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Under review as a conference paper at ICLR 2027

GenStegoBench: Auditing Persistent Covert Channels in Latent Generative Image Systems

Abstract

Modern generative image systems are increasingly built on diffusion or flow-style iterative generation, where images can often be approximately inverted to latent or noise representations. This generation–recovery property creates a security concern: an ordinary-looking generated image may carry a covert message that remains decodable after common online processing. We introduce GenStegoBench, a security audit benchmark for measuring when generative-image steganographic channels persist, when they fail, and which transformations can disrupt them. Our audit provides both attacker- and defender-side insights: generator backbones and solvers transport decoder margins and can strengthen hidden-channel reliability, while common image transformations break different recoverable invariants. GenStegoBench audits covert-channel persistence through the generation–channel–recovery lifecycle of generative images.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Image Generation, Steganography, Robustness, Benchmark

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
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Paper summary

This paper presents GenStegoBench, a benchmark designed to audit persistent covert channels in latent generative image systems. The robustness of generative image steganography is examined from attacker and defender perspectives under a unified experimental protocol spanning generator backbones, solvers, inversion regimes, single-step transformations, ordered compound channels, payload levels, datasets, and prompts. GenStegoBench is not limited to benchmarking steganographic methods; it is further designed to diagnose why hidden covert channels persist or fail and to evaluate how effectively transformations disrupt such channels.

Critical strengths

This paper formulates generative steganography as an AI security auditing problem and proposes a full-lifecycle analysis framework spanning generation-channel-recovery. A dual attacker-defender auditing perspective is adopted to analyze how model properties are exploited by adversaries to improve steganographic robustness and how common image processing operations deployed on real-world platforms perform defensively. Within this framework, steganographic success is considered to depend on the preservation of message-bearing invariants after realistic multimedia transformations.

Critical weaknesses

(1) Core concepts, including the recoverable invariant, the latent stable subspace, and the decoder margin, are presented as heuristic diagnostic tools inferred from experimental observations; the theoretical grounding for this component is not provided.

(2) Although superior stability is observed for the DCT-domain embedding scheme and is attributed to a better match between the DCT basis and the latent stable subspace, controlled-variable experiments are not reported. Consequently, the effect of the DCT basis cannot be separated from those of the coding strategy and bit allocation.

(3) The evaluation coverage of the benchmark is limited. Although the benchmark is claimed to audit all covert channels in latent generative image systems, only steganographic schemes that modify latent vectors at inference time are covered. Comparisons with mainstream generative steganography methods, such as prompt steganography, black-box coverless steganography, CRoSS, and DiffStega, are absent, which limits the stated contribution.

(4) Existing robustness benchmarks for conventional steganography already include JPEG compression, resizing, and noise perturbations. In this work, such evaluation pipelines are adapted to the latent-space inversion setting, and the evaluation metrics, namely bit error rate and extraction accuracy, are inherited from prior frameworks.

Questions for authors

(1) Core concepts, including the recoverable invariant, the latent stable subspace, and the decoder margin, are presented as heuristic diagnostic tools inferred from experimental observations; the theoretical grounding for this component is not provided.

(2) Although superior stability is observed for the DCT-domain embedding scheme and is attributed to a better match between the DCT basis and the latent stable subspace, controlled-variable experiments are not reported. Consequently, the effect of the DCT basis cannot be separated from those of the coding strategy and bit allocation.

(3) The evaluation coverage of the benchmark is limited. Although the benchmark is claimed to audit all covert channels in latent generative image systems, only steganographic schemes that modify latent vectors at inference time are covered. Comparisons with mainstream generative steganography methods, such as prompt steganography, black-box coverless steganography, CRoSS, and DiffStega, are absent, which limits the stated contribution.

(4) Existing robustness benchmarks for conventional steganography already include JPEG compression, resizing, and noise perturbations. In this work, such evaluation pipelines are adapted to the latent-space inversion setting, and the evaluation metrics, namely bit error rate and extraction accuracy, are inherited from prior frameworks.

(5) The visualization experiments are not sufficiently comprehensive. Although generative steganography is distinguished from robustness evaluation for traditional steganography in the related work section, the comparison that justifies why prior work does not address the problem targeted in this paper remains underdeveloped. The current presentation is largely limited to an enumeration of existing literature, and strong comparative arguments are lacking.

7 comments

Rebuttal — Response to Reviewer qwt6

Paper: "GenStegoBench: Auditing Persistent Covert Channels in Latent Generative Image Systems" (ICLR 2027)

We thank the reviewer for the comments. The revision adds the theoretical grounding for the diagnostic concepts, the controlled-variable carrier ablation, an explicit scoping statement for the audited schema, a dimension-level comparison with prior robustness evaluations, and a strengthened comparative related-work section. The replies below point to their locations in the revised PDF.

W1 & Q1 — Theoretical grounding of the diagnostic concepts

Core concepts, including the recoverable invariant, the latent stable subspace, and the decoder margin, are presented as heuristic diagnostic tools inferred from experimental observations; the theoretical grounding for this component is not provided.

Response. We agree that the status of each concept must be stated precisely, and the revision does so in Section 5.1 and Appendix I. The three concepts play different roles by design, and the text now states which is which:

(i) A recoverable invariant is definitional, not inferred: each audited method fixes the decoding structure that carries its message—coordinate signs (BaseGen), positional grouping (S2IRT), Gaussian-CDF bins (PARIS), projection cells (GRDH), DCT signs (GSD), diffusion coordinates (MDDM), or stable positions (LDStega)—and persistence is defined by the formal condition ID(RP(T(GP(zm))))=ID(zm)I_D(R_P(T(G_P(z_m))))=I_D(z_m) of Section 2.3. It abstracts the method itself.

(ii) A decoder margin is an exact geometric object whenever the decoding constraint is linear: for γj(z)=aj⊤z−bj\gamma_j(z)=a_j^\top z-b_j, decoding is correct if and only if γj>0\gamma_j>0, and the transported margin satisfies the identity γj′=aj⊤FP(zm)−bj=γj+aj⊤δ\gamma'_j=a_j^\top F_P(z_m)-b_j=\gamma_j+a_j^\top\delta with δ=FP(zm)−zm\delta=F_P(z_m)-z_m. The sign, DCT-sign, and projection constraints of BaseGen, GSD, and GRDH are precisely of this linear form, and we measure the empirical boundary-crossing rate Pr⁡[γj′<0]\Pr[\gamma'_j<0] rather than assuming any closed-form law for the transport map FPF_P.

(iii) The latent stable space is designed as an operational diagnostic, and the text now states this explicitly, together with its formal definition. With the clean lifecycle map FP=RP∘GPF_P = R_P \circ G_P and its local linearization FP(z+v)≈FP(z)+JFP(z)vF_P(z+v) \approx F_P(z) + J_{F_P}(z)v, the τ\tau-stable set at zz is defined as SP(τ)=\mathcal{S}_P(\tau)= { v:∥∣JF(z)v−v∥∣2≤τ∥∣v∥∣2v:\||J_F(z)v-v\||_2\leq\tau\||v\||_2 } .

