acceptodds
Under review as a conference paper at ICLR 2027

When Generative Replay Meets Evolving Deepfakes: Dual Confusion-Aware Regularization for Incremental Deepfake Detection

Abstract

The rapid advancement of face generation techniques has introduced an increasing variety of forgery methods, making incremental deepfake detection essential for maintaining robust detectors. While generative replay provides a promising solution to alleviate catastrophic forgetting without storing historical data, its effectiveness is hindered by domain confusion between generated samples and real data. We observe that replay samples fall into two categories: when the replay generator closely resembles the newly introduced forgery model, generated real samples overlap with the fake domain and become domain-risky; when the generator differs significantly, generated samples maintain clearer domain separation and can be treated as domain-safe. To address this challenge, we propose a Dual Confusion-Aware REgularization strategy, termed Dual-CARE. A Domain-aware Confusion Score (DC Score) is introduced to quantify domain confusion and dual-modulate the optimization of both replay generators and the incremental detector. Guided by DC Score, replay generators are updated to better approximate previous-task distributions, while the detector adopts different supervision strategies: domain-safe samples are directly supervised, whereas domain-risky samples are regulated using a Relative Separation Loss to balance supervision and confusion. Extensive experiments demonstrate that Dual-CARE effectively exploits generative replay and improves incremental deepfake detection under evolving forgery scenarios.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Incremental Deepfake Detection, Generative Replay

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 2 reviews, above 27% of the others.
Reviewer_7mu1OpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper identifies generator-induced artifacts in replayed real samples as a potential source of bias in face forgery detectors. To address this issue, it proposes a dynamic generator update strategy, a domain-aware fast training scheme, and a new loss function for detector learning. Together, these components aim to mitigate domain confusion between replayed samples and real data arising from limitations of the replay generator.

----- after rebuttal ----- Response addresses most of my concerns. Thus, I keep the original rating of weak acceptance.

Critical strengths
  • The motivation is clear and addresses a common practical challenge in generative replay for face forgery detection.

  • The experiments are comprehensive, with ablation studies providing evidence for the contribution of each component.

  • Under the assumptions considered in the paper, the proposed loss appears effective in reducing the influence of generator-induced artifacts on the detector.

Critical weaknesses
  • The introduction’s claim of being the first to explore the feasibility of generative replay for face forgery detection would benefit from more precise positioning relative to prior work. Existing applications already provide evidence of its feasibility, whereas this paper’s contribution appears to lie primarily in identifying and addressing a specific limitation of this approach.

  • The claim that replayed fake samples have no significant effect on detection performance, regardless of the replay generator, and that the main issue stems from replayed real samples is not sufficiently supported. RS Loss appears to suppress the influence of generator-induced artifacts in both replayed real and fake samples. Its effectiveness therefore does not, by itself, establish that replayed real samples are the primary source of the problem. Separate analyses of the two sample types would help substantiate this claim.

  • The use of centroid distance as a measure of confusion risk requires further justification, particularly the assumed positive relationship between distribution separation and confusion risk. Although the proposed explanation concerns interactions between generator-induced artifacts and forgery traces, centroid distances may also reflect semantic content and other unrelated features. Additional analysis would help establish whether this measure reliably captures the intended source of confusion.

  • The dynamic update strategy places greater emphasis on historical data when the measured discrepancy is large, while the generator must also adapt to new data. The effect of this potentially competing objective on training stability and convergence remains unclear. Further discussion and empirical evidence would help demonstrate how the strategy balances historical knowledge retention with adaptation to new distributions.

Questions for authors

see weakness

4 comments
AuthorsOpenReview ↗

Response to Reviewer 7mu1 (Part 1/2)

Thank you for the constructive suggestions on positioning, replay asymmetry, and adaptive control. We address the individual claims and their supporting evidence below.

W1. Positioning of the generative-replay claim

Response. We agree that the positioning should emphasize the limitation of replay, rather than imply that generative replay has not previously been shown to be feasible in related applications. A detector is required to distinguish real and fake content, while both replay domains are produced by a generator. Consequently, generated-real replay may introduce synthetic cues into real-side supervision, especially when those cues relate closely to the incoming forgery. Dual-CARE identifies this domain-confusion issue and uses the same task-level score to adapt generator training and detector supervision.

