Free Retries Against Replay Detectors: Sub-Hop Shift Consistency as a Security Property

A replay attack on a voice-login system needs no speech synthesis. The attacker records the victim on a phone and plays the recording back into the system's microphone. Because the speaker identity in the replayed audio is genuine, the system has to rely on a separate countermeasure: a classifier that looks for traces left by the recording and playback chain, such as loudspeaker coloration, a second room's echo, and the filters of repeated analog-to-digital conversion. Those traces are small, and many of them sit near the top of the frequency band. Deep countermeasures now report near-perfect error rates on the main benchmark. Every one of them, however, takes in a spectrogram computed on a fixed grid of analysis frames and runs pointwise nonlinearities on that grid.

Vision and operator-learning work has shown that such networks are not stable under shifts smaller than one grid step. Their output changes when the input moves by a fraction of a pixel, because the nonlinearities create high frequencies that fold back onto the grid, an effect called aliasing. We argue that in replay detection this numerical defect becomes an attack. The attacker chooses, at no cost, the exact sample at which playback starts. Unsynchronized device clocks also stretch the replayed signal by a few parts per million. If the countermeasure's score moves with these sub-frame offsets, an attacker who is allowed several login attempts can keep replaying until one offset gets through. We propose to measure this "retry advantage" in existing detectors and to remove it with a detector made alias-free along the time axis only, leaving the frequency axis untouched so the replay cues are preserved.

Core Claim

Discretization-induced equivariance error in spectrogram countermeasures is a security problem, not only a matter of accuracy. Specifically, current replay countermeasures give different scores to the same replayed utterance when it is delayed by less than one frame hop or resampled at clock-drift scale. That spread can be exploited by retrying, and it is invisible to the standard equal error rate (EER, the operating point where false accepts equal false rejects). We can make the score provably consistent under time shifts while keeping the fine spectral detail that replay detection depends on. The way to do this is to apply anti-aliasing to the time axis and not to the frequency axis.

The frequency-axis exclusion is the part that is new relative to existing alias-free networks. Alias-Free Convnets replaces ReLU-type activations with low-degree polynomials and adds low-pass filtering, which yields certified fractional-shift consistency on ImageNet. It treats both image axes the same way, it costs about 5× in training and 6.5× in evaluation, and its low-pass filters would smooth exactly the fine spectral ripples that Jung et al. found essential: moving from 512 to 2048 FFT bins cut EER from 7.83% to 3.07%. Witkowski et al. likewise place the decisive cues in the 4–8 kHz and 6–8 kHz bands. A spectrogram has no rotational symmetry and its two axes mean different things. The physically meaningful transformations are a time translation along the frame axis and a tiny scaling of frequency caused by clock mismatch. The detector should therefore respect those two transformations and leave everything else alone.

Research Program

The first part is a measurement study. For a countermeasure with score $s(x)$ on waveform $x$, let $T_\tau$ delay the waveform by $\tau$ samples, where $0 \le \tau < h$ and $h$ is the frame hop. Let $R_\epsilon$ resample it by a factor $1+\epsilon$, with $|\epsilon|$ up to about 100 parts per million (ppm), which is our assumed range for consumer clock mismatch. We define the consistency gap and the best-of-K evasion rate as

$$\Delta(x) = \max_{\tau,\epsilon} s(R_\epsilon T_\tau x) - \min_{\tau,\epsilon} s(R_\epsilon T_\tau x), \qquad E_K = \Pr_{x \in \text{replay}}\Big[\max_{k \le K} s(R_{\epsilon_k} T_{\tau_k} x) > \theta\Big].$$

Here $\theta$ is the decision threshold fixed at the clean-data EER point, and $(\tau_k,\epsilon_k)$ are random offsets the attacker draws without seeing any scores. This matches a black-box attacker who simply retries. $E_1$ equals the usual false-accept rate. The study asks how quickly $E_K$ grows with $K$ for each architecture. Because we read the threshold from the score distribution, $E_K$ can also be expressed as an effective EER under retry attack.

The second part is the detector, which keeps a strong backbone of the kind used by Channel Consistency DenseNeXt on a high-resolution log spectrum. The analysis front end changes in two ways. The STFT hop is paired with a band-limiting window so that frame-rate sampling of each frequency bin's envelope satisfies the sampling condition used in Representation Equivalent Neural Operators. Every nonlinearity is then wrapped in the upsample–activate–sinc-downsample pattern from Convolutional Neural Operators, or replaced by a degree-2 polynomial as in AFC, with the filtering applied along the time axis only. Downsampling along time uses the same band-limited filters. The frequency axis stays at full FFT resolution with ordinary convolution and no blur. Pooling is a global average over time, which turns shift-equivariant features into a shift-invariant score.

Under circular boundary handling, the time-shift guarantee follows directly from the ReNO and AFC arguments, since the frame axis is a one-dimensional periodic grid. Real utterances have hard edges, so we measure the residual error from boundaries rather than claim it away. Applying the wrapper to one axis also lowers the overhead below AFC's 2D cost. We will report the actual multiple.

