acceptodds
Under review as a conference paper at ICLR 2027

BCG-FM: A Foundation Model for Ambient Cardiac Health Sensing

Abstract

Foundation models for wearable biosignals have matched or exceeded supervised specialists across a range of clinical tasks, yet all rely on modalities that require deliberate user action–wearing a device or visiting a sleep lab. We introduce BCG-FM, the first foundation model for ambient mechanical biosignals. A piezoelectric sensor embedded in the bed surface records ballistocardiography (BCG) each night without user effort; from a corpus of 2.75 million hours of nightly recordings from 145,857 individuals, we pretrain with participant-level contrastive learning. Frozen BCG-FM embeddings achieve 3.26-year MAE on biological-age estimation (the lowest reported for any ambient, contactless modality) and yield clinically relevant discrimination across 15 self-reported health conditions and two independent external clinical cohorts. Pretrained representations from only 500 labeled participants outperform a fully supervised baseline trained on 3,372, and representation quality scales log-linearly with contrastive batch size. A second pretraining stage, in which each minute predicts how the embeddings of neighbouring minutes differ from its own, further enriches the embeddings with sleep-stage, apnea, and heart-rate information while retaining age information. These results establish ambient, longitudinal mechanical biosignals as a viable modality for health foundation models.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Foundation model, Biosignal, Ballistocardiogram, Ambient, Age estimation, self supervised learning

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_t9rWOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
3(+1)
Soundness
2
Read review
Paper summary

The paper presents BCG-FM, a contrastive foundation model for bed-based BCG. It is pretrained on about 2.04M hours of night recordings of a commercial sleep sensor, using the participant-level InfoNCE framework. The model is evaluated on the biological age estimation task, self-reported condition classification task, and externally on two small public BCG datasets

Critical strengths
  1. The topic is highly relevant in the field of Biosignal Foundation models. Bed-based BCG is under-explored in the foundation-model literature, and the dataset is far larger than any previous BCG study. The work filled the gap by creating a foundation model for the BCG signal.

  2. The data come from a commercially deployed consumer sensor that needs no user action after setup. This makes long-term, low-burden monitoring realistic, including for groups who struggle to wear devices, such as older adults.

  3. Figure 1 summarises the whole pipeline in one place with good quality: sensor and channel decomposition, positive-pair construction, the student–teacher architecture, embedding aggregation, and the downstream tasks, alongside the main results.

  4. Potential resource contribution. The authors promised to release the Twilight dataset with fixed splits and evaluation scripts. Paired BCG–PSG data of this kind is very rare and valuable for the development of this field.

Critical weaknesses
  1. The paper claims to be " the first foundation model for ambient mechanical biosignals”, but writs PPG and accelerometry are also recorded passively and continuously once the device is on. The bed sensor itself also needs initial setup. So “ambient vs. wearable” is more of a difference in form factor, not in user effort. IMU foundation models are therefore direct prior work on mechanical biosignals. For example, here are some related works the author can consider referring to:

Yuan, H., Chan, S., Creagh, A.P., Tong, C., Acquah, A., Clifton, D.A. and Doherty, A., 2024. Self-supervised learning for human activity recognition using 700,000 person-days of wearable data. NPJ digital medicine, 7(1), p.91.

Erturk, E., Kamran, F., Abbaspourazad, S., Jewell, S., Sharma, H., Li, Y., Williamson, S., Foti, N.J. and Futoma, J., 2025. Beyond sensor data: Foundation models of behavioral data from wearables improve health predictions. ICML 2025.

Gu, X., Shu, Y., Han, J., Liu, Y., Liu, Z., Anibal, J., Sangha, V., Phillips, E., Segal, B., Yuan, H. and Liu, F., 2025. Foundation models for biosignals: A survey.

  1. In the contribution part, the authors used the result: atrial fibrillation (0.954) to suggest the model can accurately estimate disease. However, in Table 5, demographics alone reach an AUROC of 0.994 for AF classification (which I find very strange), 0.040 higher than BCG-FM.

