acceptodds
Under review as a conference paper at ICLR 2027

VitalFM: A Foundation Model of High-Resolution Vital Signs in the ICU

Abstract

ICU monitors record physiology every few seconds, yet many prediction models use hourly representations that may obscure short-term changes. Clinical prediction using handcrafted summaries requires domain expertise, whereas sequence models learning directly from measurements may underperform when cohorts and positive labels are limited. We therefore introduce VitalFM, a foundation model that learns representations from dense, partially observed ICU monitoring through self-supervised pre-training, without input imputation. Its bi-axial encoder combines bidirectional state-space modeling over time with masked attention across channels, and pre-training reconstructs an entirely withheld vital sign while preserving its correlations with remaining signals. The source corpus comprises approximately 13.5 million monitoring hours from 79,000 patients, and we evaluate four outcomes in Site A and MIMIC-III. We compare VitalFM against LightGBM, tabular foundation models, and supervised deep sequence models, evaluating both frozen representations and end-to-end fine-tuning. With TabPFN-3 as a fixed classifier, frozen VitalFM representations improve over raw grids by 3.1 AUROC and 2.5 AUPRC points, outperform handcrafted features on Site A, and achieve comparable performance on MIMIC-III. Fine-tuned VitalFM achieves the highest mean AUROC and AUPRC of all methods: slightly above handcrafted features with tabular foundation models, and 3.2 and at least 7.9 AUROC points above handcrafted LightGBM and supervised deep sequence models, respectively. Pre-training accounts for much of this performance: VitalFM w/o pre-training, which uses the identical architecture trained only on the downstream task, is lower by 14.8 AUROC and 8.4 AUPRC points on average. Fine-tuned models also transfer between health systems without destination-site refitting. These results support self-supervised pre-training on dense monitoring for clinical prediction across outcomes and healthcare systems.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
foundation models, self-supervised learning, physiological time series, clinical prediction, intensive care, representation learning, missing data

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_wnKDOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
3
Soundness
3
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Paper summary

The paper investigates how to extract meaningful features from second to minute multichannel, heterogeneous data. Continuous data is encodes using patch encoders, and episodic measurements through a parse encoder. The patch representations are further encoded using a bi-axial encoder and the sparse encoder output further through channel attention. This is then used for cross channel masked reconstruction and cross vital correlation matching. The validation is done using Site A, and MIMIC III is used for external validation. Internal validation is done using held out data from Site A, and external validation through MIMIC data.

Critical strengths

Solid engineering, that first a) encodes high resolution temporal signals as patches and episodic signals through a sparse encodes, b) processes temporal signal through MAMBA in both forward and reverse directions, and vital sign processing through multi-head attention and then finally trained using standard reconstruction and cross-vital correlation loss. The results demonstrate that these features do produce better predictions. The results are presented thoroughly.

Critical weaknesses

• If a foundation model is the claim, I would have expected a much clearer separation in results from simpler methods, which does not seem to be the case. • It is unclear to me whether the second-to-minute resolution is solved through this engineering, or whether any fundamental issues of temporal multiresolution are solved. Also, not imputing is a good thing, but it is not clear any breakthrough idea has been presented through the encoding with the sparse encoder. In summary, a good engineering solution, but no methodological insights. Even the ablations consider what happens when each specific module is removed, but I got no further insights into modelling long term disparate measurement fusion.

Questions for authors

I found Figure 2 hard to interpret, perhaps a better motivation would have helped.

3 comments
AuthorsOpenReview ↗

Response to wnKD (1/2): Foundation-model scope and performance

Thank you for recognizing the study's soundness and thorough presentation. We address your comments below.

W1. Foundation-model scope and performance

We use “foundation model” to describe a self-supervised encoder reused across outcomes and evaluation settings. VitalFM is evaluated across four outcomes, two cohorts, multiple downstream learners, frozen transfer, fine-tuning, and cross-cohort transfer without destination-site refitting.

VitalFM does outperform simpler methods: fine-tuned VitalFM achieves mean AUROC 3.2 points above handcrafted features with LightGBM and at least 7.9 points above each supervised sequence baseline. Its closest competitors are not simple baselines: they combine expert-designed features with TabPFN-3 and TabICLv2, which are themselves pre-trained foundation models for tabular data. Even against these, fine-tuned VitalFM achieves the highest mean AUROC and AUPRC. Fine-tuned VitalFM learns directly from raw monitoring and outperforms those same tabular foundation models applied to raw vital-sign grids by 3.7–7.0 AUROC points and 2.8–4.3 AUPRC points on average. Finally, the identical architecture trained only on task labels is 14.8/8.4 points lower than pre-trained VitalFM. Together, these comparisons show the value of physiologically motivated pre-training for learning representations that transfer across outcomes and health systems.

