Downsample to the Precision of Expert Agreement

Models that label events in long physiological recordings, such as sleep arousals in overnight polysomnography or epileptic discharges in intracranial EEG, must first shrink millions of raw samples into a sequence short enough to process. The usual tool is a strided convolution, a filter that slides across the signal and keeps only every $K$-th output. Practitioners choose $K$ by compute budget or by trial and error. Separately, the labels these models learn from are drawn by human experts who disagree about where events start and end. This note proposes that these two facts are one problem. How precisely experts agree on event boundaries sets the finest temporal resolution the labels can actually support. A model that downsamples to that resolution, and no further, should lose essentially no accuracy while saving large amounts of compute.

The proposal has three parts. It gives a simple rule that predicts the largest safe downsampling factor from measured inter-rater boundary disagreement. It trains against boundary targets that encode that disagreement instead of a single rater's mark. And it restores the long-range context lost to striding with a stack of dilated convolutions (filters with gaps between their taps, which see far without shrinking the sequence) running on the compressed sequence. The test of success is concrete: the model's boundary errors should fall inside the envelope of human-to-human disagreement at a stride chosen without any search.

Core Claim

Suppose expert onset marks scatter around a latent true onset with standard deviation $\sigma$ seconds. A detector that runs at sampling rate $f_s$ after stride $K$ can only place boundaries on a grid of spacing $K/f_s$. Uniform quantization on that grid adds variance $K^2/(12 f_s^2)$. The expected squared boundary error measured against a fresh rater is therefore approximately

$$ E^2(K) \approx \sigma^2 + \epsilon_{\text{model}}^2 + \frac{K^2}{12 f_s^2}, $$

where $\epsilon_{\text{model}}$ is the model's own estimation error. The rater term cannot be reduced. So the stride term is negligible whenever $K/f_s$ is on the order of $\sigma$ or smaller. This yields two predictions.

The first prediction is that accuracy as a function of stride is flat up to a knee near $K^\star \approx \sigma f_s$ and degrades beyond it.

The second prediction is that training on hard single-rater boundaries wastes the resolution below $K^\star$ on fitting rater noise. Training on targets smoothed by the measured disagreement distribution should let the model reach the same error with a coarser stride.

The claim is useful for two reasons. It turns an arbitrary hyperparameter into a quantity measurable from labels alone. And the savings are large, because attention cost downstream falls as $K^{-2}$.

This builds directly on gaps the literature leaves open. Miller et al. used a kernel-63, stride-32 front-end to fit 7-million-point sleep recordings on one GPU, and they note that arousal scoring is subjective. They nonetheless trained with plain weighted cross-entropy, and they chose the stride for memory reasons. Gimeno et al. and Heo et al. argue that reduced temporal resolution acts as useful smoothing, but they give no rule for how much smoothing is justified. Our rule supplies that justification, taken from the labels themselves.

There is one caveat. The rule says nothing about events shorter than the stride. A high-frequency oscillation lasts a few milliseconds, even if experts disagree about its boundaries by tens of milliseconds. We therefore require the front-end kernel to be at least as long as the stride, as in Miller's 63-over-32 design. With that condition, brief events are summarized into a token's channels instead of falling between taps, and only their position is quantized. Whether detection information actually survives this compression is an explicit test below.

Research Program

The first step is to measure $\sigma$. On data with multiple raters per recording, we match each rater's events to the other raters' events and compute the spread of onset and offset differences. We compute this per event class, because arousals and discharges plausibly differ.

The second step is to build a model with a single strided front-end whose stride is set to $K^\star$. On top of it sits a context stack of dilated one-dimensional convolutions. Following the augmented pyramid design of Chen et al., the dilation rates are non-monotonic so that no input positions are systematically skipped. Following the parallel dilated branches of IVD-Net (Dolz et al.), the branches are fused through a bottleneck projection that controls channel growth. The stack's receptive field is sized to the clinically relevant context: tens of seconds for arousals, and seconds to a minute of background for discharges. Earlier work used dilated context to avoid downsampling. We instead apply it after principled downsampling. This keeps dilation rates modest, because each tap already covers $K$ samples, and that eases the grid-gap problem.

The third step is the training target. For each rater's event, we place a soft onset and offset profile whose width is the measured $\sigma$, and we average across raters. The loss is a boundary-distribution loss on these profiles plus a frame-level presence loss. For raters' continuous traces, we adapt the Beta-distribution belief-mismatch idea of Wu et al., who showed that modeling rater spread made emotion predictions far more robust to acoustic noise. Here, the spread being modeled is temporal instead of in value.

We deliberately avoid latent-annotator generative models such as the Latent Doctor Model and diffusion denoising such as DiN. These methods capture per-rater style on static images. Their sampling cost at inference, which the file notes as a limitation, is exactly what long-recording monitoring cannot afford. Our method adds nothing at inference.

