{and sample-dependent Jacobian all retained} \end{array} & \mathbf{1.19} & \mathbf{99.64} \\\\ \text{Linear decoder} & \begin{array}{l} \text{Nonlinear decoder replaced with} \\\\ \text{a learnable linear decoder} \end{array} & 2.04 & 99.39 \\\\ \text{w/o PCA anchor} & \begin{array}{l} \text{Nonlinear decoder retained, but} \\\\ \text{PCA subspace anchoring removed} \end{array} & 2.09 & 99.36 \\\\ \text{Shared linear direction} & \begin{array}{l} \text{Sample-dependent } J(a) \text{ replaced with} \\\\ \text{a shared learnable } W_0 \end{array} & 1.87 & 99.47 \\\\ \hline \end{array}$$ First, the linear decoder retains only a global linear structure, and its HTER increases to 2.04%, indicating that a purely linear structure cannot adequately describe the local curvature of the live manifold. Second, after removing the PCA anchor, the nonlinear decoder is still used, but HTER increases to 2.09%, indicating that allowing the manifold to learn freely can cause the low-dimensional structure to drift unstably. Finally, the shared linear direction $W_0$ is a direct simplified alternative to the sample-dependent Jacobian. Its HTER is 1.87%; although it provides a useful approximation, it remains higher than the 1.19% of the full model, indicating that sample-dependent local directions contain information that cannot be fully replaced by a shared linear direction. The corresponding results have been added to Table 7 in Section 4.3.2 of the revised manuscript. These experiments support the roles of the PCA anchor, nonlinear decoder, and sample-dependent Jacobian in live-structure modeling and local-variation explanation.
Reviewer_oWUbOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The authors propose HypLive-FAS, which shifts from joint class modeling to a live-centered manifold in hyperbolic (Poincaré-ball) space, whose exponentially expanding volume easily accommodates diverse off-manifold spoofs. It has two components: (1) Hyperbolic Live-Manifold Learning (HLM) builds a compact PCA-anchored nonlinear manifold purely from source-live samples, treats spoof samples only as outward margin supervision, and scores spoofness via a Jacobian-based regularized deviation score that filters out manifold-consistent (valid) variations while isolating unexplained deviations; CLIP visual/text encoders with prompt-guided local features provide the embeddings. (2) Liveness-Preserving Augmentation (LPA) perturbs appearance while enforcing representation-direction and deviation-score consistency, reducing reliance on domain-specific cues.

Critical strengths

The asymmetric, one-class manifold formulation is conceptually elegant and well-motivated by real attack heterogeneity. The Jacobian-regularized deviation scoring with a learnable live-primitive dictionary is a principled way to separate valid live variation from attack-specific residuals. Results are strong: under leave-one-domain-out it cuts the best prior average HTER from 1.82% (MVP-FAS) to 1.19% without relying on extra LLM semantics, and under the harder One-to-Eleven protocol it lowers average HTER from 9.55% (DGPDL) to 8.01%. Thorough ablations confirm every component's contribution, hyperbolic geometry measurably improves score separation (d′ 4.79→5.20), and inference stays real-time (~154 FPS).

Critical weaknesses
  1. The decision rule does not establish the compact live region claimed in the paper. Eqs. (6)–(7) measure the residual after local fitting, but do not check whether the fitted location is close to any observed live samples. The primitive prior constrains the correction δ, not the latent position aᵢ. A sample lying beyond the observed live distribution along the learned manifold can therefore still receive a small spoof score. This is a relevant failure mode for unseen attacks. The paper should test such cases and compare against a score that also accounts for proximity to source-live samples in latent space.

  2. The threshold and hyperparameter selection procedures are unclear. Appendix B.10 explicitly states that R_L and m are not decision thresholds, while B.11 never specifies which data or criterion determines t_dec. This leaves open whether HTER requires calibration using labeled target data. Similarly, the default curvature, PCA rank, dictionary size, and temperature all achieve the best target-domain results in their respective sensitivity tables, but no source-validation selection procedure is described. Given the substantial performance changes across these settings, these details matter. The paper should specify the selection rules and report results with a threshold fixed using source validation data.

