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SPLIT: Training-Free AI-Generated and Partially Edited Video Detection via Spatial Patch-Level Incoherence and Temporal Roughness

Conference: ECCV 2026
Paper: ECCV page
Code: https://github.com/mldljyh/SPLIT
Area: AIGC Detection
Keywords: AI-generated video detection, training-free detection, partial video manipulation, ultra-low false positive rate, frozen feature statistics

TL;DR

SPLIT is a fully training-free detector that computes two statistics over the patch tokens of a frozen vision encoder β€” Two-step Temporal Roughness (TTR, comparing accumulated 1-step and 2-step feature displacements) and Local Spatial Motion Incoherence (LSMI, the spatial gradient of a feature-space motion field) β€” fuses them multiplicatively with gamma correction, and calibrates its threshold on real videos only, reaching the highest Fake Recall at FPR = 0.1% on all three benchmarks (74.45% on FakeParts, far above the best supervised baseline ReStraV at 35.67%).

Background & Motivation

Text-to-video and image-to-video generation have made high-quality synthetic video broadly accessible, and alongside them comes a more insidious class of threat: partial edits β€” localized inpainting and outpainting, temporal interpolation and extrapolation, faceswap, style transfer. For real services this translates into a very concrete deployment constraint. Falsely rejecting authentic user content is extremely costly, so the false positive rate (FPR) on real videos must be pushed to the 0.1% level, and at such extreme operating points aggregate metrics like AUROC simply do not reflect actual behavior: AUROC measures global ranking, whereas the decision is made out in the tail of the distribution. Existing supervised detectors follow three routes β€” spatial artifacts, frequency cues, and spatiotemporal inconsistency β€” mostly built on large pretrained video encoders (DeMamba, AIGVDet, XCLIP, NPR, STIL, FTCN, MINTIME, TALL). They are strong inside their training distribution, but degrade markedly once the generator changes, post-processing is applied, or, above all, the edit is partial and most of the frame remains real. The training-free line (ReStraV's perceptual straightening, D3's clip-level second-order temporal volatility) does improve cross-generator generalization, but both of them pool at the frame or clip level.

The tension lies exactly there: the evidence left by a partial edit is sparse and spatially localized β€” typically only a small region of a frame has been altered β€” while D3 collapses a whole clip into a single scalar and ReStraV collapses a frame into one summary, and that pooling dilutes sparse evidence directly. FakeParts confirms this empirically: many detectors drop by up to 50% on partial edits, precisely because the preserved real context cancels out the criteria of global methods. The other half of the problem is the threshold itself: at deployment time no fake samples from the target domain are available, so the threshold can only be calibrated on real data β€” yet whether a threshold calibrated on one real domain still works on another had barely been quantified before.

This paper's angle is to abandon the "one embedding per frame" compression and instead compute statistics directly on the patch tokens emitted by a frozen encoder, measuring two complementary localized cues separately. Core idea: manipulation leaves two kinds of localized traces in feature space β€” a single patch's feature trajectory stops being smooth (temporal roughness), and neighbouring patches' temporal changes stop being spatially coordinated (inconsistent motion-field gradients) β€” neither of which contains any learnable parameter; fused multiplicatively and sharpened by a gamma exponent to amplify tail differences, they let a real-video-only threshold separate real from fake at FPR = 0.1%.

Method

Overall Architecture

The input is a video clip. SPLIT first extracts per-frame patch tokens with a frozen pretrained vision encoder and stacks them into a \(T\times N\times D\) tensor. On that tensor two purely statistical branches run in parallel β€” TTR walks the temporal axis to check how smooth each patch's feature trajectory is, while LSMI treats the patch-feature difference between adjacent frames as a "motion field" and checks how much it jumps in space. Each branch aggregates into a scalar; the two are multiplied and gamma-corrected into the final score \(s(x)\), which is then thresholded by a \(\tau\) calibrated on real videos only. Nothing in the pipeline is trained: the single constant \(\gamma\) is fixed once on a small held-out validation split (\(\gamma = 8\)) and then held constant across all benchmarks and all FPR targets.

This is a pure feature-statistics method with no network architecture to speak of, so no flowchart is drawn below β€” the measurement formulas of the two cues are the core of the paper.

