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Thank you for addressing the remaining reviewer comments. Congratulations on your nice work!
Please address the remaining minor comments in your response and revision. If your response is clear and satisfactory to me, it will not go back to the reviewers.
The manuscript is well written and clear
The research question is very relevant and well formulated. The design of the study is original and valid. Methods are clearly described and motivated in revised manuscript.
One small issue to address: While you basically test for equivalence in metabolic cost (based on research aim in introduction and statistical test used), you open the second paragraph of the discussion with "This study was hypothesis-driven and addressed a research question with a yes/no answer, “Does limb loss increase metabolic cost?” "
this should be adjusted.
Results and conclusions are valid within the general limitation of the simulation approach used. Potential effects of assumptions and simplifications in the simulation model are adequately discussed
Interesting study that provides valuable information and provokes relevant questions for further research. Pleasure to review
The paper is clear and well written. I just have two small comments:
Line 285: a word appears to be missing
Line 346: "GRF appear" is used. I would use "GRF appears". When looking up if this was a plural abbreviation, I noticed that the abbreviation GRF was not defined in the paper. Therefore, please make sure that all abbreviations are defined.
Concerning one comment of the first review, I would recommend to also add this information to the manuscript itself:
Line 187: why were the joint angles for which no (reliable) data was available not removed from the optimization instead of tracking 0 degrees?
If there is no tracking target then the model tends to move these joints in unrealistic ways to track the other tracking targets unnecessarily well. Zero was used to minimize the range of motion of these joints, which are typically small.
No further comments.
It makes most sense to me to report the metabolic cost the way that it is done, because scaled metabolic cost makes the results comparable to experimental studies. However, it is interesting that the unscaled results could actually lead to a different conclusion.
The consensus of the reviewers is that major revisions are required. Most suggestions seem straightforward and I am looking forward to your revision.
I tend to agree with reviewer 2 that it would be better not to normalize the metabolic cost at all. You normalized to biological mass to avoid favoring the hypothesis of similar metabolic cost. However, you may have ended up favoring that hypothesis anyway, and not seeing that metabolic cost in the amputees was (theoretically) lower, which is an important observation. If this observation is not consistent, or even opposite to, human subject studies, that can generate important new research questions. One possible issue is that normalization helped reduce the variations between your virtual participants, but since you can compare within-subject, that should not affect the p-values.
The manuscript is well-written in an organized manner and figures are well-presented. However, I suggest that the authors check the references. For example, line 36, “Pinzur et al., 1992” is not found in References. (This was found by chance, and there may be more. Therefore, a thorough check is suggested.) Also, please clarify what “maximum isometric force” (line 154) is, as opposed to “maximum isometric muscle forces” on line 153.
I agree with the authors’ statement, “the resent model is on the upper end of the complexity spectrum (line 362).” However, one concern may be the sensitivity of the muscle fiber-type composition to the metabolic cost. The metabolic-cost computation in this study is based on a mathematical model developed by Umberger et al (2003) (modified by Koelewijn et al (2018)), which includes percent fast-twitch fiber type in the computation. Therefore, different fiber compositions in the model muscles would influence the computed metabolic cost. In fact, Umberger et al. (2006) (*1) who used the same method showed different metabolic cost with different fiber types in the simulation study of cycling. Some experimental studies have shown variability of fiber types in muscles in different individuals (e.g., Staron et al., (2000) (*2)). I suggest that the authors discuss the extent of influence of the fiber type variability on the study results.
*(1) Umberger et al. (2006) Journal of Biomechanics, 39: 1472-79
*(2) Staron et al. (2000) Journal of Histochemistry and Cytochemistry 48(5): 623-39
No comment.
The primary objective of the study is to compare the metabolic cost of walking between pre- and post transtibial amputation, using a 3D dynamic simulation approach. The results further confirmed the author’s previous work using 2D models, concluding that the transtibial amputation by itself would not cause an increase in metabolic cost. The strength of the study is demonstrated in the extensive work to generate simulations and verify the models and simulation results. (Testing with different fiber type compositions is recommended as stated in Experimental Design.) I think the study was conducted well to reach the conclusion, but I personally would like to know why or how some subjects increased post-amputation metabolic cost and others decreased as shown in Figure 9. If the authors can discuss what muscle group(s) contributed to the metabolic cost increase or decrease even in a few specific subjects, I think it would further enhance the value and quality of the study. If not in this paper, I certainly look forward to it in the future.
Manuscript is well structured and generally clear. Some content might be transferred to supplementary material
Research question is well defined and methods are generally clear. Some minor issues regarding methods could be clarified and
The conclusions are sound and valid. Some additional analysis and conclusion could be added on the relation between the few observed kinetic and kinematics differences between pre-post conditions, how compensation for these differences occur and how they affect metabolic cost of walking
This simulation study investigates the metabolic energy cost of walking with a transtibial prosthesis and questions whether a post-limb loss gait would result in a different metabolic cost compared to pre-limb loss gait when initial musculoskeletal properties and body composition were maintained, besides from replacing the amputated limb by a passive transtibial prosthesis. This simulation study allows to further investigate the experimental observation that high functioning amputees do not seem to have greater energy cost than able-bodied controls. It seeks whether musculoskeletal mechanics allow a near normal gait pattern and non-significant differences in energy cost when the biological lower limb is replaced by a passive prosthesis (in the absence of other constraints such as balance control or stump-socket comfort). It is a very interesting and relevant outcome that this hypothesis could be confirmed.