  3. The component ablations do not cover the harder setting that tests generalization to unseen attack media. All ablations are conducted on Protocol 1, so they do not establish how much hyperbolic geometry, Jacobian fitting, and the primitive prior contribute under Protocol 2. Table 2 reports HTERs of 26.39% on HiFiMask and 15.12% on SiW-M-V2, with the latter worse than DGPDL’s 13.00%. Appendix E.2 acknowledges the score overlap, but does not identify its cause. Ablations on these datasets, together with separate false-acceptance and false-rejection results, are needed to distinguish failure to accommodate new live variations from failure to reject attacks.

Questions for authors
  1. Regarding the "Compact Live Region" and Decision Rule: "Given the concern that our current decision rule allows samples far from observed live data to receive small spoof scores, should we implement an additional proximity check in the latent space to strictly bound the live region, or would providing a failure analysis on unseen attacks be sufficient to address this limitation?"

  2. Regarding Hyperparameter and Threshold Selection: "To resolve the ambiguity regarding our threshold tdect_{dec} and hyperparameters (such as curvature and PCA rank), do we need to redesign our selection procedure to rely strictly on source-validation data to prove we aren't overfitting to the target, and how should we explicitly document this protocol to satisfy the reviewer?"

3. Regarding Component Ablations on Protocol 2: "Since the reviewer pointed out that our current ablations do not cover the harder generalization setting (Protocol 2) where we trail DGPDL, should we prioritize running full ablation studies on HiFiMask and SiW-M-V2 to isolate the specific failure modes, or should we focus our response on analyzing the False Acceptance/Rejection rates to explain the performance gap?"

3 comments
AuthorsOpenReview ↗

Response to W1 & Q1

Thank you for pointing out the distinction between local manifold consistency and proximity to the source-domain live support set, and for raising the specific question of extrapolative attacks. This question helped us further clarify the motivation behind the scoring design in this paper.

We do not use source-live proximity directly as the primary score for one central reason: it penalizes the entire displacement of a sample and cannot distinguish legitimate cross-domain live variation from spoof-specific deviation. Genuine live samples may be far from the finite set of source-domain live samples because of changes in identity, pose, illumination, capture device, and appearance style. If the entire distance were treated as spoofness, reasonable cross-domain live samples could be incorrectly rejected, increasing the FRR. Therefore, this paper first uses the local Jacobian directions of the learned live manifold and the primitive prior to explain variations that are structurally consistent with live samples, and then scores the remaining unexplained deviation:

S(xi)=∥ri−Jiδi∗∥μL.S(\mathbf{x}_i)=\left\lVert \mathbf{r}_i-\mathbf{J}_i\boldsymbol{\delta}_i^{\ast}\right\rVert_{\boldsymbol{\mu}_L}.

Here, Jiδi∗\mathbf{J}_i\boldsymbol{\delta}_i^{\ast} denotes the variation that can be explained by the local live-manifold structure, while S(xi)S(\mathbf{x}_i) is the unexplained residual after filtering out this variation. This design focuses discrimination on structural deviations that cannot be explained by the live manifold, rather than on the total displacement of a sample from a finite set of source-domain live samples.

Under this decision rule, the numbers of low-score attacks that were far from source-domain live samples and were incorrectly accepted in the four target domains M, C, I, and O were 1, 0, 13, and 78, respectively. This result directly confirms the extrapolation failure mode identified by the reviewer: some attack samples were far from the source-domain live reference set, but their deviation scores were still below the original decision threshold.

To examine this extrapolation failure case, we conducted a source-domain distance analysis in the four leave-one-domain-out settings of Protocol 1. For each target domain, we fixed the original model and the original decision threshold tdect_{\mathrm{dec}}. Source-domain live samples were split by identity into approximately 80% reference samples and 20% calibration samples, with no identity overlap between the two sets. We standardized the 32-dimensional latent coordinates using the mean and standard deviation of the reference live samples, and computed the average distance from each sample to its five nearest reference live samples. The distance threshold tDt_D was set to the 95th percentile of the calibration-live distances; target-domain samples were not used to determine tDt_D.