Key Designs

1. Replacing global embeddings with patch tokens so sparse evidence is not pooled away

Methods such as D3 work at the clip level with second-order differences β€” a frame must first be compressed into one vector, and then the whole clip is pooled, which is where the evidence of a localized edit gets diluted. SPLIT instead lowers the granularity: for transformer encoders (CLIP, XCLIP, DINO, etc.) it takes the final-layer patch tokens and drops the [CLS] token, yielding \(N\) tokens of dimension \(D\) per frame; for CNN encoders (ResNet, VGG, EfficientNet, MobileNet, etc.) it takes the last convolutional feature map and treats each spatial cell as a token, so that \(N=H'W'\) and \(D=C\). Stacking over time gives \(P\in\mathbb{R}^{T\times N\times D}\), and the \(N\) tokens are laid out on a 2D grid of size \(H_p\times W_p\) (the patch grid for ViT-style patchification, the feature-map size for CNNs) to prepare for the spatial neighbourhood operations later. This buys two things. First, the temporal cue is no longer flattened by frame-level pooling: the ablation shows that replacing TTR's [CLS] global embedding with patch tokens lifts Fake Recall from 54.21% to 68.29% at FPR = 0.1% (+14.08 points), the single largest gain in the paper. Second, the patch grid is itself the precondition for the spatial gradients that Design 3 relies on β€” without a grid there is no neighbourhood.

2. Two-step Temporal Roughness (TTR): comparing accumulated 1-step and 2-step displacements

This targets the local flicker, unsynchronized texture refresh, and local temporal misalignment that generation or partial editing tends to leave behind. For each patch \(n\), consecutive-frame feature displacements are accumulated along time to give the accumulated 1-step variation \(L_1(n)\); the accumulated 2-step variation is then computed and normalized so that it is comparable to the 1-step one:

\[\hat L_2(n)=\sum_{t=1}^{T-2}\lVert p_{t+2,n}-p_{t,n}\rVert,\qquad L_2(n)=\Big(\frac{\hat L_2(n)}{2}\Big)\cdot\frac{T-1}{T-2}\]

Dividing by 2 rescales the two-step displacement back to a per-step scale, and multiplying by \((T-1)/(T-2)\) compensates for the two-step sequence having one sample fewer than the one-step sequence; the definition requires \(T\ge 3\). TTR is then a log-ratio:

\[\mathrm{TTR}(n)=\log_2\frac{L_1(n)+\epsilon}{L_2(n)+\epsilon}\]

The geometric intuition is clean: if a patch's features evolve at constant velocity, the chord over two steps equals the path length of those two steps, so after normalization \(L_2\) matches \(L_1\) and TTR β‰ˆ 0; as soon as flicker, texture refresh, or local misalignment appears, successive displacements stop being aligned, the detour-inflated path length \(L_1\) exceeds the chord proxy \(L_2\), and TTR grows. The log-ratio rather than a difference is what divides out absolute motion magnitude β€” fast and slow footage are not distinguished by this quantity, only non-smoothness is amplified, which matters a lot for generalization across content. The clip-level statistic averages in log space, \(\overline{\mathrm{TTR}}=\frac{1}{N}\sum_n \mathrm{TTR}(n)\), which equals the log of the geometric mean of the per-patch roughness ratios: it aggregates multiplicative evidence, stays insensitive to a few extreme outlier patches, and yields a low-variance score β€” and low variance is exactly what lets a threshold be calibrated at ultra-low FPR. The authors are also careful to note that TTR is a statistical cue rather than a necessary property of every fake clip: real videos with hard cuts, shake, or abrupt motion also produce high TTR, and this natural tail is absorbed by calibrating the threshold on real data only.

3. Local Spatial Motion Incoherence (LSMI): the spatial gradient of the motion field

The second cue answers a question TTR cannot: are the temporal changes spatially coordinated? The patch tokens are reshaped back onto the \(H_p\times W_p\times D\) grid, adjacent frames are subtracted to give a per-step motion field \(M_t=P_{t+1}-P_t\), and forward differences are taken to obtain its spatial gradients:

\[\nabla_x M_t(i,j)=M_t(i,j)-M_t(i,j+1),\qquad \nabla_y M_t(i,j)=M_t(i,j)-M_t(i+1,j)\]

LSMI is the mean magnitude of these gradients over time and space:

\[\mathrm{LSMI}=\frac{1}{2}\Big(\mathbb{E}_{t,i,j}\big[\lVert\nabla_x M_t(i,j)\rVert_2\big]+\mathbb{E}_{t,i,j}\big[\lVert\nabla_y M_t(i,j)\rVert_2\big]\Big)\]

