A Polynomial Model for Estimation of Ex-Vivo HIFU Thermal Lesion Dynamics Based on Pressure Amplitude and Sonication Time

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

 

The manuscript reported a predictive polynomial model for potential medical applications

 

 1) The abstract needs to be summarized, because in the present form, it has a lot of information that should be moved to the experimental part or somewhere in the manuscript

2) The manuscript has some typos; revise carefully and correct them

3) Line 226 correct sentence “shown in Figure 3Figure.”

4) Chemical formulas or chemical compounds must be written according to chemical rules

5) Why were these conditions “experimental results on ex-vivo chicken breast 250 tissue” selected?

6) Figures 4, 5, and 8 were difficult to see the information (numbers and words), improve it

7) Lines 458-459 “The computational model error rate was 20% when compared to experimental results”. 20% was an adequate or acceptable error?

8) The manuscript should include the conclusion

9) The manuscript has some interesting results, but needs to improve the discussion for all figures and tables

 

Minor corrections

1) The figures quality needs to improve

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

This article by Parrotta et al. presents a solid engineering framework but a biologically immature model. The authors successfully demonstrate how to build a fast surrogate model (polynomial) from slow simulations (FEM), which is a valuable contribution to the field. However, the specific model they derived is not clinically viable because it ignores critical physiological factors (blood flow) and relies on "calibrated" rather than "predictive" physics.
The paper excels at defining a practical workflow. The transition from Complex Physics (COMSOL) -> Simplified Math (Polynomial) -> User Tool (MATLAB App) is logical and addresses a real need for faster treatment planning. The development of an "inverse tool" (where the doctor inputs the desired size, and the tool outputs the required power/time) is highly practical and more useful than standard forward-simulations. The authors are transparent about the initial errors (~20%) and the need to optimize material properties to get the model to fit. They do not hide the discrepancies in the minor-axis predictions.
Here are the major concerns and a few potential aspects the authors can improve the scientific rigor and reproducibility of this article to a standard suitable for high-impact medical physics journal. 
1. Validating a "treatment planning" tool on ex vivo chicken breast (dead tissue, no blood flow) is a major limitation. The model assumes heat only dissipates via conduction. In a real patient, blood perfusion acts as a massive heat sink. Therefore, this model would likely dangerously overheat a real patient or fail to create the desired lesion size because it doesn't account for cooling.

2. Key details like the initial temperature of the chicken breast (e.g., was it 20C room temp or 37 C body temp?) are not explicitly in the snippet. This is a critical parameter for the Bioheat equation. This 17C difference drastically changes the energy required to reach the necrosis threshold.

3. Live tissue has blood vessels that actively carry heat away. A highly perfused organ (like the kidney or liver) might require 2x-3x more energy to achieve the same lesion size as the dead tissue used in the validation. A model derived from ex-vivo data will likely overestimate lesion size when applied to live patients, potentially leading to undertreatment (cancer survival).

4. Relying on digital calipers on unstained, fresh tissue is subjective. The lack of vital staining casts doubts on the precision of their "ground truth" experimental data.
Experiments using TTC (Triphenyl Tetrazolium Chloride) or NADH-diaphorase staining are recommended. This chemically turns living tissue red and dead tissue white, providing an objective, high-contrast boundary for measurement, eliminating the "visual guess" error.

5. The article may need a plot comparing Temperature vs. Time for both the simulation and the experiment (using thermocouples), as the author must prove the tissue heated up and cooled down at the predicted rates. 
This validates the thermal diffusivity and absorption independently and mitigates the risk that a model could be scientifically wrong (e.g., calculating too much heating but incorrectly high cooling) and still accidentally result in the correct final size. This "right answer for the wrong reason" makes the model untrustworthy for different scenarios.

6. For the inverse-model-based application, the authors need to specify the boundaries used in the “fmincon” solver. For example, the range of “p” and “t”.
Additionally, once tissue reaches >100C, boiling creates steam bubbles that scatter the beam ("tadpole effect"). The polynomial model does not appear to account for this saturation point, likely failing at high intensities.

7. if animal trials are not feasible, the authors should run the COMSOL model with the blood perfusion term turned on (using standard literature values for liver/kidney perfusion). The goal is to quantify how much the lesion shrinks when blood flow is present. This would generate a "Correction Factor" to make the polynomial useful for real patients.

8. The authors admit the model failed at high power due to boiling/cavitation. They should determine the "Safety Envelope", which is the specific combination of Pressure and Time where boiling begins and restrict the polynomial model to operate only below this curve.

9. Formal statistical comparison (e.g., a paired t-test or Bland-Altman plot) to assess the agreement between the simulation and experiment, rather than just reporting the "mean error percentage" are highly encouraged. 