We have revised the opening discussion and the first contribution of the Introduction to describe the work as a systematic investigation of generative replay for incremental face forgery detection, with the identification and mitigation of domain confusion as its specific contribution. The priority claim is now stated only to the extent the literature comparison supports.

Revision location: Introduction (contribution positioning), Section 2 (motivation).


W2. Separate effects of generated-real and generated-fake replay

Response. We agree that the RS Loss ablation alone cannot attribute the effect to either replay class. We therefore use a four-way replay replacement comparison with all Dual-CARE components disabled. Each replacement is measured against the actual-real/actual-fake reference for the same incoming task. A uses actual historical real and fake samples; B replaces real replay only; C replaces fake replay only; and D replaces both. Δ\Delta denotes the change in average AUC relative to A, in percentage points.

Large-distance case: LDM → DFDCP → SDv21 → WDF; DC distance = 3.25.

Replay configurationLDMDFDCPSDv21WDFAVG AUCΔ
A99.9988.9099.6583.3092.96—
B99.8990.9296.6580.6092.01-0.95
C99.7488.9299.5781.1092.33-0.63
D96.7191.2098.8781.2992.02-0.94

Small-distance case: LDM → DFDCP → SDv21 → DDPM; DC distance = 0.26.

Replay configurationLDMDFDCPSDv21DDPMAVG AUCΔ
A99.9889.3199.4899.9997.19—
B86.6180.8995.4699.9990.74-6.45
C99.6887.0497.7099.9996.10-1.09
D83.4681.1794.2999.9989.73-7.46

(1) Effects of replacing each replay class

The two controls show the same pattern:

  1. Actual fake replay fixed. Replacing real replay reduces average AUC by 6.45 points for DDPM and 0.95 points for WDF. In the DDPM case, replacing fake replay alone costs 1.09 points.
  2. Generated fake replay fixed. Replacing real replay reduces average AUC by 6.37 points for DDPM and 0.31 points for WDF.

The larger generated-real effect in the tested DDPM transition is visible under both fake-replay conditions and does not depend on RS Loss.

(2) Why the two replay classes differ

The label relationship offers a motivation for this asymmetry: a replay-generator artifact in generated real can be associated with the real label even when similar cues occur in current fakes. For generated fake, the fake label and synthetic cues are aligned, although reliance on generator-specific shortcuts remains possible.

Revision location: Section 2 (replay asymmetry), Section 4.8 (controlled replay replacement) and Table 6.

AuthorsOpenReview ↗

Response to Reviewer 7mu1 (Part 2/2)

W3. Validity of centroid distance as a confusion proxy

Response. DC Score is computed in the detector’s own feature space, where the real and fake labels are actually applied, so the distance it reports is a separation measured where the decision is made. The smaller that separation, the less room a single boundary has to keep the two groups apart, and the more often the same features are pulled toward opposite labels; that is the confusion risk the score tracks. It is not a calibrated measure of overlap, since the features also carry identity and semantics and two centroids do not describe a distribution’s shape. The score is therefore used to order tasks, not to quantify overlap.

(1) Empirical evidence for the proxy

Two analyses provide complementary evidence:

  1. Replay replacement. The smaller-distance DDPM transition incurs a much larger generated-real replacement loss than the larger-distance WDF transition under both fake-replay conditions, using the same detector checkpoint and historical replay. Since the incoming task changes, this is evidence from two transitions rather than a general correlation or proof of the source of the distance.
  2. Distance alternatives. Table 5 reports average AUCs of 92.05 for DCS-Cos + RS-Cos and 92.91 for DCS-Cos + RS-L2, compared with 94.98 for DCS-L2 + RS-Cos. These end-to-end alternatives support the feasibility of angular measures, but do not by themselves isolate feature magnitude or establish that the score directly measures overlap.

Revision location: Section 3.2 (DC Score), Table 5 (distance ablation).