That is, it consists of directions along which the lifecycle approximately preserves latent perturbations. For linear decoding constraints, a bit error occurs when γj′=γj+aj⊤δ<0\gamma'_j = \gamma_j + a_j^\top\delta < 0. Thus, persistence is governed by the projection of the measured transport δ\delta onto the decoder normals.

We do not estimate JFPJ_{F_P} directly, and the text explains why: estimating each finite-difference column requires one additional full generation–inversion lifecycle per latent coordinate (16,384 per setting for the SD3.5 latent), while the Jacobian also varies along prompt-conditioned trajectories. The benchmark therefore measures the objects these definitions determine—boundary-crossing rates and recovered-margin distributions—which is the standard measurement stance for empirical security benchmarks, just as detectability benchmarks operationalize invisibility through trained steganalyzers. The diagnostics earn their validity from predictive content: stability-aware coordinate selection guided only by inversion displacement yields a consistent accuracy gain over the equal-budget random control (+4.54 pp; paired bootstrap 95% CI: [+3.74, +5.14] pp; sign test: 10/10, p=0.00195p = 0.00195; Table 3).

W2 & Q2(PART 1) — Controlled-variable separation of the DCT basis

Although superior stability is observed for the DCT-domain embedding scheme and is attributed to a better match between the DCT basis and the latent stable subspace, controlled-variable experiments are not reported. Consequently, the effect of the DCT basis cannot be separated from those of the coding strategy and bit allocation.

Response. We agree with the premise, and the revision adds precisely the missing controlled-variable design (Appendix I). It was motivated by an internal inconsistency in the submitted evidence: the Table-1 boundary-crossing probe reported a DCT-vs.-spatial ordering, but the two carriers compared there differed simultaneously in basis and in amplitude rule, so the probe could confirm an ordering without attributing it. We therefore (a) first checked that the ordering is not a prompt-selection artifact, then (b) ran a 2×22\times2 factorial that varies basis and amplitude one at a time, and (c) added a band-restriction arm to isolate bit allocation.

(a) Prompt robustness. The Table-1 probe was extended to 10 prompts per backbone under the same protocol (same C=Pr⁡[γ′<0]C=\Pr[\gamma'<0] definition, same solver choices; 190 generation–inversion cycles in total, all successful, no filtering). Table I-8 reports the 10-prompt means and standard deviations under the controlled-design carrier labels used throughout the revision: SpatialSign-Amp (BaseGen: spatial signs with data-dependent half-normal amplitudes ∣z0∣⋅s|z_0|\cdot s) and DCTSign-σ\sigma (GSD: DCT signs with uniform amplitudes σ⋅s\sigma\cdot s). The SpatialSign-Amp >> DCTSign-σ\sigma ordering holds on all 19 backbone$\times$solver presets (19/1919/19), and the between-carrier gaps (9.49.4–13.213.2 pp) far exceed the 10-prompt standard deviations (1.51.5–3.93.9 pp). The ordering is therefore real—but the probe alone cannot say why.

(b) The controlled design. Under the exact Table-4 protocol (SD1.5, DPM-Solver++ 20 steps, guidance 5, MSCOCO, the same secret, the same prompts and seed sequence, and the same generation–recovery pipeline; only the carrier construction changes), the seven variants form a 2×22\times2 factorial (basis {spatial, DCT} ×\times amplitude {data-dependent ∣z0∣⋅s|z_0|\cdot s, uniform σ⋅s\sigma\cdot s}), plus a fixed seeded random-orthogonal projection Q(σ⋅s)Q(\sigma\cdot s) (the aggregation hypothesis in its purest form), plus DCT restricted to the lowest/highest 25% zigzag bands. Table I-9 reports mean extraction accuracy over n=30n=30 images; all comparisons are paired on sample seed (identical secrets, identical generations). Three results follow, mapping one-to-one onto the three factors the reviewer names:

(i) Coding strategy (amplitude rule) is the dominant term: replacing BaseGen's ∣z0∣⋅s|z_0|\cdot s by the uniform rule σ⋅s\sigma\cdot s recovers +8.8+8.8 to +11.6+11.6 pp under every attack, in both bases (spatial: +10.67+10.67 pp on storage; DCT: +11.52+11.52 pp), with paired sign tests at p<10−7p<10^{-7}. The mechanism is the half-normal magnitude of ∣z0∣|z_0|: coordinates near zero carry vanishing decoder margins and flip under any transport or attack. The Table-4 DCT-over-spatial advantage is therefore explained by the coding strategy, not by the basis.

(ii) The DCT basis is statistically inert at uniform amplitude: DCT-sign vs. spatial-sign differ by +0.53+0.53 (storage), −0.35-0.35 (rescale), −1.57-1.57 (JPEG), +0.55+0.55 (blur), and −1.17-1.17 pp (median blur, the only nominally significant contrast, p=0.016p=0.016, and in the opposite direction). The submitted attribution of the DCT advantage to "a better match between the DCT basis and the latent stable subspace" is not supported by these controls and has been removed from the paper.

(iii) Bit allocation is a genuine but secondary effect: the equal-payload low-25% vs. high-25% DCT contrast isolates allocation from both basis and coding strategy, and the strict ordering low ≥\ge full ≥\ge high holds under every attack (e.g., 86.4>83.5>80.086.4 > 83.5 > 80.0 pp under 0.80.8 nearest-neighbor rescaling, and 90.7>88.7>87.190.7 > 88.7 > 87.1 pp under median blur), even though full-band carries 4×4\times the bits of the band-restricted variants. Low-band DCT also matches or beats the spatial uniform carrier in four of five attacks (storage +0.9+0.9, rescale +2.6+2.6 pp with p=0.0014p=0.0014, blur +0.7+0.7, median blur +0.8+0.8 pp; JPEG −0.5-0.5 pp, ns), consistent with the preserved low-frequency semantic structure. The frequency claim therefore survives in a corrected, quantitative form: concentrating the message in the low-frequency band helps by at most 6.46.4 pp, while the DCT basis itself is inert.

W2 & Q2(PART 2) — Controlled-variable separation of the DCT basis

Although superior stability is observed for the DCT-domain embedding scheme and is attributed to a better match between the DCT basis and the latent stable subspace, controlled-variable experiments are not reported. Consequently, the effect of the DCT basis cannot be separated from those of the coding strategy and bit allocation.

Response.

(c) Revised Core Finding I (Section 5.1) states exactly this three-way decomposition: (i) uniform rather than data-dependent half-normal amplitudes is the dominant mechanism (+8.8+8.8–11.611.6 pp in both bases, paired sign tests p<10−7p<10^{-7}); (ii) the DCT basis is statistically inert at uniform amplitude (all contrasts ≤1.6\le1.6 pp, the only nominally significant one running against DCT); (iii) bit allocation is a genuine but secondary effect (low-frequency band concentration, at most 6.46.4 pp). This is the reviewer's intuition, corrected and stated quantitatively: frequency carriers help because they concentrate the message in the low-frequency semantic region, and spatial carriers work when aligned with semantic contours; the ablation shows that low-band selection, not the DCT per se, is the operative frequency term.

