Does per-user normalization inflate wrist EDA affect recognition gains?

The question is where normalization statistics come from

Wrist electrodermal activity (EDA), the skin-conductance signal used to infer sympathetic arousal, varies in amplitude from person to person. Affect-recognition models therefore rescale the signal before classification. The paper asks a narrow but consequential question: when a model is tested on a subject it never saw, whose data produced that rescaling?

Two procedures are possible with the same sensor and the same trained classifier. A device worn for the first time must normalize using statistics learned from other people, which the paper calls global-train normalization. A retrospective benchmark can instead compute statistics from the new user's complete recording, which the paper calls per-user calibration or per-subject-z normalization. Only the first describes first-use performance; the second evaluates a model that has already seen the scale of the person it classifies. Neither is wrong, but a reader who cannot tell which was used cannot compare scores.

SAFE-EDA pretraining uses expert artifact labels

The model under test is SAFE-EDA, a compact convolutional network pretrained on expert artifact annotations from 43 subjects in the EDABE v2 release. Artifact annotations mark signal segments that reflect sensor or motion problems rather than physiology, so pretraining on them gives the network supervised exposure to what clean and corrupted wrist EDA look like before it ever sees affect labels.

The comparison arm is the identical network trained from scratch. Both arms were evaluated on WESAD (15 subjects) with leave-one-subject-out cross-validation, crossing two normalization sources with four window hops of 1, 4, 60, and 240 samples. A hop is the step between successive analysis windows, so a larger hop means fewer, less overlapping training windows per fold: 113,778 at hop 1 down to 479 at hop 240. Seeds were averaged within each subject and contrasts were subject-paired, so the unit of inference is the participant rather than the window.

Per-user statistics shrink the gain and remove significance

Under global-train normalization, pretraining beat scratch at every hop, by 0.0779, 0.1098, 0.2268, and 0.2145 macro-F1 at hops of 1, 4, 60, and 240 samples, and all four gains survived Holm correction. Under per-subject-z normalization the gains were 0.0202, 0.0343, 0.0495, and 0.0426, and none was significant. The interaction was largest at hop 60, where the global-train gain exceeded the per-subject-z gain by 0.1773 (95% CI 0.1191 to 0.2311, p = 0.000427).

The paper also shows where the larger global-train gains come from. Going from hop 1 to hop 60, scratch macro-F1 fell by 0.1350 while the transfer arm moved by only 0.0139. Sparse windowing mainly hurts the network that must infer its input scale from other subjects, and pretraining prevents that loss. Under per-subject-z the same hop change moved scratch from 0.6762 to 0.6576 and transfer from 0.6964 to 0.7071. Dense windowing raises the scratch baseline, so the measured value of pretraining depends on the hop as well as on the normalization source.

Artifact supervision outperforms self-supervised pretraining

The gain is not merely an effect of pretraining on more EDA. On the same recordings, pretraining with expert artifact labels gained 0.078 over scratch, whereas self-supervised pretraining gained 0.008. The paper reports a shuffled-label control, which indicates that supervised pretraining as such contributes alongside the content of the labels, so the artifact information is not the whole story but the label content clearly matters.

Normalization source alone also moved scores substantially. Under leave-one-subject-out, replacing training-subject statistics with the held-out subject's statistics raised scratch macro-F1 from 0.5015 to 0.6762 and transfer macro-F1 from 0.5794 to 0.6964. With per-user normalization at hop 1, the transfer arm reached 0.7815 accuracy (95% CI 0.7040 to 0.8485) and 0.6964 macro-F1 from wrist EDA alone. The original WESAD report's 0.8034 accuracy used multimodal chest sensing and falls inside that interval, but the protocols are not fully aligned, so the paper treats this as a statement about what one wrist sensor can reach rather than a ranking of the two studies.