W4. Stability and the historical/current-data trade-off

Response. Adaptation is task-level: the score is computed at the task transition, and its resulting weight is held fixed during that task. Thus, the method does not introduce iteration-by-iteration changes in the coefficient, although the generator’s parameters and optimization losses still evolve normally. A larger score gives the fake-generator objective more weight on historical generated fakes; a smaller score gives more weight to current fakes. The real generator follows its separate, unweighted update objective. Across Protocol 1 the coefficient spans 0.2245 to 0.9980, so both regimes are exercised in the main experiments.

The adaptive-weight ablation compares adaptive weighting with fixed scores: average AUC is 95.74 with adaptation, versus 93.72 and 93.12 for fixed scores 0.5 and 0.1. The learning-behavior figure compares the training trajectories with and without domain-aware fast training. Together, these support the empirical value of the task-dependent trade-off.

Revision location: Section 3.3 (generator update), Table 2 (weight ablation), Figure 5 (generator learning), Table 4 (P1 scores).

Thank the authors for providing a detailed response that addresses most of my concerns. Thus, I keep the original rating of weak acceptance.

AuthorsOpenReview ↗

Thank You and Further Discussion

Dear Reviewer 7mu1,

Thank you for your encouraging feedback and continued support. We are pleased that our detailed responses have addressed most of your concerns, and we sincerely appreciate your careful consideration of our work.

Could you please share which specific concerns remain, or which aspects you feel would benefit from further clarification or supporting evidence? We would greatly appreciate the opportunity to discuss these points with you and address them more fully. We hope that this further exchange can help resolve any remaining reservations and strengthen your confidence in our work.

Thank you again for your time and constructive feedback.

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

The paper studies generative replay for incremental face forgery detection, motivated by: forgery detection is defined as separating real from synthetic content, yet generative replay must synthesise "real" samples. A controlled experiment with four replay generators at matched FID shows detection accuracy falling to 0.5655 when the replay generator closely resembles the forgery generator and reaching 0.9962–0.9999 when it differs, motivating a domain-risky versus domain-safe distinction. Dual-CARE introduces a Domain-aware Confusion Score to modulate both generator updating and detector supervision, with domain-safe samples receiving direct cross-entropy and domain-risky ones a Relative Separation Loss. Across two incremental protocols and three backbones, it reaches 95.37 average AUC on previous tasks under Protocol 1 against 93.89 for SUR-LID.

Critical strengths
  1. The motivating experiment is a clean single-factor design. Figure 2 holds FID fixed to control generation quality and varies only the similarity between replay and forgery generators, producing a monotone trend — considerably stronger than a purely qualitative argument.
  2. The method is lightweight and its components are simple. The DC Score requires only centroid L2 distance, the RS Loss only cosine similarity, and generator updating uses LoRA adapters with only the latest pair retained. Appendix E.2 states this design intent explicitly rather than overclaiming.
Critical weaknesses

1.Treating generated "real" samples as authentic data for training a forgery detector is not a reasonable assumption. It degenerates the task into discriminating between certain data distributions, which may yield metric improvements under specific distributional conditions, yet fails to truly distinguish real from fake. 2.If the incoming forgery type is unusual and its samples sit far from everything, s is large, the case is labelled domain-safe, and direct supervision is applied — even though the generated real samples may still deviate badly. Conversely, if the incoming forgery is high quality and close to real, s is small and the RS Loss is applied — even though the generated real samples may be clean, suppressing usable direct supervision. 3.Appendix E.1 contains an unresolved cross-reference ("Fig. ??"). 4. Rombach et al. 2022a and 2022b are the same paper but denote LDM and SDv21.

Questions for authors

1.Why does the DC Score compare generated-real against current-fake rather than current-real? 2.When an incoming forgery type sits far from everything, s is large and the case is treated as domain-safe. Is direct supervision appropriate there? Are there case studies?

11 comments
AuthorsOpenReview ↗

Response to Reviewer nyVt (Part 1/2)

Thank you for identifying the central question of how generated-real replay can be used in a forgery detector. Our approach explicitly treats its supervision as conditional supervision. We clarify the resulting distinction and the evidence below.