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Paper summary

The paper presents GenStegoBench, an evaluation protocol for latent-vector generative image steganography. It treats the full generation → channel → inversion → decoding loop as the object of study. Seven methods (BaseGen sign coding, S2IRT, PARIS, GRDH, GSD, MDDM, LDStega) run on five backbones (SD1.5/2.1, SDXL, PixArt-α, SD3.5-Medium, FLUX.1-schnell), each with a matched solver/inversion pair. The images are subjected to:

  • single-step benign transformations: rescaling, JPEG, blur, noise, crop, and color/sharpness edits;
  • ordered or randomized "lifecycle" compositions up to depth 32.

Prompts come from Flickr8k, MSCOCO and Conceptual Captions.

The findings are organized as an attacker-side audit and a defender-side audit.

Attacker side.

  • DCT-sign carriers (GSD) have lower boundary-crossing rates than spatial sign carriers (BaseGen) across backbones (Table 1, single prompt).
  • Solver choice matters less than backbone, except on PixArt-α (Table 2).
  • Larger payloads push decoder margins toward the boundary (Fig. 5).
  • A "stable-space" view motivates two modifications to BaseGen: embedding only on a stable 80% of coordinates, and a learned residual module (Table 3).

Defender side.

  • Setting: MSCOCO, SD1.5 with DPM-Solver++, 10 images per setting (Table 4).
  • Nearest-neighbor rescaling is the strongest single-step disruptor for all methods.
  • JPEG costs the strongest methods 6–9 pp.
  • Median filtering hurts more than Gaussian blur.
  • In lifecycle experiments (SD2.1-DDIM subset), accuracy drops sublinearly and saturates:
    • repeated JPEG or resize: 92.45% → ~77% at T=16T=16;
    • stronger pipelines: 62.73–71.96%.

Guardrails. Stego images show Δ\DeltaFID ≈ 7.7–8.3, and classical steganalyzers (XuNet, SRNet, YeNet) stay near chance.

All validation is empirical. The formal parts introduce notation for the composed map and the margins; they do not state or prove results.

Critical strengths

1. Treating the backbone/solver/inversion setup as part of the channel, with seven methods compared in one controlled pipeline.

Each existing method reports results under its own settings, so a like-for-like comparison is useful. Table 4 already gives a coherent cross-method picture:

  • Every method loses 15–29 pp under nearest-neighbor resampling, but only about 3–10 pp under bilinear or bicubic.
  • LDStega is the only method that is highly sensitive to blur (−17 to −19 pp).
  • Carriers that aggregate over many latent coordinates (GSD, GRDH) or select stable positions (LDStega) reach about 98% clean accuracy, versus about 86% for per-coordinate sign coding.

Coverage of DiT and flow backbones (PixArt-α, SD3.5, FLUX in Table 1) is also new for this literature. This is the main reason the work could become a useful reference if scaled up and released.

2. Lifecycle evaluation.

Ordered, repeated and randomized compositions up to depth 32 go beyond the single-perturbation tables that are standard in this field. Two observations are relevant to anyone assessing platform-side risk:

  • Degradation is sublinear: Δ(8,16)≈Δ(16,32)\Delta(8,16) \approx \Delta(16,32).
  • Accuracy stays well above chance after 16–32 operations.
Critical weaknesses

1. The evidence is too thin and too fragmented to support benchmark-level conclusions.

  • Sample sizes are very small, and no variability is reported.
    • The main defense table (Table 4) uses 10 images per setting, one backbone/solver pair, and, in the main paper, only MSCOCO.
    • Table 1 and Fig. 3 use a single prompt.
    • Table 3 uses one prompt plus a 10-prompt cached probe.
    • The lifecycle results (Figs. 6–7) come from a "completed SD2.1-DDIM subset", and the guardrails from a "completed five-method subset".
    • No table or figure reports standard deviations or confidence intervals.
  • Each finding comes from a different slice of the setup. Table 3 uses SD3.5, Table 4 uses SD1.5 with DPM-Solver++, and the lifecycle uses SD2.1-DDIM. The advertised backbone × solver × method × payload × dataset × perturbation grid is never filled in for any single claim. Statements such as "frequency-domain carriers are generally more stable" (Core Finding I) are therefore not established.
  • Effective method diversity is smaller than claimed.
    • At the main operating point (ERl=1ER_l = 1), BaseGen, PARIS and MDDM agree to within 2 pp in every column of Table 4, and within 0.6 pp in 9 of the 12 attack columns:
      • identity: 86.25 / 86.60 / 86.63
      • nearest-neighbor: 69.91 / 70.12 / 70.00
      • bilinear: 82.47 / 82.77 / 82.65
      • crop: 75.81 / 75.98 / 75.76
    • This is what one would expect if 1-bit Gaussian-CDF bins and sign-separated sampling both reduce to plain sign coding.
    • GRDH and GSD likewise stay within 2.5 pp of each other in every column.
    • In practice, Table 4 covers about three carrier geometries, not seven.
    • Four methods also have identity (no-attack) accuracy of only 86–90%, which raises questions about the fidelity of the re-implementations (Q2).
  • The attacker-side "minimal modifications" (Table 3) are weakly supported.
    • The stable-80% gain (+4.6 to +5.4 pp) is reported at 80% payload, with no matched-payload control such as a random 80% subset or equivalent redundancy.
    • The large residual-module gains (+9 to +12 pp) are measured only on cached surrogates.
    • Under the end-to-end guardrail, the gains are +1.4, +2.8 and +2.6 pp at SSIM .901, .782 and .681. That is visible quality loss for small gains.
    • The trend is also not monotone (amplitude 0.15 gives 84.07 vs. 84.19 at 0.10), which contradicts the text's claim that "larger amplitudes increase recovery".

2. The central conclusions do not follow from the measurements, and the proposed mechanisms are not separated from simpler explanations.