After adding the explicit distance condition

D(xi)≤tD,D(\mathbf{x}_i)\leq t_D,

the results were as follows:

\hline \text{Target domain} & \text{FAR (\\%)} & \text{FRR (\\%)} & \text{HTER (\\%)} \\\\ \hline \text{M} & 0.00 & 20.00 & 10.00 \\\\ \text{C} & 0.45 & 0.00 & 0.23 \\\\ \text{I} & 0.00 & 100.00 & 50.00 \\\\ \text{O} & 0.03 & 86.76 & 43.40 \\\\ \hline \end{array}$$ Although this distance condition can block some attacks that are far from source-domain live samples, it severely damages cross-domain live coverage. Thus, the above failure analysis and explicit hard-proximity comparison address the reviewer's question about an additional distance check and also explain why this paper uses residual deviation as the primary decision signal instead of directly using source-live proximity for discrimination.
AuthorsOpenReview ↗

Response to W2 & Q2

Thank you for pointing out that the original Sections B.10–B.11 did not sufficiently describe the data sources and selection rules. In the revised manuscript, we will clearly distinguish the original main-experiment protocol.

In the main experiments, the model parameters were optimized using the corresponding source-domain training data and labels. Checkpoints were selected according to the lowest HTER on the target-domain test set. When multiple checkpoints yielded the same minimum HTER, we selected the checkpoint with the highest AUC. The final decision threshold tdect_{\mathrm{dec}} was selected to minimize HTER on the target-domain test set using its live/spoof labels. We have explicitly described this procedure in Appendix B.11 of the revised manuscript.

This evaluation protocol has public implementation precedents in cross-domain face anti-spoofing research. We checked the author implementations of SSDG (CVPR 2020), SSAN (CVPR 2022), FLIP (ICCV 2023), SA-FAS (CVPR 2023), and MVP-FAS (ICCV 2025). These implementations determine an EER or an approximate EER decision threshold from target-domain scores and labels and report HTER at that threshold on the same evaluation set. Accordingly, in this work, we determine tdect_{\mathrm{dec}} from the target-domain scores and labels and report HTER at tdect_{\mathrm{dec}}.

This evaluation protocol is motivated by the task. Spoofing cues in face anti-spoofing are often subtle, while changes in capture device, illumination, attack medium, and target-domain sample composition can shift the score scale and the threshold that minimizes HTER across datasets. If a source-domain threshold is applied unchanged to the target domain, the resulting HTER is affected by both the model's live/spoof discrimination ability and the mismatch between the source- and target-domain score distributions. Determining tdect_{\mathrm{dec}} from target-domain scores and labels evaluates model performance after calibrating the decision threshold to the target domain.

For hyperparameters, we first initialized the configuration based on existing work and empirical settings. For example, we used c=1c=1 following HML-FAS and included c=0.01c=0.01, used by HPDR, in the curvature-sensitivity analysis. We then conducted the ablation and sensitivity analyses of Protocol 1 under a unified configuration and finally adopted c=1c=1, PCA rank 32, dictionary size K=32K=32, and temperature τ=0.1\tau=0.1. All target domains used the same configuration; hyperparameters were not selected separately for individual target domains.

To address the reviewer's request for a source-domain fixed-threshold evaluation, we added a source-domain fixed-threshold experiment under Protocol 1. We used the following procedure. We trained the model on the source-domain training set. Using only the source-domain validation set and its labels, we selected the checkpoint and calibrated a candidate threshold. For each source domain, we constructed a feasible threshold interval in which the empirical error rate for each class was no more than 1%. We set the candidate threshold to the midpoint of the intersection of the three source-domain intervals. Source-domain leave-one-out and threshold-stability checks then determined whether this candidate threshold could be used. If any check failed, we applied a predefined fallback rule. After the threshold was saved, it was fixed for target-domain testing, and the threshold was not searched again during testing. The results for the four Protocol 1 settings were as follows:

\hline \text{Setting} & \text{Target domain} & \text{HTER (\\%)} & \text{FAR (\\%)} & \text{FRR (\\%)} & \text{AUC (\\%)} \\\\ \hline \mathrm{ICM}\rightarrow\mathrm{O} & \text{O} & 4.86 & 5.64 & 4.08 & 98.22 \\\\ \mathrm{ICO}\rightarrow\mathrm{M} & \text{M} & 4.00 & 3.00 & 5.00 & 98.58 \\\\ \mathrm{COM}\rightarrow\mathrm{I} & \text{I} & 14.19 & 3.77 & 24.62 & 97.11 \\\\ \mathrm{IOM}\rightarrow\mathrm{C} & \text{C} & 1.14 & 2.27 & 0.00 & 99.80 \\\\ \text{Four-domain average} & \text{—} & \mathbf{6.05} & \mathbf{3.67} & \mathbf{8.42} & \mathbf{98.43} \\\\ \hline \end{array}$$ These results show that, under a unified hyperparameter configuration and a fixed source-domain threshold, the source-domain decision threshold can be transferred to the target domain, although the resulting performance varies substantially across target domains.
AuthorsOpenReview ↗