Baselines

The naive reference point is the same architecture trained on a single reference label with a stride chosen for memory. This is essentially the Miller et al. configuration, which reports test AUROC 0.855 and test AUPRC 0.369 on the 2018 PhysioNet Computing in Cardiology sleep-arousal challenge. We re-run it on identical splits with its published front-end, so that differences reflect only our changes. For this dataset, beating it means matching or exceeding AUPRC 0.369 at a larger stride, or exceeding it at equal stride.

The strongest existing method on intracranial EEG is the benchmark's own pipeline. On the multi-center Omni-iEEG benchmark, Duan et al. report event-classification F1 0.8061 and AUC 0.9390 for PyHFO-Omni. The benchmark also provides a TimeConv-CNN baseline for localizing the seizure-onset zone. We use their released splits. We give both their model and ours the same tuning budget, measured in GPU-hours and in number of hyperparameter trials. Beating it means higher F1 at equal compute, or equal F1 at substantially lower compute.

The key ablations isolate each ingredient in turn. The first replaces the rater-derived soft targets with hard majority-vote boundaries at the same stride. The second keeps the soft targets but replaces the dilated context stack with a plain pooling encoder of equal parameter count. The third sweeps the stride over a grid that runs from 4× below the predicted $K^\star$ to 4× above it, with everything else fixed. If the method works, the third ablation should reproduce the predicted knee.

Why not just…?

Why not just grid-search the stride? A search will find a good stride, and on a single dataset it is a genuine competitor for final accuracy. The contribution here is predictive: the rule should locate the knee before any training, using labels alone. The stride sweep decides this directly. If the knee from the search does not land within a factor of two of $\sigma f_s$ across event types and datasets, the rule is wrong and should be abandoned. In that case only the soft-target component would stand as a result.

Why not just blur the labels with a Gaussian? Temporal label smoothing is the closest simpler method. Our soft targets are a special case of it, with the width fixed by measured disagreement instead of tuned. We compare against smoothing with a tuned width. If a tuned width gives equal results, the finding reduces to "the measured rater spread is a good default width." That is still useful, but it is a smaller claim, and we would report it that way.

Why not just rely on a U-Net's skip connections to restore resolution? Skip connections carry fine-resolution features back to the output, but they do not make labels more precise than raters are. Miller's U-Net still reached only AUPRC 0.369 and overfit early under batch size 1. For image segmentation, Dolz et al. report that dilated multi-path modules raised Dice from 0.8981 to 0.9191 over an early-fusion baseline. However, that comparison mixes fusion strategy with the context module, so it is suggestive only. Our second ablation tests the point directly on time series.

Why not just take the majority vote? On static images, the file reports that distribution-aware training beats majority vote (Latent Doctor Model, KL divergence 0.461 on Gleason2019). On noisy audio, a point-mean model lost 0.257 in concordance correlation against 0.124 for the distribution model (Wu et al.). Whether this carries over to boundaries in time is exactly what the first ablation measures.

Proposed Experiments

The first experiment is a controlled study on the PhysioNet 2018 challenge. That dataset has only one reference scoring, so we synthesize a panel of five raters by jittering each onset and offset with known $\sigma$ values from 1 to 8 seconds. We train at strides from 8 to 1024, with 200 Hz input. Because the true noise level is known, this is a clean test of whether the error knee tracks $\sigma f_s$. We also measure whether soft targets shift the knee to coarser strides. Metrics are AUPRC, AUROC, and onset error scored against held-out synthetic raters.

The second experiment uses real disagreement on Omni-iEEG, whose four epileptologists annotated more than 36,000 candidate events with Fleiss' kappa 0.92. The file does not say whether per-rater time stamps are released. If only candidate-level votes exist, we use the vote fraction as a soft presence target and drop the boundary analysis on this dataset. Here we stratify recall by event duration. This is the decisive check that high-frequency oscillations shorter than the stride survive when the kernel is at least as long as the stride. If short-event recall collapses at $K^\star$ while long-event recall holds, the "position only" caveat fails, and the method needs a dense short-scale branch.

The third experiment uses RECOLA's six continuous raters as a secondary test in the regression setting. Here $\sigma$ is the inter-rater time lag, and the metric is concordance correlation. The file reports only concordance drops for Wu et al., with no absolute values, so no reported absolute concordance result was found on Lacuna for RECOLA under this protocol. We therefore re-run their belief-mismatch model as the reference.

Across all three datasets, the headline evaluation is human-referenced. We compute the model's boundary error against each rater using leave-one-rater-out, and compare it with each rater's error against the remaining raters. We also report compute saved at $K^\star$ relative to the naive stride. The proposal succeeds if two things hold. The model should fall inside the rater-to-rater envelope at the predicted stride. And the predicted knee should match the empirical knee across synthetic jitter levels.