Making an image classifier resist adversarial examples (tiny, deliberately chosen input changes that flip its prediction) almost always lowers its accuracy on ordinary, unperturbed images. In adversarial robustness research, a new defense is judged by one comparison: does it beat heavily engineered wide networks on both clean accuracy and AutoAttack, a standardized ensemble of strong attacks? An unconventional idea, such as stochastic inference, input-dependent routing, or modular training, usually arrives at small scale with lower clean accuracy. It fails that comparison and is discarded before anyone learns whether it was promising. The field cannot simply relax its standards. Before standardized evaluation, published defenses overstated their robustness by more than 10 points (RobustBench).
We propose an admission test that a workshop, a vision track, or a lab could apply to early-stage defenses, and we propose to validate it empirically. The test has two parts. First, a defense is scored by how far it sits above a cheaply computed robustness–accuracy curve for standard methods trained at the same small budget, rather than by its leaderboard rank. Second, it must pass a short battery of checks that catch gradient masking, meaning defenses that only appear robust because they break the attacker's gradients. The central scientific question is whether this test is predictive. If a method sits above the small-budget curve, does it also sit above the large-budget curve once scaled? If the answer is yes, small labs gain a defensible route for incubating risky defenses. If the answer is no, we learn exactly where small-scale evidence about the trade-off misleads, and incubation must be designed differently.
Core Claim
We claim that the excess robust accuracy a defense achieves over a matched-budget reference curve, measured at equal clean accuracy, is a reliable and cheap predictor of its standing at full scale, provided masking checks screen the defense first. A raw small-scale leaderboard number is not such a predictor. This is a claim about the transition from incubation to mainstream evaluation, which the meta-science literature describes as ad hoc and unmonitored. It is also a claim about the robustness–accuracy trade-off: whether a trade-off advantage stays stable across model size and data size.
Prior work raises the question but does not answer it. On the meta-science side, Troubling Trends in Machine Learning Scholarship diagnoses how checklist reviewing rewards incremental, benchmark-polished work. It also argues that rigor matters, but it proposes no concrete mechanism. Blue Sky and short-format tracks (AAAI-29 summary, VLDB front matter) separate novelty from empirical completeness, but they offer no quality control. In adversarial robustness, a lack of quality control is fatal. These papers motivate the proposal. RobustBench constrains it: any admission test that weakens attack strength will reintroduce the overestimation crisis. Our test therefore keeps AutoAttack in place and changes only the reference point for comparison.
Why transfer is not guaranteed
The obvious objection is that small-scale behavior need not predict large-scale behavior. The trade-off literature gives concrete reasons to worry. Phase Transition from Clean Training to Adversarial Training shows that adversarial training leaves the clean-training loss basin once the perturbation size exceeds a critical value. For a PreActResNet18 on CIFAR-10 that value is about 0.5/255, far below the standard 8/255. The same paper shows the critical value shrinks as the training set grows. The geometry of the trade-off therefore shifts with scale, and a method's advantage at small $n$ could vanish or reverse. Architecture matters as well. AR-AT attributes its clean-accuracy gains partly to splitting batch normalization statistics between clean and adversarial inputs, and its authors leave open whether the mechanism survives in transformers that use layer normalization. A small-budget test calibrated only on convolutional networks could fail on such methods. We treat these as the main threats, and the experiments are designed to expose them.
Research Program
We first build reference curves. For each budget (model family, epochs, dataset), we trace clean versus AutoAttack accuracy for standard adversarial training and for TRADES (Zhang et al.), sweeping its trade-off weight $\lambda$ and the perturbation radius. The small budget is PreActResNet18 or ResNet-18 on CIFAR-10, CIFAR-100, and TinyImageNet-200, using a shortened schedule that a single GPU can complete in about a day. The large budget is WideResNet-34-10 with full schedules. Let $r_B(c)$ be the upper envelope of robust accuracy at clean accuracy $c$ under budget $B$. A defense with clean accuracy $c$ and robust accuracy $r$ then receives the excess score
$$\Delta_B = r - r_B(c),$$
measured in AutoAttack percentage points. When a defense's clean accuracy falls outside the swept range, we report that it is out of range rather than extrapolating.
Second, we assemble the masking battery from failure modes that are already documented. Unstable TRADES runs show a PGD-10 accuracy of 0.2872 against an AutoAttack accuracy of 0.1042 (Adversarial Robustness Overestimation and Instability in TRADES). The battery therefore includes four checks. The first measures the gap between PGD-10 accuracy and AutoAttack accuracy. The second compares the black-box Square attack against white-box attacks. The third checks that accuracy falls monotonically as the perturbation radius grows. The fourth requires an adaptive attack written against any component a standard attack does not target; for a routing defense, that component is the gate. The adaptive-attack requirement exists because Adaptive Smoothing leaves attacks on its gating network as an open vulnerability.
