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Dear authors
Thanks for providing the responses to the major points sent from reviewers in the course of the peer review.
Dear author
Your paper received a new round of review, and although I would like to provide you with a final decision, I cannot leave the concerns of Reviewer 2 at this point. I invite you to read the reviewer's comments and provide a rebuttal letter accordingly.
no comment
no comment
no comment
The authors have addressed my prior concerns.
In regards to stated Journal Criteria:
These issues are fine.
In regards to stated Journal Criteria:
The experimental design itself is fine. The dependent measures calculated are appropriate and appear to have been calculated correctly. Methods are described with sufficient detail.
In regards to stated Journal Criteria:
"Negative/inconclusive results accepted" by PeerJ - The current results are at best "inconclusive" but this is fine. No concerns if reported as such.
All underlying data have been provided -- No concerns.
"Conclusions are well stated, linked to original research question & limited to supporting results": The authors' conclusions are clearly stated, but just not supported by the results themselves as currently presented.
"Speculation is welcome, but should be identified as such": Much of the interpretation of the findings is speculative, but is not presented as such.
While the authors have again made some important improvements to the paper, I must again point out that the underlying substance of several of my prior comments has not really been addressed.
On the issue of the energetic cost results (Previous Review #2, Comment #1 and Review #1, Comment #1):
If indeed, both the current experiments and prior experiments were conducted "correctly" (and let's assume they were - that's fine - no problem), the fact that the present experiment showed changes opposite to those in prior studies using a very similar protocol is then more interesting and more important than if one or more of the different experiments had somehow not been done "correctly". If the results showing both increased and decreased energy cost are both correct, then this would seem a potentially very important finding, worthy of including in the main paper (not just the supplement) with some appropriate explanation. (This issue is, however, of somewhat lesser concern).
On the issue of interpreting the R^2 results (Previous Review #2, Comment #5 and Review #1, Comment #8):
The issue here is not really that I as a reviewer have a different "opinion" as to how to interpret these R^2 measures. To be honest, I really don't care. The issue is that the manuscript itself includes statements that contradict the conclusions being drawn. If indeed (Lines 244-246) "we cannot rule out that the passive dynamics play a role in the correlation..." and that (Line 246) "further studies are needed...", then one cannot then conclude that (Lines 283-284) "ML foot placement is adjusted to ML trunk CoM state to control ML stability..." Yes, this is one possibility. But the alternative possibility that the effects measured here could be attributable instead to passive dynamic effects, as the authors themselves directly state (Lines 244-246) still cannot be ruled out. The authors offer (Lines 60-64) evidence from other studies regarding "sensory illusions", "visual perturbations", "muscle activity" and "neurological disorders". These may be fine in the context of those experiments, but do not directly relate to THIS experiment conducted here.
I see 2 options here: One is for the authors to provide a coherent explanation for how and why, in THIS experiment, which compared walking to running and did so with and without adding passive elastic springs at the waist... why and how these specific manipulations did NOT alter the passive dynamics of locomotion. The alternative option is for the authors to offer a balanced presentation (consistent with their own statement on Lines 244-246) across the manuscript that offers changes in passive dynamics as an EQUALLY plausible explanation for the findings.
On the issue of "stability" (Previous Review #2, Comment #6 and Review #1, Comment #9):
Again, the issue here is not a difference of "opinion" but that the authors make statements (in their responses and in the manuscript) that contradict each other. They define "stability" (Line 45) as "maintaining a steady gait pattern without falling in the face of perturbations". This is great! But it remains not at all clear how (or even if) any of the measures reported here reflect this definition of "stability". Indeed, the manuscript claims (Line 52) that "foot placement strategy is the main mechanism [used] to control medio-lateral (ML) stability" But if this is true, then if R^2 is a measure of this "strategy" or "mechanism" itself (as claimed, see previous comment), then R^2 is not (itself) a direct measure of "stability" which is the result or outcome of that "mechanism". So does R^2 quantify the mechanism or the outcome of the mechanism? This is not clear, and the manuscript at various points implies both. Thus, that R^2 may or may not tell us something about "stability" is just as unclear as what it may or may not be telling us about "control". It remains true that there is still no independent or direct measure of "stability" reported here.