Response to W3 & Q3

Thank you for the suggestion. We extended the component ablation study to the more difficult Protocol 2 and conducted experiments on HiFiMask and SiW-Mv2 with three random seeds. The five variants were Full, Euclidean, w/o LPA, w/o primitive prior, and raw residual. All variants used the same data, training configuration, training budget, pretrained CLIP initialization, and checkpoint-selection rule. The results were as follows:

\hline \text{Dataset} & \text{Variant} & \text{HTER (\\%)} & \text{AUC (\\%)} & \text{FAR (\\%)} & \text{FRR (\\%)} \\\\ \hline \text{HiFiMask} & \text{Full} & \mathbf{26.39} & \mathbf{78.85} & \mathbf{38.40} & \mathbf{14.39} \\\\ \text{HiFiMask} & \text{Euclidean} & 27.83 & 76.13 & 39.33 & 16.33 \\\\ \text{HiFiMask} & \text{w/o LPA} & 29.08 & 74.51 & 45.98 & 12.18 \\\\ \text{HiFiMask} & \text{w/o primitive prior} & 28.16 & 76.20 & 41.99 & 14.32 \\\\ \text{HiFiMask} & \text{raw residual} & 28.16 & 76.20 & 42.25 & 14.06 \\\\ \hline \text{SiW-Mv2} & \text{Full} & \mathbf{15.12} & \mathbf{89.43} & \mathbf{21.18} & \mathbf{9.07} \\\\ \text{SiW-Mv2} & \text{Euclidean} & 16.45 & 89.07 & 24.86 & 8.05 \\\\ \text{SiW-Mv2} & \text{w/o LPA} & 17.63 & 88.17 & 23.76 & 11.49 \\\\ \text{SiW-Mv2} & \text{w/o primitive prior} & 16.98 & 88.76 & 25.14 & 8.81 \\\\ \text{SiW-Mv2} & \text{raw residual} & 16.91 & 88.69 & 25.14 & 8.68 \\\\ \hline \end{array}$$ After removing LPA, HTER increased by 2.69 and 2.51 percentage points on HiFiMask and SiW-Mv2, respectively, while AUC decreased by 4.34 and 1.26 percentage points. On HiFiMask, FAR increased from 38.40% to 45.98%, indicating that LPA mainly improves rejection of high-fidelity mask attacks. On SiW-Mv2, both FAR and FRR increased, indicating that LPA also helps preserve reasonable cross-domain live variation. Compared with the Euclidean variant, the Full model reduced HTER by 1.44 and 1.33 percentage points on HiFiMask and SiW-Mv2, respectively. This shows that hyperbolic geometry provides an overall benefit on both difficult domains, although the magnitude of the benefit is dataset-dependent. Removing the primitive prior or the Jacobian local fitting caused HTER and FAR to increase to different degrees on both datasets, indicating that both components provide live-structure constraints and reduce some false acceptance of attacks. The performance degradation mainly comes from false acceptance of attacks. The high-fidelity three-dimensional masks in HiFiMask preserve the geometry, texture, and identity appearance of real faces, allowing some attack variations to be explained by the source-domain live structure. Its FAR is 38.40%, clearly higher than its FRR of 14.39%. In SiW-Mv2, Partial\_FunnyeyeGlasses caused 27/64 attacks to be incorrectly accepted, and Makeup\_Cosmetic caused 20/24 attacks to be incorrectly accepted. These two attack types account for 67.14% of all false-accepted attacks. They mainly alter the eye region or local texture while preserving the overall natural face structure, and therefore are more likely to overlap with the source-domain live-like representation. The FAR on SiW-Mv2 is 21.18%, higher than the FRR of 9.07%, indicating that performance degradation on both difficult datasets mainly results from insufficient rejection of live-like spoofs rather than an inability to accommodate new live variations.

