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Paper summary
This paper presents a method for self-supervised representation learning of PPG signals. The method is based on forecasting. The main task is to predict up to four extractor-valid future beats from the prefix. The method is heavily designed for PPG signals and it is quite complex from preprocessing to pretext task. A one
Critical strengths
The experiments are relatively strong, the authors performed experiments in couple of downstream tasks, including heart rate, blood pressure and respiration. Appendix has also enough information for the reproducibility. Moreover, Appendix includes additional experiments and results including label efficiency of the methods.
Critical weaknesses
The paper is hard to follow and understand. The figure that explains the method is too crowded (Why Emojis? They are not making the figure). I spent a good amount of time to understand the SSL task but it was not clear at the end. The writing was dense in unnecessarily theoretic equations. The motivation for this complex SSL task is also not clear to me. There are no ablations showing the advantage of the task. One point I didn't understand why there is the derived streams. What motivated for deriving these?
For the derived streams, hidden standardized samples are first replaced by zero. Only then do we compute six views: normalized raw PPG, first and second finite differences, a 0.5–8 Hz zero-phase FFT band-pass signal, a Hilbert amplitude envelope, and a smoothed log bandpower envelope.
I also think that the method is not novel itself. Authors mixed so many components without a clear motivation but they are all inspired and derived from what is already out there including forecasting or feature extraction/estimation.
Overall, I believe the manuscript needs a major revision in both presentation, claims and evidence presented.
Questions for authors
1-What was the main motivation for the derived streams and specific features? Any ablations regarding that?
2-Why not WildPPG or Dalia for HR estimation? BIDMC is much easier compared to those datasets.
3 comments
I thank the authors for their respond. I read their responses. I still have these questions.
1-The evidence does not support that "six derived views are complementary" though. They are extremely redundant. You can obtain every view from the raw signal. Giving first and second differences as input is similar to feeding an image to edge detector and then feeding that view to SSL pipeline additionally. Also, the contribution of these views is not clear.
2-I would like to thank the authors to run this experiment but I would expect to see the comparison with other SSL methods as well since these numbers are close to random-init models already.
3-One additional point from other reviewer is that the authors claimed "the full tokenizer-plus-backbone pipeline is not fully patient-independent". Does that mean tokenizer weights get updated with backprop with test patients as well? Is it the case for Dalia and WildPPG?
We thank the reviewer for the constructive follow-up.
R1. Are the six derived views redundant? We agree that all six views are deterministic transformations of raw PPG and cannot introduce additional information. The edge-detector analogy is appropriate; our earlier phrase “complementary information” was imprecise. Their proposed role is to provide inductive biases under finite model capacity and training budgets, not new physiological information.
Our token- and parameter-matched raw-view control provides an aggregate comparison. Full versus raw-view achieves future-state Skill 0.3926 vs. 0.3911 (seed 0), PPG-BP SBP MAE 14.913 vs. 15.025, WESAD stress AUROC 0.953 vs. 0.948, and Stanford quality macro-AUROC 0.934 vs. 0.927. Conversely, raw-view performs better on DaLiA activity macro-F1 (0.313 vs. 0.290). These modest, task-dependent differences do not establish that all views are necessary. Five leave-one-view-out experiments remain incomplete; we claim no individual-view contribution.
Importantly, the information-boundary construction does not depend on the views providing additional information: the hidden suffix is replaced before nonlocal views are computed, preventing withheld stored samples from influencing visible derived inputs.
R2. Comparison with other SSL methods on motion HR. We agree that comparison against random initialization alone is insufficient. We completed PaPaGei-S and SIGMA-PPG fine-tuning on WildPPG HR, using 16-fold LOSO, identical 32,000 wrist windows, ECG-derived HR references, matched train/validation/test subject lists, and subject-macro MAE.
WildPPG HR (MAE ± between-subject SD, bpm; lower is better):
| Model | MAE ± SD |
|---|---|
| PulseBound FT | 9.05 ± 4.57 |
| PaPaGei-S FT | 9.59 ± 4.15 |
| SIGMA-PPG FT | 10.07 ± 5.31 |
| Random-init FT | 10.18 ± 4.93 |
| PulseBound frozen LP | 10.39 ± 4.74 |
PulseBound FT achieves 0.53 bpm lower MAE than PaPaGei-S and 1.02 bpm lower MAE than SIGMA-PPG, outperforming each on 12/16 held-out subjects. Both baselines outperform PulseBound on subjects qm9 and tz8.
This is a system-level comparison, not an objective- or compute-matched experiment: the models use different released frontends and parameter counts (5.8M/28.1M/97.6M). Results use one pretrained checkpoint and downstream seed 42; between-subject SD is not a confidence interval.
WildPPG remains challenging (PulseBound FT R² = −0.345), with median selected epoch 2 during a 10-epoch warmup. Learning-rate sensitivity remains untested.
On DaLiA, PulseBound FT achieves 5.10 ± 2.50 bpm, compared with 6.58 ± 3.63 for random-init FT and 9.37 ± 3.20 for frozen LP (15-fold LOSO). The other SSL baselines have not yet completed DaLiA evaluation.
R3. Did the tokenizer learn from test patients? Thank you for raising this question. We re-audited the implementation and clarify the distinction between MIMIC pretraining and external downstream evaluation.