AuthorsOpenReview ↗

Response to wnKD (2/2): Methodological insights and Figure 2

W2. Methodological insights

We understand the concern that VitalFM reads as an engineering solution. VitalFM addresses second-to-minute resolution through within-minute encoding followed by day-long temporal modeling; we do not claim a general solution to temporal multiresolution. We agree that the original manuscript gave the reasoning behind each modeling choice in the method description without drawing it together, and did not state the insights from the comparisons explicitly enough. The revised Discussion and Conclusion section now states three insights supported by the results:

  • Self-supervised pre-training makes deep learning on raw monitoring effective when labeled data are limited. Labeled cohorts for a given clinical question can be small, and end-to-end deep learning may then struggle to match handcrafted features paired with classical or tabular models, which can leave outcome prediction dependent on manual feature engineering. In our experiments, the same architecture trained only on task labels falls well short of expert-designed features, whereas fine-tuned VitalFM achieves the highest mean AUROC and AUPRC in within-cohort evaluation, and even the frozen encoder is competitive with expert-designed features (Section 4.4).

  • Our physiologically motivated pre-training objective turns the interdependence among vital signs into an effective source of supervision. Because vital signs tend to co-vary as a patient's physiological state evolves, VitalFM can reconstruct an entirely withheld vital from the remaining signals, without access to any of its measured values. Encouraging the decoded target and decoded context vitals to correlate as the observed signals do further improves downstream performance at little cost to reconstruction quality (mean squared correlation mismatch 0.427 vs. 0.045; mean AUROC/AUPRC gains of 1.0/1.1 points with TabPFN-3 and 1.8/1.4 points with a linear probe; Figure 3, Table 3).

  • Partially observed ICU monitoring can be modeled as it is recorded, without imputing missing measurements. VitalFM's patch encoders represent what was recorded within each minute, with a dedicated sparse encoder for episodic NIBP; bidirectional Mamba, a state-space design motivated by the evolving physiological state that vital signs reflect, models each vital's full-day trajectory, and masked attention lets the vitals available at each minute inform one another. Several of these choices are supported empirically: in matched models without pre-training, retaining NIBP adds predictive information (removing it lowers mean AUROC/AUPRC by 1.5/0.8 points) and the sparse encoder achieves higher AUROC than a shared convolutional encoder in most settings (six of eight; Table C.6); with pre-training, bidirectional Mamba outperforms approximately parameter-matched attention-based temporal backbones (mean AUROC/AUPRC gains of 2.3/1.8 points over gated attention and 2.1/2.2 points over the masked Transformer with TabPFN-3; patch encoding and cross-vital attention held fixed; Table 3). Even without observation-aware gating, VitalFM predicts well from partially observed inputs. Adding gating improves reconstruction and yields higher AUROC in five of eight settings and higher AUPRC in seven of eight with TabPFN-3. Although channel missingness and availability differ between the pre-training and downstream data, VitalFM performs well downstream and transfers across sites without refitting, suggesting that its representations remain robust under such differences in measurement availability.

Q1. Interpretation and purpose of Figure 2

Figure 2 asks whether VitalFM’s advantage holds in each cohort and outcome, not only on average, and how certain each difference is. Each point is a comparator’s performance minus fine-tuned VitalFM’s, so points left of zero favor VitalFM; bars are 95% paired bootstrap confidence intervals, and asterisks mark nominal p<0.05. It shows clear separation from most baselines. Overall, VitalFM is numerically higher in most comparisons, and none significantly favors a comparator. We revised the caption to explain how to read the comparisons.

Thank you again for your review. We would appreciate your thoughts on whether our responses address your concerns. We would welcome the opportunity to clarify anything that remains unclear.

Reviewer_gQc1OpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
3
Soundness
2
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Paper summary

This paper presents VitalFM, a self-supervised foundation model designed for high-resolution ICU vital signs. Instead of using standard hourly aggregated EHR data, the model takes 24-hour windows of eight physiological channels (heart rate, oxygen saturation, respiratory rate, temperature, and four invasive and non-invasive blood pressure signals) sampled on a 2-second grid (0.5 Hz) without imputing missing values.