  • Bit accuracy is not channel persistence.
    • The paper asks when a covert message persists, but it only measures raw bit accuracy. A channel persists if it keeps positive capacity once error correction is applied.
    • Even under an idealized binary symmetric channel, the "disrupted" end states keep substantial capacity:
      • At 68.78% (platform block, T=16T=16), 1−H(p)≈0.101 - H(p) \approx 0.10 bit per coordinate, about 1.7 kbit per 512×512 SD image (4×64×64 latent).
      • At 62.73% (human–platform block), it is ≈ 0.047 bit per coordinate, about 0.8 kbit per image.
    • A standard ECC with interleaving can carry a meaningful payload at these rates. Conversely, 98% bit accuracy without ECC fails for long messages.
    • The defender-side conclusions ("benign processing is useful as a disruption mechanism", "residual risk") therefore cannot be read off Table 4 or Figs. 6–7. Message-level success at a matched code rate, or effective capacity, is needed.
  • The mechanisms are not identified.
    • (a) The "stable space" argument is close to circular.
      • The stable space is defined as the directions whose decoder margins are empirically preserved, so "carriers aligned with the stable space are reliable" restates the definition.
      • Core Finding I is hedged both ways (frequency carriers are better, and spatial carriers are fine when aligned), which leaves almost no outcome that could contradict it.
      • The paper's own data point elsewhere. GRDH uses a keyed random orthogonal projection, not a frequency transform, yet it matches GSD (identity 97.93 vs. 98.50, with similar profiles under every perturbation). The operative factor may be non-axis-aligned aggregation rather than "frequency".
      • A control comparing a random orthogonal basis, the DCT, and band-restricted DCT would settle this.
    • (b) Lifecycle saturation has an obvious alternative explanation.
      • Repeated JPEG at a fixed quality, or repeated identical resampling, is nearly idempotent: the image itself stops changing after a few steps.
      • A(T)A(T) would then saturate because of the operator, not because "surviving components are aligned with more stable invariants" (L409–411).
      • Reporting the per-step image change, or randomizing the operator parameters at each step, would distinguish the two.
Questions for authors
  1. Scale and statistics.
    • What does "10 valid images" mean? Is any filtering applied, e.g., by decoding success or quality?
    • How many prompts/images and seeds are used per cell across the benchmark, and which cells of the full grid are actually completed?
    • Please report standard deviations or confidence intervals across images and seeds for Tables 1–4 and Figs. 6–7.
  2. Re-implementation fidelity.
    • At ERl=1ER_l = 1, do PARIS and MDDM reduce to sign coding, and is that why they nearly match BaseGen?
    • How do your identity accuracies (86–90% for BaseGen, S2IRT, PARIS and MDDM) compare with the original papers' numbers under their native settings, including any ECC they use? If yours are lower, what explains the gap?
  3. Message-level metric.
    • Can you report message recovery with a standard ECC at a matched effective rate, or capacity estimates, for Table 4 and the lifecycle curves?
    • Do the defender-side conclusions survive under that metric?
  4. Mechanism controls.
    • (a) Compare a random orthogonal basis, the DCT, and low-band vs. high-band DCT subsets under the same pipeline, to test whether "frequency" matters beyond aggregation.
    • (b) For the lifecycle runs, report the per-step image change (e.g., PSNR between xtx_t and xt+1x_{t+1}), and the curves when JPEG quality and resize factor are randomized at each step.
  5. Table 3.
    • How is the stable 80% set chosen, and is it chosen on prompts disjoint from the evaluation prompts?
    • How does the receiver know the set without access to the clean image?
    • Does a random 80% subset give a similar gain?
    • Is the residual module applied in pixel space after generation? If so, it is a post-hoc embedding, not generative steganography.
    • What is the SSIM of the 0.35 configuration behind the +9–12 pp headline?
  6. Threat model and recovery.
    • Does the receiver know the prompt, guidance scale and number of steps?
    • Which prompt is used for inversion?
    • How sensitive is recovery to a mismatch in each of these?
  7. Defender scope.
    • Within your own non-adaptive, decoder-agnostic threat model, why are the following left out? They seem to be the most natural content-preserving sanitizers.
      • VAE re-encoding.
      • Diffusion-based regeneration (e.g., Zhao et al., Invisible Image Watermarks Are Provably Removable Using Generative AI, NeurIPS 2024).
      • Small (< 8 px) translations that misalign the VAE grid.
    • How does GenStegoBench relate to latent-watermark robustness work that uses the same mechanisms (Tree-Ring, Gaussian Shading), and to the WAVES benchmark (An et al., ICML 2024)?
  8. Detectability.
    • Since the generator is public in your threat model, a warden can invert images and test the statistics of the recovered latents. Was any latent-space or generation-aware steganalyzer evaluated?
    • How were XuNet, SRNet and YeNet trained (were the covers ordinary generations from the same model?), and on how many images?
    • Please justify calling Δ\DeltaFID ≈ 8 a small shift, and state the sample size used for FID.

Minor (no effect on score):

  • Sec. 4 lists 4–5 severities per family and lifecycle depths {0,1,2,4,8,16,32}\{0,1,2,4,8,16,32\}, but Table 4 averages over "three severities" and Fig. 7 uses T∈{0,1,2,4,8,12,16}T \in \{0,1,2,4,8,12,16\}. Please state exactly which values are used.
  • ERlER_l, CC/γ′\gamma' and "cached-surrogate" are not defined in the main text.
  • Figs. 4, 5 and 7 are unreadable at print size.
  • The abstract states no concrete finding.
  • Will the code, generated images and per-cell results be released?
20 comments

Rebuttal — Response to Reviewer o7cs

Paper: "GenStegoBench: Auditing Persistent Covert Channels in Latent Generative Image Systems" (ICLR 2027)

We thank the reviewer for the detailed and technically deep review. The revision adds the requested statistics, the equal-budget controls, the message-level capacity analysis, the controlled carrier ablation, the lifecycle idempotence diagnostics, and the missing defender operations. The replies below point to their locations in the revised PDF.

W1.1 & Q1 — Scale and statistics

The evidence is too thin and too fragmented to support benchmark-level conclusions. Sample sizes are very small, and no variability is reported. The main defense table (Table 4) uses 10 images per setting, one backbone/solver pair, and, in the main paper, only MSCOCO. Table 1 and Fig. 3 use a single prompt. Table 3 uses one prompt plus a 10-prompt cached probe. The lifecycle results (Figs. 6–7) come from a "completed SD2.1-DDIM subset", and the guardrails from a "completed five-method subset". No table or figure reports standard deviations or confidence intervals. Each finding comes from a different slice of the setup. Table 3 uses SD3.5, Table 4 uses SD1.5 with DPM-Solver++, and the lifecycle uses SD2.1-DDIM. The advertised backbone ×\times solver ×\times method ×\times payload ×\times dataset ×\times perturbation grid is never filled in for any single claim. Q1: What does "10 valid images" mean? Is any filtering applied, e.g., by decoding success or quality? How many prompts/images and seeds are used per cell across the benchmark, and which cells of the full grid are actually completed? Please report standard deviations or confidence intervals across images and seeds for Tables 1–4 and Figs. 6–7.

Response.

"10 valid images" means no filtering. Each setting executes 10 complete generate–embed–invert–recover pipelines, all of which succeeded (valid == 10, invalid == 0); no image is filtered by decoding success or image quality, each image is executed exactly once, and nothing is retried. The number of generation attempts per setting therefore equals the number of reported valid images (Appendix F).

Grid completion. The full grid has been executed: 25 generator presets ×\times 7 methods == 175 method$\times$preset directories, of which 146 contain the complete 37-attack grid (some with additional rows) and 28 contain a five-attack representative subset (FLUX-schnell for all 7 methods; the DDPM-deterministic presets of SD2.1 with 7 methods and of SDXL and PixArt-α\alpha with 6 methods each, GSD not run; SD3.5 LDStega; and the SD3.5 stable-80% intervention control), plus one aggregate summary file, totaling 5,903 executed settings, each with 10 images and one seed. Beyond the main matrix: the solver ablation (7 methods ×\times 2 datasets), the four-dataset complementary attack sets (36 directories), and the lifecycle-depth suite (66 method$\times$preset directories; 1,848 settings ×\times 10 images, spanning SD1.5 with all five solvers, SD2.1 with DDIM and DPM-Solver++, PixArt-α\alpha with DDIM, and SD3.5/FLUX with their flow solvers), for a total coverage of 8,589 executed settings. The main-text slice choices select one representative view within the page limit (Appendix F).

Standard deviations and intervals, now reported. Table 1's single-prompt probe is supplemented by a 10-prompt mean$\pm$std version (Table I-8, Appendix I); all 259 (method, attack, severity) cells of Table 4 carry their within-setting 10-image standard deviations (Table F-5; mean std 2.432.43 pp, maximum 7.317.31 pp); the Stable-80% gain of Table 3 carries per-image paired bootstrap and tt intervals (95% CI [3.69,5.39][3.69,5.39] pp, Appendix B); and the Figs. 5–6 depth curves report their within-setting standard deviations in the captions (mean 2.622.62 pp, maximum 5.05.0 pp). Sample-size calibration is validated externally: a 256-prompt run of the identical protocol reproduces the 10-image Table-4 means with mean absolute deviation 0.850.85 pp and maximum 3.773.77 pp across 64 matched settings (Table F-4).

W1.2 & Q2 (PART 1)— Effective method diversity and re-implementation fidelity

Effective method diversity is smaller than claimed. At the main operating point (ERl=1ER_l=1), BaseGen, PARIS and MDDM agree to within 2 pp in every column of Table 4, and within 0.6 pp in 9 of the 12 attack columns (identity: 86.25 / 86.60 / 86.63; nearest-neighbor: 69.91 / 70.12 / 70.00; bilinear: 82.47 / 82.77 / 82.65; crop: 75.81 / 75.98 / 75.76). This is what one would expect if 1-bit Gaussian-CDF bins and sign-separated sampling both reduce to plain sign coding. GRDH and GSD likewise stay within 2.5 pp of each other in every column. In practice, Table 4 covers about three carrier geometries, not seven. Four methods also have identity (no-attack) accuracy of only 86–90%, which raises questions about the fidelity of the re-implementations (Q2). Q2: At ERl=1ER_l=1, do PARIS and MDDM reduce to sign coding, and is that why they nearly match BaseGen? How do your identity accuracies (86–90% for BaseGen, S2IRT, PARIS and MDDM) compare with the original papers' numbers under their native settings, including any ECC they use? If yours are lower, what explains the gap?

Response. The reviewer's conjecture is correct, and we now state it analytically and verify it empirically (Appendix H).

The three-way agreement is a saturation artifact. At one bit per coordinate, both PARIS's Gaussian-CDF bins and MDDM's sign-separated truncated sampling reduce to plain sign coding. Analytically: (i) BaseGen emits zi=si ∣gi∣z_i=s_i\,|g_i| with gi∼N(0,1)g_i\sim\mathcal{N}(0,1) and decodes the sign; (ii) PARIS at bits=1bits=1 splits the CDF at its median, so the two bins are exactly zi<0z_i<0 and zi>0z_i>0, zi=Φ−1((ui+mi)/2)z_i=\Phi^{-1}\big((u_i+m_i)/2\big) has half-normal magnitude, and decoding ⌊2Φ(zi)⌋\lfloor 2\Phi(z_i)\rfloor is the sign test; (iii) MDDM's tail threshold satisfies k=Φ−1(1−L/2N)k=\Phi^{-1}(1-L/2N), and the benchmark's dense adaptation forces L=N=16,384L=N=16{,}384, giving k=0k=0: the left/right tails become the negative/positive half-axes and the central fill region vanishes. All three carriers are therefore the same half-normal-amplitude sign code at this operating point—which is why the identity column reads 86.25/86.60/86.6386.25/86.60/86.63: the 0.380.38 pp spread is below each method's own within-setting 10-image standard deviation (1.181.18–1.861.86 pp, Table F-5). The collapse is a property of the dense ERl=1ER_l=1 operating point, not of the methods, and it is precisely the capacity-for-margin saturation this audit is designed to expose. Both methods have their own regimes, where they diverge sharply from BaseGen, and both regimes are now evaluated: PARIS's multi-bit CDF bins at ERl≥2ER_l\geq2 (the only multi-bit-per-coordinate coding among the seven methods; capacity–accuracy frontier in Table C-7: 0.8693→0.8327→0.7196→0.61280.8693\to0.8327\to0.7196\to0.6128 no-attack accuracy as ERlER_l goes 1→81\to8), and MDDM's sparse regime, which we executed under the exact Table-4 protocol at L=8192L=8192 (k=0.6745k=0.6745) and L=4096L=4096 (k=1.1503k=1.1503), against a BaseGen control evaluated at the identical grille coordinates from the same seed (same positions, same bits, same generations). Table H-6 reports the masked bit accuracies: MDDM exceeds the masked BaseGen control by 8.28.2–16.716.7 pp in every one of the six attack settings, and the gain is monotone in kk. The 86.6386.63 identity entry of Table 4 is thus the saturated endpoint (k→0k\to0) of a genuine capacity–margin trade-off, not the method's characteristic behavior.

W1.2 & Q2(PART 2) — Effective method diversity and re-implementation fidelity

Effective method diversity is smaller than claimed. At the main operating point (ERl=1ER_l=1), BaseGen, PARIS and MDDM agree to within 2 pp in every column of Table 4, and within 0.6 pp in 9 of the 12 attack columns (identity: 86.25 / 86.60 / 86.63; nearest-neighbor: 69.91 / 70.12 / 70.00; bilinear: 82.47 / 82.77 / 82.65; crop: 75.81 / 75.98 / 75.76). This is what one would expect if 1-bit Gaussian-CDF bins and sign-separated sampling both reduce to plain sign coding. GRDH and GSD likewise stay within 2.5 pp of each other in every column. In practice, Table 4 covers about three carrier geometries, not seven. Four methods also have identity (no-attack) accuracy of only 86–90%, which raises questions about the fidelity of the re-implementations (Q2). Q2: At ERl=1ER_l=1, do PARIS and MDDM reduce to sign coding, and is that why they nearly match BaseGen? How do your identity accuracies (86–90% for BaseGen, S2IRT, PARIS and MDDM) compare with the original papers' numbers under their native settings, including any ECC they use? If yours are lower, what explains the gap?

Response.

