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Under review as a conference paper at ICLR 2027

Per-Sample or Not: A Granularity Criterion for Test-Time Correction in AI-Generated Image Detection

Abstract

A linear head on a frozen visual foundation model provides strong AI-generated image (AIGI) detection, but its performance degrades under unseen generators, content domains, and dissemination shifts. We first establish a rank-invariance criterion showing that test-time corrections that only adjust thresholds or apply sample-shared feature translations cannot improve AUROC because they preserve the relative score ordering of real and generated samples. Motivated by the channel-wise non-uniformity and target specificity of forensic feature shifts, we propose Forensic-Shift Conditional Test-Time Affine Adaptation (FS-CTAA). Trained solely on source data with simulated forensic shifts, FS-CTAA predicts sample-specific channel-wise affine parameters from each test feature, the source training-set feature mean, and the current test-subset feature mean, requiring neither target labels nor gradient updates. Across four heterogeneous frozen backbones, FS-CTAA improves macro-average AUROC by – percentage points and, averaged over three training seeds, outperforms a sample-shared modulator trained under the same protocol by – percentage points, showing an additional ranking benefit from sample-specific rather than merely target-conditioned adaptation. Gains concentrate on challenging shifts where the frozen probe leaves substantial ranking errors, while performance remains stable on already near-saturated cases. FS-CTAA further improves balanced accuracy by – percentage points over the frozen probe and exceeds the threshold-only target-label oracle on three backbones. These results establish sample-conditioned feature adaptation as an effective approach to robust AIGI detection under distribution shifts.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
AI-generated image detection, test-time adaptation, distribution shift, image forensics, frozen foundation models

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

This paper proposes FS-CTAA, a per-sample conditional affine adaptation method for improving AI-generated image detection under distribution shifts. The authors introduce a correction granularity framework and apply sample-specific channel-wise scaling and bias to frozen visual features without test-time gradient updates. Experiments across four backbones and 16 target subsets demonstrate AUROC improvements of 1.67–3.49 percentage points, with per-sample correction outperforming shared affine adaptation.

Critical strengths

S1. Carefully designed controls. The comparison between shared and sample-conditioned correction is supported by parameter matching in both directions, a post-hoc shared variant with identical weights, three training seeds, and an inference-only substitution of the source mean for the target mean. Reporting AUROC alongside balanced accuracy throughout most tables also separates ranking gains from operating-point effects, which is good evaluation practice for this problem.

S2. A lightweight, practical plug-in. FS-CTAA requires no target labels and no test-time gradients, and it adds roughly 0.04 ms per sample. It improves collection-averaged AUROC on all four backbones and all three seeds, which makes it easy to attach to existing frozen detectors.

Critical weaknesses

W1. The ranking gain is largely attributable to a source-trained nonlinear re-scorer rather than to target-conditioned adaptation. With a frozen linear head, the corrected score equals the original score plus a learned nonlinear function of the feature and the two means. Comparing the shared and per-sample levels is therefore largely a comparison between a target-specific linear head and a nonlinear classifier. The paper’s own ablation makes this concrete. In the “w/o target-mean input” variant, the target enters only through the rank-invariant anchor, so by Proposition 1 its ranking is independent of the target. Yet it retains +0.0192 and +0.0168 AUROC on PE-CLIP and SigLIP2, which is 55–58% of the full gain. The source-mean substitution in Table 28 shows that the trained model relies on µ_t, not that target information is required to obtain the gain. The anchor term also cancels both in AUROC and under the mean-score threshold, so it has no direct effect at inference. The architecture closely resembles context-conditioned approaches such as ARM-CML (Zhang et al., 2021), which is not cited, and the rank-invariance criterion is a standard property of rank statistics.

W2. Augmentation and capacity are confounded with adaptation. The modulator is trained with compression, resizing, spectral, and noise episodes and a classification loss, whereas the reference probe is trained for two epochs without augmentation. The post-processing evaluation in Fig. 4 therefore tests transformations covered by the training episodes against an unaugmented baseline. The source-side controls in Table 29 report only balanced accuracy at an unstated threshold and omit AUROC, contrary to the paper’s own argument that accuracy conflates ranking with the operating point. The most direct control, an augmented MLP head of matched capacity without target context, is missing. The adapted baselines are also weakened forms; TENT, for example, is reduced to a scalar logit offset that performs below the probe. A frozen-model, gradient-free output correction such as LAME (Boudiaf et al., 2022) is not compared.