The model is pretrained on 13.5 million monitoring hours from two private hospital systems (Site A and Site B). For downstream evaluation, the authors test frozen representations (using TabPFN-3 and linear probes) and end-to-end fine-tuning on Site A and the MIMIC-III matched-waveform database across four binary outcomes: mortality, invasive mechanical ventilation, vasoactive support, and continuous renal replacement therapy.

Critical strengths

This paper is a very clear and complete engineering study on how to use ICU data to train an 8-feature, 43,200-step Mamba-based model with combined loss terms. It reads like a well-executed textbook project for biomedical deep learning, with solid ablation studies and downstream experiments to show the utility of the trained model.

Critical weaknesses
  • Lack of core machine learning contribution and reproducibility: The technical pipeline is quite straightforward: the authors have access to private data from Site A and Site B, apply an existing Mamba architecture with two standard loss terms, and use their compute to train a predictor on an 8-feature, 43,200 context window to predict ICU outcomes. There is very little methodological novelty for an ICLR audience. More importantly, because Site A and Site B are private hospital datasets that cannot be easily shared with the public, and the public evaluation relies on the older MIMIC-III dataset, the broader ML community cannot reproduce the pretraining or gain much actionable insight from this training log.

  • Lack of motivation, If such work is accepted into ICLR, what’s next? Is there a multi-year grant or pathway saying that VitalFM will be merged into the Site A & B clinical workflow? Will this mamba-based architecture be merged and embedded into the vital machines? The reviewer thinks this paper is a well-written paper but it does not fit the ICLR venue.

Questions for authors
  • What is the fundamental motivation for building VitalFM? From the reviewer's perspective, there are three possible points the authors might be trying to make, and I would appreciate clarification:
    (1) The selling point is the data: the authors have large private datasets from Site A and Site B and believe this data is sufficient to represent the general patient distribution for a foundation model.

(2) Clinical deployment need: there is a clinical team urgently looking to deploy a bedside, 0.5 Hz continuously running model into the healthcare systems at Site A and Site B, and the authors are building the system for this specific hardware use case.

(3) "Vitals are all you need": the authors believe that high-frequency machine readouts from just 8 signals are the most crucial features for predicting patient futures in the ICU, making broader multimodal EHR foundation models or text-based clinical models unnecessary.

  • What is the planned real-world impact for VitalFM? Is the goal to merge it into a live bedside system, or is it only for retrospective data analysis? If it is for live deployment, showing results from a silent trial at Site A and Site B would be far more useful than the current manuscript. If it is only for retrospective analysis, why do we need 2-second resolution data? In normal retrospective EHR tables (like standard MIMIC or HiRID), vitals are only stored every few minutes or hourly, unless matched to specific waveform subsets

  • Given the heavy reliance on private hospital cohorts and the lack of full reproducibility for the pretraining pipeline, why not consider submitting this work to a clinical or biomedical journal where retrospective multi-site validation studies are a much better fit?

8 comments
AuthorsOpenReview ↗

Response to gQc1 (1/3): Methodological contribution, reproducibility, and reuse

W1. Methodological contribution

We agree that the original manuscript did not state the contribution clearly; the revision now lists it explicitly and states the resulting insights in the Discussion and Conclusion. We also clarify three points in the summary. First, VitalFM is a pre-trained encoder for dense, partially observed ICU vital-sign data represented on a two-second grid, and it is reused across outcomes and health systems rather than trained as a single outcome predictor. Second, Mamba does not process 43,200 time steps: patch encoders summarize up to 30 two-second measurements per minute, giving 1,440 steps per vital over 24 hours. Third, VitalFM is not an existing Mamba applied directly but a bi-axial design. Vital signs reflect a patient’s evolving physiological state, which makes a state-space model a natural fit for the time axis. This choice is also supported empirically: with patch encoding and cross-vital attention held fixed, bidirectional Mamba outperforms approximately parameter-matched attention-based temporal backbones. The vital axis serves a different role: reconstructing an entirely withheld vital requires combining information across vitals, even though their availability changes from minute to minute. Masked attention lets the available vitals inform one another without using information from naturally absent channels.

The objective is not two standard losses; both terms follow from one physiological property: vital signs change together as a patient’s state evolves. VitalFM therefore reconstructs a withheld vital from the others and preserves how it co-varies with them. Reconstruction alone achieves similar error but leaves a much larger target–context correlation mismatch (0.427 vs. 0.045), and preserving it improves mean AUROC/AUPRC by 1.0/1.1 points with TabPFN-3 and 1.8/1.4 with a linear probe.