For DaLiA and WildPPG, unequivocally no. Neither dataset was used to train the Event-VQ tokenizer or PulseBound backbone. Event-VQ is strictly frozen during backbone pretraining (no gradients, evaluation mode, EMA updates disabled) and is not instantiated during downstream training or inference (build_tokenizer=False; tokenizer.* weights excluded). Furthermore, each LOSO test subject is excluded from training, validation, and checkpoint selection. Our audit confirms zero subject-isolation violations across 93 folds.
For MIMIC, the distinction concerns the initial tokenizer-training split. Event-VQ uses a random 80/20 file-level split, independently of the backbone's subsequent 90/5/5 patient-group split. This does not establish tokenizer-level patient independence, although no tokenizer updates occur during backbone training or downstream evaluation. We will clarify this protocol and restrict the group-disjoint claim to backbone pretraining.
Thus, no DaLiA/WildPPG test subject contributes to tokenizer optimization, backbone pretraining, or downstream model selection, and the MIMIC-specific splitting limitation does not compromise our external motion-HR evaluation.
R4. Revision and contribution. We will correct the tokenizer provenance description once the executed training configuration is verified, and revise Figure 1 and the contribution statements to emphasize the formalized and empirically audited stored-window information boundary, rather than claiming independent novelty or necessity for individual derived views.
We thank the reviewer for the direct critique. We agree that the central contribution should be separated from supporting architectural choices, and we have now completed the requested motion-HR evaluation.
R1. Central contribution. We do not claim forecasting, signal transformations, or auxiliary physiological supervision is individually novel. Our contribution is the explicit construction and formalization of an information-access boundary for predictive PPG representation learning. Causal attention alone does not guarantee one-sided access when full-window normalization, nonlocal transforms, or companion views can transmit withheld samples into visible inputs. PulseBound enforces the boundary during input construction via content-independent cutoff sampling, prefix-only normalization, suffix replacement before derived-view construction, and aligned masking. Proposition 1 formalizes stored-suffix invariance, while the intervention/gradient audit tests the implementation at this interface. Future-beat supervision provides an interpretable task within this boundary. We will revise the introduction and contribution bullets to center this testable contract rather than claim novelty for individual components.
R2. Why six derived views? They provide complementary descriptions: normalized raw PPG (waveform), first/second differences (slope/curvature), 0.5–8 Hz band-pass (pulse-related frequency content), Hilbert amplitude envelope (local amplitude), and smoothed log band-power envelope (spectral variation). They are structured input views, not independently validated biomarkers. Crucially, the suffix is replaced before constructing nonlocal views; otherwise withheld samples could affect visible features.
We agree the current evidence does not establish an independent gain from every view. The token-matched raw-view control gives seed-0 future-state Skill 0.3911 vs. 0.3926 for the full model. Downstream effects are mixed: the full model is stronger on BIDMC HR, PPG-BP SBP, WESAD stress, and Stanford quality, while the raw-view control is higher on DaLiA activity macro-F1. This is an aggregate control, not leave-one-view-out evidence. Five per-view drop runs (d1, d2, band-pass, envelope, spectrum) across three pretraining seeds are in progress; we will make no per-view contribution claim before completion.
R3. Motion-HR evaluation. The reviewer is right that BIDMC is easier and that DaLiA activity classification is not HR evidence. We therefore evaluated HR regression on PPG-DaLiA and WildPPG, neither used in pretraining. Both use strict leave-one-subject-out evaluation (15 folds/DaLiA, 16/WildPPG), with subject-macro MAE in bpm as the primary metric. HR references are independent ECG (DaLiA chest ECG; WildPPG Lead-I), never input PPG. All windows, including activity transitions, are retained.
All 6/6 runs completed with no partial runs, and every fold was evaluated on its held-out test subject:
Under identical subject splits, FT beats random-init on 15/15 DaLiA and 16/16 WildPPG subjects (31/31 total), with mean MAE reductions of 1.481 bpm (22.5%) and 1.124 bpm (11.0%), respectively. FT also beats LP on 15/15 DaLiA and 14/16 WildPPG subjects. Thus, under strict subject-disjoint evaluation, pretrained fine-tuning consistently improves over training the same architecture from scratch on both a controlled motion dataset and a more in-the-wild wrist dataset. LP being worse than random-init further shows that the benefit is not obtained simply by freezing the pretrained representation.
We note one protocol limitation: WildPPG selects best checkpoints unusually early (13/16 folds at epochs ≤3, with a 10-epoch warmup), so its absolute 9.052-bpm result should be interpreted cautiously. We therefore do not use it to claim an upper bound on generalization and will add a learning-rate sensitivity check. The paired FT-vs-random-init comparison nevertheless uses identical LOSO splits and training protocol.
R4. Readability and Figure 1. We agree Figure 1 is too dense and the motivation arrives too late. We will restructure it into: (i) stored-window boundary construction, (ii) representation learning/future-beat prediction, and (iii) training-only auxiliary supervision followed by PPG-only downstream inference. The six views will be defined before tokenization, implementation details moved to the appendix where possible, and main-text notation reduced.
Overall, the new HR evaluation directly addresses the reviewer’s concern: subject-disjoint motion-HR generalization is measurable beyond BIDMC, and pretrained fine-tuning consistently improves over random initialization across all 31 held-out subjects.