  2. Some information in Table 1 seems inconsistent and needs clarification. Disease (Train) have fewer participants than Pretrain (50,128 vs. 136,575) but more segments (168M vs. 122M) and more hours (2,793,434 vs. 2,041,288), despite Disease being described as a “pretrain subset”. The total hours of Disease Train + Disease Test (3.49M) even exceeds the total hour listed in the bottom row (2.75M). It is very unclear to me how these numbers in Table 1 add up. Also, the signal-quality filtering rules are not described for the pretraining cohort. Why is signal quality filtering only needed for pretraining but not for finetunning? External Dataset 1 has 153 sessions, 153 segments and 2.5 hours, which means each segment is only about 1 minute. Section 3.1 described External Dataset 1 as 153 nights, which does not appear to be "overnight", so it does not test the paper's central claim. Please add a column to Table 1 reporting the mean or median recording length per session and std, and state whether a session is one night.

  3. “The first to show that BCG supports general-purpose health prediction” is a bit overstated. BCG has a substantial prior literature on heart rate, sleep, and heart-failure monitoring. For example:

Sadek, I., Biswas, J. and Abdulrazak, B., 2019. Ballistocardiogram signal processing: a review. Health information science and systems, 7(1), p.10.

Aydemir, V.B., Nagesh, S., Shandhi, M.M.H., Fan, J., Klein, L., Etemadi, M., Heller, J.A., Inan, O.T. and Rehg, J.M., 2019. Classification of decompensated heart failure from clinical and home ballistocardiography. IEEE Transactions on Biomedical Engineering, 67(5), pp.1303-1313.

In addition, the two external datasets used in this study were themselves released for BCG-based cardiac assessment.

  1. Baseline models trained with traditional domain features such as overnight heart rate, HRV, respiratory rate, etc are missing as a comparison.

  2. In the Discussion section, the authors attributed the performance improvement to four times more pretraining hours and participant-level pretraining across nights compared to other models, but there are no results to support this claim. Each row of Table 3 uses a different dataset, population, age range, and health definition, so the MAEs are not directly comparable.

  3. The experiment results have no standard deviations or confidence intervals. It is unclear if the improvements are significant or not. Please report seeds or bootstrap 95% CIs and paired tests, plus prevalence and number of positives per task.

Questions for authors
  1. The paper described that the supervised E2E baseline was trained with 3372 users, why can't it be trained with all 136K users, the same as the BCG-FM?

  2. The paper compared the BCG-FM biological age prediction performance to the PpgAge, ECG-age, and Brain-age papers, but only showed its accuracy in age estimation. However, the value of biological age is more about the age gap (predicted biological age - chronological age) and its association with health outcomes rather than the accuracy of age estimation. Could the author report MAE and the bias-corrected age gap in the non-healthy tiers and the disease cohort, and test the association of the gap with the different conditions?

4 comments

Thank you for the constructive review. The new baselines are in Table A under CW5.

CW1.

We have dropped both "first" claims. We would keep one narrow distinction for "ambient": after a one-time setup, a bed sensor records every night with nothing to wear or charge, whereas a wrist device records only while it is worn and charged. We agree this is a difference in form factor and now present it that way. IMU models use a different sensor (a wrist accelerometer rather than a piezoelectric sensor under the body) but capture related mechanical information, so §2 now discusses them as prior work (Yuan et al., 2024; Erturk et al., 2025; Gu et al., 2025).

§2 also covers Sadek et al. (2019) and Aydemir et al. (2019) as prior BCG work, and states that both external datasets were released for BCG-based cardiac assessment.

CW2.

The 0.994 is an age effect. External 1 has only 4 AF subjects, aged 71, 74, 75 and 91 in a cohort with median age 48, so age alone gives 0.975. This cohort cannot validate AF detection, though embeddings alone reach an AUROC of 0.941 (0.954 with demographics).

CW3.

In Table 1 the Disease and Healthy rows count every in-bed and out-of-bed minute of a session, while Pretrain counts only quality-filtered in-bed minutes; "pretrain subset" refers to subset of the pretrain participants that has self-reported disease labels. The Total row adds Pretrain, Healthy and External only. We filter in pretraining to keep contrastive pairs clean and embed all minutes downstream, as in deployment; the filter rules are now in the appendix. Table 1 now has a minutes-per-session column (mean ± SD): Pretrain (sessions with data) 477 ± 163, Healthy (Train) 777 ± 270, Disease (Train) 620 ± 190, Twilight 475 ± 47 in bed, External 2 629 ± 89.