W1. Treating generated-real samples as real

Response. We agree that assigning an unconditional real label to generated-real replay can introduce a misleading training signal. In fact, identifying and addressing this failure is the motivation of Dual-CARE. The method does use a real-label cross-entropy term for generated-real samples, but weights that term according to the DC Score and complements it with relative separation. In Eq. (8), the generated-real contribution is sLce+(1−s)Lrss\mathcal L_{\mathrm{ce}}+(1-s)\mathcal L_{\mathrm{rs}}: when the measured distance is small, direct supervision is reduced and relative supervision receives more weight. Current real, current fake, and generated-fake samples receive direct supervision.

The problem is therefore conditional, and the condition is simple, namely how close the replay generator is to the forgery generator. In Fig. 2 the four generators have comparable FID, so the replayed images are of similar quality. Fidelity, however, is not the same as usefulness: two equally faithful replay sets can be worth very different amounts to the detector, and a matched FID does not make the four settings interchangeable. Accuracy nonetheless falls to 0.5655, close to the 0.5 of random guessing, when the two are most alike, and rises to 0.7715, 0.9962 and 0.9999 as they diverge. Since image quality was held equal across all four settings, the drop cannot be explained by it.

(1) Adaptive supervision and relative separation

The detector uses the two replay types through distinct supervision signals:

  1. Generated-real supervision. Cross-entropy provides a real-side signal, weighted by ss according to the measured relationship with the incoming fake data.
  2. Relative separation. Generated-real and generated-fake replay share a generator backbone, while their adapters represent different historical domains. RS Loss separates generated-fake features from the generated-real centroid, using their relative relationship to retain historical information.

(2) Evaluation across forgery datasets

The concern that the detector may only be learning a boundary between particular distributions is what the unseen-forgery evaluation addresses. Protocol 1 and Protocol 2 differ in sequence and in the mix of classical and diffusion-based forgeries, and none of DFD, DDIM, UADFV or WDF appears in either the current task or the replay data, so there is no replay geometry to exploit on these four sets. Our AUCs are 77.97, 92.45, 96.25 and 70.73, against 73.31, 91.20, 95.76 and 68.88 for SUR-LID. The gain holds on all four, which is the behaviour expected when what the detector has learned is forgery evidence rather than the separation between two replay distributions.

Revision location: Section 2 (domain confusion), Section 3.4 (detection objective), Appendix Table 14 (unseen forgeries).


W2. Interpretation of the score in extreme cases

Response. These cases distinguish replay fidelity from potential supervision conflict. Confusion, as we use the term, is not an attribute of replayed real samples but a relation between them and the current fakes. DC Score measures the distance between their feature centroids in the detector’s representation; it is designed as a proxy for the latter relationship, not as a measure of whether generated-real images faithfully reproduce the real distribution.

(1) How the score changes supervision

  1. Large DC Score. The centroids are far apart, so direct generated-real supervision receives more weight. This does not establish that replay is unbiased or that all individual samples are separable.
  2. Small DC Score. The centroids of the two label groups are close, so RS Loss receives more weight. Even high-quality replay may be difficult to distinguish from a high-quality forgery in the detector’s representation.

Revision location: Section 3.2 (DC Score), Eq. (8) (detection objective).

AuthorsOpenReview ↗

Response to Reviewer nyVt (Part 2/2)

W3. Unresolved cross-reference

Response. Thank you. We have corrected the unresolved reference to Figure 6, the replay-size comparison, and verified its number against the compiled revision.

Revision location: Appendix E.1 (replay size), Figure 6.


W4. Duplicate bibliography entries

Response. Thank you. The duplicate entries refer to High-Resolution Image Synthesis with Latent Diffusion Models. We have consolidated the duplicate LDM entries into one and corrected the SDv21 citation to DF40, the dataset source used in Section 4.1.

Revision location: References (duplicate entries), Section 4.1 (datasets).


Q1. Why compare generated real with current fake?

