acceptodds
Under review as a conference paper at ICLR 2027

FOCUS: A Foundation Model for Wearable A-Mode Ultrasound

Abstract

Wearable A-mode ultrasound (AUS) enables continuous, non-invasive monitoring of deep tissue, and advances in conformable transducers and low-power electronics have enabled increasingly large and diverse wearable datasets. Because wearable probes communicate over bandwidth-limited wireless links that cannot stream raw echo data continuously, processing must largely run on the device, calling for compact models that can be adapted to each user with limited labeled data. However, learning approaches for wearable AUS are developed for individual tasks, subjects, or acquisition systems and trained from scratch on small datasets, and no foundation model (FM) exists for this setting. We introduce FOCUS, a compact FM for wearable AUS (6.3 M encoder parameters), pre-trained on 24.7 million unlabeled A-mode scans from five wearable and benchtop acquisition systems and multiple body locations, including the neck, upper and lower limbs. A frequency-aware multi-tokenizer maps raw signals acquired at different sampling frequencies to patches spanning an approximately constant physical depth. We evaluate FOCUS on eight subject-specific downstream tasks from five wearable datasets, spanning hand-gesture, forearm-position, and gait-phase classification, as well as upper- and lower-limb kinematic regression. Pre-training improves mean performance over the same architecture trained from scratch on all eight tasks, and fine-tuning with only 40% of the labeled training data outperforms training from scratch with the complete labeled dataset on all eight. FOCUS also outperforms the previously reported results on seven of the eight benchmarks. Across three model capacities (0.8 M, 6.3 M, and 85 M parameters), downstream performance generally improves with model size, and larger models benefit more consistently from additional pre-training data. FOCUS requires 669–856 MMACs per channel update under sequential inference, a compute budget compatible with future on-device deployment for wearable AUS.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
foundation models, self-supervised learning, representation learning, wearable sensing, A-mode ultrasound, masked autoencoders, heterogeneous sensing, biomedical signals, label efficiency

Reviews

Among:
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1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_r5wYOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

The authors propose a foundation model for wearable A-mode ultrasound. The model is pre-trained on ~24.7M unlabeled scans from five platforms, including a newly collected multi-site dataset. They propose a frequency-aware multi-tokenizer that adjusts the patch size according to the sampling frequency. Later linear projections map these patches into token sequences with the same embedding dimension. The model is pre-trained through masked reconstruction, processing each channel independently with a shared encoder. Experiments on different ultrasound benchmarks show improvements over the same architecture trained from scratch on all eight tasks. Fine-tuning with 40% of the labeled training data also outperforms training from scratch with the full dataset on all eight tasks.

Critical strengths
  • The paper introduces a foundation model for wearable A-mode ultrasound through large-scale pre-training.
  • The frequency-aware tokenizer reflects the relationship between sampling frequency and physical depth in ultrasound. The design is simple and easy to understand.
  • The paper provides a clear and reusable framework for pre-training and evaluating A-mode ultrasound models.
Critical weaknesses
  • The simple method is a strength. However, the paper lacks analysis of why its main design choices work better than other alternatives. Such comparisons are particularly important for a work that aims to provide a foundation for future research in this modality.
  • The frequency-aware tokenizer is an important component, but the paper does not report comparisons with a fixed patch size across sampling frequencies or with resampling all signals to a common sampling frequency. These comparisons would help clarify the benefit of the proposed tokenizer over simpler alternatives and its contribution to the reported improvements.
  • The choices of masked reconstruction and a shared encoder are also not sufficiently examined. Comparisons with other pre-training objectives (e.g., contrastive learning) would help explain the role of reconstruction. Similarly, comparisons with channel-specific encoders, or with pre-training that jointly uses multiple channels, would help clarify the benefits of shared weights.
  • As described in the limitations, the evaluation is limited to subject-specific models. Evaluating transfer to unseen users would help assess how well the pre-trained model generalizes across users.
Questions for authors

The release of the code, checkpoints, and dataset would be important. Clear description of how to access and replicate the existing results would be important for future comparisons.

4 comments
AuthorsOpenReview ↗

Reply to reviewer r5wy

We thank the reviewer for recognizing the value of large-scale AUS pre-training and the reusable framework. We agree that understanding the contribution of individual design choices is essential for informing future research.

We address the specific weaknesses below:

1. Frequency-aware tokenization vs simpler alternatives

This is reported in “Applicable to all reviewer - Input harmonization strategies”

Following your suggestion, we compared the frequency-aware multi-tokenizer with two simpler alternatives: resampling all signals to a common 20 MHz grid, and interpolating each scan to 800 samples, both followed by a single tokenizer with a fixed patch size. With the full corpus, the three perform equivalently after fine-tuning, so frequency-dependent routing gives no advantage. It is also the weakest option when a sampling rate is absent from pre-training: with the 8 MHz WULPUS data held out, hand-pose accuracy is 67.3% against 70.4% for resampling. We therefore replaced it with a single tokenizer on a common 20 MHz grid, which keeps a fixed physical depth of 0.308 mm per token on every platform (Appendix D.1, Table 11).

2. Contribution of masked reconstruction and comparison with contrastive approaches.

This is reported in: “Applicable to all reviewer - Extended the ablation studies with different pre-training objectives”

We added a wav2vec-inspired contrastive pre-training comparison using the same backbone as the main model, corpus and downstream evaluation protocols (Appendix D.2, Table 12). This tests whether reconstructing echo waveforms or discriminating latent representations yields more useful features for AUS tasks. The downstream evaluation is still running; we will report the results in a follow-up comment.

3. Benefit of shared channel encoding

Shared, independent encoding allows pre-training across systems with different channel counts and configurations without requiring channel correspondence between datasets (§3.3). This is the design rationale; we agree that it does not establish superiority over channel-specific or jointly trained multichannel encoders.

We added a comparison of CNN fusion and a flatten-plus-linear readout to examine how independently encoded channels should be combined (Appendix D, Table 13). This comparison is still running with the updated main model, and we will report it in a follow-up comment. It isolates downstream aggregation, not encoder sharing. Channel-specific encoders and joint multichannel pre-training remain untested, and we retain them as future directions (§5). This is also reported in: “Applicable to all reviewer - Extended the ablation studies with different pre-training objectives”

4. Does the model generalize to unseen users?

Our evaluation is subject-specific, following the reference benchmark protocols (§4.2; Appendix C.1), and therefore does not establish unseen-user generalization.

The new WULPUS-exclusion experiment (also reported in Applicable to all reviewers- Leave one platform, dataset and anatomy out experiments) provides complementary evidence of transfer to an unseen platform and forearm anatomy: PosePos-USVR hand-pose balanced accuracy is 70.4%, compared with 75.5% when WULPUS is included, and HWR-23DoF RMSE is 13.17° versus 13.26° (§4.6; Table 9). We explicitly distinguish these results from unseen-user transfer, which remains future work.

5. How can the code, checkpoints and data be accessed and the results reproduced?

The code and model checkpoints will be made publicly available after review to preserve anonymity. We’ll also open-source the WULPUS Multi-site dataset specifically collected for this work. We believe this open-sourcing of both code, model checkpoints, and data will help the community and foster more subsequent research.

Thank you for your detailed response. I really appreciate the clarifications regarding the scope of the work and the commitment to releasing the code and data. I also look forward to seeing the contrastive learning results, which I believe will be helpful. However, I still have one critical concern. If the simpler alternatives perform as well as or better than the original frequency-aware multi-tokenizer, and the main method is now being replaced, I feel this is a substantial change for a rebuttal. I considered the frequency-aware tokenizer to be one of the key technical contributions of the original submission. Therefore, I would like to ask whether the authors consider the main contribution of the work to have changed, and how they would position the novelty of the revised method. At this point, this concern makes it difficult for me to reconsider my original rating.

AuthorsOpenReview ↗

Reply to reviewer r5wY

We thank the reviewer for the follow-up and for engaging so closely with our work. We address the two questions directly.

The key contributions of the paper remain unchanged, and the additional experiments conducted during the rebuttal period strengthen them further. We position the novelty at the level of the modality and the framework, not of a single architectural component:

  • The first foundation model for A-mode ultrasound (AUS), pre-trained on A-mode signals and evaluated for transfer across acquisition systems and downstream tasks.
  • Heterogeneous pre-training across hardware platforms. Data from benchtop systems to wearable devices are combined into a single framework, and the approach applies from linear-array probes down to a single transducer.
  • A systematic, controlled study of design choices. We compare input harmonization strategies (resampling vs frequency-aware multi-tokenizer vs interpolation), pre-processing strategies and pre-training objectives (masked reconstruction vs contrastive) under consistent conditions, including different pre-training corpus compositions. The contrastive comparison you were waiting for is complete: masked reconstruction is better than a wav2vec 2.0 objective on seven of the eight tasks after fine-tuning and on all eight with a frozen encoder (Appendix E.2, Table 12; numbers in our follow-up comment to all reviewers). Showing which choices matter, and that simple harmonization is sufficient and more robust, is a non-obvious result for this modality and a useful reference point for future work.
  • Edge deployment of the pre-trained model, which is required for the wearable, low-power applications where AUS is most relevant. The model runs on a low-power microcontroller (160.5 ms and 12.7 mJ per scan), and we report its current rate limits.

The rebuttal experiments reinforce these contributions. The corpus-composition analysis (Section 4.6, Appendices D.3 and E.1) extends the systematic study and shows that the benefits of heterogeneous pre-training hold across corpus configurations and do not depend on a specialized input representation. The extended label-efficiency analysis, now including the CNN baseline (Figures 2 and 6), shows that the fine-tuned foundation model stays ahead of CNNs trained from scratch as training data increase. The contrastive results (Appendix E.2) further support our choice of masked reconstruction as the pre-training objective.

What changed is one component of the architecture: the input harmonization strategy. Following experiments requested by the reviewers, the frequency-aware multi-tokenizer has been replaced by a simpler resampling-based approach. We understand why the reviewer saw the tokenizer as a key contribution, given its prominence in the original submission. However, it was one way of handling heterogeneous inputs, in service of the main goal of building the first foundation model for AUS.

To provide more details, with full-corpus pre-training, the multi-tokenizer and resampling perform on par (Appendix E.1, Table 11): on this setting alone, we could have kept the original method as the reference implementation. However, when WULPUS data are excluded from pre-training, resampling outperforms the multi-tokenizer (Figure 7; Appendix E.1, "Transfer to a platform absent from pre-training"). The multi-tokenizer therefore offers no advantage in either configuration, while resampling is equal or better in both. We adopted resampling as the reference configuration and report both results openly. This decision was driven entirely by results: presenting the configuration best supported by the evidence, instead of keeping the original design because it was already in the submission, is in our view the scientifically correct choice.

This also resolves a question the original submission left open: since simple resampling is sufficient, the gains come from AUS pre-training and the data, not from a specialized input representation. We believe this strengthens the paper's main claim.

We will release all code, models and pipelines needed to reproduce the evaluations in the paper. Together with the systematic comparison of design choices, we believe this provides a strong, reproducible baseline and a shared toolchain that the community can build on, so that more specialized methods for AUS can be developed and compared under consistent conditions.

Again, I really appreciate your response. I appreciate the additional experiments and agree that establishing a foundation model for a new modality is valuable, especially in our field. However, my main concern remains. I believe that an important research contribution in developing foundation models for new modalities is identifying and addressing the unique challenges of those modalities. The frequency-aware tokenizer was, to me, the most distinctive technical contribution in this regard. Given that simpler, existing techniques perform equally well or better, I am not yet convinced that the work provides sufficient new insights beyond demonstrating that a combination of established techniques works well for A-mode ultrasound. While I appreciate the systematic analysis and the value of providing a strong baseline, this concern remains insufficiently addressed for me to revise my rating.

