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Under review as a conference paper at ICLR 2027

PulseBound: Future-Beat State Forecasting Under an Explicit Information Boundary

Abstract

Predictive representation learning from photoplethysmography (PPG) has a subtle failure mode: causal attention does not guarantee one-sided information access when normalization, nonlocal transforms, or companion views can depend on withheld samples. We introduce PulseBound, a PPG representation learner that couples physiologically structured future-beat prediction with an explicit stored-window information boundary. A content-independent cutoff separates a visible prefix from the prediction target; prefix-only normalization, suffix replacement before derived-view construction, and aligned masking make every encoder input a function of the visible prefix and cutoff alone. This yields stored-suffix invariance: for fixed model state, randomness, prefix, and cutoff, changing the stored suffix cannot change the forecast context. Within this contract, a shared horizon-conditioned head predicts nine deterministic rhythm and morphology descriptors for up to four extractor-valid future beats, with elementwise validity masks and optional ECG-derived pulse-arrival-time supervision confined to training.On groups held out from PulseBound backbone pretraining within MIMIC and VitalDB, PulseBound reduces nine-state transformed-space MAE relative to last-visible-beat persistence by 28.06% and 22.22%, respectively, and improves MAE, MAE-Skill, and Spearman correlation in all 40 source–cutoff–horizon cells. In a separate seven-model comparison across 13 downstream tasks, PulseBound attains the best mean on nine frozen linear-probe tasks and seven full-fine-tuning tasks. Stored-suffix interventions produce zero recorded change in forecast contexts or predictions, with zero suffix-input gradient at audited precision under the declared stored-window interface. Together, these results frame predictive physiological representation learning around three separately testable choices: what information is accessible, what future structure is supervised, and how the learned representation transfers.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Photoplethysmography, Self-supervised Learning, Representation Learning, Physiological Time Series, Future-Beat Forecasting, PPG Foundation Model

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Reviewer_Ly82OpenReview ↗
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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

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:

  • DaLiA: FT 5.100 ± 2.501 bpm, LP 9.371 ± 3.199, random-init 6.581 ± 3.628.
  • WildPPG: FT 9.052 ± 4.572 bpm, LP 10.394 ± 4.745, random-init 10.176 ± 4.925.

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.

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):

ModelMAE ± SD
PulseBound FT9.05 ± 4.57
PaPaGei-S FT9.59 ± 4.15
SIGMA-PPG FT10.07 ± 5.31
Random-init FT10.18 ± 4.93
PulseBound frozen LP10.39 ± 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.

Reviewer_Q87vOpenReview ↗
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Paper summary

This work introduces PulseBound, a self-supervised learning architecture for photoplethysmography (PPG) representations. It combines the ability to forecast future beat states with a well-defined information access boundary. The authors have identified a potential limitation in causal attention and traditional masking techniques, namely that future information could potentially flow back to affect the input to the model via normalization or other non-local transformations of the data. In order to mitigate this issue, PulseBound utilizes several techniques: content-independent cutoff sampling; prefix-only normalization; suffix replacement prior to constructing derived views from the original signal; and aligned masking. Additionally, the authors define a stored-suffix invariance property, and demonstrate that it is met through intervention and gradient analyses.

In this context, the model uses a horizon-conditioned predictor to forecast nine PPG-derived physiological descriptors for up to four subsequent extractor-valid beats, with optional ECG-derived pulse arrival time as a form of training-only supervision. The model is trained using data from both MIMIC-III and VitalDB, and its ability to forecast future-beat states and transfer learned representations to different downstream tasks is evaluated separately. When comparing the results of the experiments conducted with PulseBound to those using a "last visible beat" persistence baseline (where the last beat observed in the visible prefix is used as the reference for predicting future beats), there were substantial reductions in transformed-space prediction MAE. Specifically, the reduction in MAE for MIMIC was 28.06%, while the reduction in MAE for VitalDB was 22.22%. Additionally, when compared against six other models across 13 downstream tasks, PulseBound achieved the best mean performance on nine of the 13 linear-probe tasks (where the weights learned by PulseBound are held constant) and on seven of the 13 full-fine-tuning tasks (where all weights in PulseBound are allowed to vary).

Critical strengths

The authors address a significant methodological concern regarding the use of temporal attention as the sole means for preventing future observations from influencing forecasts. They provide a precise formulation of the problem, along with a systematic construction of methods (cutoff sampling, normalization, derived-view generation, and masking). Proposition 1 provides a clear characterization of stored-suffix invariance, and the authors also evaluate whether their implementation adheres to the properties they claim. This combination of formal specification and evaluation of implementations represents a significant contribution to the methodological rigor of physiological representation learning.