GRDH/GSD proximity is predicted by the carrier mechanism. The controlled carrier ablation (Appendix I, Table I-9)—reported in full in the reply to W2.2(a) & Q4(a) below—varies the carrier's basis and amplitude rule one at a time under the exact Table-4 protocol and shows that the Table-4 proximity is what the mechanism predicts, not an artifact: the amplitude rule dominates (uniform vs. data-dependent amplitudes recover +8.8+8.8–11.611.6 pp under every attack), while at uniform amplitude keyed orthonormal projection, DCT, and random-orthogonal carriers are statistically interchangeable (basis contrasts ≤1.6\le1.6 pp; the aggregation arm tracks within ±1.4\pm1.4 pp), and only low-frequency band allocation survives as a genuine but secondary modulator (at most 6.46.4 pp). Equal accuracy still does not identify channels: GRDH uses rounding-cell recovery over a keyed projection, while GSD is per-coefficient DCT sign coding, and they respond differently to the generation–recovery transport across backbones. Counting mechanisms rather than accuracy profiles, the benchmark evaluates five distinguishable method families at ERl=1ER_l=1—sign (BaseGen; with PARIS/MDDM saturating onto it), rank (S2IRT), keyed projection (GRDH), frequency sign (GSD), and stable-position (LDStega)—of which the keyed-projection and frequency-sign families are carrier-equivalent at uniform amplitude but distinct in recovery and failure families—plus two methods with distinct non-degenerate regimes (PARIS at ERl≥2ER_l\geq2, MDDM at rate <1<1). Method differentiation rests on the mechanism analysis of Sections 5.1–5.2 together with these regime-specific evaluations.

The 86–90% identity band vs. native settings. The native pipelines differ from the benchmark's unified operating point in backbone, decoder, and error protection (Table H-7): PARIS (Yang et al., 2024, IEEE TMM) uses a GAN generator with gradient-descent latent recovery under a noise layer; S2IRT (Zhou et al., 2023, IEEE TDSC) uses a bijective flow-based Glow generator with "almost 100% accuracy"; MDDM (Xu et al., 2025, ICML) uses SD1.5 with DDIM 30 steps, guidance 7.5, a sparse payload (512–2048 bits in the released demo), and optional repetition-3 / Hamming(7,4) ECC, with perfect clean recovery reported. The benchmark reports bit accuracy, forces ERlER_l density, and transplants all methods onto DPM-Solver++ 20 with guidance 5. The message-level question the reviewer raises(ECC)—what survives once standard error correction is applied—is answered separately, in the reply to W2.1 & Q3 below and in Appendix K of the paper. The 8686–90%90\% identity band is the measured quantity, not a broken pipeline: (i) in the same pipeline GRDH/GSD/LDStega reach 97.93/98.50/98.16%97.93/98.50/98.16\%, so the pipeline itself is not systemically lossy; (ii) the identity ordering is mechanism-consistent—projection averaging, DCT aggregation, and stability-based position selection inherently survive the generation–inversion transport better than rank grouping, which in turn beats bare sign coding—an ordering that a faulty re-implementation would not reproduce; (iii) the pipeline is deterministic and reproducible: an independent control run reproduces Table-4's BaseGen cells to 0.060.06 pp or better on 5/6 settings (Table H-6, full column), and the legacy 256-prompt runs match the 10-image main table within 0.850.85 pp on average (Table F-4). The unification is deliberate (Section 4): reported results in this literature are highly pipeline-dependent, and a method transplanted into another method's pipeline often degrades substantially; under this control, discovering which mechanisms saturate at ERl=1ER_l=1 and which do not is itself an audit finding.

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Paper summary

This paper introduces GenStegoBench, a security audit benchmark for assessing the persistence of generative-image steganographic channels through the generation–channel–recovery lifecycle. Covering seven latent-vector steganographic methods, the authors examine how generator backbones, solvers, payload levels, and image transformations affect recoverable invariants and decoder margins. Results from the tested configurations show that frequency-domain carriers are generally more stable than spatial carriers in the clean generation–recovery loop. Under the evaluated lifecycle policies, repeated benign processing reduces bit accuracy, but lifecycle-level anti-stego gains saturate as depth increases.

Critical strengths
  1. A unified audit benchmark. The paper brings image generation, channel transformations, and message recovery into a unified framework covering seven latent-vector steganographic methods, making it easier to compare how different stages affect covert-channel persistence.
  2. A clear interpretation of failure patterns. Using decoder margins and boundary crossings, the authors connect failure patterns across methods and help explain why increasing the payload makes decoding errors more likely.
  3. Practical insight from lifecycle experiments. Figures 6–7 show that, under the tested conditions, lifecycle-level anti-stego gains saturate as depth increases, highlighting the limits of relying on repeated benign processing to erase covert channels.
Critical weaknesses
  1. Evidence for generalizability is limited. Table 4 uses only 10 valid images per setting, while Figures 6–7 focus on the SD2.1-DDIM configuration on MSCOCO. Broader quantitative summaries across configurations and uncertainty estimates are needed to establish the robustness of the findings.
  2. The gains from stable coordinate selection are not fully isolated. The “Stable 80%” results in Table 3 are based on cached clean-transport probes and use 80% of the original payload. An equal-payload baseline using randomly selected coordinates would help isolate the benefit of stable coordinate selection.
  3. Defense comparisons need to account for image quality. Section 5.3 mainly evaluates quality changes caused by embedding. It does not show how the processing strategies compare in disrupting covert channels at comparable levels of image-quality loss.
Questions for authors
  1. What criteria define a valid image in Table 4, and what was the total number of generation attempts per setting? Could you report sample sizes and uncertainty estimates across datasets and generator backbones to help assess the generalizability of the lifecycle findings?
  2. How are the empirically stable 80% of coordinates identified, and does their selection depend on the test prompts or secret messages? How much does this selection improve extraction accuracy over randomly selecting 80% of coordinates at the same payload?
  3. Could you report the trade-off between the quality of transformed images and extraction accuracy? Were XuNet, SRNet, and YeNet trained on generated images from the same generator as the test images, and what were the train/test splits and sample sizes?
3 comments

Rebuttal — Response to Reviewer JNf9

Paper: "GenStegoBench: Auditing Persistent Covert Channels in Latent Generative Image Systems" (ICLR 2027)

We thank the reviewer for the careful reading and the constructive questions. The revised paper adds the requested experiments, uncertainty estimates, and controls; the replies below point to their locations in the revised PDF.

W1 & Q1 — Generalizability, sample sizes, and uncertainty estimates

Evidence for generalizability is limited. Table 4 uses only 10 valid images per setting, while Figures 6–7 focus on the SD2.1-DDIM configuration on MSCOCO. Broader quantitative summaries across configurations and uncertainty estimates are needed to establish the robustness of the findings. Q1: What criteria define a valid image in Table 4, and what was the total number of generation attempts per setting? Could you report sample sizes and uncertainty estimates across datasets and generator backbones to help assess the generalizability of the lifecycle findings?

Response. We agree that sample sizes and uncertainty must be reported explicitly, and the revision does so.

Valid-image criterion and generation attempts. A sample is counted as valid when the full pipeline—embedding, text-conditioned generation, inversion-based extraction, and the applied transformation—completes without error and yields a well-defined per-sample bit accuracy. Each sample is executed exactly once per setting and is never retried, so the number of generation attempts per setting equals the number of reported valid images (10 for Table 4); no image is post-hoc filtered out (Appendix F).