The intuition: in real video neighbouring patches usually move together β€” one object or one camera motion covers a whole region β€” so the motion field is spatially smooth and its gradient is small. Local generation or editing, by contrast, induces temporal change inside a region that differs from its surroundings, so adjacent patches jump relative to each other and the gradient grows. Importantly this "motion" lives entirely in feature space: no RAFT-style optical-flow network is needed, hence no extra forward pass. The ablation shows LSMI is very weak on its own (8.04% at FPR = 0.1%), but it carries spatial-coordination evidence that TTR completely lacks: the fusion is best at every operating point, and at the strictest threshold it adds another 6.16 points over patch-level TTR alone. That is why both cues are kept β€” they are not substitutes but cover two different dimensions.

4. Gamma-corrected multiplicative fusion with real-data-only threshold calibration

The two cues combine multiplicatively into a score, \(s(x)=\mathrm{TTR}^{\gamma}\cdot\mathrm{LSMI}\), where \(\gamma\) is a fixed, non-learned sharpening constant. Multiplication rather than averaging is chosen because if either cue fails the score should be pushed down β€” LSMI is weak alone and TTR is also inflated by shake in real videos β€” so the product means "fake only if both are high". The gamma exponent then raises TTR to a high power, amplifying its relative differences in the score. This is not a cosmetic addition: the decision happens at FPR = 0.1% in the extreme tail, where what matters is not global ranking ability but separation at the two ends of the tail. The authors selected \(\gamma\) on a small held-out split: from 1 to 8 every operating point improves consistently, beyond 8 it saturates and can even regress marginally at some FPR levels, so \(\gamma = 8\) is fixed throughout.

The decision threshold uses no fixed constant at all; it is solved for in a "service-aligned" way. Given a target false positive rate \(\alpha\in\{0.1\%,1\%,5\%\}\), the smallest threshold satisfying the false-positive constraint on a calibration set \(\mathcal{R}\) of real videos only is taken:

\[\tau_\alpha\triangleq\inf\{\tau:\ \Pr_{x\sim\mathcal R}[s(x)\ge\tau]\le\alpha\}\]

At test time \(s(x)\ge\tau_\alpha\) predicts manipulated, otherwise real. So that methods which happen to be well calibrated on only one real domain are not over-credited, the authors further propose cross-real threshold transfer: two separate thresholds are calibrated on two disjoint real sets β€” ROVI (the real subset of FakeParts) and MSR-VTT (the real subset of GenVideo) β€” both are applied to the test benchmarks, and the harmonic mean of the two resulting Fake Recall values is reported. The main tables use this harmonic mean.

A Worked Example

Take a 2-second, 8 fps clip (the patch count below is illustrative only): 16 frames encoded by XCLIP-B/16 at 224Γ—224 give 14Γ—14 = 196 patches, so \(P\in\mathbb{R}^{16\times196\times D}\). For patch \(n\), \(L_1\) sums 15 adjacent-frame displacements while \(L_2\) sums 14 two-step displacements, divided by 2 and multiplied by 15/14. Suppose a small region in the lower-right corner was inpainted: its patches' features jump once around the edited frames, and the amount by which \(L_1\) exceeds \(L_2\) is that region's TTR. Averaging the 196 per-patch TTRs in log space gives the clip-level TTR. On the LSMI side the 196 tokens are laid out as a 14Γ—14 grid, 15 motion fields are computed, each is differenced in x and y, and the mean gradient magnitude is taken over the valid positions (dropping the last row and column). The two branches are multiplied and raised to the 8th power, yielding one scalar. Finally the 0.1% quantile of the calibration set is used as \(\tau\): above it, the clip is judged manipulated. End-to-end latency on 1,000 FakeParts T2V samples matches D3 with the same backbone β€” essentially all of the cost is the frozen encoder's forward pass.

Loss & Training

SPLIT has no training stage and no loss function, requires no training data, and therefore has no optimization strategy or learning-rate hyper-parameters β€” the only hand-picked constant in the whole method is \(\gamma = 8\). For comparison, the ten supervised baselines are all trained on GenVideo-100K as the sole training set: NPR, STIL, FTCN, MINTIME, TALL, XCLIP, and DeMamba are reproduced with the official DeMamba repository, while FID, AIGVDet, and ReStraV are trained and evaluated with their respective official implementations, and D3 is evaluated with its official repository. Implementation-wise the default encoder is XCLIP-B/16; segments of up to 2 seconds are extracted, frames are sampled at 8 fps at uniform intervals, 10% is cropped from the longer side, and all frames are resized to 224Γ—224. All experiments run on an AMD EPYC 9554 64-core CPU with a single NVIDIA RTX A6000.