The authors perform experiments under many different forecasting conditions and use 13 downstream tasks such as regression, classification, activity recognition, and signal quality evaluation. They compare their model to existing PPG foundation models using three different pretraining seeds for the primary results. Additionally, they complete several component analysis evaluations. The forecasting results show that their approach is consistently better than using persistence to predict future states across the evaluated cutoff and horizon configurations. Also, their linear-probe and fine-tuning results indicate that the representations learned during pretraining can be transferred to many other physiological tasks. This provides empirical support for the authors' approach.

Critical weaknesses

The information-boundary guarantee does not apply to the raw physiological signal, which limits its implications for predicting future events.

The main contribution in terms of method is that it controls what can be used by the forecasting model as far as information is concerned; however, the control over the information that can be used begins with the preprocessed, stored PPG window instead of the original signal. As stated in Appendix E.2, the VitalDB preprocessing pipeline has forward–backward filtering and full-window min–max normalization, so the stored prefix before PulseBound sets its information limit could include some information from the future part of the original waveform.

The authors recognize this restriction and distinguish stored-window invariance from end-to-end streaming causality; however, the distinction is significant as the proposed framework was developed based on the objective of predicting future physiological states. Stored-suffix intervention experiments are conducted by modifying the stored suffix without altering the stored prefix; therefore, it cannot be determined if the original future waveform had an effect on the prefix. Additional experiments with boundary-preserving upstream preprocessing would be required to ascertain whether the reported forecasting improvements continue to exist under genuinely prospective information access.

Future-beat supervision's role and physiological relevance have not been fully demonstrated.

While PulseBound produces positive results for forecasting, its main forecasting baselines are the median value of the training dataset and the persistence of the last observable beat. Both of these methods provide useful comparisons. However, these comparisons do not establish an advantage over learning-based causal forecasting models trained on the same physiological descriptors. Additionally, although the no-state and shuffled-target controls offer further insight, the no-state forecasting comparison uses a different fitting method for prediction. Also, there is a mix of positive and negative effects on downstream task performance when explicit state supervision is applied. Therefore, it is still uncertain whether or not future-beat supervision independently contributes to the transferability of the learned representations.

The forecast targets are automatically extracted from physiological data rather than independently verified. The target-quality assessments in Appendix F.4 report cross-signal peak-matching sensitivities relative to automatically detected ECG peaks of 55.52% on MIMIC and 50.71% on VitalDB. Even though there were high rates of available target data reported, these results raise concerns regarding the consistency of beat extraction and the physiological interpretation of the targets, although the sensitivities do not directly measure the accuracy of every descriptor. If we could obtain independent verification of the forecast target data, we would have much more confidence that the improvements in forecasting performance reflect meaningful physiological dynamics.

The evaluation protocol itself also warrants consideration, since the frozen Event-VQ tokenizer was trained on the entire processed MIMIC corpus prior to the split of patients into groups. Although the authors state this fact and appropriately limit their group-disjoint claims to backbone pretraining, it does limit how we can interpret the performance of MIMIC forecasting as an evaluation of a completely independent pretraining pipeline.

Questions for authors

Can the authors assess the effectiveness of the suggested framework by using a boundary-preserving preprocessing technique with the raw PPG data? It would also be interesting to see if the stored prefix representation and forecasting performance would be different if the upstream filtering/normalization were only performed on observations made prior to the cutoff. By doing so, we will better understand how the suggested information boundary applies in practical forecasting settings.

The authors have the opportunity to evaluate PulseBound against separately trained causal forecasting models (e.g., an autoregressive or Transformer-based predictor) on the same prefix inputs, target states for prediction, and evaluation support. Furthermore, comparing the full model to the no-state variant for all of the downstream tasks would allow the authors to determine if providing explicit future-beat supervision generally yields better transferred representations.

Can the authors assess how accurately the extracted future-beat descriptors agree with a manually verified beat annotation set or a clinically validated signal-processing reference? The relatively low cross-signal peak-matching sensitivity values shown in Appendix F.4 make evaluating the performance of the descriptors across various signal-quality levels and irregular rhythm types especially valuable.

How could the forecasting results be affected by training the frozen Event-VQ tokenizer using only the MIMIC training-group data? Since the Event-VQ tokenizer being used has had prior exposure to held-out recordings as well as the training data before splitting the patient groups, comparing the performance of the model using a tokenizer trained only on the training-group data would allow us to assess how much effect its exposure to the held-out recordings has had upon the reported forecasting results.

1 comment

We thank the reviewer for the precise technical reading. We agree that several claims should be narrowed.