External 1 consists of 153 short recordings (20–45 s, 1–3 per subject) rather than nights; Table 1's 2.5 h counted each as a padded 60-s input. §3.2 is corrected and we now present it as a short-segment transfer test.

CW4.

See CW1.

CW5.

We added hand-crafted baselines under the same probes and splits: 21 signal features (band powers, HR, RR, HRV, movement) and the device's own HR/RR/HRV/sleep outputs.

Table A (BCG-FM age = Table 2 Ridge row)

ModelAge MAE, ridge probe, yr [95% CI]Internal AUROC, embeddings only (macro, 14 conditions)
BCG-FM3.80 [3.71, 3.90]0.686
Chronos-Bolt5.97 [5.83, 6.11]0.614
MOMENT-1-large6.05 [5.89, 6.23]0.619
PaPaGei-S6.50 [6.35, 6.64]0.595
Signal features7.23 [7.08, 7.38]0.605
Device outputs7.92 [7.74, 8.11]0.577
Demographics–0.658

BCG-FM is ahead of all baselines across 14 conditions (irregular heartbeat, with one test positive, is dropped), and adding the features to BCG-FM is not adding information. General and cardiac foundation models (Chronos, MOMENT, PaPaGei) are 2.2–2.7 years behind on age.

CW6.

Both attributions are removed and Table 3 is presented as context. We did not ablate cross-night positives, so we make no claim about them. For data scale we ran a controlled ablation with batch size 384: with 1%, 10% and 100% of the pretraining devices, validation age R² is 0.404 / 0.436 / 0.458 and Twilight staging κ 0.269 / 0.357 / 0.415.

CW7.

Tables now give n, n+, prevalence and 95% subject-bootstrap CIs, with paired tests against baselines. Examples: age MAE (Transformer head, ages 18–70) 3.26 [3.17, 3.34] yr; External 2 AF per window 0.699 [0.578, 0.811]; External 1 heart failure (embeddings only) 0.841 [0.72, 0.94] with 7 positives. Pretraining is a single run per configuration, so the intervals cover test-set sampling only.

Q1.

By design the age model is trained only on the healthy cohort, so that predicted age reflects healthy ageing. A supervised model trained on all 136K users would learn a different target, age in a population that includes disease. Pretraining needs no labels, so it can use everyone. With 500 labelled users the frozen probe (4.38 yr) already outperforms the supervised model trained on 3,372 (4.41 yr).

Q2.

We tested the bias-corrected age gap on 63,065 participants outside the healthy cohort, adjusting for age and sex. A larger gap is associated with 8 of 14 conditions (FDR < 0.05): OR per SD is 1.14 [1.12, 1.17] for hypertension, 1.09 for heart conditions and for snoring, and 1.08 for asthma/COPD. Diabetes, thyroid disorder and cancer show no association.

The gap also grows with the number of reported conditions: +0.21, +0.49, +0.59 and +0.93 yr for 0, 1, 2 and 3+ (+0.29 yr per condition [0.25, 0.33]). MAE (ridge probe) is 4.19–4.45 yr across these groups against 3.80 on the healthy test set (Table 2), and 4.32 yr with a mean gap of +0.66 yr in the disease cohort (≥ 1 condition). Effects are modest and labels self-reported, so we read this as supportive evidence only.

Thank you for the detailed reply and the additional results. Most of my concerns have been addressed. Two points remain:

  1. In Table A, all hand-crafted baselines score below demographics alone. The more informative comparison is therefore against demographics plus domain features. Could the authors report the AUROC for demographics + hand-crafted signal features, ideally with paired confidence intervals? This would show how much BCG-FM adds beyond what demographics and standard physiological features already provide. It would also support the statement that adding the features to BCG-FM does not add information.

  2. The authors explain that AF in External Dataset 1 is confounded by age: there are 4 AF subjects aged 71–91 in a cohort with median age 48, and age alone gives AUROC 0.975. This dataset therefore cannot support an AF-detection claim, as the authors note. The embeddings-only AUROC of 0.941 is also likely driven by the age information the embeddings carry. Would the authors remove AF detection on External Dataset 1 from the contributions, abstract and conclusion?

Thank you for the follow-up and acknowledgement of resolved concerns.

  1. In Table B we compare BCG-FM to signal and device baselines with and without demographics. All arms use the same split, probe and 64 sampled minutes per user. Demographics are age, sex and BMI.

Table B

ArmMacro AUROC [95% CI]Paired Δ vs BCG-FM [95% CI]
BCG-FM + demographics0.696 [0.687, 0.704]reference (+ demographics)
BCG-FM (embeddings only)0.686 [0.677, 0.694]reference (no demographics)
Signal features + demographics0.674 [0.665, 0.683]−0.022 [−0.029, −0.015]*
Device outputs + demographics0.671 [0.662, 0.680]−0.025 [−0.032, −0.017]*
Demographics0.658 [0.650, 0.667]−0.037 [−0.046, −0.029]*
Signal features0.605 [0.596, 0.615]−0.081 [−0.090, −0.071]*
Device outputs0.577 [0.567, 0.587]−0.109 [−0.119, −0.099]*

Macro AUROC over 14 conditions; Δ = arm − BCG-FM with the same demographics setting; paired 1,000-rep user bootstrap; * 95% CI excludes 0.

Adding the signal features to BCG-FM + demographics changes macro AUROC by −0.001 [−0.002, 0.000].

  1. AF on External Dataset 1. We agree. We will remove AF detection on External Dataset 1 as a claim and any mention in the abstract, contributions and conclusion.

We hope these additions address your remaining concerns and that you will consider adjusting your score accordingly.

Thank you for your detailed response. I appreciate the additional results. I will raise my score to 3.

Reviewer_QoV8OpenReview ↗
Rating
4
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

This work presents BCG-FM, as the foundation model for ambient ballistocardiography (BCG) signals collected from bed-embedded piezoelectric sensors. Trained via participant-level contrastive learning on millions hours of recordings from 14W+ individuals, it learns general-purpose physiological embeddings in a self-supervised manner. A second-stage neighbor-context pretraining further enriches the embeddings with sleep-stage, apnea, and heart-rate information while preserving age-related traits. Frozen embeddings achieve state-of-the-art age estimation performance among contactless modalities, and show clinically relevant discrimination across 10+ self-reported conditions and two independent external clinical cohorts. The authors also plan to release the Twilight paired BCG-PSG dataset as a public research resource.

Critical strengths

(1) It is said that this is the first work to scale foundation models to ambient, contactless BCG signals, with a dataset orders of magnitude larger than all prior BCG studies combined. It proves passive bed sensors can encode enough physiological info for population-level health modeling, a fundamentally new finding for the field. (2) It follows rigorous foundation model evaluation practices: frozen backbone probing, few-shot label efficiency, batch-size scaling, plus both internal and external disease validation. The planned Twilight dataset release is also a very valuable community contribution.

Critical weaknesses

(1) The contrastive learning framework and EfficientNet encoder are heavily adapted from prior PPG foundation model work, with limited algorithmic innovation tailored to unique BCG signal properties. (2) Internal disease benchmarks use self-reported health labels, which are unreliable due to asymptomatic and under-diagnosed conditions.(3) All data comes from one single commercial sensor product, with no testing across other hardware or placement setups. (4) The custom Health Status Score makes direct age MAE comparisons to other papers difficult. (5) Privacy risk noted but unaddressed. The paper flags biometric identity retrieval as a risk, but proposes no technical mitigation strategies. (6) The two independent clinical cohorts are extremely small (85 and 46 participants), providing very limited statistical power and no ability to test subgroup performance or cross-population generalization.