Why 10 images, validated externally. During protocol design we swept the per-setting sample size over {1,5,10,50,100}\{1,5,10,50,100\} and observed that the setting-level mean stabilizes around 10 images, which we adopted as the cost–stability balance point. To substantiate this externally, we compared the Table-4 settings against a 256-prompt run of the identical protocol (SD1.5, DPM-Solver++ 20 steps, guidance 5, MSCOCO, ERl=1ER_l=1). Across the 64 matched (method, attack, severity) settings covered by both experiments (BaseGen, GRDH, GSD, PARIS), the mean absolute deviation between the 10-image and the 256-prompt setting-level means is 0.850.85 percentage points and the largest deviation is 3.773.77 pp, so the 10-image means reproduce the large-sample means at the precision reported in the paper (Table F-4 reports the paired means and standard deviations). The same records show that latent-space embedding is fairly insensitive to prompt variation: in the identity (storage) setting, per-prompt accuracy spans 5.55.5 pp for PARIS and 8.18.1 pp for GRDH across all 256 prompts, and the spread is driven by a few harder prompts—after removing the single most extreme prompt on each side the ranges shrink to 4.24.2 pp (PARIS) and 1.51.5 pp (GRDH), with a within-setting standard deviation of ≈1.7\approx1.7–2.32.3 pp (Appendix F).

Uncertainty estimates added. Standard deviations are now reported alongside every headline number: all 259 (method, attack, severity) cells of Table 4 carry their within-setting 10-image standard deviations (Table F-5; mean std 2.432.43 pp, maximum 7.317.31 pp); the Table-1 boundary-crossing probe is supplemented by a 10-prompt mean$\pm$std version (Table I-8, Appendix I); the Stable-80% gain of Table 3 carries per-image paired bootstrap and tt intervals (95% CI [3.69,5.39][3.69,5.39] pp); and the Figures 5–6 depth curves report their within-setting standard deviations in the captions (mean 2.622.62 pp, maximum 5.05.0 pp).

Coverage beyond the shown slices. The lifecycle experiments were executed beyond the SD2.1-DDIM slice shown in the main text: the lifecycle-depth suite covers 66 method$\times$preset directories (1,848 settings ×\times 10 images), spanning SD1.5 with all five solvers ×\times 7 methods, SD2.1 with DDIM and DPM-Solver++ ×\times 7 methods, PixArt-α\alpha with DDIM ×\times 7 methods, and SD3.5/FLUX with their flow solvers ×\times 6 methods. More broadly, the full backbone$\times$solver$\times$method$\times$attack$\times$severity grid has been executed: 25 generator presets ×\times 7 methods == 175 method$\times$preset directories, of which 146 contain the complete 37-attack grid and 28 contain a five-attack representative subset (FLUX for all 7 methods; the DDPM-deterministic presets of SD2.1/SDXL/PixArt-α\alpha; SD3.5 LDStega; the stable-80% control), totaling 5,903 executed settings (Appendix F). The main-text slice choices select one representative view within the page limit.

W2 & Q2 — Isolating the gain from stable coordinate selection

The gains from stable coordinate selection are not fully isolated. The "Stable 80%" results in Table 3 are based on cached clean-transport probes and use 80% of the original payload. An equal-payload baseline using randomly selected coordinates would help isolate the benefit of stable coordinate selection. Q2: How are the empirically stable 80% of coordinates identified, and does their selection depend on the test prompts or secret messages? How much does this selection improve extraction accuracy over randomly selecting 80% of coordinates at the same payload?

Response. We agree that an equal-payload random-coordinate baseline is the necessary control, and we have added it to Table 3 (red row). At the same 80% payload budget, Random-80% attains 72.41%72.41\% clean extraction accuracy versus 72.40%72.40\% at full payload—budget reduction alone yields no gain (+0.01+0.01 pp)—while Stable-80% attains 76.95%76.95\%, i.e., +4.54+4.54 pp over the equal-budget random control (+4.55+4.55 pp over the full-payload reference; relative gain 6.27%6.27\%). The advantage is consistent across images: per-image gaps are [+1.6,+5.8][+1.6,+5.8] pp, the image-level paired bootstrap 95% CI is [+3.74,+5.14][+3.74,+5.14], the paired tt-interval is [+3.69,+5.39][+3.69,+5.39], and the sign test is 10/1010/10 positive (p=0.00195p=0.00195).

How the stable 80% is identified. The selection comes from generator inversion, not from recovery accuracy: on cached clean-transport probes (full-payload encode →\to generation →\to inversion), each latent coordinate is scored by its inversion-induced displacement ∣z′−zm∣|z'-z_m|, and per channel the 80% of coordinates with the smallest displacement are retained (3,277 of 4,096 per channel; 52,432 of 65,536 overall). No recovery accuracy, decoder output, or BER of the secret enters the selection, so the mask is not recovery-guided (Appendix B states the full protocol).

W3 & Q3 — Defense comparisons at matched image quality

Defense comparisons need to account for image quality. Section 5.3 mainly evaluates quality changes caused by embedding. It does not show how the processing strategies compare in disrupting covert channels at comparable levels of image-quality loss. Q3: Could you report the trade-off between the quality of transformed images and extraction accuracy?

Response. We agree, and the revision adds a quality-matched comparison of image transformations (Appendix L), which treats image quality as a common yardstick for how destructive different transformations are to covert channels. For every stego image we compute LPIPS between IstegoI_{\mathrm{stego}} and T(Istego)T(I_{\mathrm{stego}}) (VGG16 backbone, fixed implementation), and compare the extraction accuracy of JPEG (Q=10/30/50/70/90Q=10/30/50/70/90), Gaussian blur (k=3/5/7/9k=3/5/7/9), AWGN (σ=0.01/0.05/0.1/0.2\sigma=0.01/0.05/0.1/0.2), and resize (nearest/bilinear/bicubic, f=0.2f=0.2–1.01.0) at matched LPIPS levels, with matching targets chosen data-driven from the observed LPIPS distributions and the achieved LPIPS and matching error reported per row. All transformations are applied to the identical stego images (same seeds, same secrets, same decoders). In total: SD1.5 with DPM-Solver++ (20 steps), LDStega ×\times 3 datasets and MDDM ×\times 2 datasets, 219 configurations, 2,190 image-level samples (n=10n=10 per configuration).

Three findings follow. (i) At matched LPIPS, the disruption ranking is method-dependent: for LDStega, Gaussian blur is the most destructive transformation per unit quality loss (Flickr8k at LPIPS ≈0.141\approx0.141: a 12.712.7 pp gap, 92.8%92.8\% vs. 80.1%80.1\%, Table 6); for MDDM the ordering reverses (Conceptual Captions at LPIPS ≈0.205\approx0.205: blur k=7k=7 retains 79.6%79.6\% while JPEG Q=30Q=30 drops to 72.6%72.6\%). (ii) Per-family averaging hides method-specific weak spots, which motivates the quality-matched view as a complement to Section 5.3. (iii) The framework extends to all seven methods on the existing dpm20 crop/contrast/sharpen grids (3 datasets, 189 configurations, 1,890 images): at matched LPIPS, sharpening is no more disruptive than contrast for six methods, yet it is the most disruptive family for LDStega on 3/3 datasets (MSCOCO: 88.9%88.9\% vs. 91.0%91.0\%; Table L-11)—consistent with LDStega's unique sensitivity to high-frequency distortion.