Again, I see 2 legitimate options here: One is for the authors to provide such a measure (I had previously recommended MoS / XCoM, but there are others). The alternative option is to remove references to "stability" and to describe the findings directly in terms of what the dependent measures themselves ACTUALLY calculate. With regard to R^2 for example, Wang & Srinivasan (2014) state "Thus, most conservatively, our results are only about the pelvis state’s predictive ability of the next foot position." This is factually correct. To go beyond this (e.g., to "control" or to "stability", etc.) is speculation.
I would like to ask the authors to kindly address the reviewers' comments. Please take attention to the fact that the manuscript manuscript continues to make claims that results may not support and that methods and primary dependent measures simply cannot (by design) tease out. It would be valuable to provide explanation for the seemingly contradictory energy cost results.
• The authors provide the raw data from this study, and code used to analyze these data. In the resubmission, the authors have improved clarity with the addition of new documentation.
• The authors have clearly addressed the majority of my previous concerns regarding experimental design.
• The fifth hypothesis seems out of place. I understand the authors’ desire to include this question, as it was pre-planned. However, I did not think this hypothesis was justified based on the background information provided in the Introduction. The stated hypothesis does not appear to include a direction (e.g. faster speeds increase the correlation between pelvis state and foot placement), so I found it unclear what the expected/hypothesized effect actually was. Further making this hypothesis seem out of place, the statistical test used to test it is not described in the Statistical Analysis section. The manuscript may be clearer if this question is described as a pre-planned analysis (with results included in the Supplementary Material), but is not listed as one of the primary hypotheses in the Introduction.
• It was not clear to me how mid-stance was defined (see p. 7, line 10).
• I’m not sure that I understand the new analysis presented in Figure 3. I think it would be beneficial to describe in more detail (in the Methods) exactly what was done to arrive at these percentages. For example, was “significance” of each beta value determined for leg of each individual participant?
• The authors addressed the majority of my previous comments regarding their findings.
• I suggest not including the paragraph on page 13, lines 10-13. The referenced data are not included in the main text, so I think this conclusion/discussion would better belong in the Supplementary Material.
• I found the sentence starting with “The first hypothesis…” on page 8 line 21 difficult to follow. This may just be an issue of grammar.
• In the legend for figure 7, the (A) panel label is missing.
Previous Comment #1: My primary comment had been that there was an over-emphasis on “hypothesis” testing throughout the manuscript. The authors’ response addresses (mostly) the HARKING question. However, the authors did not address the initial and more fundamental concern that this work is "exploratory" in nature and not fundamentally “hypothesis driven”. The present work focuses on testing "predictions": i.e., of what the authors expected to observe. As I stated previously, this itself is fine for exploratory research. Conversely, a "hypothesis" poses a possible *explanation* for the expected observation. While the results presented in this work are interesting, no true hypothesis regarding the underlying explanations for the results observed is tested. Several possible explanations are speculated in the Discussion and elsewhere, but new experiments would be needed to directly test any of those. Thus, the notion that this work is fundamentally "hypothesis" driven remains over-emphasized throughout the manuscript.
Previous Comment #6 (Previously under “Experimental Design”): I had said that the lack of speed differences across running speed did not justify pooling or averaging data across speeds, when this could not also be done for the walking trials (where only 1 speed was assessed). I suggested the very reasonable alternative of picking one of the 3 running speeds as “representative” and run statistical comparisons between that condition and the walking. The authors responded, stating that “averaging only decreases the variability for the running condition” – But this was exactly my point! Because you averaged across 3 speeds for the running condition, you reduced the variability for *that* condition - but you do not have 3 speeds for walking, so you cannot treat the walking data in the same way. Thus, the walking data will have more variability not because it is inherently different from running, but because the walking and running data were processed differently. Even if “ANOVA is… reasonably robust against violation of the assumption equality of variances”, there is simply no reason rely on this assertion. The alternative I had suggested before would avoid this, removes any doubt of differences found being due to differences in data processing, and is very simple to implement.