Response. The distance is measured against the current fakes because that is where the risk arises. The real replay carries a real label and the current forgeries carry a fake label; if the two look alike in the detector's features, the same evidence is asked to support opposite decisions, and the two supervision signals work against each other. Distance to the current real domain answers a different question, namely how faithfully the replay reproduces real data, and a small value there does not mean that real-labelled replay can be told apart from the fakes.

Revision location: Section 3.2 (DC Score), Eq. (8) (detection objective).


Q2. Direct supervision for a distant incoming forgery

Response. A large distance is a reason for assigning greater weight to direct supervision in our design, rather than proof that generated-real replay is unbiased. To examine the consequence, we compare two fourth-task transitions with the same first three tasks, LDM → DFDCP → SDv21, the same pre-transition detector, and the same historical replay samples. The fourth task is DDPM in the small-distance case and WDF in the large-distance case; WDF is introduced for this analysis and is not part of Protocol 1's sequence. Their unnormalized distances are 0.26 and 3.25. All Dual-CARE components are disabled, and all groups use ordinary direct classification.

(1) Controlled replay replacement

For each transition, we compare four replay configurations:

  • A: Actual historical real and fake samples.
  • B: Generated real and actual fake samples.
  • C: Actual real and generated fake samples.
  • D: Generated real and fake samples.

Δ\Delta denotes the average-AUC change relative to A, in percentage points.

Large-distance case: LDM → DFDCP → SDv21 → WDF; DC distance = 3.25.

Replay configurationLDMDFDCPSDv21WDFAVG AUCΔ
A99.9988.9099.6583.3092.96—
B99.8990.9296.6580.6092.01-0.95
C99.7488.9299.5781.1092.33-0.63
D96.7191.2098.8781.2992.02-0.94

Small-distance case: LDM → DFDCP → SDv21 → DDPM; DC distance = 0.26.

Replay configurationLDMDFDCPSDv21DDPMAVG AUCΔ
A99.9889.3199.4899.9997.19—
B86.6180.8995.4699.9990.74-6.45
C99.6887.0497.7099.9996.10-1.09
D83.4681.1794.2999.9989.73-7.46

(2) Results

Replacing actual real with generated real costs 0.95 points for WDF versus 6.45 points for DDPM when fake replay is actual. When fake replay is generated, the corresponding AUC losses, C minus D, are 0.31 and 6.37 points. Thus, direct use of the same generated-real replay is much less damaging in the tested large-distance transition, under both fake-replay conditions. The fourth task changes between the two cases, so this comparison supports the design for these transitions rather than establishing distance as the sole cause of the difference.

Revision location: Section 3.4 (detection objective), Section 4.8 (controlled replay replacement) and Table 6.

AuthorsOpenReview ↗

Follow-up on Our Rebuttal

Dear Reviewer nyVt,

Thank you again for your thoughtful feedback. We have devoted substantial effort to thoroughly addressing all of your concerns, including those regarding the supervision of generated-real samples, the interpretation of domain confusion, and the validity of the DC Score, through extensive additional controlled experiments and detailed clarifications.

We are also encouraged that another reviewer has recommended acceptance, recognizing the contributions of our work and the effectiveness of our rebuttal.

We would greatly appreciate your feedback on our responses and warmly welcome further discussion. We are confident in our ability to resolve any remaining concerns and hope our additional evidence will encourage you to reconsider your initial assessment.

Thank you for your time and consideration.

Comments on the paper

8 comments
AuthorsOpenReview ↗

Response to Reviewer LWLr (Part 1/3)

Thank you for the detailed analysis of the adaptive coefficient, ablation tables, and identity evaluation. These comments expose distinctions that should be made explicit in the manuscript.

W1. Meaning and validation of the DC Score

Response. The reported P2 values are the coefficients used by the objectives: 0.9997, 0.9999, and 0.9769. Their implications differ on the two sides:

(1) Interpretation of the P2 coefficients

  1. Detector objective. ss multiplies generated-real cross-entropy, and 1−s1-s multiplies RS Loss. Direct supervision therefore receives the predominant coefficient in these P2 transitions.
  2. Fake-generator objective. ss weights historical generated fakes, and 1−s1-s weights current fakes. The explicit coefficient on current fake data is correspondingly small.