These choices yield transferable representations. Without fine-tuning, a single frozen encoder is comparable to expert-designed features under the same classifier, and fine-tuned VitalFM achieves the highest mean within-cohort AUROC and AUPRC, while the identical architecture trained without pre-training is 14.8 AUROC points lower.

W1, Q3. Reproducibility and reuse

The Sites A/B corpus cannot be shared, limiting independent repetition of pre-training. Abbaspourazad et al. [1] report a similar restriction on sharing the Apple Heart and Movement Study sensor data used to train their wearable models. We will release code for pre-training, fine-tuning, and evaluation upon publication. Upon institutional approval, we will also make the pre-trained weights available to researchers under a data-use agreement, following the gated release approach used for MOTOR [8] and Context Clues [9], both ICLR papers with models trained on non-public clinical records. With these weights, researchers could extract frozen VitalFM embeddings for standard classifiers or multimodal models, fine-tune VitalFM on new outcomes and cohorts, and evaluate it on MIMIC-III. With the code alone, researchers can pre-train VitalFM on their own monitoring data. MIMIC-III, excluded from pre-training, provides an external evaluation dataset accessible to credentialed researchers.

AuthorsOpenReview ↗

Response to gQc1 (2/3): Motivation, resolution, impact, and venue fit

W2, Q1–Q2. Motivation, scope, and resolution

We appreciate the opportunity to clarify our motivation, which differs from the three possibilities outlined: we do not claim that two cohorts represent the general population, that VitalFM is deployment-ready, or that vital signs replace multimodal models. The original submission already stated this scope. The Limitations describe the work as a retrospective study and note that prospective performance and utility with other clinical modalities remain to be established. The Ethics Statement describes VitalFM as a research model that was not developed or evaluated as a clinical decision-making system. Retrospective evaluation is a standard approach for physiological foundation models [1, 2, 6, 7]; bedside use would require prospective clinical validation, a separate step beyond the scope of this paper. Regarding data scale, our pre-training corpus includes 79,334 patients across two health systems. For context, recent ICLR foundation models for other physiological signals were pre-trained on data from 13,517 participants (PaPaGei, PPG [2]), an archive of 14,987 subjects (CBraMod, EEG [6]), and 18 or 58 subjects (MVPFormer, intracranial EEG [7]).

Labeled cohorts for a given clinical question can be small, so deep models trained on outcome labels alone may fall short of handcrafted features; we ask whether pre-training on unlabeled monitoring removes this dependence on feature engineering. It does: the same architecture trained only on task labels falls well short of expert features, whereas pre-trained VitalFM achieves the highest mean AUROC and AUPRC.

We focus on two-second vital signs because our corpus and the MIMIC-III matched waveform subset retain second-scale measurements, and in our handcrafted-feature resolution analysis (Introduction, first paragraph; Appendix C.3), the two-second data outperformed coarser inputs in AUROC in 23 of 24 comparisons against hourly aggregation, and in 20 and 18 against five- and one-minute aggregation.

The intended impact is to support clinical prediction research with reusable representations of dense bedside monitoring. Rather than replacing multimodal models, VitalFM is designed as a vital-sign encoder that can be combined with encoders for other modalities. Its embeddings can serve as fixed features in multimodal models such as HAIM [4], or, in a system such as MedFuse [5], it could be fine-tuned alongside other encoders so that its vital-sign representation adapts to the task, which fixed handcrafted features cannot do. We discuss these potential uses in the revised Discussion and Conclusion.

W2, Q2–Q3. Impact and fit

Reproducibility, reuse, and motivation are addressed above (W1/Q3, W2/Q1–Q2). The work fits ICLR's scope in self-supervised representation learning and transfer learning, and prior ICLR work includes physiological and clinical foundation models trained on non-shareable wearable data [1] and non-public clinical records [8, 9], as well as multi-center ICU benchmarking (YAIB [3]).

We welcome further discussion of any remaining concerns.

References are listed in the reply below.

AuthorsOpenReview ↗

Response to gQc1 (3/3): References

References for the response above

[1] Abbaspourazad et al. Large-scale Training of Foundation Models for Wearable Biosignals. ICLR 2024.

[2] Pillai et al. PaPaGei: Open Foundation Models for Optical Physiological Signals. ICLR 2025.