Comments on the paper

12 comments
AuthorsOpenReview ↗

Response to W1 & Q1

Thank you for highlighting the need to clarify our evaluation and selection procedures.

In the main experiments, model parameters were optimized using the corresponding source-domain training data and labels. Checkpoints were selected according to the lowest HTER on the target evaluation set. When multiple checkpoints yielded the same minimum HTER, we selected the checkpoint with the highest AUC. The decision threshold tdect_{\mathrm{dec}} was selected to minimize HTER on the target evaluation set using its live/spoof labels. Thus, checkpoint selection and threshold calibration in the original main results did use target-domain labels. We explicitly state this in the revised manuscript, with additional details provided in the newly added red text in Appendix B.11.

This evaluation protocol has public implementation precedents in cross-domain face anti-spoofing research. We checked the author implementations of SSDG (CVPR 2020), SSAN (CVPR 2022), FLIP (ICCV 2023), SA-FAS (CVPR 2023), and MVP-FAS (ICCV 2025). These implementations determine an EER or an approximate EER decision threshold from scores and labels on the target test set and report HTER at that threshold on the same evaluation set. Accordingly, in this work, we determine tdect_{\mathrm{dec}} from the target-domain scores and labels and report HTER at tdect_{\mathrm{dec}}.

This evaluation protocol is motivated by the task. Spoofing cues in face anti-spoofing are often subtle, while changes in capture device, illumination, attack medium, and target-domain sample composition can shift the score scale and the threshold that minimizes HTER across datasets. If a source-domain threshold is applied unchanged to the target domain, the resulting HTER is affected by both the model's live/spoof discrimination ability and the mismatch between the source- and target-domain score distributions. Determining tdect_{\mathrm{dec}} from target-domain scores and labels evaluates model performance under a decision threshold calibrated to the target domain.

For hyperparameters, we first initialized the configuration based on existing work and empirical settings. For example, we used c=1c=1 following HML-FAS and included c=0.01c=0.01, used by HPDR, in the curvature-sensitivity analysis. We then determined a unified configuration from the average HTER and AUC over the four target domains of Protocol 1, including c=1c=1, PCA rank 32, dictionary size K=32K=32, and temperature τ=0.1\tau=0.1. All target domains used the same configuration; hyperparameters were not selected separately for individual target domains.

To distinguish target-domain model selection from final target-domain testing, we further added a source-domain calibration experiment under Protocol 1. We kept the final hyperparameters above fixed, trained the model on the source-domain training set, and used only the source-domain validation set and its labels for checkpoint selection and threshold calibration. The threshold was determined using a predefined quantile rule: for each source domain, we constructed a common feasible threshold interval under an empirical error constraint of 1% for each class, took the midpoint of the intersection, and used predefined source-domain internal checks and fallback rules to determine the final threshold. After the threshold was saved, it was fixed for transfer to the target domain. Target-domain labels did not participate in determining the threshold value, selecting the checkpoint, or making per-run decisions, and the threshold was not searched again during testing.

The results of three random seeds in Protocol 1 were as follows:

\hline \text{Setting} & \text{Target domain} & \text{HTER (\\%)} & \text{FAR (\\%)} & \text{FRR (\\%)} & \text{AUC (\\%)} \\\\ \hline \mathrm{ICM}\rightarrow\mathrm{O} & \text{O} & 4.86 & 5.64 & 4.08 & 98.22 \\\\ \mathrm{ICO}\rightarrow\mathrm{M} & \text{M} & 4.00 & 3.00 & 5.00 & 98.58 \\\\ \mathrm{COM}\rightarrow\mathrm{I} & \text{I} & 14.19 & 3.77 & 24.62 & 97.11 \\\\ \mathrm{IOM}\rightarrow\mathrm{C} & \text{C} & 1.14 & 2.27 & 0.00 & 99.80 \\\\ \text{Four-domain average} & \text{—} & \mathbf{6.05} & \mathbf{3.67} & \mathbf{8.42} & \mathbf{98.43} \\\\ \hline \end{array}$$ This experiment shows that, with fixed hyperparameters and a source-domain-calibrated threshold, the model can still transfer to the target domain, although its performance is affected by threshold transfer.
AuthorsOpenReview ↗

Response to W2 & Q2

Thank you for asking us to clarify the fairness of the Euclidean comparison and the contribution of hyperbolic geometry.