Reviewer_gxipOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

FOCUS is a compact foundation model for wearable A-mode ultrasound, pretrained through masked reconstruction on 24.7 million scans from five acquisition platforms. It selects patch sizes according to sampling frequency to obtain approximately comparable physical depth per token, and adapts independently encoded channels through a convolutional fusion module. The evaluation covers eight subject-specific classification and regression tasks across five datasets. Pretraining improves mean performance over the same architecture trained from scratch on all eight tasks. The paper also investigates frozen representations, label efficiency, model capacity, and pretraining data scale.

Critical strengths

The paper provides useful evidence for shared pretraining in a comparatively underexplored sensing setting. The evaluation spans several acquisition systems and both classification and regression, including UltraPro, whose acquisition platform is absent from pretraining. This gives the contribution value beyond improving a single task.

The experimental comparisons support the practical benefit of pretraining. Table 2 includes the same architecture trained from scratch, a frozen pretrained encoder, full fine-tuning, and a CNN with approximately matched parameter count. Fine-tuning improves mean performance over both scratch baselines on all eight tasks. The label-fraction experiments provide additional evidence that the pretrained initialization remains useful with fewer labeled examples.

Critical weaknesses

The contribution of the frequency-aware tokenizer is not isolated. The MAE backbone follows prior ultrasound work, and the multiple-patch design is explicitly inspired by MOIRAI. The distinctive methodological step is therefore the physical-depth-based routing, but the ablations examine preprocessing and ALiBi rather than this routing rule. It remains unclear whether the proposed tokenizer improves transfer over simpler input harmonization. A comparison with a fixed-sample tokenizer and with common-grid resampling, using the same corpus and objective with reasonably matched capacity and computation, would establish how much this design contributes.

Low-dimensional graph variation is not sufficient evidence that patient graphs are nearly identical. Section 3.4.1 reports an effective rank of 1.72 and 84.9% of the variance along the leading direction. These measurements describe the concentration of variation, not its magnitude or relevance to prediction. A graph family varying mainly along one direction can still differ substantially across patients and encode useful information. The reported 73% departure from the original prior also does not measure differences between patients. Table 3 provides a useful static-graph control, but unchanged classes at one threshold do not establish negligible effects on continuous predictions. Please quantify distances between patient graphs and, with the trained model fixed, replace each patient-specific graph with the training-set mean graph and measure the changes in gene representations and predicted probabilities. This would distinguish a low-dimensional but functional conditioning mechanism from one with little patient-specific effect.

Questions for authors
  1. Does the low-dimensional graph variation persist when using a nonsaturating edge generator on a task with established molecular signal?

  2. With the trained model fixed, how do gene representations and predicted probabilities change when each patient-specific graph is replaced by the training-set mean graph?

2 comments
AuthorsOpenReview ↗

Reply to reviewer gxip

We thank the reviewer for recognizing the value of shared AUS pre-training and the evidence provided by the downstream and label-efficiency experiments.

Changes in the manuscript arising from comments common to all or more than one reviewer are reported in the comment above. We address the comments below:

Contribution of frequency-aware tokenization.

This is also reported in “Applicable to all reviewer - Input harmonization strategies”

We agree that the original experiments did not isolate the benefit of frequency-dependent routing. We therefore compared it with two simpler strategies under the same corpus, objective and protocols: resampling all sources to a common 20 MHz grid, and interpolating each scan to 800 samples, both followed by a single tokenizer. With the full corpus, the three are equivalent after fine-tuning, so frequency-dependent routing gives no advantage. It is the weakest option when a sampling rate is absent from pre-training: with the 8 MHz WULPUS data held out, hand-pose accuracy is 67.3% against 70.4% for resampling, and HWR-23DoF RMSE is 14.09° against 13.17°. We replaced the multi-tokenizer with a single tokenizer on a common 20 MHz grid, which keeps a fixed physical depth of 0.308 mm per token (Appendix D.1, Table 11).

Further evidence and practical scope.

We added comparisons of reconstruction versus contrastive pre-training and CNN versus flatten-plus-linear readout (Appendix D, Tables 12–13). These runs are being completed with the updated main model; we will report the findings in a follow-up comment. This is also reported “Applicable to all reviewer - Extended the ablation studies with different pre-training objectives”.

We also demonstrate GAP9 deployment: embedding extraction requires 153 ms per scan, or approximately 0.61 s and 51 mJ per four-channel prediction (§4.7; Appendix E), for the backbone at the final input length. This establishes embedded execution while explicitly acknowledging the current throughput limitation. This is reported in “Applicable to all reviewer - Demonstrated edge deployment”

Q1–Q2: Patient graphs and gene representations.

These questions, and the accompanying discussion of graph rank and patient-specific conditioning, appear to concern another submission. FOCUS operates on ultrasound scans and contains no patient-graph or gene-representation components. We would be grateful for clarification and would be happy to address any further questions about our work.

AuthorsOpenReview ↗

Update for reviewer gxip

The isolation of the tokenizer that you asked for is complete, with final numbers (follow-up comment to all reviewers; Appendix E.1, Table 11). With the full corpus, the multi-tokenizer, fixed-length interpolation and common-rate resampling perform comparably after fine-tuning. With the 8 MHz source (WULPUS) held out of pre-training, the multi-tokenizer is the weakest on all four affected tasks (PosePos-USVR pose 67.3% against 70.9% for resampling; HWR-23DoF 14.09° against 13.43°); paired within subject, resampling is better on 13 of the 16 subject-task pairs (two-sided sign test, p = 0.021). The main model now uses resampling with a single tokenizer. The objective and readout comparisons are also complete (Appendix E.2 and E.3, Tables 12 and 13). We would be glad to answer any remaining question before the discussion closes.

Reviewer_hHiDOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
3
Soundness
3
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Paper summary

This paper considers training foundation models on A-Mode ultrasound, with a particular focus on learning from heterogeneous acquisition systems and different body locations. The paper pre-trains a masked autoencoder with per-sampling-rate tokenizers on over 2 million examples, and applies their model both as a frozen encoder or with full fine-tuning on different downstream tasks. The results show consistent gains over training the same architecture from scratch and compared to a simpler CNN baseline, outperforming supervised models even when given substantially less supervised task labels. The paper also conducts scaling experiments to show how more data helps larger models, and discusses the potential for their model to be compatible with on-device deployment.