Questions for authors

(1) Do you plan to test cross-device generalization of BCG-FM on other BCG sensor platforms? Right now all data comes from one commercial product, so it’s unclear how transferable the embeddings are across different hardware designs. (2) Are there plans to validate key clinical findings (heart failure, AF detection) on larger, multi-site clinical cohorts? The current external cohorts are quite small and limit the strength of clinical conclusions. (3) The paper identifies biometric identity retrieval as a privacy risk. Have you considered adding privacy-preserving pretraining strategies, like de-identification constraints or differential privacy, to the training pipeline? (4) Self-reported disease labels are known to have substantial noise, especially for asymptomatic cardiovascular conditions like atrial fibrillation and early heart failure. Have you quantified how much label noise may be inflating your reported performance? Have you considered validating on larger, publicly available clinical BCG datasets with confirmed diagnoses?

2 comments

Thank you for the careful and encouraging review.

CW1.

The objective and encoder are inherited from PPG work and we claim no new one. What is specific to BCG is the lossless breathing/heart channel split, co-sleeper negatives (only possible with bed sensing), and the finding that synthetic augmentations and masked reconstruction degrade BCG representations (Appendix A–B).

CW2, Q4.

Self-report is a limitation, as you note. To see whether it could inflate our results, we simulated label noise, and it lowers AUROC instead of raising it. With random errors added to the test labels, hypertension falls from 0.796 to 0.764 (10% noise) and 0.698 (30%) (the test was done on 64 one-minute samples per person for computational efficiency and the results are therefore slightly different from results in the paper). Therefore, the model performance is not inflated due to label noise.

CW3, Q1. Both external cohorts are public datasets recorded on other BCG hardware, and frozen embeddings transfer to them without fine-tuning the backbone (Table A under CW6). Generalization across hardware at scale is still to be established, as we say in Limitations.

CW4. The Health Status Score plays the same role as the healthy-cohort definitions in other bio-age work: the age model is trained on healthy people. Appendix E specifies it in full, and Table 3 is context only.

CW5, Q3.

We agree this needs a clearer treatment. Participant-level contrastive pretraining pairs recordings from the same person, as in S. Abbaspourazad, et al. 2024, so the embeddings can match full night recordings to one another (rank-1 92.5%). For reference this drops to 31.6% for minute to minute retrieval. This is matching within a closed, pseudonymous set: it links recordings to the same anonymous participant, not to a real identity. That would require a reference set of BCG labeled with names, and our BCG, unlike faces or voices, can only be recorded by a bed sensor. All data were de-identified before pretraining, with participant consent for research use under our privacy policy. We do not release the encoder or embeddings, and users who request deletion are excluded from later training. We have not yet tested differential privacy or identity-adversarial training, and we will add this to the Limitations section as future work.

CW6, Q2, Q4.

We agree that the external datasets are small and therefore we will release the Twilight dataset (195 PSG nights) alongside the paper to aid the community in making analysis on BCG data more accessible. In the future we hope to be able to validate clinical findings. This paper (partially) aims to show the viability of BCG foundation models for these tasks. We are not aware of large-scale publicly available BCG datasets with confirmed diagnosis.

Table A

AUROCn+BCG-FM, embeddings only [95% CI]DemographicsChronosMOMENTPaPaGeiSignal features
Ext. 1 heart failure70.841 [0.72, 0.94]0.6450.2140.5290.4820.480
Ext. 1 abnormal rhythm180.793 [0.65, 0.90]0.7750.4650.7000.5880.783
Ext. 1 PVCs80.657 [0.44, 0.84]0.5260.3210.5240.4740.537
Ext. 2 AF, per window10 subjects0.699 [0.578, 0.811]0.2960.5200.6050.5730.619
Reviewer_QoV8OpenReview ↗

Comment

Thank you for the detailed responses and additional analyses. The label-noise simulation, cross-hardware transfer, and paired baseline comparisons address my main concerns, while the small external cohorts and untested privacy methods remain limitations. Given the strong empirical evidence and the planned Twilight dataset release, I keep my rating at 4 (clear accept).

