acceptodds
Under review as a conference paper at ICLR 2027

Maturity-Guided Supervision Shaping for Data-Free Model Extraction Defense

Abstract

Publicly accessible black-box models are vulnerable to model extraction attacks: by repeatedly querying the prediction interface and collecting its outputs, an attacker can train a substitute model with similar functionality. Existing defenses typically weaken clone training through output modification, randomized responses, query monitoring, simulated attack queries, or dynamic execution. Although effective, their defense signals often come from outside the model itself, making them sensitive to changes in query strategy, repeated-query smoothing, or deterministic-service requirements, which can lead to unstable defense performance or inconsistent service behavior. To avoid such external dependence, we propose Maturity-Guided Supervision Shaping (MGSS), a defense that derives its signal from the victim model's own inference process. MGSS exploits how class evidence matures across semantic depth and uses the resulting cross-stage maturity discrepancy as a victim-internal shaping signal. Internally aligned evidence supports utility-preserving responses, whereas stronger discrepancy steers the exposed supervision toward a less extractable direction, making it harder for the attacker to recover the original decision rule. MGSS freezes the victim backbone, fine-tunes only a lightweight module to adjust the final output, and preserves a deterministic fixed inference path without query history, randomized responses, or simulated attack queries. Experiments show that MGSS reduces clone accuracy under both soft-label and hard-label model extraction across multiple datasets and clone architectures. In the CIFAR-10 soft-label DFME setting, MGSS reduces the average accuracy of three clone architectures from 78.83% to 37.89%, while maintaining 94.46% clean victim accuracy.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
model extraction defense, data-free model extraction, supervision shaping, cross-stage semantic maturity, black-box model security, knowledge distillation

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_eqJBOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The paper investigates active defense for black-box model extraction attack in the data-free setting, where an adversary queries a target classifier and trains a substitute model using the returned hard or soft labels. The objective is to reduce the quality of the extracted model while preserving the normal utility of the victim model. The key insight is that synthetic extraction queries from attackers tend to produce more inconsistent class predictions across the victim model’s intermediate layers than in-domain clean samples. Based on this observation, the proposed method uses the discrepancy between intermediate and final predictions to control how strongly a trained residual head modifies the returned logits or labels. Experiments on CIFAR-10, CIFAR-100, and MiniImageNet show that the method consistently lowers clone accuracy while largely preserving clean accuracy.

Critical strengths
  1. The paper studies an important security problem in model extraction, which is increasingly relevant as deployed models represent valuable intellectual property.
  2. The evaluation covers both soft-label and hard-label settings, with experiments across several datasets and models, together with extensive ablation studies.
Critical weaknesses
  1. The assumed attacker capability is not well justified. The evaluated attacks query the model in a way that is largely separated from normal in-domain data, which may itself be the main source of separability. Specifically, the paper states that "the query distribution Q is unknown to the defender and is not assumed to be out-of-distribution" (Line 193). It is unclear why an attacker cannot query in-domain samples like a normal user, or how the defense affects normal users whose queries are also outside the training distribution.
  2. The robustness to different extraction query designs is not sufficiently evaluated. Tables 4, 8, and 13 show noticeable variation in the maturity signal and defense performance under different query or coverage constructions. It is unclear whether MGSS would remain effective under a broader range of extraction queries, and whether its advantage over baseline DNF (Luan et al., 2025) would still hold under the DFME variants in Table 4. Moreover, MGSS shows large variation across different coverage datasets in Table 13 (40.61%–52.13%), while the baseline DNF reports relatively small variations across different OOD training datasets (its Table 3), raising concerns about MGSS's sensitivity to defense training data.
  3. The advantage over prior defenses is not clearly established. Lines 161–166 mainly contrast victim-internal signals with external mechanisms, but it is unclear what limitation of prior methods this resolves. For example, what is the practical drawback of early-exit defenses such as DNF that motivates replacing dynamic routing with a residual head?
Questions for authors
  1. Can the authors justify why this data-free threat model is the most relevant setting, and provide in-domain extraction evaluation similar to DNF (Luan et al., 2025)?
  2. If normal users are always accessing the defended API, would an attacker who successfully copies this API already have achieved the goal of model extraction?
  3. Some of the discussion feels abrupt and not well justified. For example, the research question in Lines 048–053 looks reverse-engineered from the proposed method rather than driven by a clearly identified problem. It treats signals outside the frozen victim as a limitation and directly motivates victim-internal signals, but it is unclear why the former is necessarily problematic.