Critical strengths
  1. I appreciate the simple and physiologically motivated design. Matching patches to actual tissue depth is a well motivated idea that induces domain knowledge into new architectural improvements from past work (MOIRA's adaptive patch design). This enables the work to scale to using substantially more domains and heterogeneous data sources.

  2. The empirical results are presented clearly and are easy to follow. The main results combined with the label efficiency arguments are good evidence of their approach learning something meaningful.

Critical weaknesses
  1. The primary weakness is that his paper lacks methodological novelty and simply applies existing machinery with small tweaks to a new approach for their new setting. This in and of itself is not necessarily bad, but the evaluation depth is too limited to actually test the core claims that their tweaks improve performance, that adapting to the heterogeneous setting, or that their approach is really an improvement over baselines and past work. Without any of these, it's hard to take away any learnings from this work beyond simply applying a well-established approach to a new application.
  • A primary motivation for the work is being able to scale to pre-train from heterogeneous sources. However, the benefit of this is never actually tested. There is no single source or leave-one-source-out baselines that really show that learning from these different sources is beneficial across the board.
  • Their primary architectural tweak is matching patches to tissue depth. However, they never compare this approach to simpler baselines, such as resampling all data sources to the same sampling rate. Even more, they did not evaluate on any unseen sampling rates, which the resampling approach is amenable to, but their approach is unable to handle.
  • The actual improvement over the baselines are confounded by two things: 1) super small sample sizes resulted in large margins of errors (without any statistical significance tests, most of these intervals overlap), and 2) the fully supervised transformer approach performs substantially worse than the baseline CNN and past work. This inflates the delta columns and the label efficiency plots, as the baseline being used is not the strongest one possible.
  1. The on-device argument is asserted as a major contribution of the work in the abstract, but has very limited evidence and discussion. The discussion around the on-device side should come with more results and evidence, or should be de-emphasized.
  • The works considers that the weights would be 6.5-6.7MB under quantization schemes, but a) never showed this true with evidence, and b) never considered evaluating their model under the quantization scheme, as the small model could degrade in performance. Given how close the model's performance is to the baseline CNN, if quantization does hurt the foundation model accuracy, it's unclear why this would be preferred over a simpler CNN.
  • The MMAC number cited is per channel update. However, given the sampling rate, wouldn't this actually result in substantial compoute per second?
Questions for authors
  1. How much does scaling to heterogeneous sources actually help FM training for downstream tasks?
  2. How do simpler/different approaches for handling variable sampling rate, which could handle unseen sampling rates during training, perform compared to the proposed approach?
  3. How does the label efficiency argument change if the baseline it the CNN instead of the fully supervised proposed architecture?
  4. How does on-device argument hold up in real settings, with quantization and actual updates per second?
  5. Is their leakage of the same subject across training and test? The split seems to be by trial/body location instead of by subject. What is the potential for leakage given the model could learn a person's anatomy during training?
5 comments
AuthorsOpenReview ↗

Reply to reviewer hHiD (1/2)

We thank the reviewer for the constructive comments. Your criticism and the limitations you highlighted motivated additional ablations and explorations, which we believe have strengthened the contribution of this work. In the “Applicable to all reviewers” comment, you can find a description of the changes in the manuscript arising from comments shared by more than one reviewer.

We address the main concerns and specific questions below:

Improved take-away learnings and architectural explorations: thank you for pointing this out. It is very important to us that the paper has a clear scientific take-away and will not leave readers feeling like they learned nothing. To this extent we have expanded the evaluation of the original paper to address three additional questions:

  • Which pre-training objective is better suited to A-Mode Ultrasound (AUS)?

Comparing masked reconstruction with wav2vec-inspired contrastive learning tests whether reconstructing echo waveforms or discriminating latent representations provides more useful features for downstream AUS tasks (Appendix D.2, Table 12). The downstream evaluation of the contrastive model is still running; we will report the comparison in a follow-up comment.

  • How to best combine independent ultrasound channels?

We compare CNN-based fusion with a flatten-plus-linear readout to test whether explicitly learning local interactions across channel features improves downstream prediction (Appendix D, Table 13). This comparison is still running with the updated main model; we will report it in a follow-up comment.

  • What is the best approach to treat heterogeneous AUS data? This is also reported in “Applicable to all reviewer - Input harmonization strategies” and explicitly addressed below (Q2).

We think these experiments enhance the research questions explored by the paper by a considerable amount. We have also revised the discussion to emphasize these findings.

Q1. How much does heterogeneous pre-training help downstream performance?

We enhanced our ablation experiments by excluding all WULPUS recordings from the pre-training data. This removes both the downstream acquisition platform (WULPUS) and all forearm acquisitions from the pre-training (Table 1). After fine-tuning, we see that on PosePos-USVR, hand-pose balanced accuracy changes from 75.5% to 70.4%, and on HWR-3DoF the RMSE increases from 9.63° to 10.00°. On HWR-23DoF the RMSE is unchanged (13.26° versus 13.17°). These results showcase that the model can transfer to a completely unseen platform (WULPUS) and anatomical site (forearm) (§4.6; Appendix C.6, Table 9).

Crucially, these excluded-platform models still improve over training from scratch: 70.4% versus 54.9% on PosePos-USVR hand pose, 10.00° versus 10.09° on HWR-3DoF, and 13.17° versus 15.86° on HWR-23DoF (Tables 2 and 9). Thus, the benefits do not depend exclusively on pre-training exposure to the downstream platform or forearm recordings. We agree that this does not establish that increasing source diversity is uniformly beneficial, since source composition and data volume change together. Such a study needs more open raw ultrasound data from diverse devices and body locations; recently released collections of pre-beamformed data such as Open-H-RF (https://open-h.github.io/Open-H-RF/) are a step in this direction.

Q2. How do simpler approaches to variable sampling rates compare?