This is a very relevant study, using a state of the art modelling approach. The procedure is generally well described and the conclusion is generally sound. It is of interest to the scientific and clinical community. Nevertheless, there are some issues that would deserve more attention to further enhance clarity and of the methods, results and interpretation.
Major comments:
- The results demonstrate that metabolic cost does not differ significantly between simulations per and post limb loss and that deviations in the gait pattern are limited. Nevertheless, they indicate some deviations that are similar to experimentally obtianed data from amputee gait. Specifically, they observe reduced peak anterior GRF and reduced second vertical GRF peak on the prosthetic side. Next to some other small kinematic changes, of course plantar flexion of the prosthetic ankle was absent. It is of interest to further analyse to what extend these changes in gait kinetics and kinematics affect energy requirement and how this is compensated in the post-limb loss gait pattern. For instance, it would be of interest to know how much mechanical energy was stored and released in the prosthesis, as this energy does not need to be generated by muscles at the expense of metabolic energy (hence this might reduce energy cost post-limb loss). Similarly, it is of interest how the reduced propulsive GRF (reduced anterior and vertical peak) affect mechanical and metabolic work? From a mechanical perspective the increased energy cost of prosthetic walking has been attributed to reduced push of which increased the energy required for step-to-step transitions (e.g. Kuo and Donelan Physical Ther 2010, Houdijk et all G&P2009). Did external mechanical work differ between pre- and post-limb loss simulations? or did joint (or muscle) work distribution differ between pre-post? As the authors have the data to answer these questions, it would be interesting to expand the results section and discussion a bit in this direction.
- The normalization of metabolic energy cost to body mass is an issue that deserves much attention in the results and discussion of the manuscript. While it is indeed not trivial which mass should be used for normalization and this is indeed often not well reported in literature, in this case I wonder whether any mass normalization would be required. The authors stress that they investigate the effects of limb-loss on metabolic cost with emphasis on only altering the mechanical properties of the lower limb, keeping all other musculoskeletal properties and body composition equal (and without taking into account other constraints such as balance and comfort). Hence, it is the same person with similar cardiorespiratory (aerobic) capacity that walks with and without prosthesis. The true absolute energy consumption will be most relevant to him/her, regardless of which mass you divide it by. As you compare pre-post limb loss energy consumption within a participant, there is no need to normalize to body mass and absolute aerobic strain seems the best comparison. (see also Wezenberg et al APMR 2012;94;1714-20. Who use energy consumption normalized to aerobic capacity, i.e. relative aerobic load, as important factor in amputee gait)
- In the cost function for optimization the authors include two terms; one related to deviations in the gait pattern and one related to energy cost. There is no explicit weighing between both I believe. Is this correct and would the results chance when the weighing between these two terms would be different?
It might be that the variable w is regarded as a weight factor. Although, it seems that that factor is used more to obtain realistic metabolic values from this approximated term for energy cost in the cost function, than that it is meant as a weight factor between the two terms in the cost function.
- There are two tests for the validity of the model in the methods section (comparing the model to experiments with different masses to the leg and using an ankle brace). These validity tests are very relevant and adequate, but they are described very brief and the accompanying figures are rather prominent in the manuscript next to the main results of the study. Could these validations be transferred to supplementary material, where they can be described in little more detail and presented as addition experiment?
- Figure 8-10 contain some overlapping information, one or two could be removed or merged. In my opinion
Minor comments:
- Line 83-91: several changes and additions were made to the original model of Dembia. Could you motivate why item 3-5 were modified/added? Was this crucial for this studies aim? Were these characteristic in the original model not valid?
- Figure 2 is bit redundant as it only concerns one of many muscle groups in the model and it does not concern a main result of the study. Could be just in text references.
- Line 137: does y in this equation only apply to the longitudinal displacement of stump relative to socket?
- Line 143: The methods and results of this analysis could be presented in supplementary material
- Line 154: maximum isometric force should be deleted from this sentence I guess, as it is already mentioned in the sentence before.
- Line 160: I believe that a clinical relevant difference is more important than a minimal detectable difference. But no real consensus is available on clinical relevance difference on energy cost. Often 5-10% is used for walking in patients (no clear reference available on this)
- Line 191: explain here that the output of the energy cost model used (Koelewijn 2018) cannot be used directly in the Moco software, and therefore you use this proxy equation. (now this is only clear at the end of the discussion line 372)
- Line 192: can the excitation parameter t range between 0-1?