Protocol 2 is domain-safe by construction, since every incoming forgery in it is a classical manipulation while the replay generator is an LDM. Near-unity coefficients are therefore the intended behaviour rather than a degenerate case: where replay does not conflict with the incoming forgery, the relative term should not be forced on. On P2 the gain is carried by direct supervision and by the historical weighting of the fake generator, not by RS Loss.

(2) The complementary regime

On Protocol 1 the coefficient is far from saturated: the five transitions yield 0.9980, 0.9963, 0.2245, 0.6650, and 0.9557. The two smallest values occur at the transitions to DDPM and to DiT, both diffusion-family forgeries and the closest in the sequence to the LDM replay generator, an ordering consistent with Fig. 2. Saturation is therefore a property of Protocol 2 rather than of the DC Score, and on Protocol 1 the relative term is active on exactly those transitions where conflict is present.

(3) Component and weight ablations

The P1 ablations provide complementary evidence across a sequence containing diffusion-based forgeries:

  1. RS Loss. With DGS enabled and DFT disabled, adding RSL changes average AUC from 91.15 to 92.91. With DGS and DFT enabled, it changes AUC from 93.66 to 95.37.
  2. Generator-side strategy. With both detector components enabled, the DFT-off and DFT-on results are 92.91 and 95.37.
  3. Adaptive weighting. The adaptive-weight ablation reports 95.74, versus 93.72 and 93.12 for the two fixed-score settings.

(4) Distance and replay harm

To probe the connection between distance and replay harm independently of Dual-CARE, we compare the DDPM and WDF transitions after the same first three tasks, using the same pre-transition detector and historical replay. All Dual-CARE components are disabled. For each transition, A uses actual historical real and fake samples; B replaces real replay only; C replaces fake replay only; and D replaces both. Δ\Delta denotes the average-AUC change relative to A, in percentage points.

Large-distance case: LDM → DFDCP → SDv21 → WDF; DC distance = 3.25.

Replay configurationLDMDFDCPSDv21WDFAVG AUCΔ
A99.9988.9099.6583.3092.96—
B99.8990.9296.6580.6092.01-0.95
C99.7488.9299.5781.1092.33-0.63
D96.7191.2098.8781.2992.02-0.94

Small-distance case: LDM → DFDCP → SDv21 → DDPM; DC distance = 0.26.

Replay configurationLDMDFDCPSDv21DDPMAVG AUCΔ
A99.9889.3199.4899.9997.19—
B86.6180.8995.4699.9990.74-6.45
C99.6887.0497.7099.9996.10-1.09
D83.4681.1794.2999.9989.73-7.46

Generated-real replacement costs 6.45 versus 0.95 average-AUC points when fake replay is actual, and 6.37 versus 0.31 points when fake replay is generated, for distances 0.26 and 3.25, respectively. This supports the score as a behavioral proxy in these two transitions.

Revision location: Eqs. (5), (8) (weighting); Table 9 (component ablation), Table 10 (P2 scores), Table 2 (weight ablation), Table 4 (P1 scores), Table 6 (replay replacement).

AuthorsOpenReview ↗

Response to Reviewer LWLr (Part 2/3)

W2. Inconsistent ablation configurations

Response. Thank you for identifying a real ambiguity, which we have since verified.

(1) Reported configurations

  1. “w/o DC-guided Gen” (92.91), now labelled “w/o DFT” in Table 5. The replay generator is still updated at each task, but DC-guided weighting is removed from its update objective. Its per-dataset values match Table 9’s DFT off, DGS on, RSL on configuration.
  2. “w Det. All” (94.98), now labelled “w DGS + RSL” in Table 5. The generator is frozen and the complete detector objective is applied, as stated in Section 4.4; it is therefore a different configuration from the all-on model, not a repeat of it.
  3. All components on (95.37). The all-on configuration reported in Table 9.

The statement that the generator-side strategy is disabled was intended for the detector-side rows alone; presenting it as applying to the whole table was our error.