[3] van de Water et al. Yet Another ICU Benchmark: A Flexible Multi-Center Framework for Clinical ML. ICLR 2024.

[4] Soenksen et al. Integrated multimodal artificial intelligence framework for healthcare applications. npj Digital Medicine 2022.

[5] Hayat et al. MedFuse: Multi-modal fusion with clinical time-series data and chest X-ray images. MLHC 2022.

[6] Wang et al. CBraMod: A Criss-Cross Brain Foundation Model for EEG Decoding. ICLR 2025.

[7] Carzaniga et al. A Foundation Model with Multi-Variate Parallel Attention to Generate Neuronal Activity. ICLR 2026.

[8] Steinberg et al. MOTOR: A Time-to-Event Foundation Model for Structured Medical Records. ICLR 2024.

[9] Wornow et al. Context Clues: Evaluating Long Context Models for Clinical Prediction Tasks on EHR Data. ICLR 2025.

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

This paper introduces VitalFM, a foundation model for self-supervised representation learning from dense, partially observed ICU monitoring data. The proposed architecture combines bidirectional state-space modeling along the temporal dimension with masked attention across physiological channels. The pretraining objective involves reconstructing an entirely masked vital-sign channel while preserving relationships with the remaining physiological signals. Importantly, the approach does not require explicit imputation of missing values. The model is pretrained on approximately 13.5 million hours of physiological monitoring data from 79,000 patients and evaluated on four downstream clinical prediction outcomes using data from two healthcare systems (Site A and MIMIC-III). The authors compare VitalFM against models based on handcrafted features, tabular foundation models, and supervised deep sequence architectures. Both frozen representations and end-to-end fine-tuning are evaluated. The reported results suggest that self-supervised pretraining substantially improves downstream performance, with additional evidence for cross-institutional transfer without destination-site refitting. Overall, the paper addresses an important problem in clinical representation learning and proposes a potentially interesting architecture for multivariate physiological time series. The experimental evaluation is relatively comprehensive, and the reported performance improvements are encouraging. However, several methodological and experimental questions remain insufficiently addressed, particularly concerning the architectural design choices, the separation of pretraining and evaluation data, the interpretation of the reported performance metrics, and the statistical analysis.

Critical strengths
  1. The paper addresses a relevant limitation of clinical prediction models that operate on hourly aggregated physiological measurements, potentially discarding clinically meaningful short-term dynamics. The use of dense ICU monitoring data for self-supervised pretraining is well motivated, particularly because labeled datasets for specific clinical outcomes may be relatively small. The scale of the pretraining corpus, comprising approximately 13.5 million monitoring hours from 79,000 patients, is an important strength.

  2. The bi-axial architecture, which combines temporal state-space modeling with masked attention across physiological channels, represents a potentially useful contribution. Separating temporal dependencies from cross-channel interactions is conceptually appealing for multivariate physiological monitoring data. In particular, explicitly accounting for missing measurements without conventional input imputation is an interesting design choice that may improve robustness in heterogeneous clinical datasets.

3.The evaluation includes a useful range of comparators, including LightGBM with handcrafted features, tabular foundation models, and supervised deep sequence models. The comparison between raw measurement grids, handcrafted features, and pretrained representations is particularly informative because it addresses whether foundation-model representations can reduce dependence on expert-designed feature engineering. The evaluation of both frozen representations and end-to-end fine-tuning is another strength.

  1. The reported performance difference between pretrained VitalFM and the identical architecture trained from scratch is substantial, averaging 14.8 AUROC and 8.4 AUPRC percentage points. This suggests that self-supervised pretraining, rather than architecture alone, plays a major role in the reported downstream performance.

  2. The inclusion of evaluations across two healthcare systems and experiments involving transfer without destination-site refitting is valuable. Cross-institutional generalization is particularly relevant for ICU models because patient populations, monitoring practices, and measurement availability may differ between institutions.

Critical weaknesses
  1. My main methodological concern relates to the motivation for combining bidirectional state-space modeling (Mamba) with masked attention across physiological channels. Both, Mamba and Transformer-based architectures, are established approaches for learning representations from multivariate time series. Although combining them may be beneficial, the paper should more clearly explain why this specific architectural decomposition is preferable to existing alternatives. If state-space modeling is applied exclusively along the temporal dimension and attention exclusively across channels, these components serve different purposes and are not necessarily redundant. However, the authors should explicitly justify this division of responsibilities. In particular, the following questions arise: • Why is state-space modeling preferable to temporal self-attention for physiological monitoring data? • Why is attention the preferred mechanism for cross-channel interactions, rather than state-space modeling or another channel-mixing operation?

  2. The paper should provide a transparent account of how patients, monitoring episodes, and healthcare institutions were separated across pretraining, downstream fine-tuning, validation, and final evaluation. This is particularly important for foundation models trained on large amounts of clinical data, where the same patient or hospitalization may contribute multiple monitoring windows. If downstream evaluation patients were also represented in the pretraining corpus, the evaluation would need to be interpreted as transductive or in-domain self-supervised learning rather than strictly independent transfer.

  3. The paper reports AUROC and AUPRC improvements across several clinical prediction tasks. However, AUPRC depends strongly on the prevalence of the positive outcome. Without reporting the positive-class prevalence for each downstream task and evaluation cohort, it is difficult to interpret the absolute AUPRC values and their practical significance.

  4. Another important concern is the statistical interpretation of the reported performance differences. The paper compares multiple architectures, representation-learning strategies, downstream tasks, evaluation datasets, and performance metrics. This creates a substantial number of statistical comparisons. It should be made explicit which improvements are statistically significant, how uncertainty was estimated, and whether the authors corrected for multiple testing.

  5. The proposed pretraining objective of reconstructing a withheld physiological channel while preserving relationships with the remaining signals is interesting.However, the motivation for using a Pearson-correlation-based objective requires further justification. Pearson correlation primarily captures linear dependence between variables. Physiological signals often exhibit nonlinear, state-dependent, delayed, and potentially nonstationary relationships. A loss based exclusively on Pearson correlation may therefore encourage the preservation of linear associations while failing to capture more complex dependencies. Possible alternatives include nonlinear dependence measures, or learned contrastive objectives that capture relationships beyond linear correlation.

An additional question concerns the temporal alignment of relationships: if the objective evaluates only contemporaneous correlations, it may fail to capture clinically important delayed interactions between physiological channels.

  1. Another concern relates to the pre-training window selection described in Appendix A.3. The authors use strictly non-overlapping windows, which may introduce boundary artifacts and potentially disrupt temporal dependencies across adjacent windows. At a minimum, the authors should empirically investigate the extent to which this design choice affects representation learning and downstream predictive performance.
Questions for authors
  1. What is the specific rationale for combining temporal state-space modeling with cross-channel attention? What is the advantage compared to alternative channel-mixing strategies?
  2. Were patients and monitoring episodes in the downstream test sets entirely excluded from pretraining? If not, how does this affect the interpretation of the reported transfer results?
  3. What are the positive outcome prevalences for each downstream task and evaluation dataset? Can the authors report random-classifier AUPRC baselines?
  4. Which performance improvements are statistically significant after correcting for multiple comparisons? What statistical tests and correction procedures were applied?
  5. Why was Pearson correlation selected for the correlation-preservation objective? Have the authors evaluated nonlinear dependence measures or objectives accounting for time-lagged relationships? Can they compare against alternative approaches such as constrative learning?
  6. How much of the observed improvement can be attributed specifically to the proposed architecture, rather than to self-supervised pretraining in general?
  7. How robust is the model to changes in missingness patterns, measurement frequency, and channel availability across healthcare systems?
  8. Can the authors assess potential boundary artifacts due to the non-overlapping window selection described in Appendix A.3?
5 comments
AuthorsOpenReview ↗

Response to weMG (1/3): Architecture, evaluation protocol, and statistics

Thank you for the constructive assessment. We address your comments below.

W1, Q1. Why Mamba over time and attention across vitals

Vital signs reflect a patient’s evolving physiological state, which makes a state-space model a natural fit for the time axis. This choice is also supported empirically: with patch encoding and cross-vital attention held fixed, approximately parameter-matched gated-attention and masked-Transformer temporal backbones trail bidirectional Mamba by 2.3/1.8 and 2.1/2.2 mean AUROC/AUPRC points with TabPFN-3 (Table 3). The vital axis serves a different role, set by the pre-training task: reconstructing an entirely withheld vital from the remaining ones requires combining information across vitals, even though which vitals are available changes from minute to minute. Masked attention provides a direct mechanism for this, letting the available vitals inform one another while naturally absent channels are excluded as attention sources. Mamba processes inputs in sequence, and the eight vital signs have no natural order. Each axis therefore uses the operation suited to its role: state-space modeling for vital-sign dynamics over time, and attention for exchange between vitals.

W2–W4, Q2–Q4. Evaluation protocol and statistical analysis

These details are reported in the manuscript, mainly in the appendix; to make them easier to find, the revision now summarizes them in the main text.

W2, Q2. Separation of patients, monitoring episodes, and institutions

MIMIC-III was excluded entirely from pre-training, Site B was used only for pre-training, and Site A pre-training episodes matched to downstream evaluation patients through identity-linkage records were excluded; all downstream splits are grouped by patient (Section 4.1, Appendix A.2).

W3, Q3. Positive-outcome prevalence and random-classifier AUPRC

Positive-outcome prevalence, which equals each task’s random-classifier AUPRC, ranges from 2.8% to 24.4% at Site A and from 1.3% to 13.0% in MIMIC-III (Section 4.1, Table A.2).

W4, Q4. Statistical significance after correcting for multiple comparisons

In addition to the two-sided paired patient-cluster bootstrap intervals and nominal p-values (Section 4.1, Appendix C.2), we now report Benjamini–Hochberg correction at a 5% false discovery rate as a sensitivity analysis: of the 128 comparisons, 70 are nominally significant and 64 remain significant, all favoring fine-tuned VitalFM, and none significantly favors a comparator (Table C.4).

AuthorsOpenReview ↗

Response to weMG (2/3): Correlation matching and pre-training

W5–W6, Q5. Correlation matching and alternative objectives

Our pre-training objective combines MSE reconstruction with an auxiliary Pearson correlation-matching term. We chose Pearson correlation because it is scale-free and directly measures the co-variation we aim to preserve. In the matched ablation, adding the correlation term reduces the held-out mean squared mismatch between decoded and observed correlations from 0.427 to 0.045, while maintaining similar reconstruction error. It also improves mean AUROC/AUPRC by 1.0/1.1 points with TabPFN-3 and 1.8/1.4 points with a linear probe.

Because the correlation term supervises only zero-lag Pearson correlation, we also assessed lagged Pearson (±1, ±5, and ±15 minutes) and zero-lag Spearman correlation, which captures monotonic nonlinear dependence, on held-out pre-training validation windows. Across the tested nonzero lags, the mean squared mismatch between decoded and observed target–context correlations is 0.050–0.055 with VitalFM versus 0.200–0.334 with MSE only; for zero-lag Spearman, it is 0.062 versus 0.429 (Section 4.6, Appendix C.6.3). Thus, although the correlation term supervises only zero-lag Pearson correlation, the tested lagged and rank-based associations are also better preserved, so its benefit extends beyond the contemporaneous linear associations it directly targets.

We did not pre-train nonlinear-dependence, lag-aware, or contrastive variants. Each would require design choices specific to ICU monitoring. A lag-aware loss would require choosing which delays to supervise and how to form valid shifted pairs. We did not add a nonlinear-dependence loss because we had not established which additional physiological relationships it should preserve or how best to measure them. A contrastive variant would require defining appropriate positive pairs or views: treating two windows from the same patient as positives can encourage similar representations for different clinical states, such as a stable day and a day of clinical deterioration. Augmentations such as amplitude scaling, used in waveform-based contrastive learning, are less straightforward for bedside vitals, whose absolute levels carry clinical meaning, such as a systolic arterial pressure of 80 versus 120 mmHg. Augmenting one vital independently can also produce physiologically implausible combinations with the other vitals. Our objective instead derives supervision directly from relationships among vital signs: reconstructing a withheld vital from the others and preserving its co-variation with them, without requiring contrastive positive pairs or additional augmented views. Both losses use observed measurements as targets. The matched MSE-only ablation above isolates the contribution of the correlation term.

Q6. Architecture and pre-training contributions

Pre-training provides the largest gain, while the architectural design also contributes to VitalFM's performance. Our randomly initialized control isolates the effect of pre-training: the identical architecture trained only on task labels performs substantially worse than pre-trained VitalFM (14.8/8.4 mean AUROC/AUPRC points lower), so pre-training contributes substantially to the observed improvement. With pre-training enabled, the architecture also matters: under the same pre-training protocol, bidirectional Mamba outperforms approximately parameter-matched gated-attention and masked-Transformer temporal backbones, and observation-aware gating adds further gains (Table 3). In the matched comparison without pre-training, retaining episodic blood pressure improved prediction, and the dedicated sparse encoder achieved higher AUROC than a shared convolutional encoder in most settings (Table C.6). Together, these comparisons show that the tested architectural choices contribute to prediction performance both with and without pre-training.