I am open to increasing my score if most of my concerns are clarified, especially for the assumptions about attacker query distributions (weakness 1) and the practical advantages over prior defenses (weakness 3).

1 comment

Attacker data access. An attacker can submit in-domain images and receives the same response as any user submitting the same input. We focus on DFME because API access alone can yield an accurate substitute when representative data are scarce. Truong et al. (CVPR 2021) reached 92% of the victim’s CIFAR-10 accuracy with 20M queries and no surrogate dataset. An unknown QQ means that MGSS constructs its training targets without estimating the attacker’s query distribution. Generated queries can approach the task distribution, and an attacker can exploit predictions preserved in those regions. Extraction from representative in-domain seeds is a separate data-access setting from the DFME protocols evaluated here.

Utility under benign shifts. We compared the original victim and MGSS on the same 10,000 CIFAR-10 images, using fixed checkpoints and CIFAR-10-C corruptions (Hendrycks & Dietterich, ICLR 2019). Each entry is the change in accuracy, in percentage points, relative to the original victim on the same inputs.

SeverityBrightnessDefocus blurGaussian noise
1−0.86−1.01−10.37
2−0.96−1.85−16.55

Clean accuracy changed from 95.25% to 94.59%. The mean loss across the six shifts was 5.27 points: 1.17 for brightness and blur, 13.46 for Gaussian noise. Under Gaussian noise at severity 2, accuracy fell from 61.04% to 44.49%, and the mean total variation distance between the two models’ output distributions rose from 0.0230 on clean inputs to 0.4439. This identifies a benign shift that substantially affects both labels and probabilities.

Why use cross-stage evidence? Shaping a response requires deciding how much to adjust it and which competing class should gain weight. Intermediate stages reveal which classes had strong support earlier but lost it by the final layer. Our main-text ablation tests both choices under the same CIFAR-10 DFME protocol. Using final confidence alone to set the adjustment strength yielded 80.59% clone accuracy. Retaining cross-stage strength but directing the adjustment toward the final-logit runner-up yielded 47.81%. Using cross-stage evidence for both yielded 39.35%.

Practical advantage. MeCo jointly optimizes the victim and a perturbation generator, ACT uses pseudo-data to learn an active watermark, and DNF trains intermediate exits and selects one by confidence. MGSS trains one residual head with 1.45% as many parameters as the frozen victim and retains a fixed inference path. On the same RTX 3090, total defense training times over five runs (minutes, mean ± SD) were 3.69 ± 0.02 for MGSS, 4.89 ± 0.06 for DNF, 17.20 ± 0.34 for ACT, and 141.70 ± 11.37 for MeCo. At batch size 64, MGSS processed 5,646 images/s versus 5,297 for DNF, retaining 97.7% of undefended throughput. Across three CIFAR-10 clone architectures, MGSS reduced vanilla DFME clone accuracy by 8.78–14.56 points relative to DNF, with clean service accuracies of 94.46% and 94.34%, respectively.

Query and coverage sensitivity. At the same 20M budget, DFME-Smooth, CA-DFME, and DFME-ISF raised ResNet18-8x clone accuracy against MGSS from 39.35% to 48.19%, 46.94%, and 50.73%. Direct comparisons with DNF cover vanilla DFME and MAZE (Kariyappa et al., CVPR 2021). Under MAZE, clone accuracies were 15.68%, 14.20%, and 14.90% for MGSS versus 22.46%, 21.10%, and 20.94% for DNF. In the fixed-seed coverage study, using only strongly augmented target-task images yielded 52.13% clone accuracy and 94.36% service accuracy. Switching coverage to CIFAR-100 yielded 40.61% and 94.46%. Thus, target-task data alone suffice to train MGSS, while coverage choice materially affects defense strength. DNF’s smaller spread was measured with different coverage sources on ImageNet200/Swin.

Cost of copying the protected API. Successfully reproducing the service constitutes extraction. The practical question is what the attacker obtains for a given query budget. On CIFAR-10, DFME trained a ResNet18-8x clone to over 70% accuracy with 5M queries to the undefended API. Against MGSS, the same attack reached 39.35% with 20M queries, while the service retained 94.46% accuracy. Even at four times the query budget, the clone remained well below the accuracy it had already reached against the undefended API.