You asked for this comparison and for evidence at an unseen sampling rate; both are now in the paper (Appendix D.1, Table 11). Resampling all sources to a common 20 MHz grid, followed by a single tokenizer, gives results comparable to the multi-tokenizer when the full corpus is used for pre-training. However, the two approaches differ when the WULPUS (8 MHz) data is held out of pre-training. In this case, the multi-tokenizer has no branch for that rate, so each token spans 0.77 mm, 2.5 times the depth seen in pre-training. Resampling keeps 0.308 mm per token and transfers better (hand pose 70.4% versus 67.3%, HWR-23DoF 13.17° versus 14.09°). We therefore adopted resampling as the main model; the depth-matching idea you highlighted is retained and is now exact on every platform. Holding out WULPUS changes rate, platform and anatomy together, so we compare the strategies under the same exclusion. The third experiment (fixed-length interpolation) performs similarly on our corpus, where most sources cover 30 to 38 mm, but the depth per token depends on the acquisition depth.

AuthorsOpenReview ↗

Reply to reviewer hHiD (2/2)

Q3. Does the label-efficiency advantage hold against the CNN baseline?

We are repeating the label-efficiency analysis with the BaseCNN as the reference, using the updated main model. These runs are still in progress; we will report them in a follow-up comment.

Q4. Does deployment remain practical after quantization and at realistic update rates?

This is an extremely relevant and practical question, and we decided to try it out. To this end, we apply INT8-bit post-training quantization to FOCUS, reducing the model size to around 6.5 MB. And interestingly, post-training quantization preserves downstream task performance with only around 0.8-point degradation in accuracy on the UltraPro gesture classification task and 0.12° RMSE degradation on HWR-23DoF (full table of results in Appendix E.1, Table 14). We will confirm the exact quantization results in a follow-up comment.

We also demonstrate actual hardware deployment on a low-power edge microcontroller (GAP9 SoC), and this is, to the best of our knowledge, the first deployment of an AUS foundation model at the edge.

Since each scan is resampled to 20 MHz before tokenization, every token represents a fixed physical depth of approximately 0.31 mm. The evaluated scans cover an imaging depth of approximately 3.8 cm, corresponding to 124–125 tokens per scan. At this sequence length, the backbone processes a single scan in 153 ms, consuming 12.7 mJ at 82.8 mW on GAP9. On-device resampling (e.g.: WULPUS scan from 8 to 20 MHz) has a negligible contribution (0.28 ms and 5 µJ on WULPUS).

The time per prediction, and therefore the pulse repetition rate (PRR) that can be processed without skipping scans, depends on how the channels are acquired; we now distinguish the two cases in §4.7. If all channels are acquired concurrently, each pulse yields C scans and every embedding must be recomputed before the task head: for HWR-23DoF (C = 4) this takes approximately 0.62 s and 51 mJ (four backbone evaluations, 0.61 s and 50.7 mJ; head, 4.5 ms and 0.24 mJ), which limits the PRR to about 1.6 Hz (0.8 Hz for the eight channels of UltraPro). If the channels are acquired sequentially, as on WULPUS, each pulse yields one scan, the embeddings of the other channels are reused and only the new scan is processed: each prediction update takes 157.7 ms, which limits the PRR to about 6.3 Hz, i.e. about 1.6 Hz per channel for C = 4 (§4.7; Appendix E.2).

In the revised manuscript, we also clarify the distinction between sampling frequency and pulse repetition rate (PRR). The MHz sampling frequency refers to the acquisition of samples within each ultrasound echo trace, corresponding to the acoustic time-of-flight and therefore the tissue-depth axis. It does not determine how frequently new scans are acquired. Instead, successive scans are acquired at the PRR, while the complete-frame acquisition rate also depends on the number of channels when sequential excitation is used. We now report the PRRs in Table 3 and explicitly distinguish acquisition rates from measured inference throughput in §4.7.

Finally, we discuss the practical limitations of the current implementation in §4.7 and §5. While our results demonstrate that FOCUS can execute on a low-power microcontroller with limited accuracy degradation, both limits are below the native acquisition rates (5–20 Hz per channel, Table 3), so intermediate scans are skipped, and a complete refresh of all channels (about 0.6 s) exceeds the 100–300 ms latency budget typically required by time-critical applications such as prosthetic control. Reducing this latency through weight-transfer optimization, model distillation, and early channel fusion remains an important direction for future work (§5).

Q5. Could participant overlap or the evaluation splits cause leakage?

Our downstream evaluation is explicitly subject-specific: training and test partitions contain the same participant, following the original benchmark protocols. It measures adaptation within a participant, including held-out sessions where applicable, rather than unseen-user generalization (§4.2). Appendix C.1 details chronological splits for UltraPro, session-held-out evaluation for PosePos-USVR, HWR-3DoF and HWR-23DoF, and trial-held-out evaluation for K2MUSE.

Participant identities were anonymized by the source authors, so we cannot reliably verify identity overlap across independently collected datasets. The WULPUS-exclusion experiment nevertheless removes all WULPUS recordings from pre-training, ruling out pre-training exposure through that source while retaining improvements on WULPUS downstream tasks (Table 9). We will state this distinction explicitly: it strengthens the evidence for transfer, but does not establish unseen-subject generalization.

I appreciate the new experiments and updated results throughout. I believe many of these new results help answer the main questions I have. However, I believe they also validate many of the concerns I had about the paper, and many of the new results reduce the novelty and change the paper in meaningful ways that require further scrutiny. The pending claims can't be validated yet, though the contrastive setup that the authors are testing is not a standard one and requires more discussion and research.

  1. I believe the move from the frequency-aware tokenization to resampling is sound and correct. However, this drastically reduces the novelty of the paper, where frequency-aware tokenization was a key aspect of the methodological contribution that was originally promised. I also believe this is a major change to the paper that requires more review and more scrutiny, and is not simply a small change that the rebuttal time is meant for.

  2. The leave-one-out experiment presented her is compared to the Transformer that had substantially worse performance compared to the Base CNN. The gains seem to be much smaller compared to this baseline, undermining the performance of the proposed model under the heterogeneous pre-training.