(2) Correction of the ablation description

The rows are now grouped under the explicit headers “Core component ablation” and “Distance metric ablation”, and the caption states which row updates the generator and which freeze it. Table 5 now identifies the reference for ΔAvg\Delta_{\mathrm{Avg}} as the 94.98 “w DGS + RSL” row, rather than the 95.37 all-on result in Table 9. Finally, we have standardized DFT, DGS, and RSL across Section 4.4 and Tables 5 and 9, since the same components were previously labelled differently.

Revision location: Section 4.4 (ablation protocol), Tables 5 and 9 (configuration labels).


Q1. Are the Table 10 scores the actual coefficients?

Response. Yes. The normalized score is used as the coefficient ss in both objectives; it is evaluated at the task transition and held fixed during the task. At values near one, the fake generator is weighted mainly toward historical generated fake data, while the generated-real detector term is weighted mainly toward direct cross-entropy and only weakly toward RS Loss. W1 gives the P2 values, the P1 values that show the complementary regime, and the component evidence that isolates each term.

Revision location: Eqs. (5), (8) (weighting), Table 10 (P2 scores), Table 4 (P1 scores).

AuthorsOpenReview ↗

Response to Reviewer LWLr (Part 3/3)

Q2. Feature magnitude and classification confusion

Response. The coefficient is normalized, so its effect on training is bounded regardless of the raw distance. Both groups are taken from the same detector at the same task, so they share one latent space rather than coming from two models with different scales. Replay also keeps that space stable across tasks, since each task is trained together with replay from the previous ones. The distance therefore compares two groups inside a maintained representation. Magnitude contributes to it, and we do not separate magnitude from direction; the score is used to rank tasks by risk, not to estimate overlap. In Table 6, the transition with distance 0.26 loses 6.45 points when real replay is replaced, against 0.95 points at distance 3.25.

Revision location: Section 3.2 (DC Score), Appendix E.2 (distance metric), Table 5 (distance ablation), Section 4.8 (controlled replay replacement) and Table 6.


Q3. Which ablations isolate generator-side contributions?

Response. The “w/o DC-guided Gen” row matches the DFT off / DGS on / RSL on row in Table 9, both at 92.91. In Table 9, the corresponding DFT on / DGS on / RSL on result is 95.37, giving a 2.46-point difference with the two listed detector components held on. The 94.98 “w Det. All” row freezes the generator, so it measures what is lost by removing DC-guided updating altogether rather than by degrading it; it is therefore not the contrast that isolates the generator-side contribution. The row-level settings are now documented in Section 4.4 and the captions of Tables 5 and 9, as described in W2.

Revision location: Tables 5 and 9 (component settings).


Q4. Identity-recall protocol and privacy interpretation

Response. We agree that identity matching and privacy against inference attacks are distinct questions. Table 12 reports ID Recall of 0.08% with ArcFace and 0.05% with CosFace. These results concern matches under the particular face-embedding evaluation protocol; they do not by themselves establish resistance to memorization or membership-inference attacks. Likewise, the classifier comparing generated and actual replay evaluates source distinguishability, not membership-inference resistance.

The protocol is now specified. For both ArcFace and CosFace we compare 10,000 generated images against a reference gallery of 10,000 real images, and count a probe as a match when its best cosine similarity to the gallery exceeds 0.5. ID Recall is the share of probes that match: 8 of 10,000 (0.08%) under ArcFace and 5 of 10,000 (0.05%) under CosFace. That threshold sits between the two reference levels reported in Fig. 9: cross-video pairs, that is, two different identities, average 0.024, whereas same-video pairs, that is, two frames of one identity, average 0.814. Generated-versus-training pairs average 0.0177, at or below the cross-video level. Replayed faces are therefore no more similar to training identities than two unrelated videos are to each other, which is the specific claim the identity evaluation supports.

Revision location: Section 4.9 (privacy analysis), Figures 8 and 9 (embedding similarity and reference distributions), Table 12 (identity recall), Appendix E.4 (further privacy evidence).

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

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