Towards Field-Deployable Wearable IMU Systems for Occupational Activity Recognition

The core finding that aggregate statistics conceal large per-subject variance is well-supported and important for the HAR literature. The systematic sweep across sensor placements, window sizes, and classifiers under a single consistent protocol provides evidence-grounded guidance. The CTGAN analysis is a particular strength: the authors demonstrate via Kolmogorov-Smirnov testing that synthetic samples are not distributionally faithful and offer a clear mechanism---CTGAN treats each time-step as an independent tabular row, destroying autocorrelation.

The dataset is small ($n=13$, only 3 female) and entirely lab-collected, yet the paper's title and framing promise field-deployable systems without validating any claim outdoors or on a construction site. The CNN baseline is intentionally simple (a from-scratch 1-D CNN), so its poor performance ($55.7$% accuracy) is used to suggest prior ~99% deep-learning results are merely protocol artifacts; however, the authors never re-implement those prior architectures under LOSO, leaving a genuine architecture gap unaddressed. The citation of Leng et al. [12] to support the claim that 'GAN-based augmentation does not reliably outperform standard time-series transforms' appears imprecise: Leng et al. study cross-modality virtual IMU generation (video/text-to-IMU) and report that it significantly improves performance over classical augmentation, which is a different generative paradigm than CTGAN tabular augmentation. Finally, the personalised calibration result is only reported for the four weakest participants, without a corresponding full-cohort control.

The evidence strongly supports the central claim that subject-independent evaluation drastically lowers accuracy and reveals hidden variance. The comparisons to prior VTT-ConIoT studies are fair in noting that many use $k$-fold or subject-blind splits rather than LOSO. However, the within-paper comparison between classical classifiers and the deep-learning baseline is weaker: the authors chose a deliberately simple CNN to reflect 'out-of-the-box deployment,' but then use its failure to argue that classical models are 'more sample-efficient.' Without testing the actual architectures from prior work under the same LOSO protocol, this comparison is incomplete. The hyperparameter tuning check (at most $1.1$ pp delta) is a useful robustness control.

The authors commit to open science: code and aggregated results are available on GitHub. Most hyperparameters are fixed to scikit-learn defaults with only the random seed set, which improves reproducibility. The preprocessing pipeline is clearly described (147 statistical features, $z$-score standardisation per fold). However, the CTGAN subset selection (6 of 13 folds) and the nested search details (search space, budget) are underspecified. The personalised calibration relies on a 'temporal order' split to avoid window-overlap leakage, but the exact split implementation should be described more precisely. Independent reproduction is feasible for the main experiments, though the small dataset size means variance estimates will remain noisy.