The evaluation split matters as much as the normalization

Before the grid, the authors checked how the split alone changes a single model's score. With random assignment of windows, the transfer arm reached 0.9966 macro-F1, against 0.5794 under leave-one-subject-out. The 0.4172 difference arises because random assignment evaluates recordings already represented in training, and the paper uses it only as a reference for how much leakage can inflate a score. A single fixed subject holdout with three seeds reversed the order of the arms (transfer 0.4787, scratch 0.5258), showing how unstable one partition can be. All remaining inference is therefore based on leave-one-subject-out.

Aggregate gains also hide class-level shifts. Under global-train normalization, transfer changed WESAD amusement accuracy by −5.94 percentage points while baseline rose 11.96 and stress rose 9.80; under per-subject-z the largest net change was amusement at +4.57 points. A positive overall gain can coexist with a loss in one class, and the distribution shifts with the normalization. Probability calibration moved differently from discrimination: subject-level expected calibration error changed little under per-subject-z (0.2116 to 0.2031, p = 0.48871) but fell under differencing (0.2583 to 0.2263, p = 0.00537), so macro-F1 gains should not be read as calibration gains.

A second dataset reverses the direction of the interaction

Across 13 configurations in two datasets, the pretrained network was better in 12. But on the second dataset, the PhysioNet Wearable cohort of 26 subjects, per-user normalization increased the gain instead of reducing it. The paper's normalization ladder there spans five transforms at hop 60, and the direction of the interaction therefore depends on the data.

The authors state that differences in tasks, amplitude distributions, and preprocessing may explain the reversal, but the one-dimensional Wearable scans cannot separate these factors, and two identifiers missing from the processed copy reduced power. The honest reading is that the WESAD result is a demonstration of a mechanism, not a universal law: per-user statistics can absorb the difficulty that pretraining would otherwise solve, but whether they do so is dataset-dependent.

Few WESAD studies state their normalization source

The paper coded the Methods sections of 50 published WESAD studies. A split type could be identified in 28 (56%, 95% Wilson CI 42–69%), 13 of which used leave-one-subject-out; 26 stated the window length (52%, 39–65%); 15 gave the hop (30%, 19–44%); six stated overlap explicitly (12%, 6–24%); and 11 specified metric aggregation. Only five identified the data used to compute normalization statistics (10%, 4–21%), and four of those five used the evaluated user's own window or baseline.

The counts record whether a field is described, not whether the pipeline was sound, and the survey is a fixed, non-exhaustive sample coded by a single author. Still, the gap between window length and normalization source is not a difference in reporting habits. Window length determines how much signal enters one example; normalization source determines whose observations shape the numerical representation of that example. A study can report the first carefully and leave the second open.

Report the normalization source before comparing scores

The paper's practical priority follows directly from the interaction: a reported score should state the split, window length, hop, normalization formula, source of the normalization statistics, and when the user's data become available. An evaluation of first-use monitoring should use only information available at prediction time; complete-record calibration answers a different question. The 0.1773 interaction at hop 60 is the clearest threshold in the paper: under global-train statistics pretraining is worth roughly 0.23 macro-F1, and under per-user statistics it is worth about 0.05 and not distinguishable from zero.

Several boundaries qualify that number. Both downstream datasets record laboratory-evoked affect, and the 0.7815 wrist-only accuracy was obtained under per-user normalization, so neither establishes daily-life or clinical performance. The fixed 12-epoch budget left losses at sparse hops unconverged, so part of the measured gain reflects faster optimization rather than a better final solution. The effect is established for one backbone only, the decomposition branch was mostly inactive, and the classical baselines and permutation control ran only at global-train, hop 1. The paper makes no claim of superiority over other compact models.

The judgment worth carrying away is therefore conditional rather than general: if a benchmark uses the evaluated user's own recording to set the input scale, its pretraining gain measures performance after calibration, and the first-use benefit that SAFE-EDA demonstrates on WESAD may be several times smaller than the reported number suggests. Whether per-user statistics help or hurt the measured gain depends on the dataset, so the normalization source belongs next to the score, not in an appendix.

Sources used in this answer