W3. The gains are concentrated, and the transductive evaluation is favorable. On PE-CLIP, the overall gain of +0.0349 comes almost entirely from Mirage (+0.1068), while GenImage and ITW change by −0.0016 and −0.0004. Weighting all 16 subsets equally reduces the gains to 1.2–2.6 points. The main protocol relies on benchmark-defined, class-balanced subsets that each contain a single generator. The boundary-free stream is evaluated on only two backbones, and the label-free threshold offers no control over the false-positive rate, which matters for forensic use. The bootstrap intervals reflect only test-sample variation at one seed, whereas the seed-to-seed standard deviations are larger than their half-widths.

Questions for authors

Q1. Could the authors compare FS-CTAA against a parameter-matched classifier that takes the concatenation of the sample feature and the target mean as input, in the spirit of ARM-CML, trained with the same episodes and objective? It would also help to include an augmented MLP head of matched capacity that receives no target context. Reporting AUROC for both would show whether the feature-wise affine form and the target context contribute beyond nonlinear rescoring with augmentation. This is the question most likely to change my assessment.

Q2. In the “w/o target-mean input” variant, the target enters only through the anchor, so its ranking is independent of the target. How do the authors reconcile its +0.0192 AUROC gain with the claim that the ranking improvement stems from target-conditioned adaptation? Relatedly, why does the unconditional adapter, which also lacks target-dependent information, reach only +0.0039, and were the two variants tuned with the same effort?

Q3. Could the authors report AUROC for the augmented linear head and the matched MLP in Table 29, state the threshold used for their balanced accuracy, and add the augmented probe to the post-processing evaluation in Fig. 4? This would show how much of the robustness gain survives once the baseline receives the same augmentations.

Q4. In the composition audit, the mean-score threshold at π = 0.8 should move by about 30% of the class-mean score gap relative to the balanced case, yet balanced accuracy changes by only 0.28 points. Could the authors report the threshold values and class-wise true-positive and true-negative rates at each ratio? In the mixed-stream experiment, a fully shuffled stream carries no subset information, so it is unclear why the EMA context outperforms the globally pooled context. Does the EMA include the current image, and how is the stream ordered?

Q5. Could the authors extend the unknown-boundary stream evaluation to all four backbones and report true-positive rates at fixed low false-positive rates? Since the label-free threshold provides no control over the false-positive rate, such operating points would better reflect forensic deployment.

5 comments

We thank the reviewer for the detailed and constructive review. Our reply has four parts. Part 1 answers Q1, Part 2 answers Q2, Part 3 answers Q3 and W2, and Part 4 answers Q4, Q5 and W3. Points of W1 are addressed in Parts 1 and 2. Rebuttal tables are labeled R3-x, and values are AUROC in percent unless stated otherwise. Tables R3-1, R3-2, R3-5, R3-6 and R3-12 average three training seeds, and the other tables use the main checkpoint.

Part 1. Q1 and W1. Context-conditioned and augmented nonlinear heads

We ran the requested controls over three training seeds. Parameter matching applies to the nonlinear Matched MLP, Aug. MLP and Context MLP, against the corresponding FS-CTAA modulator; the linear heads are reference baselines. Matched MLP uses clean source features. Aug. linear, Aug. MLP and Context MLP use the four forensic-shift families, as does FS-CTAA. The parameter budget, forensic-shift augmentation families, and classification supervision are matched, with residual penalties defined in their respective output spaces. Context MLP is an ARM-CML style classifier: it maps [z, μt] through one hidden layer to two logits, with a score residual relative to the anchor-corrected frozen-head score.

Table R3-1. AUROC of source-head controls and FS-CTAA, with mean gain over the probe.

MethodSigLIP2PE-CLIPMetaCLIPDINOv2Mean gain
Frozen probe91.4989.0079.6870.02
Matched MLP91.5389.0379.7469.99+0.03
Aug. linear90.9591.3478.4570.57+0.28
Aug. MLP90.8290.7879.6871.68+0.69
Context MLP92.3990.7280.0671.63+1.15
FS-CTAA94.4492.5381.8372.22+2.71

Table R3-2. Pairwise AUROC differences between separately trained models in Table R3-1.

ComparisonSigLIP2PE-CLIPMetaCLIPDINOv2Mean
Matched MLP minus probe+0.04+0.03+0.06−0.03+0.03
Aug. MLP minus Matched MLP−0.71+1.75−0.06+1.69+0.67
Context MLP minus Aug. MLP+1.57−0.06+0.38−0.05+0.46
FS-CTAA minus Context MLP+2.05+1.81+1.77+0.59+1.56

Augmented nonlinear rescoring explains part of the gain, but three observations show that it is insufficient to explain the full result. First, Matched MLP stays within 0.06 points of the probe on every backbone, so additional nonlinear capacity alone does not reproduce the improvement. Second, Aug. MLP helps on PE-CLIP and DINOv2 but not consistently across backbones; its mean gain is 0.69 points versus 2.71 for FS-CTAA. Third, Context MLP already combines nonlinear scoring, forensic-shift training and target-mean input, yet FS-CTAA exceeds it on every backbone by 0.59 to 2.05 points, averaging 1.56. Thus, access to the target mean through a generic classifier does not reproduce the benefit of using it with the sample feature to predict a feature-wise correction before the frozen head. These controls support the additional value of the FS-CTAA parameterization over the tested alternatives. The differences compare separately trained models, not additive contributions of individual ingredients. Part 2 further distinguishes dependence on target context from the gain obtainable after retraining without it.

Table R3-3 adds a control that keeps every trained weight of FS-CTAA. Shared FS-CTAA averages the predicted scale and offset within each subset, so only the per-sample variation is removed.

Table R3-3. Same trained weights at the main checkpoint, per-sample versus subset-averaged correction, gain over the probe.

CorrectionSigLIP2PE-CLIPMetaCLIPDINOv2
Per-sample, FS-CTAA+2.88+3.49+1.72+1.67
Subset-averaged, same weights+0.63+0.42−3.88+0.53

Most of the gain disappears with identical weights, so the gain is not a matter of parameter count and requires the per-sample variation of the correction. Because averaging also makes the score a shared affine function of z again, this control alone does not separate per-sample correction from nonlinear scoring, which is the role of Tables R3-1 and R3-2. The revised PDF reports Table R3-1 as Table S1 in Section 4.4 and Table R3-2 as Table S4 in Appendix A.20, and cites ARM-CML. Rank invariance is classical for scores, and we use its extension to feature-level corrections to separate operating-point effects from ranking changes.

Part 2. Q2 and W1. The "w/o target-mean input" variant, the anchor and the unconditional adapter

At inference this variant ranks images independently of the target, and its gain shows that a source-trained per-sample mapping repairs part of the ordering. In the tested variants, recovering the full gain also requires target input.

Table R3-4. Gain over the probe on SigLIP2 / PE-CLIP for each variant.

VariantTarget-dependent ranking at inferenceGain
Unconditional adapterNo+0.34 / +0.39
w/o target contextNo+0.51 / +0.68
w/o target-mean inputNo+1.68 / +1.92
w/o mean anchorYes+2.02 / +2.30
FS-CTAAYes+2.88 / +3.49

Feeding μt adds a further 1.20 / 1.57 points with the anchor and 1.51 / 1.62 without it, showing a consistent benefit across anchor choices. These compare separately retrained models, not an additive decomposition. The w/o target-mean input variant retains the source reference and anchor; the unconditional adapter removes both means and the anchor. The two anchor-free variants without target input retain less than one fifth of the full gain. This supports a training role for the anchor, which aligns each shifted episode's batch mean to its clean source mean. At inference with a fixed context, the shared anchor translation cancels between score and threshold under Eq. 8, as the reviewer notes; its direct operating-point effect applies to a source-fixed threshold.

Table R3-5 summarizes the inference-time swap to all four backbones.

Table R3-5. Gain over the probe over three training seeds, with μt or μs at inference.

Context at inferenceSigLIP2PE-CLIPMetaCLIPDINOv2
Target mean μt+3.0+3.5+2.2+2.2
Source mean μs+0.4+0.6+0.3+0.2

The two tests answer complementary questions. Inference-only substitution tests what the trained model relies on; retraining without target input tests how much gain can be obtained without it. Retraining recovers part of the gain, but target input adds 1.2 to 1.6 points with or without the anchor. Together, these results support contributions from both the source-trained per-sample mapping and target conditioning in the tested variants. All variants share one 12-candidate search budget and, within each backbone and seed, the same episodes, source split, training steps and sample counts.

Part 3. Q3 and W2. Augmentation, capacity and adaptation baselines

Thresholds and AUROC of the augmentation and capacity control. The probe, Aug. linear and Matched MLP use a threshold selected on source validation and then fixed, the same rule as the probe in our main results. MLP + FS-CTAA places a separately trained FS-CTAA modulator on the frozen Matched MLP and uses the label-free rule of Eq. 8. Table R3-6 adds the threshold-free AUROC that the reviewer requested.

Table R3-6. AUROC in percent over three training seeds. The frozen probe is common to all seeds.

HeadSigLIP2PE-CLIPMetaCLIPDINOv2Mean gain
Frozen probe91.4989.0079.6870.02
Aug. linear90.9591.3478.4570.57+0.28
Matched MLP91.5389.0379.7469.99+0.03
MLP + FS-CTAA94.0992.0281.2771.29+2.12

Neither source-side change helps consistently. Augmentation moves AUROC of the linear head in both directions, from +2.34 on PE-CLIP to −1.23 on MetaCLIP, and added capacity leaves it within 0.06. Placed on the same Matched MLP, FS-CTAA raises AUROC on every backbone by 1.3 to 3.0 points, so its benefit persists after source-head capacity is increased.

Augmented baselines under the Figure 4 conditions. We evaluate the augmented heads and Context MLP on the same images and 17 conditions at source-fixed operating points. Table S5 of the revised PDF reports their mean balanced accuracy.

Table R3-7. Mean balanced accuracy over the 17 post-processing conditions of Figure 4 on PE-CLIP.

ManifestAug. linearAug. MLPContext MLPFS-CTAA
GenImage81.6583.4389.7792.18
Chameleon74.9390.7874.2892.34

With the same augmentation families and source-fixed operating points, FS-CTAA remains best on both manifests and is the only method strong on both, since Aug. MLP falls behind on GenImage and Context MLP on Chameleon. The robustness of FS-CTAA is therefore not a by-product of training on the evaluated transformations.

Adaptation baselines. Our diagnostic suite already contains TENT with the LayerNorm affine parameters updated by gradient. We add two further baselines. TENT-LN restores the source weights and resets the optimizer at the start of every subset and evaluation order, and takes one entropy-minimization step per batch of 128 images. LAME uses the official optimization code with a two-class probability interface and online batches of 128.

Table R3-8. Adaptation baselines on PE-CLIP at the main checkpoint.

MethodTest-time gradientsAUROC
Frozen probeNo89.00
TENT, LayerNorm affineYes88.16
TENT-LN, reset per subset and orderYes68.14
LAMENo52.11
FS-CTAANo92.49

TENT with LayerNorm updates stays below the probe on all four backbones, by 0.48 to 1.27 points. Despite the resets, TENT-LN collapses within subsets. On all four Mirage subsets and all five orders, the last tenth of batches predicts a single class, with mean predictive entropy below 7e-6 nats. This is consistent with the collapse risk of online entropy minimization discussed by Niu et al. 2023, so we keep the stronger TENT row as the main reference. LAME yields saturated probabilities with many tied scores. FS-CTAA needs no target-time optimization. Table 6 reports 0.0408 ms per image for the PE-CLIP correction module, excluding the encoder and context estimation. The revised PDF reports these tables in the appendix and cites LAME.

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Paper summary

This paper studies test-time correction for AI-generated image detection and proposes a rank-invariance criterion to analyze when per-sample correction can improve detection performance. The authors introduce FS-CTAA, a lightweight method that uses simulated forensic shifts to learn sample-conditioned feature corrections. Experiments across multiple vision backbones and datasets show improvements in AUROC over frozen detectors, although the method’s reliance on target-set statistics may limit its effectiveness in real-world deployment.

Critical strengths
  1. Under the stated fixed-context setting, the rank-invariance criterion explains why monotone recalibration and shared feature translation cannot improve AUROC, separating threshold effects from ranking changes.

  2. Experiments cover four heterogeneous frozen backbones across three collections, with matched controls, ablations, post-processing tests, confidence intervals, and multiple seeds. All four backbones show positive collection-level macro-average AUROC gains over frozen probes.

Critical weaknesses
  1. The main evaluation uses benchmark-defined target subsets to estimate target statistics. Although Appendix A.17 examines finite-sample, streaming, EMA, and unknown-boundary settings, robustness to arbitrary and continuously changing mixtures remains insufficiently established.
  2. The threshold is set to the mean corrected score (Eq. 8). Appendix A.12 examines class proportions from π = 0.20 to 0.80, but performance when one class is extremely rare or absent remains unclear.
  3. Despite extensive controls and ablations, the distinct contributions of the rank-invariance criterion, sample-conditioned architecture, and forensic-shift training could be articulated more explicitly relative to existing conditional modulation and statistics-based adaptation methods.
Questions for authors
  1. How sensitive is FS-CTAA to target subsets that mix images from different generators, semantic domains, and post-processing pipelines? Although the paper evaluates several distribution shifts, it remains unclear whether the reported gains hold for target distributions that do not align with the benchmark-defined subsets used in the main evaluation.
  2. How reliable is the mean-score threshold when the target subset contains only real images, only generated images, or a highly imbalanced mixture? While the appendix studies varying class proportions, the failure modes under extreme imbalance or the absence of one class remain unclear. Can the authors characterize the conditions under which this thresholding rule becomes unreliable?
  3. The main evaluation estimates target statistics from benchmark-defined target subsets. Although the appendix investigates finite-sample and streaming settings, it would be helpful to quantify how performance depends on the number and representativeness of available target samples, particularly under continuously changing distributions. Could the authors also clarify how unreliable target statistics could be detected or mitigated in practice?
  4. To what extent do the evaluated benchmarks and simulated forensic shifts capture distribution changes encountered in real-world image dissemination? Additional evaluation on generators or dissemination conditions not covered by the current benchmarks would help establish the generalizability of FS-CTAA beyond the evaluated settings.
3 comments

We thank the reviewer for the constructive questions. Part 1 answers Q1 to Q3, and Part 2 answers Q4 and W3. Tables are labeled R2-x, and values are AUROC in percent unless stated otherwise. FS-CTAA keeps the encoder and head frozen at inference. The offline target audits use disjoint context and query images; streaming contexts use past images. TENT's LayerNorm updates are identified separately.

W1 and Q1. Targets that mix generators, semantic domains and pipelines

On PE-CLIP we build targets that mix sources along each axis, and a joint axis that mixes generators and processing pipelines together. Each of five samplings uses 2,000 unlabeled context images and 2,000 balanced query images.

Table R2-1. Mixed targets.

MixtureGeneratorsSemantic domainsPost-processingGenerators and pipelines
Probe98.8367.8280.7088.16
FS-CTAA99.1378.6381.0990.05

FS-CTAA improves every mixture, and the gain is largest where the probe is weakest, reaching 10.81 points when semantic domains are mixed. The target mean only has to describe the shift that a batch shares, so it stays informative when a target combines several sources rather than a single benchmark subset.

W2 and Q2. Extreme imbalance and single-class targets

We evaluate ADM, Chameleon, Mirage-Human and SocialRF over five samplings of 256 context and 256 query images. Every method thresholds at its own unlabeled query mean by Eq. 8, and a nominal 1 percent means 3 of 256 generated queries.

Table R2-2. AUROC / BA, probe → FS-CTAA.

Backbone1% generated99% generated
SigLIP291.55 / 72.39 → 92.09 / 75.5689.47 / 75.08 → 94.26 / 77.10
PE-CLIP92.35 / 72.14 → 93.61 / 73.7494.36 / 74.95 → 96.65 / 75.86
MetaCLIP74.87 / 66.35 → 74.64 / 65.6078.48 / 69.21 → 81.21 / 69.62
DINOv266.48 / 59.34 → 68.79 / 60.1262.89 / 59.95 → 65.03 / 60.99

Both metrics improve in 7 of 8 settings, so the rule remains useful at these extreme ratios, including 3 of 256 images. The clear failure case is a target with one class absent, because Eq. 8 then splits a single-class set around its own mean and necessarily assigns part of it to the missing class, while AUROC is undefined. For targets that may contain one class, the source-fixed threshold used in our post-processing study can replace Eq. 8. This avoids estimating the decision threshold from target composition while preserving the corrected ranking. Revised Section 3.3 states this alternative.

W1 and Q3. Number and representativeness of target samples, and changing distributions

AUROC averages six subsets and five samplings with balanced 512-image queries. Finite contexts are class balanced and drawn from the same subset, and the full context keeps the available composition.

Table R2-3. AUROC by context size.

ContextSigLIP2PE-CLIPMetaCLIPDINOv2
Probe89.3489.0676.8365.45
8 images92.6892.7278.6067.28
32 images92.6992.6778.4867.22
128 images92.6092.6678.4167.24
512 images92.5992.6778.4067.30
Full subset92.4892.6877.9667.35

In this six-subset audit with class-balanced finite contexts, eight images yield gains of 1.77 to 3.66 points. Mean AUROC is at least as high as the full-context result on three backbones and only 0.07 points lower on DINOv2. A separate wrong-context audit lowers AUROC below the probe by 0.49 on SigLIP2 and 0.38 on PE-CLIP when the mean comes from another subset. These results distinguish limited context size from systematic mismatch: small representative contexts remain effective in the tested audit, while a mismatched mean can be harmful. The practical concern therefore includes whether the context represents the current target, not just its size.

For continuously changing distributions, we track μt with an exponential moving average that starts from μs and is updated only after each image is scored, over five orders per stream type.

Table R2-4. Gain over the probe in changing streams.

StreamSigLIP2PE-CLIPMetaCLIPDINOv2
500-image blocks+2.29+2.93+0.89+1.15
Gradual transition+1.20+2.16−0.52+0.94

The history-only EMA improves every backbone on block streams and three of four under gradual transitions, supporting adaptation to changing targets. Changes in the context mean could be monitored as a deployment heuristic, with shrinkage of the context estimate toward μs or fallback to the probe as possible responses. The revised limitations present these as proposals requiring deployment validation.

Part 2. Q4 and W3

Q4. New generators and real dissemination conditions

On PE-CLIP we evaluate recent generators from MLLMGenSet that none of our original benchmarks contains, and the real dissemination conditions of RRDataset, including internet-platform transfer and redigitization. Aug. MLP and Context MLP are nonlinear controls matched to the FS-CTAA modulator's parameter budget. Both use forensic-shift training and classification supervision; Context MLP also receives μt.

Table R2-5. New generators and dissemination conditions.

TargetProbeAug. MLPContext MLPFS-CTAA
FLUX.299.1698.8599.1799.32
GPT Image 296.6596.4897.1696.92
Nano Banana 290.8592.1593.4994.70
Qwen Image 2.199.1098.3098.9099.24
MLLMGenSet mean96.4496.4497.1897.55
RRDataset Original98.2798.0098.0597.70
RRDataset Transfer92.7091.1093.6295.42
RRDataset Redigital80.1981.0883.2182.55
RRDataset mean90.3990.0691.6391.89

FS-CTAA has the best mean on both benchmarks and improves the probe on every new generator, by 3.85 points on Nano Banana 2, where the probe is weakest. On real dissemination it gains 2.72 points under transfer and 2.36 under redigitization, while near-saturated original images decrease by 0.57. The improvements under transfer and redigitization support the utility of forensic-shift training on additional dissemination benchmarks.

W3. Distinct contributions relative to existing methods

The three components answer different questions, supported respectively by the rank analysis, matched controls and episode ablations.

Table R2-6. Contribution of each component, with evidence.

ComponentQuestion it answersEvidence
Rank-invariance criterionWhich corrections can change ranking at allEvery L1 and L2 rule leaves AUROC unchanged on all four backbones
Sample-conditioned affine formWhether per-sample correction beats shared correction+1.22 to +1.58 over an identically trained shared modulator over three seeds, with capacity matched both ways
Forensic-shift trainingWhether the episode structure matters+3.49 with the four families against +0.82 with unstructured noise on PE-CLIP, with the gain dropping to 1.45 to 2.32 when any one family is removed

Table R2-7. Existing test-time corrections starting from the same detectors, ΔAUROC over the probe at the main checkpoint.

MethodSigLIP2PE-CLIPMetaCLIPDINOv2
Test-time normalization+0.33−0.55−0.78+0.09
TENT with LayerNorm updates−0.61−0.84−1.27−0.48
Trained shared modulator+1.49+1.88+0.81+0.78
FS-CTAA+2.88+3.49+1.72+1.67

TENT updates the encoder's LayerNorm parameters, relaxing the frozen-encoder constraint. Statistics-based normalization changes AUROC with a backbone-dependent sign, gradient-based entropy minimization lowers it on every backbone, and a shared modulator trained like FS-CTAA reaches about half of its gain. A generic context-conditioned classifier that concatenates the feature and μt also trails FS-CTAA on both new benchmarks in Table R2-5. FS-CTAA builds on both lines of work but uses the target mean to predict a per-channel correction of the feature that the frozen head already reads, and learns it from source episodes without target gradients. The revised Sections 2 and 3 make this positioning explicit.

Dear Reviewer, thank you again for your thoughtful comments. We have added analyses covering mixed target distributions, extreme class imbalance, limited and external context, evolving streams, new generators, and dissemination conditions, and have further clarified the practical limitations of mean-score thresholding and the complementary roles of the rank-invariance criterion, sample-conditioned correction, and structured forensic-shift training. Together, these results provide broader evidence for the robustness and generalization of FS-CTAA across the evaluated settings. We would welcome the opportunity to discuss these results with you further and to hear any additional suggestions you may have.

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Paper summary

This paper studies adapting an AI-generated image detector with unlabeled target data while keeping the vision foundation model and linear head frozen. The approach is interesting, though some gains are modest.

Critical strengths
  1. The paper presents an interesting finding: a source-domain training module that leverages the target-domain mean without gradient updates on target data can improve the ranking produced by a strong frozen detector, while providing additional gains over an independently trained shared affine calibration module.

  2. The proposed method requires no backpropagation at test time, making these improvements practically valuable. However, the performance gains are not positive on every subset, a limitation the authors transparently report.

Critical weaknesses

1)Proposition 1 is correct, but it merely restates the basic property that rank-based statistics are invariant under strictly increasing transformations, as the authors acknowledge on page 3, lines 151–153. Although the proposition rules out ranking improvements from L1/L2, it provides no criterion for choosing between L3 and L4, nor does it explain when per-sample conditioning is preferable to shared calibration.

2)In Table 2, why are the AUROC scores for “+ closed-form calibration” nearly identical to those in the preceding row?

Questions for authors

See weaknesses.

3 comments

We thank the reviewer for recognizing the practical value of improving a frozen detector without test-time backpropagation. Rebuttal tables are labeled R1-x, and gains are AUROC points over the frozen probe. Table R1-2 averages three training seeds, and the other tables use the main checkpoint.

W1. What Proposition 1 contributes, and when L4 is preferable to L3

Rank invariance under strictly increasing maps is classical for scores. What Proposition 1 contributes is its extension to feature-level corrections applied before a frozen head. It states the property for the score function that a correction induces, so whether a correction can change ranking is decided by its functional form alone. On this basis we introduce the L1 to L4 granularity hierarchy, which organizes test-time corrections by what they share across a target set, from monotone score maps and shared translations to shared and per-sample feature transforms.

Table R1-1. Diagnostic suite, ΔAUROC over the frozen probe.

CorrectionLevelSigLIP2PE-CLIPMetaCLIPDINOv2
Prior-matching calibrationL10000
Label-oracle calibrationL10000
Closed-form calibrationL10000
Global mean alignmentL20000
Test-time normalizationL3+0.33−0.55−0.78+0.09
Trained shared modulatorL3+1.49+1.88+0.81+0.78
FS-CTAAL4+2.88+3.49+1.72+1.67

Every L1 and L2 rule leaves AUROC unchanged on all four backbones, as the criterion predicts, even when the threshold is set with target labels. The L2 values are below 1e-7, which is numerical precision. Only L3 and L4 can change ranking. Test-time normalization changes sign across backbones, whereas the trained L3 modulator and FS-CTAA improve every backbone, FS-CTAA by the larger margin. The practical value is that accuracy gains of threshold rules, which are common in test-time correction, can be identified as operating-point effects without running them.