Reviewer_UPnLOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper presents BCG-FM, a foundation model for bed-based ballistocardiography, pretrained on a large proprietary dataset of more than 100K users / 2M hours of nightly recordings from a commercial sensor. The pre-training method was a contrastive learning process adapted from Abbaspourazad et al. (2024). BCG-FM used a 1D-convolutional network as backbone and within-participant InfoNCE that emphasizes between-subject trait differences. After pre-training, the authors evaluate the model through probing with frozen backbone on age estimation, a few self-reported conditions, on two small public BCG cohorts and an in-lab BCG–PSG dataset. The paper also proposes a second pre-training stage that predicts neighboring-minute embedding differences.

Critical strengths

The following strengths were noted: A bed-based BCG is a meaningful and practical sensing setting, and the pre-training corpus is extremely large for this modality. It would be actually interesting as an ablation to see whether this scale actually produces meaningful downstream improvements or even a smaller pre-training cohort would suffice for the results that are presented in this paper. Also, of course the planned release of Twilight would benefit the community.

Critical weaknesses

The following weaknesses are noted:

  1. The main limitation of the presented analysis is the complete absence of downstream comparisons. The experimental results are solely compared to demographic-only or simple supervised baselines, which is quite a weak claim to make, given the scale and the power of the pre-training as described. Moreover, BCG is a well-researched modality, despite not in such scale, hence its physiological features are fairly well understood. I would at least expect the authors to compute and compare their model against such validated features, e.g., heart rate and breathing rate, HRV, absolute movement, automatic sleep metrics etc. Even further, since the authors propose a foundation model in a novel biosignal, comparisons should include at least a few general time-series models, e.g., Chronos, or even foundation models of sub-signals of BCG such as those centered on cardiac activity. Without proper comparisons, there is no way to judge whether the learned representation of BCG-FM adds anything beyond standard features. My most fundamental question in the end is whether BCG is a modality that needs its own foundation model or existing features and time-series models can cover its needs.

  2. In terms of the chosen methodology, the novelty is itself limited as the architecture and method is largely inherited from a previous study, however the main consequence is that BCG-FM will inadvertently be biased to subject-specific traits and artifacts. This is because the model is trained in a contrastive way that considers positives within the same participant even from unrelated days far from each other. As a result, the model would be plausibly good in between-subject comparisons but might not be useful in more subtle within-person changes, which is also of interest to the community. The t-SNE graph in Figure 1 shows exactly this bias through the clusters saturating per individual participant. The authors acknowledge this limitation in the Appendix, but the evidence for within-person sensitivity is limited to small probes on Twilight without any baseline comparison. Longitudinal within-person change (e.g., health changes across nights) is not discussed.

  3. The authors spend considerable space claiming robust results on age estimation. However, their main evidence (Table 3) is still not a valid comparison (as honestly stated in the caption) as different modalities, datasets, cohorts and age ranges are compared in a single framework. As an additional comment, it is not clear why the BCG-FM performance is bolded in that table, although other models in the same table perform better. A few results are also inflated by runs where AUROC falls substantially below the random chance threshold. The gains wherever reported should be grounded to a proper random chance threshold.

  4. The rationale of the paper is hard to follow because of a handful of inconsistent and selectively reported numbers. Heart failure AUROC is reported as 0.841 in the abstract and as 0.822 in other places within the text. Diabetes appears as both 0.853 and 0.852, which could be just a typo to fix. Also, the result of AF on External 1 (0.954) is listed as a headline in places but demographics alone reach 0.994, which substantially weakens the claim. Participant counts vary, as both 145,857 and 136,575 are reported for the number of pre-training users, and a healthy test set of 4,708 (Table 1), 4,646 (Fig. 1e) and 4,645 (Table 3) is also confusing. Since the paper also proposes a dataset release, these inconsistencies are a particular concern. In general, the authors should give a few more passes on the manuscript to improve the flow and the readability, as some subsections (for example Limitations) are written note-like or contain frequent grammatical errors (“each night the user sleep”, “BCG-FM perform worse”).

Questions for authors
  1. How does a model on hand-crafted BCG features (HR, HRV, respiratory rate, movement, device sleep metrics) perform on age, the internal conditions, and the external cohorts?
  2. Similarly, how do general time-series models perform on the same tasks? These are the bare minimum questions that need to be addressed.

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