AuthorsOpenReview ↗

Response to weMG (3/3): Measurement availability and window boundaries

Q7. Missingness, measurement frequency, and channel availability

As the reviewer notes, handling missing measurements without imputation may help across datasets with different observation patterns. Across pre-training Sites A/B and downstream Site A/MIMIC-III, arterial pressure is observed at 24/32/16/31% of two-second positions and has no valid observation in 67/58/74/56% of input windows; the corresponding values for temperature are 8/29/4/3% and 90/63/94/96% (Section 4.4, Table A.3). VitalFM performs well across these differences, including when transferred between Site A and MIMIC-III without destination-site refitting, where it achieves the highest mean performance in 10 of 16 task–direction–metric comparisons against the three strongest handcrafted-feature pipelines (Section 4.5, Table 2). These results are consistent with robustness across the naturally occurring measurement patterns in the evaluated sites.

W7, Q8. Window selection and boundary effects

Non-overlapping 24-hour windows cover the monitoring corpus without processing the same measurements repeatedly. Any fixed-length input limits past context near its start and future context near its end. Overlapping pre-training would allow observations on both sides of a given boundary to appear together in another window, but individual inputs would still have boundaries. To test whether reconstruction degrades near input boundaries, we compared withheld-vital reconstruction error between edge and interior hours of held-out windows. Averaged across vitals, normalized RMSE was 0.0041 higher in the first hour and 0.0020 higher in the last hour than in interior hours, with confidence intervals excluding zero (Section 4.6, Appendix C.6.4, Figure C.3). These small differences suggest a modest boundary effect that diminishes toward the interior of the window. We did not pre-train with overlapping windows because the additional matched pre-training runs and downstream evaluation were beyond the time and compute available for this revision. These results therefore do not isolate the effect of non-overlapping window selection on learned representations or downstream prediction.

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Summary of manuscript revisions

We thank weMG for highlighting the value of learning from dense monitoring without hourly aggregation, using pre-training when labeled cohorts are small, testing whether pre-trained representations reduce reliance on expert-designed features, and evaluating transfer across health systems. We also thank gQc1 for noting the solid ablation studies and downstream experiments, and wnKD for noting that the model's design produces better predictions and that the results are presented thoroughly.

Several reviewers found it difficult to identify what the work contributes beyond its engineering and evaluation, and what insights it offers. We agree that the original manuscript could have made this clearer: the Introduction ended with a detailed recital of results rather than an explicit list of contributions; the reasoning behind each modeling choice was given in the method description but not drawn together; and the insights from the comparisons were not stated explicitly enough. We have revised the Introduction to state the contributions explicitly, the Discussion and Conclusion to state the insights supported by the results, and the Reproducibility Statement to specify what will be released (changes highlighted in blue):

  • Explicit contributions. The Introduction now lists the main contributions: to our knowledge, the first foundation model to learn representations jointly across vital signs from partially observed ICU monitoring at two-second resolution over day-long windows; a bi-axial architecture with dense and sparse within-minute patch encoders, bidirectional Mamba over time, and masked attention across available vitals, without imputing missing measurements; and two physiologically motivated pre-training objectives that reconstruct an entirely withheld vital sign from the remaining signals and match correlations between the decoded target and each decoded context vital to those of the corresponding observed pairs.
  • Insights and future directions. The Discussion and Conclusion section now states three insights supported by the results: self-supervised pre-training makes deep learning on raw monitoring effective when labeled data are limited; the physiologically motivated pre-training objective turns the interdependence among vital signs into an effective source of supervision; and partially observed ICU monitoring can be modeled as it is recorded, without imputing missing measurements, supported by matched architectural comparisons and by transfer across sites without refitting. It also identifies integration with multimodal clinical models as a concrete next step, either through frozen VitalFM embeddings, which perform well with standard tabular classifiers, or by fine-tuning VitalFM alongside encoders for other modalities.
  • Reproducibility and reuse. The Reproducibility Statement now specifies release of pre-training, fine-tuning, and evaluation code and, upon institutional approval, access to pre-trained weights under a data-use agreement.

We also clarified the evaluation protocol and added three analyses: a multiple-comparison sensitivity analysis, an evaluation of lagged and rank-based cross-vital associations, and a window-boundary reconstruction analysis, as detailed in the individual responses. No previously reported results have changed.

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