- Line 194: explain the meaning of parameter w
- Line 238: explain which initial guess is meant here (on which variables), how can these result from different values of w in the cost function? And why use the best out of three?
- Line 262: when you talk about biological mass post-limb loss, do you mean the mass of the body with the mass of the amputated part of the leg, or the original biological mass before amputation?
- Line 268: why use two one-sided tests and not one two-sided test?
- Line 284: would AP impulse not be more relevant and reliable than peal anterior force, It is the impulse that relates velocity.
- Line 291: “few larger changes” : which do you mean
- Line 291: did you test the observed kinematic and kinetic differences statistically?
- Line 355: IJmker et al did not conclude that energy cost of frontal plane balance is similar with and without transtibial limb loss, but suggested that constraints of the external stabilization system might conceal potential effects. In both your 2D and 3D model you remove the need for ML balance control. Also the 3D model is ML stable because of tracking a cyclic motion including similar step width between models. As such you cannot investigate the effect of balance control in the 3D model and in that regards 2D and 3D model are equivalent I believe.
- Line 422: I do miss some extra discussion on the few differences that exist in kinematics and kinetics between pre and post limb loss and how energy cost can be similar between both simulations despite these difference in gait pattern. Fig 4-6 present these kinematics and kinetics in detail but deserve limited attention in the text.
- Fig 4: explain non-zero GRF in swing phase (most prominent in AP GRF)
- Fig 5 knee extension differences in stance are remarkable and opposite than I would expect (I would expect moor knee extension in stance after limb loss, conform literature)
Overall, this was good. I have one comment regarding figure 4, and a couple of possible typos:
1. Figure 4: In both the pre- and post- simulation, there is ground contact after about 80% of the gait cycle, while the simulation should still be in the swing phase. Could you elaborate on what is happening there?
2. Line 165 and 167: First you mention 26 subjects are required, and then 36 are created. Why the difference?
3. Line 163: shouldn’t the third word be tests instead of test?
4. Line 416-417: this sentence has “only” twice.
The experimental design is appropriate for the presented research question. I do have a couple of questions regarding the methods:
1. Line 112-118: Why did you use the metabolic model developed by Koelewijn et al. (2018). I would not recommend to use this metabolic model for any post-simulation analysis. It was developed purely to be able to solve predictive simulations, and the outcome is different from the outcome of the original Umberger model, which is validated against data.
2. Line 237-239: I would like to know a little bit more about the initial guesses that were used for the pre-op simulations, because the description was a bit vague here. It says that the initial guesses were from more preliminary simulations, but what preliminary simulations? And what were the initial guesses for these preliminary simulations?
3. Line 148-159. What were these different ratios based on? Do I understand correctly that the total mass of the person was not altered? Why was that decision made? Why were the segment lengths not altered? I recently found that the effect on the final result is larger when changing the full body mass and length than the muscle parameters, so I was a bit surprised. Also, maximum isometric force and maximum isometric muscle force is mentioned twice. What is the difference?
4. Line 187: why were the joint angles for which no (reliable) data was available not removed from the optimization instead of tracking 0 degrees?
5. Line 130-144: Why is a double exponential function appropriate to model the socket motion? If this is presented, please add a justification. On the other hand, I am not sure if it really makes sense to mention this aspect so explicitly, when it is not actually used in the results.
6. Line 191-198: I am a bit unsure about how you describe the choice of tracking weight here. If metabolic cost is the outcome parameter, it does not make sense to me to also only use metabolic cost to set the weight of the objective function. Then, you don’t know if maybe somehow two errors inside the simulations/analysis pipeline are cancelling each other. Since in my opinion an absolute comparison of the outcome of a metabolic energy model (only the modelled muscles + basal rate) to direct calorimetry measurements (which includes all muscles and other metabolic processes) does not really mean much anyways, this process is not convincing to me. However, the validation simulations are a good support for the choice of weights. Also, the kinematics do look realistic.
Overall, the presentation of the findings was good and meets the criteria.
1. Section 3.3: I am not surprised that the damping values are so small, it is in my opinion surprising that they did not decrease to 0 exactly, because the higher the damping, the more energy is removed from the system, thus the higher the objective. However, this might actually be related to the tracking that is also included in the objective. Is there a way to actually compare the numbers to what is common in a current prosthesis? Numbers are presented for the stiffness in the discussion (line 376-391), but not for damping. I wouldn’t know where to find those myself.
I also have two comments regarding the supplementary data/code:
• I changed line 267 to: path = [pwd filesep];% '/Users/rosshm/Documents/Matlab/TTA3D_solns/';
Then, the code should work when the current folder is TTA3D_solns for any computer.
You could probably even add a check to see if the user is in the right folder as follows:
curpath = pwd;
strcmp(curpath(end-10:end), ‘TTA3D_solns’);
• If possible, it makes sense to me to also share to .osim files of the models. I did not find those in the data.
I enjoyed reading this paper and it is great that such a study can be performed with the MoCo software.
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