R1. Scope of the information-boundary guarantee. Proposition 1 establishes stored-window suffix invariance, not end-to-end raw-signal causality: with parameters, persistent state, randomness, prefix, and cutoff fixed, changing the stored suffix cannot change encoder inputs, forecast context, or predictions. For VitalDB, forward-backward filtering and window-level min-max normalization are offline and may allow future raw samples to influence the stored prefix. We will therefore consistently use “stored-window information boundary”.

We directly audit the declared interface: 10,000 windows/source × 3 checkpoint seeds × 5 cutoffs × 5 suffix interventions. All 750 invariance-summary rows and 30 gradient-summary rows pass. Maximum deviation in visible states, typed registers, forecast contexts, and predictions is 0; maximum suffix-input gradient is 0, while minimum prefix-gradient L2 norm is 34.9533. This supports the stored-window contract, but does not audit raw-to-HDF5 preprocessing or constitute a full-Jacobian proof. A raw-prefix-preserving replay with a leaky positive control is the appropriate next test; we will not call it complete without audited results.

R2. Forecasting baselines and state supervision. On identical paired support, across 9 PPG states × 5 cutoffs × 4 horizons, PulseBound reduces transformed-space MAE versus last-visible-beat persistence by 28.06% on MIMIC and 22.22% on VitalDB. MAE, MAE-Skill, and Spearman favor PulseBound in all 40 source–cutoff–horizon cells; these are related evaluation conditions, not independent replications.

No-state probes achieve 0.2844 Skill (Ridge) and 0.3488 (MLP), while the shuffled-target predictor gives 0.0038. These are post-hoc probes, not causal forecasters, and use different support from the main comparison; we therefore do not rank them against it. Removing PAT supervision gives 0.3940 vs. 0.3926 for the full model at seed 0, so we do not claim a positive aggregate PAT benefit. A same-support GRU/TCN/causal-Transformer comparison is queued; until reported, we make no superiority claim over independently trained causal models.

R3. Target validity. The nine targets are deterministic PPG-derived proxies, not clinical ground truth. Our 20,000-window audit finds whole-window PPG–ECG sensitivity of 55.52%/50.71% and PPV of 73.50%/81.27% on MIMIC/VitalDB, with matched-interval MAE 82.65/73.48 ms. These are extraction diagnostics, not target accuracy: matching covers the whole window, not specifically the four future beats, and ECG peaks are algorithmically detected. We will describe the task as prediction of operationally defined signal-derived descriptors, not validated clinical event prediction. Manual beat/morphology annotation remains future work.

R4. Event-VQ tokenizer exposure. Appendix C.2 shows that the frozen Event-VQ tokenizer was trained on the full processed MIMIC corpus before the 90/5/5 patient split, so its training data include groups later assigned to validation/test. The backbone uses only training groups, but the full tokenizer-plus-backbone pipeline is not fully patient-independent. We will qualify the claim as patient-disjoint backbone pretraining. A train-only tokenizer with matched backbone training/evaluation is queued; we will not assume exposure has no effect without comparison.

R5. VitalDB reconstruction. We recovered the converter, schema, preprocessing config, log, and corpus manifest. The corpus contains 1,149,347 windows across 114 shards; three sampled windows were reconstructed with 0 maximum finite absolute difference for checked arrays/masks. This is a partial reconstruction audit: all three samples start at source-grid index 0 and use the same VitalDB SDK grid; it does not establish exhaustive native-timestamp, device-offset, or full-corpus equivalence.

Overall, we narrow the claims to the evidence: PulseBound provides a formally defined and empirically audited stored-window information boundary and improves future-state prediction against the specified persistence reference. We explicitly distinguish this from raw-signal causality, clinical target validity, fully patient-independent tokenizer training, and superiority over independently trained causal forecasters.

Reviewer_FtAhOpenReview ↗
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Paper summary

During pre-training, causal attention alone does not prevent future-information leakage. Therefore, the paper proposes PulseBound, a representation learning framework for PPG signals using future beat prediction while ensuring that context representations are constructed only from auditable, admissible past observations. PulseBound prevents information from leaking from the future suffix into the visible prefix. The model predicts 9 deterministic rhythm and morphology descriptors. Experiments indicate that PulseBound outperforms other PPG-FMs on 9/13 linear probing tasks and 7/13 full fine-tuning tasks.