For the trade-off itself, we report full LPIPS–accuracy (and LPIPS–BER) curves for every (method, dataset) pair (Figure L-4) and per-family ranges (Table L-12). The curves cross substantially at mid-range LPIPS (e.g., LDStega/MSCOCO at LPIPS ≈0.14\approx0.14–0.160.16: JPEG Q=50Q=50 92.7%92.7\% vs. AWGN σ=0.05\sigma=0.05 83.9%83.9\% vs. bilinear f=0.4f=0.4 85.5%85.5\%), which is precisely why a matched comparison is needed to rank transformations fairly.

Q3 — Training protocol of XuNet, SRNet, and YeNet

Were XuNet, SRNet, and YeNet trained on generated images from the same generator as the test images, and what were the train/test splits and sample sizes?

Response. Yes. All covers and stegos, for training and testing alike, come from one SD1.5 pipeline identical to the benchmark's: full sd-v1-5 weights, a 20-step DPM solver, guidance 5, 512×512512\times512, MSCOCO prompts, ERl=1ER_l=1; covers are clean images with no message embedded. For each steganographic method, 5,000 stego/clean pairs were generated from one shared pool of 5,000 MSCOCO prompts, then split disjointly into 4,000 training, 500 validation, and 500 test pairs. The training set mixes four methods in equal proportions (BaseGen, GRDH, PARIS, S2IRT; 1,000 pairs each), while GSD appears only in the test set—an unseen-method evaluation under the same checkpoints. XuNet and YeNet operate on grayscale 512×512512\times512 inputs and SRNet on RGB inputs; XuNet uses 90∘90^\circ random-rotation augmentation, YeNet uses rotation plus mirroring, and SRNet uses no augmentation. YeNet selects the best validation-accuracy checkpoint, while XuNet and SRNet use their final saved checkpoints. Training accuracy itself stayed near chance (e.g., $\approx$58% for XuNet), consistent with the near-random test accuracies in Table D-3 (the full protocol is now stated in Appendix D).

We thank the reviewer again for the helpful questions; all code, generated images, and experimental results will be released.

Comments on the paper

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Summary of Rebuttal Responses and Revisions

We thank the reviewers for their positive and constructive feedback during the author–reviewer discussion period. Below, we summarize our responses to their main concerns and the corresponding revisions made during the rebuttal phase:

1. The basis and amplitude choice in the robustness–security trade-off. We implemented a controlled carrier ablation (basis ×\times amplitude rule) that separates two previously confounded variables: the amplitude rule is the dominant accuracy term (uniform amplitudes recover +8.8–11.6 pp under every attack in both bases), the basis is inert for accuracy (all contrasts ≤1.6 pp), and low-band allocation is only a secondary modulator (≤6.4 pp). For latent-space detectability the roles reverse, the spatial arm is detected decisively (KS D=0.125), while the DCT and random-orthogonal arms are indistinguishable from clean (D≤0.004). Robustness and security can therefore be adjusted independently: amplitude controls accuracy, while the choice of basis controls detectability. The Gaussian Shading statement is corrected accordingly. (Revised in Sec. 5.1; App. I; App. O, Table O-19; App. N.)

2. Stable space and the residual module. We added an equal-budget Random-80% control to confirm that budget reduction alone gives no gain (72.41% vs. 72.40%), so the improvement comes from stability-based selection. We disclosed that the original per-image mask was selected from each image's own clean round trip (shared data); disjoint-calibration controls show the effect survives without it, and a fixed pooled mask is now the deployable result (+1.57 pp over the random control, 10/10 images). Cross-image transfer follows semantic content, and the receiver protocol is specified. (Revised in Table 3 and Sec. 5.1; App. B; App. G.)

3. New operations and the boundary of the residual-risk claim. We applied pixel-scale translations, which destroy all seven channels (by d=6 px); the VAE-grid-aligned shift does not restore recovery; a resynchronizing receiver restores all methods (1024-bit preamble, 6.25% overhead, all within 2.32 pp of storage), so translation disrupts only non-resynchronizing receivers. SDEdit-style regeneration brings six of seven methods to chance while S2IRT survives (≈72%). Active generative purification is a strictly stronger threat class than any passive operation. VAE re-encoding is mild for a matched VAE and hits the backbone-specific LDStega carrier hardest. The residual-risk claim is now bounded: passive processing degrades but does not erase channels; active purification does. (Revised in Sec. 5.2; App. N.)

4. Lifecycle saturation. We added per-step PSNR diagnostics showing that the saturation is not a distortion artifact: the per-step image change stays constant while the per-step accuracy loss collapses (GSD: 4.3 pp after step 1 vs. 0.34 pp per step at depth 17–32). The BSC capacity conversion reproduces the quoted endpoints (≈1.7 and ≈0.8 kbit per image at the two platform blocks; −83%/−92% reductions) and strengthens the defender-side conclusions quantitatively. (Revised in Sec. 5.2, Figs. 5–6; App. J; App. K.)

5. Quality and detectability. We added a quality-matched LPIPS comparison and extended it to all seven methods; the result shows the most destructive transformation per unit quality loss is method-dependent (blur is most destructive for LDStega: 92.8%→80.1% at LPIPS ≈0.141; for MDDM the ranking reverses). Our latent-space steganalysis finds six of seven methods indistinguishable from clean recoveries, with LDStega detected decisively (18% latent-norm drop); per-method image-domain detectors confirm the split (LDStega 85.5–98.8%; GRDH/GSD within the noise floor). The FID shift is reframed as modest and perceptually minor (n=5,000), and ablation-scale quality uses per-image BRISQUE. (Revised in Sec. 5.3; App. L; App. O; Table 7, App. D.)

6. Statistical rigor, method diversity, positioning. Standard deviations now accompany every headline number (all 259 cells of Table 4, mean std 2.43 pp); a 256-prompt run validates the 10-image design externally (mean absolute deviation 0.85 pp over 64 settings); full grid accounting is disclosed (5,903 + 1,848 settings). At ERl=1ER_l=1, PARIS and MDDM saturate to sign coding, while MDDM's sparse regime beats a masked BaseGen control (by 8.2–16.7 pp); Table 4 rows are relabeled (†) as SD-transplanted adaptations. The audited schema is scoped to latent-vector steganography and positioned against prior benchmarks. (Revised in App. F; App. H; Table 4 and Sec. 2.2; App. P.)

We thank all the reviewers and the Area Chair for their careful evaluation, constructive comments, and dedication through the review process.

Best regards,

The Submission 11532 Authors

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