Previous Comment #3 (Previously under “Experimental Design”): I had requested justification for using the stiffness of 1260 N/m. The authors’ explanation (in their response and in the paper) is that 1260 N/m was selected (Lines 123-125) “since in a previous study no significant reductions of energy cost, step width, and step with variability were found beyond this stiffness” [cites Ijmker et al., 2013]. The problem is that study was done by the same group in the same lab with the same (or nearly the same?) experimental set-up. And that study reported significant *reductions* in metabolic cost with added lateral stabilization (which is now cited as the rationale for the current study design). However, the present study reports significant *increases* in metabolic cost with the same lateral stabilization. This appears to be a rather glaring contradiction – e.g., it seems very possible the lateral stabilization was simply imposed incorrectly… Or perhaps the metabolic data were recorded / analyzed incorrectly… Or perhaps the Ijmker study was conducted incorrectly. However, rather than addressing this contradiction, the authors merely pushed their energy cost results into their Supplement and then only speculate that (Supplement, p. 7, Lines 7-8) that “These conflicting findings in literature, may be explained by differences in experimental conditions or designs” – but that is not an explanation at all.
Previous Comment #7: The issue of the energy cost results still remains significantly problematic. Pushing these findings to the Supplement does not resolve the discrepancies. Likewise, the revised text (Supplement, pp. 6-7) makes clear that all of the prior studies cited found either significant decreases in energy cost, or no significant changes… Thus, the fact that the present study reports significant *increases* in energy cost with lateral stabilization remains contrary to all of those prior published findings and the current manuscript lacks any explanation for this. Indeed, the main manuscript still claims (Lines 168-169): “Reduced energy costs in stabilized conditions would support that the control of ML stabilization requires energy consumption…” and there is no mention in the main manuscript that the findings themselves were the exact opposite of this assertion, and no explanation in either the paper or the Supplement as to why this occurred.
Previous Comment #8 (also comments #10, 17, & 18): I had pointed out that conclusions about “active control” are simply not supported, either by the results or by the methods used here. The present study computed correlations of CoM state to subsequent foot placement – period. At the beginning of their Intro (Lines 48-49), the authors admit at the outset that “motions of the CoM relative to the BoS are thought to be controlled by passive dynamics as well as active processes [1-3].” The calculations of the correlations themselves alone cannot distinguish what is driving those correlations: active control, passive dynamics, or something else. Indeed, the authors state in their Discussion (Lines 237-242) that these correlations “could also be due to passive dynamic coupling of lower extremity movements to movements of the upper body” and that “the results of current study cannot answer the question whether active control or passive coupling is the underlying cause of this correlation”. This is true! The authors are also correct that aspects of “control” (muscles, reflexes, etc.) likely do influence these correlations also. The fundamental problem is that calculating correlations themselves *cannot* distinguish these! There may well be differences in “control” between walking and running. There may well be differences on “control” without and with external lateral stabilization. And these differences in “control” may affect these correlation calculations. BUT! There absolutely *are* differences (significant ones!) in passive dynamics of walking vs. running. And there absolutely *will be* (by construction) differences in the passive dynamics of stabilized vs/ not-stabilized gaits (precisely because you are adding a passive stabilizing mechanism). And these will also affect these correlation calculations! So the fact that the correlations differ between running and walking and/or between stabilized and not-stabilized cannot be used (by themselves) to infer any reasonable conclusions about the degree to which “control” contributes to these differences.
Previous Comment #9: I had pointed out that references to notions of “stability” in this paper were misplaced, as no measures of "stability" were computed or presented here. The authors largely concurred and re-phrased a number of statements in the paper, but 2 issues remain:
First, I had recommended perhaps computing XCoM-based measures such as “Margins of Stability” (MoS). In their response, the authors indicated that “the XCoM indicates where to place the foot to come to a static equilibrium state. Clearly this is not appropriate for walking/running.” This seems highly disconcerting (1) because of the large body of literature using XCoM & MoS to quantify “stability” of gait (both walking and running) and (2) perhaps more importantly, because both of the more senior authors here (Bruijn and van Dieen) have (together and separately) published multiple papers that used XCoM measures precisely to characterize gait “stability”. So if the claim now is that "Clearly this is not appropriate for walking / running" then one could only conclude that that entire body of literature is now invalid?