Resampling invariance is a separate case. A clock-drift stretch of $\epsilon$ moves a bin at frequency $f$ by $\epsilon f$, which is much less than one bin even at 8 kHz. We expect it to be covered approximately by the same smoothness and will test this empirically rather than certify it.

Baselines

The naive reference point is the official CQCC-GMM baseline. On the ASVspoof 2019 physical-access evaluation set it reaches 13.54% EER and 0.302 t-DCF, a combined cost of speaker verification plus countermeasure, as quoted by Xie et al.. We run it unchanged to see whether a frame-based statistical model already has a small consistency gap because it averages over frames.

The standard deep references are ResNet and LCNN. Xie et al. quote 1.97% and 2.03% EER for them. The same paper's deformable-convolution ResNet with time-frequency attention reaches 1.03% EER and 0.025 t-DCF. We include it specifically because its learned fractional offsets are evaluated with bilinear interpolation, the operation Weiler showed blurs high-frequency content. We predict it has the largest consistency gap.

The strongest single competitor is Channel Consistency DenseNeXt. It reports 0.46% EER and 0.0137 t-DCF as a single system on the 2019 physical-access evaluation set, and 0.282% EER with 0.00785 t-DCF when fused (Zhang et al.). The file does not list public code for it. We will therefore reimplement it, check that our version lands near the reported single-system number, and build our detector on that reimplementation so that the backbone, data, augmentation (including its 30-dimension spectral masking), number of epochs and hyperparameter search budget are identical. No reported result on Lacuna exists for the consistency gap or retry evasion rate of any replay countermeasure, so those columns will be our own measurements for every model.

Beating DenseNeXt means two things together. Clean EER must stay within the seed-to-seed noise of the reimplemented baseline. At a matched compute budget, $E_{K}$ for $K=10$ must be lower and the consistency gap must be smaller by a margin outside that noise.

Two ablations isolate the key ingredient. The first applies 2D AFC-style anti-aliasing to both axes. We expect it to remove the gap but hurt clean EER by blurring spectral ripples, which tests the frequency-axis argument. The second keeps the alias-free time wrappers but returns to plain ReLU, showing whether the activation treatment or the front-end hop/window change does the work.

Why not just…?

Why not just augment training with random sub-hop delays and resampling? This is the most likely threat, because it is cheap and attacks the exact transformations we care about. Vision evidence suggests it falls short. Alias-Free Convnets reports that a standard ConvNeXt trained with the usual augmentation dropped from 82.1% to 73.6% under a black-box translation attack while the AFC model held at 81.04%. Audio may behave differently, though. We will train DenseNeXt with dense offset and drift augmentation as an explicit baseline. If its $E_K$ curve matches ours, the honest conclusion is that augmentation is sufficient, and the paper becomes a measurement paper about the threat.

Why not just average the score over many offsets at test time? Test-time averaging over $M$ shifts shrinks the spread directly and needs no retraining. It is a real competitor, and it gives no guarantee: the attacker still picks among offsets of the averaged score, so the residual gap shrinks roughly like the spread over $M$ samples rather than vanishing. It also multiplies inference cost by $M$. We will compare at equal inference cost, setting $M$ so that averaged DenseNeXt matches our detector's measured overhead, and report $E_K$ for both.

Why not just use a one-sample hop or a raw-waveform model? A hop of one sample removes sub-hop offsets only at the first layer. Any later strided layer or pointwise nonlinearity reintroduces aliasing, which is the central point of ReNO and CNO. Finer grids also only approach equivariance asymptotically, at large cost, as Inal and Cesa found for fixed sampling grids. We will include a small-hop DenseNeXt variant to check this directly.

Why not just add BlurPool before downsampling? BlurPool leaves the aliasing that activations generate between downsampling steps, which AFC identifies as the dominant source. It is a cheap ablation, so we will report it.

Proposed Experiments and Decisive Checks

All models are trained on the ASVspoof 2019 physical-access training split, which has 5,400 bona fide and 54,000 replay samples (ASVspoof 2019 database). They are evaluated on its evaluation set with EER, t-DCF, the consistency gap, and $E_K$ for $K \in \{1, 3, 10, 30\}$. Because 2019 physical-access replays are acoustically simulated and contain no real clock mismatch, we also evaluate on real-device recordings from the ASVspoof 2017 challenge and ReMASC. On these sets we estimate the actual drift between playback and capture by cross-correlating against the bona fide source where it is available, which also tells us whether our ±100 ppm range is realistic. No reported numbers exist on Lacuna for ReMASC.

Three outcomes decide the project. First, if existing countermeasures show $E_{10}$ no larger than $E_1$, there is no retry threat and the proposal stops at a negative measurement result. Second, if the threat exists, our time-only alias-free detector must reduce $E_{10}$ to near $E_1$ while matching clean EER. In the same comparison, the 2D ablation must lose clean EER, otherwise the frequency-axis argument fails.

A secondary analysis tests a weaker hypothesis taken from the operator-learning literature: that grid-tied aliasing contributes to the gap between development and evaluation performance on unseen acoustic configurations. We will check whether per-model consistency gap predicts the size of that gap, but we do not stake the proposal on it.