Third, we run candidate defenses through both budgets. The candidate set mixes methods believed to shift the trade-off curve with methods believed not to. It includes AR-AT, Adaptive Smoothing (using the released Bai-YT/AdaptiveSmoothing code), TRADES with the Gaussian-noise fix from the instability paper, and a perturbation-radius curriculum that starts below the critical value and grows it. It also includes a modular variant in the spirit of Deep Incubation. That paper trains sub-modules separately inside a small fixed "meta model" before stitching them together, but only for clean ImageNet training; here, clean-trained modules would be robustified one at a time. These last two candidates play the role of "risky, unproven" entries. We do not claim they work. Their purpose is to give the test genuinely uncertain cases. Finally, we include deliberately masked models, namely the unstable TRADES runs at low $\beta$, as known-bad entries.
Baselines
The naive reference point is current practice. A defense is ranked by its raw clean and AutoAttack accuracy at whatever scale it was trained, and compared against published large-scale numbers. Under this rule every small-budget defense fails, so the baseline makes explicit how many eventually-good methods it would reject. For a fair comparison, the naive rule and our test see exactly the same small-budget runs.
The strongest competitor for predicting large-scale standing is the raw small-budget AutoAttack accuracy itself, used without any reference curve. It costs the same, and a skeptic would argue that it already carries the signal. We beat it if $\Delta_B$ achieves a higher Spearman rank correlation with the large-budget excess score across candidates and seeds, under a paired bootstrap. Ranking by robust accuracy at matched clean accuracy is precisely what our score formalizes. If a simple pairing by nearest clean accuracy performs as well as the full fitted curve, we will report that the simpler form suffices.
The strongest existing defense anchors the large-budget curve. AR-AT reports 90.89% clean and 50.77% AutoAttack accuracy on CIFAR-10 with WideResNet-34-10, versus 84.33% clean accuracy for TRADES at similar robustness (AR-AT). On CIFAR-100, Adaptive Smoothing reports 85.21% clean and 38.72% AutoAttack accuracy (Adaptive Smoothing). We reproduce both under our pipeline and use the reproduced values, not the reported ones. We found no reported result on Lacuna for AR-AT at CIFAR-100, Imagenette, or TinyImageNet scale. All methods receive the same data, the same attack suite, and the same hyperparameter-search budget per method at each scale, a fixed number of trials.
Two ablations isolate the proposal's ingredients. The first drops the reference curve and keeps the masking battery. The second keeps the curve and drops the battery. Together they show whether prediction comes from the comparison point, from the screening, or from both. Against the known-masked models, the battery is judged by its recall, and against the honest runs by its false-positive rate.
Why not just…?
Why not just require full AutoAttack at full scale, as RobustBench does? That remains the gold standard for final claims, and nothing here replaces it. The barrier is the cost of training a WideResNet with multi-step attacks, which Zhang et al. put at roughly ten times standard training before TRADES' own overhead. Running AutoAttack itself is not the expensive part. The question is whether a cheaper training budget gives enough evidence to decide which ideas deserve that cost. The correlation experiment answers this directly. If the correlation is low, the honest conclusion is that there is no shortcut.
Why not just send risky defenses to a Blue Sky track with no evaluation? In this field, unevaluated defense claims tend to be wrong. RobustBench documents overestimates above 10 points, and the TRADES instability paper shows a 0.183 gap between PGD and AutoAttack accuracy within a single method. Our known-masked entries measure how many of them a no-evaluation track would admit. That number is plausibly all of them.
Why not just sweep TRADES' $\lambda$ at full scale and call the curve the bar? That curve is our large-budget reference, so we agree that it is the right bar. Building it at full scale for every new idea is exactly the cost incubation must avoid. At low $\beta$ it is also unstable: 7 of 10 runs were unstable at $\beta=3$ (TRADES instability). For that reason, every point on our curve must itself pass the masking battery.
Why not just add unlabeled data, which RobustBench found raises both accuracies? Extra data is a real way to move the curve, and we treat it as one more candidate method rather than as an alternative to the test. It also illustrates the transfer risk. The phase-transition result says more data lowers the critical radius, so data-dependent advantages are the most likely to change rank between scales. We report them separately.
Decisive Checks
The test succeeds if three things hold. The excess score must rank-correlate with large-budget standing clearly better than raw small-scale AutoAttack accuracy does. The masking battery must flag the unstable TRADES runs while passing their stable counterparts. And none of the candidates admitted at small scale may collapse below the large-budget curve after scaling. The test fails informatively if the correlation breaks specifically for data-heavy methods or for batch-normalization-dependent methods moved to vision transformers. Breakage in those two places would tie the limits of small-scale incubation to the scale-dependent trade-off geometry identified in Phase Transition and to the architecture caveat that AR-AT leaves open.
References
- RobustBench: a standardized adversarial robustness benchmark
- Troubling Trends in Machine Learning Scholarship
- A Summary of the Twenty-Ninth AAAI Conference on Artificial Intelligence
- Front Matter
- Phase Transition from Clean Training to Adversarial Training
- Rethinking Invariance Regularization in Adversarial Training to Improve Robustness-Accuracy Trade-off
- Theoretically Principled Trade-off between Robustness and Accuracy
- Adversarial Robustness Overestimation and Instability in TRADES
- Improving the Accuracy-Robustness Trade-Off of Classifiers via Adaptive Smoothing
- Deep Incubation: Training Large Models by Divide-and-Conquering