To increase transparency, PeerJ operates a system of 'optional signed reviews and history'. This takes two forms: (1) peer reviewers are encouraged, but not required, to provide their names (if they do so, then their profile page records the articles they have reviewed), and (2) authors are given the option of reproducing their entire peer review history alongside their published article (in which case the complete peer review process is provided, including revisions, rebuttal letters and editor decision letters).
Thank you for your clear headed analysis that got to the heart of the problem (no pun), and delivered a clear and effective corroborative statement to your hypothesis. I am happy to join the reviewers in approving your manuscript, and wish you a large readership.
Rather than a 'number of Minor Revisions', it is in fact just one correction in figure 4 that is necessary, as proposed by the reviewer. After your resubmission, the next step should be publication.
The article is now generally well reported.
The only change I would suggest is an alteration to figure 4. L0 is now discussed in absolute terms showing a difference between control and CHF patients and the implications of this discussed. However, the figure still shows normalized data meaning it has little relevance to the text.
The authors may wish to revise this
The experiment was well designed and conducted and the data now fully test the presented hypotheses.
The study presents valid findings and draws appropriate conclusions from them.
I find the manuscript much improved and suitable for publication. Although the authors may wish to consider how figure 4 fits with the description of the results
As you will notice, the reviewers had general positive comments, though they did raise a number of points that when addressed should improve the clarity of exposition. Note also that both reviewers had some difficulties with the interpretation of figures, particularly figures 1 and 2. I also appreciated the suggestion of reviewer 1 to add a graph displaying stiffness. Another relevant issue is the explicit mentioning of passive forces. Please carefully review the comments on the presentations of some of the statistical results, and please consider introducing multi-linear regressions! Some good feedback was also given in stylistic choices (long paragraphs and so forth). Please address those as well.
Looking forward to read the revised manuscript!
The article is well written and general clear. Figures are appropriate and clear although should be better referenced in the text - parts A and B often show very different things and the results could be better followed if specific parts were referenced.
An additional figure (bar chart?) could be included to show stiffness values. These seem central to the paper so should be more prominently displayed and easier to assess. This may also allow different values (using different normalization - see validity of findings section) to be displayed and functional significance assessed.
Sufficient data (including raw data) is presented to test the stated hypothesis.
The experiment appears to have been well conducted. The muscle in question has been isolated. EMG was used to assess activity levels during passive trials. Care has been taken to match activity levels - often a confounding factor in such studies. Both men and women are used in this study, and given the high levels of variability in the data, it may be worth considering whether this has an effect on the findings.
Ethical standards appear to have been met.
Some care needs to be taken throughout about the language used to describe what the study addresses. The language in the discussion and conclusion is appropriate as it states that changes in passive force are a result of changes in muscle size and the goes on to speculate about what these changes might mean for locomotor performance in CHF patients. However, in other places there is more of an implication that the study is assessing whether reduction in size or quality underpin the ability of muscle to generate force actively in CHF patients. This is particularly true in the title and introduction. The title uses ‘quality’. Quality is typically used to refer to the ability of muscle to produce active force and so should be removed. The introduction talks about the loss of voluntary strength in CHF patients and using passive force to understand whether this kind of decline in active is a result of a reduction in muscle size or muscle quality. However, the study does not test this and there are many factors which would complicate assessing active force production from passive properties. It should therefore be made explicit throughout that passive forces are being assessed and any comment on the implications of this left to the discussion.
A better description of the range of angles rotated though maybe helpful, plantar flexion and dorsiflexion could be annotated on figure 1?
In the methods, pennation angles are measured. But these are never described. And passive force is corrected using a pennation angle. This correction makes sense for active force as force is produced along the length of a fiber. But makes a little less sense for passive force.
There is a section on calculating active force-lengths curves. Active force in the soleus is estimated over a range of lengths. However, this is not well integrated into either the rationale for the study or the discussion of findings. If this section is to remain, it should be better incorporated into the study.
The data collected are largely appropriate to the conclusions drawn.
The data as a whole shows very high variability. This is a common issue in human studies with limited subjects and it appears that care has been taken to minimize this where possible. However, this variability should be acknowledged, particularly when showing a lack of significant differences between groups.
All of the pertinent data measured should be presented. For example, there does not seem to be clear presentation of PCSA anywhere. This is essential as the question is about muscle size.
I am a little confused about some of the data. It is unclear to me how joints can be rotated through the same range of angles with smaller fiber length changes – this is what figures 2A and B appear to show? Additional stretch occurs in the tendon? This should be addressed somewhere. More explicit presentation of the rotation conditions and morphological parameters in the 2 groups early on in the results may help this.
The authors should carefully consider normalization throughout, and the implications of this should be better explained. For example, calculating stiffness from normalized forces and lengths gives the most information about muscle properties. However, this ignores the higher effective stiffness experienced in CHF patients. In some cases it may be better to calculate a variety of parameters and discuss the implications of them. Significant differences in L0 are shown, however, the normalized plot obscures these.