Reviewer_BDKQOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper introduces a novel defense against model extraction attacks based on the progressive model maturity during the inference process for classification tasks. Instead of applying randomized output transformations, the authors propose to use internal signals from the model’s own inference and implement a maturity-guided supervision shaping (MGSS) as a defense that primarily maximized the discrepancy between the exposed API output and the maturity signals derived from MGSS without degrading utility. The proposed approach is plug-and-play, doesn’t require any major changes to the victim model architectures, and needs few training efforts. Evaluations have been conducted on three datasets, three models, and results have been compared against different baseline defenses, under different extraction attacks.

Critical strengths
  • The paper tackles an important problem regarding model extraction attacks, which is a major challenge in the security of model serving APIs.
  • The paper introduces a smart and simple design based on the model's own maturity signals during the inference process to guide somehow a noising process that masks the victim model’s decision boundaries that an adversary can use for extraction to create a clone model.
  • The evaluation is comprehensive on different attacks, baseline defenses, three datasets and three models for image classification. Results look promising, generally outperforming SOTA defenses on CIFAR-10 and CIFAR-100.
  • The paper is well motivated and flows nicely.
Critical weaknesses
  • The paper’s motivation is clear and understandable, however, there’s little to no discussion on how this is different from existing early-exit approaches (even with a frozen model, early-exits can still be applied by training a plug-and-play routing mechanism). Early-exit has been shown to be a good defense against privacy attacks in general and model extraction attacks in particular (“Defending Against Membership Inference Attacks on Iteratively Pruned Deep Neural Networks, NDSS” and “Dynamic Neural Fortresses: An Adaptive Shield for Model Extraction Defense, ICLR”). So without a proper evaluation against existing early-exit defenses and dedicated discussion on how MGSS differs in design and principles, it’s unclear if MGSS is just a variant of early-exit methods that rely on confidence maturity throughout the inference process. To strengthen the MGSS novelty, the authors should make this clear early-on in the paper.
  • There’s no latency or hardware measurements reported to quantify how much overhead the added MGSS components add to the victim models. While the training overhead is minimal compared to other defense baselines, the inference overhead is not reported. The authors should add hardware-related measurements to quantify the defense-efficiency tradeoff.
  • The evaluated models are limited to only ResNet, MobileNet, and DenseNet. I suggest adding more models and explaining how MGSS could also scale to transformer models (small ViT models) and whether MGSS will have similar formulation when attention layers are involved.
  • The authors didn’t justify the choice of the reported baseline defenses and attacks, specifically on how representative, recent, and strong they are. It’d be great if further justification is reported to make the evaluation and comparisons strong for drawing useful research insights.
  • The ablation results are extremely important and shouldn’t be buried in the appendix. I suggest moving at least Table 11 to the main paper.
Questions for authors
  • Could you clarify and discuss more the difference between MGSS and existing early-exit based defenses for model extraction attacks?
  • Could you quantitatively compare MGSS against early-exit based defenses?
  • Could you report latency or any hardware-related measurements to quantify the inference overhead added by MGSS?
  • Could you evaluate on more models and clarify how MGSS scales to transformer-based models?
  • Could you justify the choice of the reported baseline defensed and attacks?
1 comment

Response to Reviewer BDKQ

Thank you for highlighting the paper’s motivation and empirical evaluation. The original submission includes a direct comparison with DNF in Tables 1–2 and evaluates a ViT as the victim in Appendix E.4 (Table 10). We have also measured inference latency and throughput to address your question about deployment cost.

Relationship to early-exit defenses. DNF uses intermediate confidence thresholds to select the exit that supplies the API prediction. MGSS always completes the forward pass. Its intermediate readouts track how support for individual classes changes across stages. In particular, a class supported at an intermediate stage but suppressed in the final prediction provides a direction for adjusting the final logits. The discrepancy in MGSS is thus between intermediate and final class support. It guides the residual head’s adjustment to the logits. We will clarify this distinction when introducing MGSS.

Across all 18 settings in Tables 1–2 (three datasets, two attacks, and three clone architectures), MGSS yields lower mean clone accuracy than DNF. On CIFAR-10 under DFME, clone accuracy averaged across architectures is 49.15% for DNF and 37.89% for MGSS, a difference of 11.26 percentage points. Their clean victim top-1 accuracies are 94.34% and 94.46%, respectively (Table 3). The ablation in Table 11 directly tests whether final confidence can substitute for cross-stage evidence. Using final-layer confidence alone to set the shaping strength raises ResNet18-8x clone accuracy from 39.35% to 80.59%.

Inference overhead. We measured all methods on CIFAR-10 test inputs using one RTX 3090 in FP32 with TF32 disabled. Latencies are in milliseconds per batch. B1 and B64 denote batch sizes 1 and 64.

MethodB1 p50 / p95B64 p50 / p95B64 throughput (images/s)
Undefended3.25 / 3.3611.03 / 11.185,780
DNF4.97 / 5.2612.04 / 12.185,297
ACT4.23 / 4.3512.85 / 13.064,950
MeCo5.01 / 5.0813.74 / 13.914,633
MGSS4.37 / 4.6511.28 / 11.415,646

Relative to the undefended model, MGSS adds 1.12 ms (34.5%) to median single-sample latency. At batch size 64, it adds 0.25 ms per batch (2.3%) and retains 97.7% of the original throughput. On this hardware and in-distribution workload, MGSS has 12.1% lower median latency than the measured DNF implementation at B1 and 6.3% lower at B64.

Transformer applicability. For the 12-block ViT in Table 10, we read intermediate representations from blocks 4, 8, and 12. These representations feed into the same prototype construction, class-support computation, and residual shaping used for CNN victims. Under DFME with a ResNet18-8x clone, MGSS reduces clone accuracy from 55.99% to 27.33%, while clean ViT accuracy changes from 90.46% to 90.20%. Table 10 also evaluates MobileNetV2 and DenseNet121 as victims. We will highlight these single-run transfer results and their evaluation protocol in the main text.

Choice of defenses and attacks. The baselines cover four distinct mechanisms: input randomization with distributionally robust training (MeCo, 2023), Bayesian active watermarking (ACT, 2024), weight perturbation (AAUG, 2024), and dynamic early exit (DNF, ICLR 2025). DNF provides the closest comparison because both methods use intermediate representations.

Following prior defense evaluations, we use DFME for probability-vector access and DFMS-HL for top-1-only access, with MAZE as an additional soft-label evaluation on CIFAR-10 (Table 9). On the undefended CIFAR-10 victim, DFME trains a ResNet18-8x clone to 87.36% accuracy. Under the same total query budget, the three adaptive DFME variants in Table 4 raise mean clone accuracy against MGSS from 37.89% to 45.52%–49.28%, quantifying how much performance the attacker recovers by changing its query strategy.

Ablations in the main text. We will move Table 11 to Section 5.5 and retain both clone and victim accuracy so readers can assess how cross-stage evidence, shaping direction, and continuous modulation affect extraction resistance and clean utility.

Reviewer_8JgDOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes MGSS, a defense against data-free model extraction. The victim backbone is frozen; prototype-based class-support distributions are read out at three intermediate stages, and the mass of non-top-1 classes that intermediate stages support but the final posterior suppresses (“maturity discrepancy”, ρ) is used as a signal. A lightweight residual head adds a logit correction, trained with a CE “service” loss on weakly augmented in-distribution data and a “defense” loss that pushes the posterior on strongly augmented coverage data (by default CIFAR-100) toward a target with zero mass on the victim’s top-1 class. The defense is deterministic and stateless. Experiments on CIFAR-10/100 and MiniImageNet under DFME, DFMS-HL and MAZE report lower clone accuracy than MeCo/ACT/AAUG/DNF with ~0.5% clean-accuracy loss; ablations, sensitivity, architecture transfer, and three adaptive DFME variants are included.

Critical strengths
  1. A deterministic, stateless, backbone-frozen defense with ~1.5% parameter overhead and minutes of training is practically attractive, and the architecture-transfer results (ViT, MobileNetV2, DenseNet121) suggest the recipe is not ResNet-specific.

  2. The offline diagnostics are careful: stage-final agreement separates clean inputs (80.8%) from DFME queries (51–56%), and the random-network control (13%) rules out an architectural artifact. The limitations section is candid.

Critical weaknesses
  1. The method does not implement its motivation. Both branches of Eq. 9 are normalized over non-top-1 classes, so α=ρ/(ρ+κ) only interpolates between two counter-supervision targets; ρ never decides whether to shape. Proposition 1 confirms the target excludes the victim’s top-1 for every input. The claimed “aligned → utility-preserving” behavior (abstract, Fig. 1) therefore comes from the service loss on P_task—i.e., from the external P_task/P_cov data split—not from the internal maturity signal. The ablations contradict Eq. 10 (ρ_final as “shaping strength”, α_gate=0 as “no shaping”, an "α_max" that does not exist in Eq. 10), and App. A.1 says the head also consumes raw stage features, which Eq. 6 omits. Either the equations or the experiments describe a different method. Relatedly, the central selling point—no external dependence—does not hold: the default coverage data is CIFAR-100 and clone accuracy swings 40.6%→52.1% with the coverage source (Table 13), exactly as in Adaptive Misinformation’s outlier exposure or DNF’s GAN-OOD data. On DFME queries H(q₃)≈2.22≈ln 10, so the “semantic” target reduces to near-uniform over non-top-1 classes; the “not arbitrary label noise” claim is unsupported and the uniform-target ablation is missing.

  2. Baselines are copied, not reproduced, and the gains over SOTA are mostly within noise. All 48 baseline clone numbers and 9 of 10 clean-accuracy numbers in Tables 1 and 3—including every “Undefended” row—are digit-for-digit identical to the values published in the MeCo, ACT, AAUG and DNF papers, while Sec. 5.1 states results are five-run means and App. A.2 implies official code was used for reproduction (only AAUG is disclosed as copied). MGSS is thus compared across pipelines and hardware, and the table is assembled from four papers of one lineage that never benchmarked each other. Two entries do not match their sources (DNF CIFAR-100 clean 75.54 vs. 78.73±0.30 in the DNF paper; the “measured on RTX 3090” MeCo/ACT training times are exactly 0.4× the A6000 hours in ACT’s Table 14). Against the best baseline per column, MGSS wins clearly only on CIFAR-10 soft-label DFME (~5–7 pts, ~2σ) and MAZE; on CIFAR-10 hard-label, CIFAR-100 and MiniImageNet the differences are within one standard deviation, and AAUG is better on one column. Adaptive Misinformation (the closest structural ancestor), Prediction Poisoning and GRAD (whose code Table 5 lists as “used for baseline comparison”), ModelGuard and MISLEADER are not compared; data-based attacks (Knockoff/ActiveThief) are excluded even though an ID-preserving defense is most vulnerable to near-ID queries; no benign distribution-shift utility (e.g., CIFAR-10-C) is reported although the method flips predictions on high-discrepancy inputs. Novelty is incremental: the conditional-misinformation structure is AM (CVPR 2020), the per-stage prototype-cosine support and stage–final discrepancy come from the OOD/misclassification-detection literature (Shallow-Deep Networks’ confusion metric, DkNN, Prototype Fusion), and the frozen-victim + lightweight-head + OOD-auxiliary-data template is already in DNF (ICLR 2025).

Questions for authors
  1. Under Eq. 10, α=0 still yields a target with zero mass on the victim’s top-1. What guarantees utility preservation on aligned inputs other than the service loss? Is the implemented target actually (1−α)·p_T + α·q_counter? Please reconcile Eq. 10 with the “shaping strength”/”α_max” definitions in App. F.
  2. Which numbers in Tables 1 and 3 were run by the authors? Where does DNF’s CIFAR-100 clean accuracy of 75.54 come from? Were the MeCo/ACT times in Table 14 measured or rescaled?
  3. Report δ_Q (protected–victim top-1 disagreement) on DFME and DFMS-HL queries, and the values of κ, ε, w_s and the A_s augmentation strength.
  4. Add a uniform-over-non-top-1 target ablation; add AM, P-poison, GRAD and ModelGuard; add a data-based attack; add CIFAR-10-C utility. Does the “w/o cross-stage maturity” variant also remove stage features from the head input, and was κ re-tuned to ρ_final’s scale?
  5. State in the main text that P_cov defaults to CIFAR-100, and discuss whether baselines were given the same auxiliary data.

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

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