Key Experimental Results

Main Results

Overall Fake Recall (%) on the three benchmarks (cross-real threshold transfer, i.e. harmonic mean over the two real-domain thresholds):

Benchmark FPR SPLIT (training-free) Best supervised D3 (training-free)
FakeParts 0.1% 74.45 35.67 (ReStraV) 2.28
FakeParts 1% 83.58 61.89 (ReStraV) 37.42
FakeParts 5% 89.70 77.75 (ReStraV) 70.59
GenVideo 0.1% 85.16 45.52 (ReStraV) 5.47
GenVideo 1% 93.09 81.89 (ReStraV) 66.50
GenVideo 5% 97.35 92.32 (ReStraV) 90.52
ViF-Bench 0.1% 84.52 33.93 (ReStraV) 0.97

The breakdown of FakeParts into its eight manipulation categories at FPR = 0.1% (%) β€” the table that best exposes the difference between partial edits and full generation:

Manipulation type SPLIT ReStraV D3 Note
Style Change 98.80 18.60 0.34 Whole-clip style rewrite, densest cue
Extrapolation 97.86 23.27 0.00 Temporal extension, trajectory clearly unsmooth
Outpainting 96.52 91.45 2.72 Frame expansion, ReStraV is also strong here
TI2V 95.27 73.13 0.66 Image-to-video, the whole clip is generated
T2V 76.74 46.65 14.46 Fully generated clip
Interpolation 67.81 0.18 0.00 Frame interpolation, localized temporal rewrite
Faceswap 60.09 12.98 0.04 Face swap, unrelated to face-specific detectors
Inpainting 2.48 19.09 0.00 The only failing category, smallest edit region

Ablation Study

Component ablation (FakeParts Overall, Fake Recall %, cross-real threshold transfer):

Config 0.1% 1% 5% Note
CLS global-embedding TTR 54.21 76.72 88.77 patch tokens not used
Patch-level TTR 68.29 82.09 89.37 swapped to patch tokens, +14.08
LSMI only 8.04 14.63 25.07 weak standalone
Patch-level TTR + LSMI 74.45 83.58 89.70 full model, another +6.16

Encoder ablation and post-processing robustness (both on FakeParts Overall):

Config 0.1% 1% 5% Note
SPLIT + XCLIP-B/16 (default) 74.45 83.58 89.70 best combination
SPLIT + CLIP-B/16 71.47 81.56 89.39 transformer, same granularity
SPLIT + ResNet18 61.23 77.87 88.01 lightweight CNN still far above D3
D3 + XCLIP-B/16 2.28 37.42 70.59 training-free baseline, same backbone
Gaussian Blur Οƒ = 1 62.54 77.49 88.71 post-processing: mild blur
Gaussian Blur Οƒ = 2 55.42 73.50 88.47 post-processing: strongest disruption
JPEG q = 90 70.45 80.89 88.83 post-processing: small effect
JPEG q = 80 64.40 77.11 87.12 post-processing: still limited
Flip (x-axis) 75.73 82.79 88.84 horizontal flip essentially lossless
Flip (y-axis) 66.92 80.42 88.52 vertical flip, modest drop

Cross-real threshold transfer stability (calibration domain β†’ test domain; entries are the actual FPR %, against targets of 0.1 / 1 / 5):

Method MSR-VTT→ROVI @0.1 @1 @5 ROVI→MSR-VTT @0.1 @1 @5
SPLIT 0.03 0.29 4.22 0.56 2.18 5.49
D3 0.00 0.07 1.52 1.18 4.06 9.04
ReStraV 0.00 0.00 0.00 15.30 39.86 66.10
AIGVDet 13.22 25.12 31.69 0.00 0.00 0.02
FID 0.62 8.25 38.64 0.01 0.16 0.67
FTCN 0.48 2.28 7.40 0.01 0.28 2.68

Key Findings

  • Patch granularity is the biggest contributor; LSMI is the complement. Replacing TTR's [CLS] global embedding with patch tokens yields +14.08 (54.21 β†’ 68.29), the single largest gain; LSMI alone sits at 8.04, but the fusion adds another +6.16 at the strictest threshold. The authors read this as patch-level temporal roughness being the primary discriminative cue, with LSMI supplying the spatial-coherence evidence that further separates real from fake in the strict, real-calibrated tail.
  • The gap only shows up at ultra-low FPR. On all three benchmarks SPLIT's advantage is largest at FPR = 0.1% and shrinks as the operating point relaxes (on FakeParts from +38.78 points down to +11.95). This is exactly the paper's central claim: aggregate metrics such as AUROC cannot see this regime, and service-aligned operating points are what actually separate methods.
  • Inpainting is the only failing category. At 0.1% SPLIT reaches just 2.48% and actually loses to ReStraV's 19.09%. The authors attribute this to the edit region per frame being too small; SPLIT ranks second within this category, but the case shows patch-level statistics can be swamped by the natural tail of real videos when the edit is minute and neighbourhood smoothing applies.
  • The method is encoder-agnostic, but finer spatial granularity helps. Across seven backbones (CLIP, XCLIP, DINOv2, ResNet18, VGG16, EfficientNet-b4, MobileNet-v3) SPLIT beats D3 by a wide margin on the same backbone, and B/16 variants consistently outperform B/32 β€” consistent with the hypothesis that localized artifacts need higher patch resolution. The gains therefore come from patch-level scoring rather than from any particular pretrained representation.
  • Robust to post-processing and not dependent on high-frequency pixel artifacts. Blur hurts most (74.45 β†’ 55.42 under Οƒ = 2, still marginally above the strongest supervised baseline ReStraV at 54.73), JPEG compression is clearly milder (64.40 retained at q = 80), and geometric flips are nearly lossless (75.73 horizontal, 66.92 vertical), showing the score aggregates patch-level spatiotemporal evidence without relying on absolute spatial orientation. By contrast, the frequency-domain method NPR reaches only 0.12% on FakeParts Overall at 0.1%, confirming that high-frequency artifacts have no discriminative power in the tail.
  • Thresholds transfer across real domains. SPLIT keeps the transferred actual FPR close to target in both directions (0.03 / 0.56 against a target of 0.1), whereas ReStraV drifts to 15.30% in one direction and AIGVDet to 13.22% in the other β€” for those methods a threshold calibrated for ultra-low FPR on one real domain simply stops working on another, which would break in real deployment.
  • Training-free without losing throughput. With the same backbone, SPLIT's end-to-end inference time matches D3's; the lightweight TTR / LSMI computation is negligible next to the frozen encoder's forward pass, yet it lifts FakeParts Overall @0.1% from 2.28 to 74.45.

Highlights & Insights

  • A geometric path-length vs chord-length intuition that needs no training. Under constant-velocity evolution the two-step chord equals the two-step path length, and only a detour separates them. The clever part is that this construction turns "non-smoothness" into a log-ratio insensitive to absolute motion magnitude β€” no training, no optical-flow network, no annotation β€” while aiming directly at flicker and local temporal misalignment, the artifacts generation actually leaves. It is the most reusable idea in the paper.
  • The multiplicative fusion with a gamma exponent is a direct reply to "the decision lives in the extreme tail." Averaging optimizes global ranking, whereas power sharpening amplifies relative differences in the tail. Deriving the fusion function from the deployment constraint (FPR ≀ 0.1%) rather than reporting AUROC after designing the fusion is the transferable mindset, more so than the formula itself.
  • Cross-real threshold transfer may be the most transferable contribution. Any detector that calibrates its threshold on real data only can use this protocol to measure calibration stability, not just this one. It turns a routinely ignored engineering question β€” can a threshold move domains? β€” into a quantifiable metric, and the experiments genuinely expose ReStraV and AIGVDet as non-portable at ultra-low FPR.
  • Transfer directions. TTR and LSMI need only "a per-frame token sequence plus a spatial grid", so they move to other modalities directly: audio AIGC detection can compute temporal roughness over spectrogram token sequences; image AIGC detection can generalize LSMI to a single image by replacing the temporal motion field with adjacent-patch differences; and the forward difference over the patch grid can be swapped for any spatial operator (Laplacian, neighbourhood variance) to build new spatial-incoherence measures.

Limitations & Future Work

  • The authors concede TTR is only a statistical cue. Real videos with hard cuts, shake, or abrupt motion also produce high TTR; this is absorbed by the tail of the real-data calibration, which means the method is more vulnerable in domains where real videos are themselves rough.
  • The authors concede a marked degradation under blur. From 74.45 down to 55.42 under Οƒ = 2, roughly 19 points, indicating part of the signal still depends on relatively fine spatial structure rather than purely high-level semantics.
  • The missing localization ability is the clearest weakness. The paper's whole motivation is patch-level evidence, and TTR(n) and LSMI are per-patch quantities by construction, yet the pipeline only averages them into one clip-level scalar β€” there is no spatial heatmap and no manipulation-region localization experiment at all. FakeParts provides pixel-level and frame-level annotations, so omitting localization discards what may be the method's biggest latent advantage; upsampling per-patch TTR back to the original resolution as a heatmap is the most natural next step.
  • The gamma selection procedure is under-specified. The method is training-free and needs no training set, yet \(\gamma = 8\) was chosen on a held-out validation split; the paper does not say whether that split overlaps the test generators, nor whether \(\gamma\) remains optimal for other backbones (only the same trend on GenVideo / ViF-Bench is reported, in the supplementary material).
  • The Inpainting failure needs a finer explanation. The 2.48% vs ReStraV's 19.09% gap is large. The authors attribute it to the tiny edit region, but it could equally be patch-level statistics being smoothed away by the neighbourhood, or the natural tail of real videos drowning the signal. Finer patch granularity (B/32 β†’ B/16 is already shown to help) and local normalization or saliency weighting are two paths worth trying.
  • The experimental setup is narrow. Only 2-second, 8 fps, 224Γ—224 clips are tested; the variance of TTR and the portability of the threshold on longer videos, at higher resolution, and across resolutions remain unverified.
  • vs D3: D3 is also training-free, but measures second-order temporal volatility at the clip level with central differences, and must first compress a frame into one global embedding. SPLIT keeps patch tokens and splits "temporally unsmooth" from "spatially uncoordinated" into two cues that are then multiplied. With the same backbone (XCLIP-B/16), FakeParts Overall @0.1% rises from 2.28% to 74.45%, showing the gain comes mainly from lowering the aggregation granularity rather than from a stronger feature extractor.
  • vs ReStraV: ReStraV is also built on frozen feature dynamics (the perceptual-straightening observation that natural videos trace straighter trajectories in DINOv2 feature space), but it must train a lightweight classifier on frame-level statistics (step distances, curvature) and its statistics are frame-level or globally abstract. SPLIT has no learnable parameters, needs no training set, and pushes the granularity down to patches. ReStraV is the strongest supervised baseline on all three benchmarks (FakeParts 35.67%, GenVideo 45.52%, ViF-Bench 33.93%) yet is far surpassed by SPLIT; it also drifts severely under cross-real threshold transfer (15.30% in one direction), indicating its score distribution is more sensitive to the real domain.
  • vs supervised video detectors such as DeMamba / AIGVDet: These are strong on near-domain benchmarks (GenVideo Overall @0.1%: DeMamba 10.00%, AIGVDet 45.38%) but degrade clearly on new generators or partial edits β€” at the same FPR their ViF-Bench Overall drops to 3.30% and 25.69% respectively. SPLIT, with no training at all, ranks first on every individual generator in ViF-Bench.
  • vs the frequency-domain method NPR: NPR relies on upsampling artifacts left by generators and is nominally cross-generator, yet at ultra-low FPR it is almost always zero (FakeParts Overall @0.1% is just 0.12%). This corroborates SPLIT's relative insensitivity to JPEG compression: high-frequency pixel-level artifacts have no discriminative power in the distribution tail, whereas patch-level spatiotemporal statistics do.

Rating

  • Novelty: ⭐⭐⭐⭐ [Both cues are classic statistical intuitions (path vs chord length, motion-field spatial gradient), but their combination, the gamma-sharpened fusion, and the cross-real evaluation protocol are new; training-free plus patch-level granularity genuinely opens new ground for partial-edit detection]
  • Experimental Thoroughness: ⭐⭐⭐⭐⭐ [Three benchmarks, eight manipulation categories, 10+ generators, eleven baselines, an encoder ablation over seven backbones, robustness to four post-processing families, and cross-real calibration stability β€” very broad coverage]
  • Writing Quality: ⭐⭐⭐⭐ [Method and motivation are clearly explained with restrained formulas, but the layout of Table 6 and the overlaid annotations of Figure 3 are hard to read, and key settings such as the gamma selection split are pushed to the supplementary material]
  • Value: ⭐⭐⭐⭐ [Training-free, plus ultra-low-FPR deployment constraints, plus cross-real threshold calibration, aims straight at real service scenarios; the Inpainting failure and the entirely absent localization ability limit near-term adoption]