The proposition separates corrections that can change ranking from those that cannot; it does not by itself rank L3 against L4. For the channel-wise affine family, L3 gives s3(z)=(w⊙γC)⊤z+bCs_3(z)=(w\odot\gamma_C)^\top z+b_C, one reweighted projection for the target set. If an attainable shared affine score induces the target likelihood-ratio ordering, L3 is sufficient in principle. Our experiments establish the additional benefit of L4 over the trained L3 controls.

The empirical test favors L4 on every backbone. The independently trained L3 module uses the same statistics, forensic-shift episodes and objective as FS-CTAA, and omits only the per-sample feature input.

Table R1-2. L3 versus L4 over three training seeds.

BackboneL3, sharedL4, FS-CTAAL4 minus L3Paired 95% interval
SigLIP2+1.55+2.95+1.40+1.12 to +1.68
PE-CLIP+1.95+3.53+1.58+1.31 to +1.87
MetaCLIP+0.93+2.15+1.22+0.93 to +1.51
DINOv2+0.94+2.20+1.26+0.94 to +1.58

The interval excludes zero on every backbone. The L3 module itself is positive on all four backbones and all three seeds, so L4 is compared against a strong shared baseline.

Part 2. Controls for capacity and weights, and W2

Table R1-3. Controls at the main checkpoint that hold capacity or weights fixed.

VariantLevelSigLIP2PE-CLIPMetaCLIPDINOv2
Trained shared modulatorL3+1.49+1.88+0.81+0.78
Shared modulator widened to the L4 budgetL3+0.70+0.50−4.30+0.60
Shared FS-CTAA with the same weightsL3+0.63+0.42−3.88+0.53
FS-CTAA shrunk to the L3 budgetL4+2.60+3.10+1.40+1.40
FS-CTAAL4+2.88+3.49+1.72+1.67

Matching capacity in either direction keeps every L4 row above every L3 row on every backbone. Widening L3 does not help, while shrinking L4 keeps most of its gain, so parameter count does not explain the advantage. Shared FS-CTAA averages the predicted scale and offset within each subset using identical trained weights, and most of the gain disappears. Together with the three-seed L4-minus-L3 margin of 1.22 to 1.58 AUROC points, these controls support an additional benefit from per-sample conditioning. Averaging also restores a shared affine score, so the same-weight control alone does not distinguish per-sample correction from nonlinear scoring. Revised Section 3.1 separates the proposition's diagnostic role from this empirical evidence.

W2. Why closed-form calibration leaves AUROC unchanged

This equality holds by construction and the row serves as a control. Closed-form calibration subtracts the same estimated mean from every score, si′=si−m^s_i'=s_i-\hat{m}. Hence si′−sj′=si−sjs_i'-s_j'=s_i-s_j, every real and generated pair keeps its order, and AUROC cannot change. Balanced accuracy can still rise because the operating point moves. This is the L1 case of the criterion.

Table R1-4. Balanced accuracy and AUROC in percent, main checkpoint.

BackboneBA, probeBA, calibrationBA, FS-CTAAAUROC, probe and calibrationAUROC, FS-CTAA
SigLIP282.785.689.191.4994.38
PE-CLIP79.785.488.289.0092.49
MetaCLIP69.273.775.279.6881.40
DINOv265.766.668.070.0271.69

Calibration raises balanced accuracy on every backbone while AUROC stays identical, which isolates the operating-point effect. FS-CTAA adds a further 1.4 to 3.5 balanced-accuracy points and raises AUROC on every backbone, a ranking improvement that no threshold rule can produce. The revised caption states this.

Dear Reviewer, thank you again for your careful and constructive review. We have clarified the role of Proposition 1 as a diagnostic boundary, showing why monotone calibration and shared translation cannot change sample ordering, and added controlled L3/L4 comparisons in which the seed-averaged L4−L3 AUROC difference is positive for every backbone, with parameter-matched controls yielding the same ordering. We have also explained why closed-form calibration preserves AUROC while potentially improving balanced accuracy through a change in the operating point. We would welcome the opportunity to discuss these points with you further and to hear any additional suggestions you may have.

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

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