  3. The deployment experiments are nice and seem sound, but confirm my fears regarding the overclaiming regarding the the potential for deployment. The models are not ready for on-device deployment without reduced rates, which once again takes away a major novelty claim for the paper. I also think it would be valuable to understand whether a more basic CNN would be more on-device ready, given the small gap difference between the proposed model the base CNN.

Overall, the new results validate my concerns but improve soundness. I believe the novelty of the work is quite limited and I will keep my score, though I appreciate the new results solidifying many of my open questions.

Reviewer_DcYwOpenReview ↗
Rating
4
Confidence
3
Informativeness
3
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Paper summary

This paper appears to be the first serious attempt to create a foundation model for wearable A-mode ultrasound (AUS). Typical A-mode ultrasound uses a single semi-focussed ultrasound transducer, producing a 1-dimensional signal where tissue depth (essentially acoustic time delay) is the independent variable. Existing ultrasound foundation models require a 2-dimensional image (or video). Also, some (but not all) AUS AI systems process the raw "RF"/acoustic waveforms, whereas typical B-mode ultrasound AI requires input of human-understandable demodulated images (raw beam-formed waveforms -> bandpass filtering -> rectification -> envelope detection -> time gain compensation -> 2D B-Mode image -> normal ultrasound AI). This paper creates and trains an AUS foundation(al) model that can handle multiple types of AUS transducers, applied to multiple anatomic targets, using multiple AUS depth resolutions (which result from using different acoustic frequencies), to infer multiple anatomic/physiological clinical values. Their model can ingest 1D input in multiple formats: raw ultrasound waveforms, semi-processed (bandpass filtered) waveforms, and post-envelope-detection 1D AUS scan-line "images." The paper has a (mostly) thorough analysis, and the label-efficiency studies are particularly compelling.

Critical strengths

Creating a first-of-its-kind foundation(al) model for wearable A-mode ultrasound (AUS) is a major contribution. Thorough experimentation shows consistent improvements when using this model as pre-trained weights for a wide variety of application-specific fine-tuning scenarios.

Critical weaknesses

Their foundation model was not tested on unseen domains, and the authors did not demonstrate improved generalization to unseen uses. There is a fair question of what it means to be a "foundation model" within a narrow application like AUS. The authors clearly demonstrated they made a great contribution with a new pretrained general-purpose AUS encoder. They did not prove they achieved generalized learning that enables zero shot or few-shot transfer to new domain, so "foundation model" may be a stretch. I suggest the authors soften their claim to something like "created a pre-trained, general-purpose AUS backbone as a first step toward creating a domain-specific AUS foundation model. Future work towards a complete AUS foundation model will evaluate zero-shot and few-shot transfer to new AUS domains." This paper would substantially benefit from adding unseen-subject transfer experiments.

Major (not critical) weaknesses include possible lack of preservation of high-acoustic-frequency detail when encoding to 0.3mm patches, and they should site a wider range of time-series foundation models and biosignal foundation-models. They might also compare their model against some self-supervised learning baselines. I would be better if they added 3 types of leave-one-out pretaining experiments: leave-one-platform-out pretraining, leave-one-dataset-out pretraining, leave-one-anatomy-out pretraining.

Questions for authors

Please slightly revise your title and soften your claims, to clearly state you've proven the utility of your pre-trained, general-purpose AUS encoder/backbone, and that you are working towards showing true foundation-model generalization that enables use on new AUS domains. I also think you could more clearly take credit for producing a model that accepts as input both raw waveforms as well as post-envelope "pixel" intensities; I had to read through the appendix to understand that you made this impressive accomplishment.

3 comments
AuthorsOpenReview ↗

Reply to reviewer DcYw

We thank the reviewer for the positive assessment of our paper, particularly for recognizing the contribution of a general-purpose AUS encoder and the value of the label-efficiency experiments. We have made changes to the paper according to your suggestions; they are as follows:

Changes in the manuscript arising from comments common to all or more than one reviewer are reported in the comment above. We particularly invite the reviewer to consider the leave-one-platform-out experiment, which addresses one of the “Critical weaknesses” of your review.

We address the remaining reviewers’ comments below:

  1. Leave one platform, dataset and anatomy out experiments: reported in the “Applicable to all reviewers” comment.
  2. Comparison with self-supervised baselines: reported in the “Applicable to all reviewer - Extended the ablation studies with different pre-training objectives”
  3. Scope, terminology and transfer capabilities. We agree with the reviewer that the core contribution of this work is a pre-trained, general-purpose AUS backbone, and that zero-shot transfer is not shown. We use “foundation model” as in the biosignal literature (e.g. LaBraM, Neuro-GPT): a model pre-trained on heterogeneous unlabeled data and adapted to several downstream tasks by fine-tuning.

Following your suggestion, we added evidence of transfer to a new domain: with all WULPUS data removed from pre-training, FOCUS adapts to an unseen platform, sampling rate and anatomical site, and still outperforms training from scratch on all four affected tasks (see the common reply).

We acknowledge that our evaluations remain subject-specific (§4.2) and focused on physiological applications. Broader transfer settings, as well as dedicated exploration of zero-shot or few-shot adaptation to new domains, will be part of future work (§5).

  1. Related work. We have expanded §2 including more examples of time-series and biosignals FMs, with specific references on how they handle heterogeneity.
  2. Input versatility. We appreciate the suggestion to make our ablation experiments on input versatility more prominent. We added a dedicated discussion in §4.3.
  3. Preservation of acoustic detail. Each 0.308 mm patch holds 8 samples and is projected linearly to 256 dimensions, so the embedding is not a bottleneck, and pre-training reconstructs the raw samples of masked patches (Appendix A.2).
  4. Self-supervised comparison. To this end we added a wav2vec-inspired contrastive pre-training comparison to FOCUS using the same backbone as the main model and utilizing the same pre-training data and downstream data and protocols (Appendix D.2, Table 12). The downstream evaluation of this model is still running; we will report the results in a follow-up comment.
AuthorsOpenReview ↗

Reply to reviewer DcYw

The two experiments you suggested are complete, with final numbers (details in our follow-up comment to all reviewers).

  • Leave-one-platform-out: without any WULPUS data in pre-training, the fine-tuned model remains above training from scratch and above the BaseCNN on all four WULPUS tasks (PosePos-USVR pose 70.9% against 54.9% and 67.7%; HWR-23DoF 13.43° against 15.86° and 14.43°; Section 4.6, Appendix D.3, Table 9).
  • Self-supervised baseline: masked reconstruction is better than a wav2vec 2.0 objective on seven of the eight tasks after fine-tuning and on all eight with a frozen encoder (Appendix E.2, Table 12).
Reviewer_DcYwOpenReview ↗

Thank you for the updates

Hello, thank you for the updates!

Comments on the paper

3 comments
AuthorsOpenReview ↗

Applicable to all reviewers

We thank all reviewers for their constructive feedback on how to improve the paper. In response, we made the following additions to the original paper that we describe below:

Status of the revision. Following the reviewers’ suggestions, we changed the input tokenization of the main model (see below) and are re-running every experiment with it. The main results, the input-harmonization comparison and the platform-exclusion experiment are complete and reported here. The remaining ablations and the on-device measurements are still running; we will report them in a follow-up comment and upload the revised PDF as soon as they complete. Section and table numbers below refer to that revised PDF.

  • Input harmonization strategies. In response to the lack of comparison of simplified approaches to handle differences in the input data (reviewer hHiD, gxip and r5wY), we compared the submitted multi-tokenizer with two simpler strategies under the same corpus, objective, backbone and downstream protocols: resampling every scan to a common 20 MHz grid, and interpolating every scan to 800 samples. Both use a single tokenizer with P = 8.
ApproachPhysical depth per token
Multi-tokenizer0.31 to 0.39 mm
Fixed-length interpolation (800 samples)0.19 to 0.39 mm, set by the depth range
Common-rate resampling (20 MHz) + fixed patch size0.308 mm for every source

With the full corpus, the three strategies are equivalent after fine-tuning: each is best on two or three of the eight tasks, and all differences lie within between-subject variability. However, they differ when the downstream sampling rate is absent from pre-training. WULPUS is the only 8 MHz source, so excluding it removes that rate together with the platform and the forearm site. The multi-tokenizer is then the weakest on all four WULPUS tasks: hand pose 67.3% against 70.4% (resampling) and 71.2% (interpolation), and HWR-23DoF 14.09° against 13.17° and 13.62°. Without an 8 MHz branch, it routes these scans through the P = 8 branch, so each token spans 0.77 mm, 2.5 times the depth seen in pre-training; resampling keeps 0.308 mm for any rate. With a frozen encoder, resampling is best on five of eight tasks. We therefore adopted common-rate resampling with a single tokenizer as the main model (§3.1; Table 2). It keeps the principle of the submission, tokens spanning a fixed tissue depth, and makes it exact.

Extensive results are reported in Appendix D.

  • Extended the ablation studies with different pre-training objectives and channel aggregation strategies. We compare masked reconstruction with wav2vec-inspired contrastive pre-training to assess the learning objective (Appendix D.2). In addition, we compare CNN fusion with a flatten-plus-linear readout to examine how channel representations should be combined (Appendix D, Table 13).
  • Leave one platform, dataset and anatomy out experiments. We evaluate transfer after excluding WULPUS from pre-training. This removes both the downstream acquisition platform (WULPUS) and dataset, as well as all forearm acquisitions from the pre-training (Table 1). After fine-tuning, hand-pose balanced accuracy on PosePos-USVR changes from 75.5% to 70.4% and forearm-position accuracy from 82.1% to 81.5%; RMSE changes from 9.63° to 10.00° on HWR-3DoF and from 13.26° to 13.17° on HWR-23DoF. The model still improves over training from scratch on all four tasks, for example 70.4% versus 54.9% on hand pose and 13.17° versus 15.86° on HWR-23DoF. It therefore transfers to an unseen platform, sampling rate (WULPUS is the only 8 MHz source) and anatomical site (§4.6; Appendix C.6, Table 9).
  • Demonstrated edge deployment. We provide, to the best of our knowledge, the first hardware deployment of an AUS foundation model on a low-power edge microcontroller. We also quantify how quantization affects accuracy, and we provide latency/energy profiling of the model running on the edge (§4.7; Appendix E, Tables 14–16). The latency and energy measurements use the final input length; the quantization accuracy will be confirmed in a follow-up comment.

We address the reviewer’s specific comments in the dedicated sections.

AuthorsOpenReview ↗

Follow-up to all reviewers

Correction to our first comment. Some pre-training recordings are sampled at 40 MHz. We added a low-pass (anti-aliasing) filter before downsampling them to 20 MHz, pre-trained every encoder again and re-ran every experiment. The numbers below supersede those in our first comment. The fine-tuned results of the main model moved by at most 0.2 percentage points and 0.08°, and no conclusion changes. Two statements need correcting:

  • Without WULPUS in pre-training, HWR-23DoF RMSE is 13.43°, which is 0.20° above the full-corpus model (we had reported 13.17°).
  • The GAP9 figures are now measured on the final model and include the preprocessing of each new scan: one update takes 160.5 ms and 12.7 mJ (up to 6.2 Hz), not 157.7 ms and 6.3 Hz; a complete four-channel prediction takes 0.63 s and 49.5 mJ, not 0.62 s and 51 mJ (Section 4.7, Appendix F.3).

Platform exclusion and comparison with the BaseCNN (fine-tuned; Tables 2 and 9).

TaskFull corpusWithout WULPUSFrom scratchBaseCNN
PosePos-USVR pose, bal. acc. (%)75.670.954.967.7
PosePos-USVR position, bal. acc. (%)82.281.468.478.3
HWR-3DoF, RMSE (°)9.559.8910.0910.22
HWR-23DoF, RMSE (°)13.2313.4315.8614.43

With no exposure to the WULPUS platform or the forearm site, the model remains above both references on all four tasks. With a frozen encoder the cost of the exclusion is larger (PosePos-USVR pose 76.7% to 68.3%, HWR-3DoF 11.23° to 13.00°): transfer to an unseen platform requires fine-tuning, which recovers most of the gap on three of the four tasks (PosePos-USVR pose stays 4.65 points below the full-corpus model).

Input harmonization without WULPUS (Appendix E.1, Table 11, Figure 7). Multi-tokenizer / fixed-length interpolation / common-rate resampling, with WULPUS excluded from pre-training: PosePos-USVR pose 67.3 / 70.2 / 70.9%, position 79.9 / 81.0 / 81.4%, HWR-3DoF 10.05 / 9.88 / 9.89°, HWR-23DoF 14.09 / 13.69 / 13.43°. The multi-tokenizer is the weakest on all four tasks and resampling is the best on three. With the full corpus, the three strategies perform comparably. Paired within subject, resampling is better than the multi-tokenizer on 13 of the 16 subject-task pairs without WULPUS (two-sided sign test, p = 0.021; Wilcoxon signed-rank test, p = 0.008), and the two do not differ with WULPUS (6 of 16; p = 0.45). The exclusion also costs the multi-tokenizer more on 12 of the 16 pairs (Wilcoxon, p = 0.016; sign test, p = 0.077), with no such effect on UltraPro, whose platform is absent from pre-training in both settings (p = 0.55). Resampling and fixed-length interpolation do not differ significantly (p ≥ 0.13); we prefer resampling because every patch then spans the same tissue depth (0.308 mm) at the same sampling rate on every platform.

Label efficiency against the BaseCNN (reviewer hHiD; Section 4.4, Figures 2 and 6). With 20% of the labels, fine-tuned FOCUS exceeds the BaseCNN trained on all labels on seven of the eight tasks, and with 40% on all eight. The same holds against the Transformer trained from scratch. FOCUS is above the BaseCNN at every label fraction on every task. With all labels, fine-tuning improves over the BaseCNN on all eight tasks and the frozen encoder on six.

Pre-training objective (reviewers r5wY, DcYw, hHiD; Appendix E.2, Table 12). We implemented the wav2vec 2.0 objective on the same backbone, 20 MHz input, corpus and schedule, following its adaptation to 1D seismic signals in SeisLM: span masking (10 tokens, 50% coverage), a Gumbel-softmax quantizer (2 codebooks of 320 entries) and 50 distractors from the same scan. The FOCUS patch tokenizer replaces the convolutional feature encoder, so that both objectives share the input pipeline. After fine-tuning, masked reconstruction is better on seven of the eight tasks; the differences are at most 0.4 percentage points and 0.25°, except on PosePos-USVR pose (75.6% against 71.1%). With a frozen encoder it is better on all eight, with the largest gaps on the WULPUS tasks (PosePos-USVR pose 76.7% against 71.7%, HWR-23DoF 15.22° against 17.17°). Reconstruction therefore gives representations that are more useful without adaptation.

Channel readout (reviewers r5wY, hHiD; Appendix E.3, Table 13). The convolutional readout is better than flatten-plus-linear on all eight tasks (UltraPro gesture 84.7% against 77.8%, PosePos-USVR pose 75.6% against 68.6%, HWR-3DoF 9.55° against 10.94°). Mean pooling matches or exceeds it on three tasks (PosePos-USVR position 83.6% against 82.2%) and fails on kinematic regression (HWR-3DoF 11.27° and HWR-23DoF 17.38° against 9.55° and 13.23°).

Quantization (Appendix F.2, Table 14). We re-measured INT8 post-training quantization on the final weights for all eight tasks (411 fine-tuned models, one seed). Accuracy changes by at most 0.2 percentage points, R² by 0.001 and RMSE by at most 0.05°.

AuthorsOpenReview ↗

Closing comment: Summary of the revision and of the discussion

We thank all reviewers for the discussion. As the author-reviewer period closes, we summarize what the revision establishes; the experiments were run at the reviewers' request.

What the revision establishes

  • Pre-training helps beyond a task-specific CNN (hHiD). Fine-tuned FOCUS exceeds the BaseCNN on all eight tasks, and with 40% of the labels it exceeds the BaseCNN trained on all labels on all eight (Section 4.4, Figures 2 and 6).
  • The model transfers to an unseen platform (DcYw). With WULPUS excluded from pre-training, it remains above training from scratch and above the BaseCNN on all four WULPUS tasks (Section 4.6, Appendix D.3, Table 9).
  • Simple input harmonization is sufficient and more robust (gxip, hHiD, r5wY). Resampling to a common rate matches the multi-tokenizer with the full corpus and is better on 13 of the 16 subject-task pairs when a platform is held out (Appendix E.1, Table 11, Figure 7). It is now the main configuration.
  • Masked reconstruction is the better objective (DcYw, r5wY, hHiD). It outperforms a wav2vec 2.0 objective on seven of the eight tasks after fine-tuning and on all eight with a frozen encoder (Appendix E.2, Table 12).
  • The convolutional readout is better than flatten-plus-linear on all eight tasks (r5wY, hHiD; Appendix E.3, Table 13).
  • FOCUS runs on a microcontroller. On GAP9, one update takes 160.5 ms and 12.7 mJ, and INT8 quantization stays within 0.2 percentage points and 0.05° of FP32 on all eight tasks (Section 4.7, Appendix F, Tables 14 to 16).

Where the discussion stands

Reviewer hHiD writes that the additional experiments address many of the soundness concerns, and reviewer r5wY agrees that establishing a foundation model for a new modality is valuable. One point remains open: both consider the tokenizer the most distinctive technical contribution, and that replacing it leaves a combination of established techniques. We understand this view, since the tokenizer was prominent in the original submission. It was introduced there as an adaptation of MOIRAI (Woo et al., 2024) and was not among the three listed contributions (the first foundation model for wearable A-mode ultrasound, its evaluation on eight tasks, and the scaling study), which are unchanged.

The requested comparison also gives a finding specific to this modality: transfer to a new platform depends on a token covering a similar tissue depth as in pre-training. Resampling guarantees this (0.308 mm per token on every platform). The multi-tokenizer assigns an unseen 8 MHz platform a patch 2.5 times deeper than those seen in pre-training, and loses accuracy there (Appendix E.1).

We thank the reviewers and the AC for their time.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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