10. The planning tool assumes the patient has a uniform block of tissue (like the chicken breast). Real HIFU planning is dominated by aberration (distortion of the beam by fat/muscle layers) and obstruction (ribs). A polynomial based on "Source Pressure" is meaningless if 50% of that pressure is lost passing through a fat layer before it hits the target.  The "Pressure Amplitude" at the focus can be much lower than the "Source Pressure" predicts, because energy is lost or scattered on the way in.
How would the authors address the discrepancy in the polynomial model? 

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have substantially addressed the reviewer’s comments, although they did so primarily by clarifying the study's scope and limitations rather than performing the requested new biological experiments (such as in-vivo tests or vital staining). While the authors successfully clarified the scope of their work as an engineering framework, the following limitations persist:

1. The authors correctly identified a fundamental flaw in the reviewer's suggestion to use vital stains (TTC or NADH-diaphorase) on supermarket chicken breast. They rejected the request for staining with a scientific justification. They argued that because they used supermarket chicken (unknown time since death), the enzymatic activity required for these stains would be degraded, making the results unreliable. While their defense is valid for this specific study, it highlights a weakness in their experimental design: the use of supermarket meat. A "gold standard" validation would use freshly excised tissue (from a lab animal) where staining is possible. 

2. The authors fully acknowledged that validating on ex-vivo tissue ignores blood perfusion, stating that the current model accounts "only for thermal conduction". They introduced a "corrective factor" to the polynomial model. By recalculating the coefficients to include a theoretical perfusion term (based on the Pennes bioheat equation), they created a "corrected polynomial formulation" intended to represent perfused tissue. They explicitly committed to validating this framework on "perfused organs and... under in-vivo experimental conditions" in future studies.
They did not re-train their model on perfused simulations. Furthermore, they assume perfusion is a constant heat sink. In reality, blood flow changes dynamically during heating (vasodilation) and stops completely when the tissue burns (vascular shutdown). A simple "subtraction" term cannot capture this non-linear behavior.
If the goal were to create a truly "predictive" tool for treatment planning (as the title implies), the authors should have taken one of the following approaches, ranging from computational improvements to experimental gold standards:
a. Instead of adding a "correction factor" to the end of the equation, they should have included perfusion in the training data. By Re-runing the COMSOL parametric sweeps (the 30+ simulations) with the biological perfusion term (w_b) turned on in the heat transfer physics. The derived polynomial coefficients (beta) would inherently "learn" how blood flow fights against the heating. This would capture the non-linear relationship between Power, Time, and Perfusion, rather than just subtracting a constant value at the end.
b. If animal trials were impossible, they could have used a wall-less flow phantom. Use a tissue-mimicking gel with channels running through it, connected to a water pump to simulate blood flow. They could validate if their model correctly predicts the "cooling effect" of a simulated vessel. This provides physical validation of the "heat sink" effect without needing ethical approval for animals.

c. To truly claim "patient-specific planning," they needed In Vivo data.

Unlike the biological limitations (which they argued against or pushed to "future work"), these are technical omissions regarding data transparency and statistical validity that they neither fixed nor acknowledged:
3. The entire scientific value of the paper rests on the derived polynomial equation. However, even in the revised manuscript, the authors did not publish the numerical values of the coefficients (beta_0, beta_1, etc.). Without these numbers, the "predictive model" is useless to anyone else. No other researcher can use their equation to plan a treatment or verify their results. The paper remains a description of a method rather than a provider of a tool. he authors did not discuss why they withheld this data, nor did they offer to upload it to a repository (e.g., GitHub or Data In Brief).

4. The authors stuck to a sample size of N=6 for their experiments without providing a Power Analysis to justify why this number is sufficient. In biological studies, tissue variability is high. A sample size of 6 is statistically fragile. Furthermore, they compare the Simulation vs. Experiment using simple "Mean Error" percentages. They did not perform formal statistical tests (such as a Bland-Altman analysis or a Paired t-test) to prove that the simulation results are statistically equivalent to the experimental results. They presented the error bars in the new figures but did not acknowledge that "visual overlap" of error bars is not a substitute for rigorous hypothesis testing.

5. For any Finite Element Method (FEM) study, it is standard practice to prove "Mesh Independence", showing that the results don't change if you make the mesh finer. The authors state they used "Adaptive Mesh Refinement," but they did not include a convergence graph or table showing the error drop-off. Without this, we cannot be sure if their simulation error (approx. 10-20%) is due to the physics or just a coarse mesh. This is a standard technical requirement for physics journals that was seemingly overlooked in the revision process.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf