- Rating
- 1
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 1
- Soundness
- 1
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Paper summary
This paper studies continuous arterial blood pressure waveform prediction from a single photoplethysmography window on previously unseen cases. Papers falling under the category of AI in interdisciplinary healthcare, identifying scientific problems within the medical field and seeking solutions through AI. The authors employ a shared ResNet-1D backbone followed by "common" and "private" branches, fusing their waveform outputs via smooth convolution. Training adds Public-waveform supervision, a representation-difference penalty, contrastive learning between two augmentations of a window, and training-case identity classification. The evaluation uses a curated VitalDB subset with 300 training, 30 validation, and 30 test cases. The paper reports case-macro-averaged waveform and pressure-statistic errors against four reproduced baselines and a sequential component ablation.
Critical strengths
As seen on page 6, section 4.1 of the paper, they used complete case data instead of randomly split data windows to divide the samples, which is good because this approach aligns with the generalization problem discussed in the paper. Furthermore, they incorporated several methods, such as public-head supervision and private-head zero-initialization methods.
Table 1 reports improvements across all seven displayed metrics, and the percentage reductions in Section 4.3 agree with the table. Table 2 also reports monotonically decreasing waveform errors. The predictor does improve on the reported metrics. The missing controls, discussed below, make it hard to tell why.
Critical weaknesses
In my assessment, the work in its current form is not sufficiently developed to support its central claims. The missing validation concerns the proposed Public/Private separation itself, and the conflicting method descriptions leave me unable to determine exactly what was evaluated. Stronger experimental controls are also needed to establish whether the numerical gains amount to an independent empirical contribution. Addressing these issues would require substantial additional work before I could consider the paper ready for acceptance.
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My main concern is that the experiments do not demonstrate the separation on which the paper bases its contribution (Abstract; contributions on p2; Sections 3.3-3.6; Table 2; Conclusion). Shared/private encoders and difference penalties already appear in Domain Separation Networks, and subject-shared/private physiological representations appear in the cited MDNet. IPPD differs by using an input-dependent Private branch to correct an unseen case's waveform. I would like to see evidence of what this adaptation adds.
The Public head is supervised against each case's complete ABP waveform, which contains individual variation. The identity classifier encourages the Private branch to retain case information, but that alone does not show that the two branches learn the proposed roles. A cross-covariance penalty constrains second-order dependence; it does not identify which branch contains reusable physiology or individual variation. The experiments do not test even the weaker claim that one branch is relatively more shared and the other more sensitive to the individual. The contrastive positives are two augmentations of one window, so their agreement does not establish stability across different windows from an individual.
Table 2 does not resolve this: the Private branch brings both extra capacity and another loss, and the remaining rows test just one sequence of component additions. There is no fixed-capacity removal of the difference penalty, separate test of Public-head supervision, or direct branch-role diagnostic. The conclusion leaves role stability and interpretability to future work (p8), even though the paper already relies on those roles to explain its results. A capacity-matched residual control and frozen-feature comparisons of case information and within-case stability would test the existing claim. Without those tests, I cannot attribute the gain to the proposed decoupling or judge whether it is needed.
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I could not determine exactly which model and loss produced the results (Figure 1 and Section 3.4, p4; Equations 6-7, p5; Sections 3.7-4.2, p6). Figure 1 calls the Private encoder a Transformer; Section 3.4 says it has the same two-layer convolutional architecture as the Public encoder. These are materially different models.
Equation 6 calls its expression a cross-covariance estimate without specifying centering or reshaping. If the intended inputs are centered BT-by-C matrices, the extra division by B makes the squared penalty 1/B² times the usual mean squared sample cross-covariance: a factor of 65,536 at the stated batch size of 256. This calculation assumes the interpretation above and applies to the written formula; I do not have the implementation. The missing details matter because they change the strength of the decoupling penalty. Equation 7 also leaves the view indexed by q_j undefined, and the contrastive temperature and pooling parameter k are unspecified.
The paper further uses standardized PPG, normalized ABP, and final errors in mmHg without defining the transformations or their inverse. To assess the calibration-free claim, I need to know whether absolute pressure can be recovered using only statistics available at inference. These omissions conflict with the statement on p8 that the full architecture and hyperparameters are provided. The authors need to provide the executed architecture, exact loss operations and scales, and normalization protocol before the method can be reproduced faithfully.
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The empirical evidence is also insufficient to justify the contribution on predictive performance alone (Sections 4.1-4.4, pp6-7). The closest reported baseline, PaPaGei, is worse by 0.5564 mmHg in waveform RMSE and 0.5153 mmHg in MAE; the KS difference is 0.0023. Table 1 does not define its “±” values, and the manuscript supplies neither a run count nor paired case-level uncertainty. I therefore cannot tell how consistently the gains hold across runs or cases.
The reproduced baselines' waveform adaptations, pretrained-weight use, and model-specific training and selection procedures are insufficiently described. The paper cites a directly relevant waveform method, INN-PAR, ICASSP 2025, but omits it from evaluation. That work also studies subject-disjoint prediction without subject calibration. The authors should explain how IPPD differs and, where feasible, compare the two under the same VitalDB protocol. Its published numbers from other datasets cannot substitute for that comparison. To judge the practical gain, I would need paired case-level results and enough detail to check how the baselines were trained. A direct waveform method evaluated under the same protocol would also help. The current table is not enough to support the broader claim of better individual-level modeling.
I will not change my score in this round.
Questions for authors
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Does the gain survive removal of the difference penalty with capacity, augmentation, and other losses fixed? Can branch probes show the proposed relative shared/individual roles across distinct windows? Positive results would directly address the main contribution objection and could raise Contribution to 2 or higher.
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Which Private encoder generated the tables, and what tensor operations implement Equation 6? The executed specification and loss magnitudes would resolve the contradiction; a materially different regularizer would require corresponding corrections to the claims and results.
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What are the PPG/ABP normalization and inverse transformations, and how were the 360 cases and splits selected? An inference-valid protocol without target ABP statistics would substantiate the calibration-free interpretation. I have not established that leakage occurred.
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What do the uncertainty values represent, how were baselines adapted, and do paired case-level gains persist against a matched direct waveform method? Consistent gains under documented, comparable training would improve my assessment of the empirical contribution, while leaving the mechanism question to be answered separately.
Hi authors, I'm looking forward to discussing the paper. If my concerns are addressed, I will reconsider my score.