Critical strengths
  • The auditable information boundary which is empirically validated is important to ensure forecasting and predictions that are trustworthy. This is evaluation takes into account many factors, making it rigorous.
  • PulseBound's forecasting accuracy on the aggregate metrics is strong given that it is favored in all 40 cutoff horizon cells.
Critical weaknesses
  • Applicability beyond the 30s: The paper only addresses auditability on the 30s window interface. PPG signals are continuous waveforms in many durations and sampling rates, whether PulseBound will extend to PPG in general remains unclear. Some health conditions require longer duration PPG signals such as 60s or 120s. How would PulseBound extend in this case or streaming scenarios?
  • Downstream performance and results: PulseBound positions its downstream evaluation as a system-level comparison rather than attributing performance gains to a specific objective. However, it uses many training objectives and compares itself to existing PPG-FMs on downstream task performance. This raises the following questions: (1) Is there a specific reason PulseBound shouldn't be compared to self-supervised baselines (e.g., SimCLR or Masked Reconstruction using the same data? (2) Are the additional steps worth the performance, and what are the trade-offs between auditability and downstream performance?. Furthermore, the results are only described at the surface level without offering interpretations or how PulseBound is useful.
Questions for authors
  • Writing: The paper's writing can be greatly improved. Currently, it references terms particularly in the abstract that require the reader to understand the methods (e.g., stored-window information boundary, etc.). The dense jargon makes it difficult to understand the main contributions.
2 comments

We thank the reviewer for the careful assessment and for recognizing the value of an auditable information boundary. We agree that the contribution should be separated from the choice of pretraining objective, and that the current 30-s setting does not establish end-to-end streaming.

R1. Relation to standard SSL.
We do not claim that future-state prediction is universally superior to contrastive/reconstruction SSL. Our central question is: what information reaches a predictive representation when part of the signal is withheld? Causal attention or token masking alone cannot guarantee this when full-window normalization, nonlocal transforms, or companion views can transmit suffix information into the visible prefix. PulseBound therefore enforces the boundary at input construction, formalized by Proposition 1.

Our seven-model benchmark compares complete pretrained systems under matched evaluation settings: PulseBound is best on 9/13 frozen linear-probe and 7/13 full-fine-tuning tasks, while other methods lead on several tasks. The state-supervision controls further isolate target alignment: at seed 0/epoch 79, Skill is 0.3926 (full), 0.3527 (capacity-matched no-state MLP), and 0.0032 (shuffled-target predictor). Three-seed no-state probes still recover future-state information (Ridge 0.2844; MLP 0.3488, available-case support). These are not substitutes for matched SSL controls.

New matched SimCLR control. We completed a 30-epoch SimCLR run using the same pulse_omega_base backbone, Event-VQ tokenizer, MIMIC+VitalDB data, 90/5/5 patient split, samples-per-epoch, and downstream LP protocol (seeds 42/43/44), changing the pretraining objective only. At the prespecified 30-epoch endpoint, the three-seed means are: PPG-BP SBP MAE 16.40 mmHg; PPG-BP hypertension AUROC 0.537; WESAD stress AUROC 0.897. This directly controls for backbone/data/split/evaluation differences and strengthens the objective-level comparison. It is not compute-matched to PulseBound's 80-epoch schedule, so we do not claim universal superiority over SimCLR at equal budget. A matched masked-reconstruction control is not yet reported, and we do not claim superiority over reconstruction SSL.

R2. Longer windows and streaming.
We agree that 30-s windows do not establish 60/120-s or continuous streaming capability. Our guarantee starts at the stored, preprocessed-window interface. VitalDB uses forward-backward filtering and window-level min-max normalization, so future raw samples may affect the stored prefix before PulseBound receives it. Thus our claim is stored-window suffix invariance, not raw-signal streaming causality. We will state this explicitly in the abstract, method, and limitations and frame boundary-preserving streaming preprocessing as future work.

R3. Downstream interpretation and cost.
The downstream benchmark compares complete pretrained systems, not isolated losses, and performance is task-dependent. We will avoid interpreting aggregate task counts as universal superiority. The model has 98.49M trainable parameters. On an A100-SXM4-80GB, BF16 eager encoder-only benchmarking of the instantiated architecture without loaded weights gives 1,549.59 windows/s (batch 64) and 14.37 ms mean batch-1 encoder latency. These are hardware-specific architecture measurements, not end-to-end streaming latency, trained-model throughput, or wearable efficiency.

R4. Presentation.
We agree that Figure 1 is too dense. We will reorganize it into: (i) information-boundary construction, (ii) representation learning/future-beat prediction, and (iii) training-only auxiliary supervision followed by PPG-only downstream inference. We will introduce each component's purpose before implementation details and move lower-level details to the appendix.

Overall, our revised claim is intentionally narrower and more testable: PulseBound is a predictive physiological representation-learning framework that explicitly constructs, formalizes, and audits the information available to the model. The new matched-backbone SimCLR result strengthens the evidence that the observed transfer is not simply an artifact of a different encoder or evaluation pipeline, while we explicitly acknowledge the remaining compute-matching and reconstruction-SSL gaps.

Thank you the clarifications. With the SimCLR experiment and revised claim, my concerns have been addressed. I will increase my score.

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