This is also true of the stats where non-normalized values are compared at 0, 20, 40%….. of maximal angular excursion and stretch. You should be very explicit about what these comparisons mean. For example, if angular excursions are similar between the groups this is more like an absolute comparison. However, if maximal muscle stretch differs between the groups, using these categories is effectively comparing normalized lengths. These things don’t necessarily need to be changed but it would be beneficial to the reader to understand what is being compared. If possible, it may also be beneficial to use more sophisticated statistical analysis. Linear or generalized linear regressions could be used in R to assess data without using the % categories
Some of the stats terminology is a little confusing. For example It is not clear to me how an interaction between group and moment would be found. Interactions occur between 2 independent variables (e.g. group and sex) not a dependent and an independent variable (e.g. group and moment) (line 284). This use of interaction should be addressed throughout the results.
Reasonable conclusions are drawn from the data and some potential functional implications discussed.
I have the following minor recommendations regarding the figures:
Figure 1. Please update the x- and y-axis labels to designate the sign convention. For example, in both, it seems dorsiflexion is the positive convention.
Figure 2. Do these data also correspond to the 20-100% stretch labels shown on Figure 3? If so, I would include them here as well.
Figures 2-3. I suggest arranging these panels side-by-side rather than top-to-bottom to avoid possible attempts to compare these panels across their x-axes.
Captions. In all captions, I recommend making note of the muscle being investigated (e.g., "Soleus passive force-length").
This generally well-written manuscript primarily describes a comparison of passive soleus muscle forces obtained via a combination of in vivo measurement and computer simulation in people with and without chronic heart failure. In my opinion, the study is well-justified and experimentally sound. I do have several minor comments, but most are geared toward improving the clarity of the presented material.
L28. “Impaired skeletal muscle” is too vague.
L31. Revise: “altered contractile properties [and/or] architecture” as differentiating these roles is of primary concern.
L38 and L42. The difference between “absolute muscle length” and “equivalent levels of muscle stretch” should be clarified, perhaps by referring to the former using “relative.”
L45-46. This closing statement is not a complete sentence.
L54. I suggest more specifically defining/describing “deficiencies in skeletal muscle” and “limited functional capacity.”
L60. More clearly describe the relation between aerobic exercise capacity and muscle size and strength.
L62-L63. This sentence is very difficult to follow - I suspect “reduction in muscle” is a typo.
L73. This first use of “motor deficits” is overly vague.
L76. Silder et al. found little to no difference in passive contributions to net joint moments between old and young adults during walking. Is this a good example for the functional relevance of passive forces?
L85. Consider revising: “…investigate passive forces in the…. participants, including their relationship to muscle architecture…”
L88-L93. I recommend introducing the importance of the soleus muscle during functional activities and in CHF prior to stating the study’s aim.
L107. The activity level of participants may or may not be well-matched. CHF subjects’ exercise is prescribed and detailed according to their standard patient care, but my guess is that controls simply self-reported their physical activity. I suggest revising to: “The control participants self-reported similar levels of weekly exercise.”
L113. First mention of active force measurement. Introduction suggested these would be excluded. I also recommend the authors add or move (e.g., L150-155) to this section details regarding the study protocol.
L126. I do not know what it means to fit the data by visual inspection.
L133-135. This one sentence description of the modeling efforts are unclear until more details are provided 4-pages later. Suggest reorganizing for clarity.
L136-138. This sentence should be moved to a new paragraph added to the discussion on study limitations.
L136-177. This is a huge paragraph. I recommend several shorter paragraphs with clear topic sentences.
L165-166. The word “above” could be interpreted as “over” or “proximal” and should be replaced for clarity. Where exactly along the tendon was this placed? Also, are two motion capture markers enough to co-register the ultrasound images with the medial malleoli markers? Finally, use of the medial malleoli as a surrogate for ankle joint center should be discussed as a limitation.
L172. Was the tendon’s line of action defined using its midline? If so, please state this.
L178-181. This sentence is quite difficult to follow.
L196-201. It is not clear why the authors could not simply use the measured passive forces rather than resorting here to model fits.
L205. The different ankle angles referred to here are never reported, but should be.
L221. My interpretation here is that inverse kinematics was used to drive the model to match marker trajectories measured from subjects seated in the Biodex and performing the MVCs. If this is true, I recommend stating.
L270. The “passive joint angles” outcome measure should be more clearly defined. Also, the comparison described by “were affected” is unclear.
L276. Revise: “stiffnesses”
L292. I recommend moving “maximal strain” to the next paragraph, as it is derived from the normalized curves presented in Figure 3b.
L299. This sentence largely repeats that from the methods section and can be removed.
L301. The relevance of reporting the angle at which Lo occurred is not clear.
L309. Revise: “However, and also in agreement with our hypothesis, passive force was not different between groups after… These results indicate that muscle size…”
L312. The inclusion of “stiffness” here is a bit misleading. Neither absolute nor normalized stiffness differed between groups. Thus, it would seem that neither muscle size nor intrinsic properties influence stiffness in CHF.
L326. Revise: “… for both groups [but] significantly…”
L327. Revise: “… patients [may indicate] that…”
L344. As an alternative, consistent with ideas proposed on L332-334, more dorsiflexion during stance could emerge due to more tendon strain, without affecting muscle strain, in people with CHF. Because of this possibility, I find the discussion of a reliance on passive muscle forces as an energy conserving mechanism in CHF highly speculative.
L353. As discussed earlier, I suggest the authors add a thoughtful discussion of study limitations.
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