The corresponding HLM+LPA and ELM+LPA experiments use matched settings. They use the same feature-extraction and normalization procedures and the same source-domain live-feature scale calibration. They retain the same CLIP backbone, prompt module, nonlinear manifold encoder and decoder, primitive module, and network capacity. They also use the same loss terms, AdamW optimizer, parameter-group learning rates, weight decay, and training strategy. The residual scores share the same computation pipeline, including the reconstruction residual, local fitting, and remaining deviation. The only differences are the center estimation, coordinate mapping, distance computation, and residual norm appropriate to each space. Therefore, the Euclidean comparison changes the geometric operations rather than the network capacity, optimizer, or scoring terms.

To further test whether the input-side nonlinear transformation alone could produce the performance gains reported in the paper, we added an ablation with only Exp⁡0\operatorname{Exp}_0 and Euclidean operations. This comparison retained the input exponential map but replaced all subsequent operations with Euclidean operations, while keeping network capacity, loss terms, and optimization settings identical. The mean HTER over three random seeds in the M, C, I, and O target domains was 2.08±0.432.08\pm0.43\\%, 0.69±0.310.69\pm0.31\\%, 3.34±1.353.34\pm1.35\\%, and 3.25±0.473.25\pm0.47\\%, respectively. All were higher than the corresponding results of the full model in Table 1. Thus, retaining only the input exponential map cannot reproduce the performance gains of the full model under this experimental setting, indicating that the FAS task is well matched to hyperbolic space.

Our choice of hyperbolic space is consistent with the modeling assumption in the paper: live features have a relatively concentrated common structure, whereas attack types are diverse and appear as different peripheral deviations from the live structure. The peripheral region of hyperbolic space expands with radial distance, providing more representation capacity for these heterogeneous deviations. This matches the design of modeling the live manifold and identifying attacks through deviations from that manifold.

AuthorsOpenReview ↗

Response to W2 & Q3

Thank you for pointing out the ambiguity between the fixed PCA anchor and the refreshed geometric quantities.

The descriptions of “fixed” and “refreshed” in Appendices B.5 and B.6 were ambiguous. This was a problem in our wording, and we thank the reviewer for pointing it out. In the resubmitted paper, we have corrected the description; details are provided in the Geometric Refresh section of Appendix B.5. The implementation distinguishes the fixed initial PCA anchor from the derived subspaces obtained from the current network weights.

The initial PCA basis U0U_0 is computed from source-domain live samples and is used to initialize the encoder and decoder, namely WE(0)=U0⊤W_E^{(0)}=U_0^{\top} and W0(0)=U0W_0^{(0)}=U_0. After initialization, U0U_0 remains fixed during training and serves as the fixed anchor for the subspace regularizer Lsub\mathcal{L}_{\mathrm{sub}}.

At the same time, the encoder weights WEW_E and the decoder's linear weights W0W_0 are updated by gradient descent. The orthonormal bases corresponding to the current weights are obtained by QR decomposition: WE⊤=QEREW_E^{\top}=Q_E R_E and W0=QGRGW_0=Q_G R_G. Therefore, QEQ_E and QGQ_G change with the current weights and are used to compute the subspace regularizer relative to the fixed U0U_0. They are derived quantities required for regularization, rather than fixed coordinate systems for storing sample coordinates.

Latent coordinates are also recomputed from the current features and current network parameters: ai=WEyia_i=W_E y_i, where yiy_i is the centered tangent-space coordinate under the current geometric state. The reconstruction is

y^i=Gϕ(ai)=W0ai+W2GELU⁡(W1ai+b1).\hat y_i=G_{\phi}(a_i)=W_0 a_i+W_2\operatorname{GELU}(W_1 a_i+b_1).

Geometric refresh updates the radial reference, live center, and tangent-space mean, while retaining the learned parameters of the encoder, decoder, primitive-assignment network, and primitive vectors. After refresh, coordinates and reconstructions are recomputed under the new current geometric state.

Thus, the fixed U0U_0 provides a stable anchor, while the current QEQ_E, QGQ_G, center, and tangent-space mean are updated with the training state, and latent coordinates are recomputed under the current state. We will use these terms consistently in the revised manuscript to improve reproducibility.

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

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