Second, the title still refers to “control of mediolateral stability”. In the Abstract, "stability" is mentioned twice in the first 3 sentences and again in the final "We conclude..." sentence. The Introduction starts (Lines 45-46) by defining “gait stability”. First sentence of the 2nd paragraph states that “The foot placement strategy is the main mechanism to control medio-lateral (ML) stability in walking and running.” And so on… So the changes made to the Discussion and Conclusions to remove multiple references to “stability” are laudable, they fall short when the entire paper remains, from the beginning, framed in the context of “gait stability”.
Overall, I do like the findings of the study and I do find the results themselves interesting, thought-provoking, and potentially relevant. However, I think this revised manuscript, while much improved, still goes way too far in trying to connect what was actually calculated to concepts of “control” and concepts of “stability” in ways that are simply not justified here, either by the experimental design or by the dependent measures themselves. While I have no objections to the calculations themselves, I think the authors are getting well out “in front of their skiis” in how they are interpreting them. The paper at this point just needs to be re-written from a neutral and un-biased perspective – reporting the correlations that were calculated at face value for what they are and nothing more than that.
Dear authors. We have new received comments from three reviewers on your paper. Two of reviewers indicated major review or rejection. While most of the concerns should be addressable in a suitable revision, some may require a better description or revision in the approach to the data. Therefore I invite you to reply the reviewers comments providing a rebuttal letters with detailed responses to each question from the reviewers, and a revised version of your manuscript with the edits made visible to the reviewers and editor.
• I have not previously reviewed for PeerJ, so I don’t have a frame of reference for how raw data is typically shared. The authors clearly provide extensive raw data and code, which is admirable. I wonder if it would be possible to provide documentation that makes interpreting these data (or performing future analyses) easier for readers.
• The authors list 5 hypotheses to be tested (lines 91-100). It was unclear to me exactly which statistical tests were used to address each of these individual hypotheses. Would it be possible for the authors to draw a more explicit link between the hypotheses and the statistical methods?
• Could the authors more clearly define “ML foot placement position”? The Methods section reads to me as if this was defined as the mediolateral displacement between the heel of the trailing leg and the heel of the leading leg upon heel strike. I think this is fine, but could cause confusion. While inconsistent across the field, some prior work has defined this measure as “step width”, while “mediolateral foot placement” was defined as the displacement between the CoM/pelvis midline and the heel of the leading leg upon heel strike. Again, I think either definition is fine – as long as it’s clearly defined.
• For clarity, please explicitly state what gait events were used to define the start and end of gait cycles. I think this is defined as heel-strike to heel-strike, but making this explicit would be helpful.
• I think it would be worth stating in the Methods if the ANOVAs included interaction terms (see line 187).
• Did the authors check whether metabolic rate reached a plateau within the 5-minute trials (even if just through visual inspection)? While this is a typical trial duration for quantifying metabolic rate, I wonder if the unusual nature of walking/running in lateral stabilization could potentially lengthen the time until a plateau is reached.
• In my opinion, the presented results are interesting, but also quite complex. I think that readers could be helped by a more detailed Results section – including a description of some of the potentially counter-intuitive results. For example, the authors state that their second hypothesis is supported by a significantly stronger CoM-FP relationship in walking than running. However, I think that the significant difference between ~30-40% of the gait cycle (visible in Fig. 3) is actually due to a stronger relationship in running than walking (based on Fig. 2). Is this correct? If so, I don’t think this contradicts the authors’ big-picture explanation, but probably deserves to be mentioned. Additionally, I think the results presented in Figure 5 would benefit from more explanation. What exactly is indicated by a significant main effect of Condition (Fig. 5A)? By a significant main effect of Mode of Locomotion (Fig. 5B)? By a significant interaction (Fig. 5C)? Presently, only the interaction effects are mentioned – and only focus on one aspect of the apparent significant differences.
• I think including slightly more information in the figures or figure legends would be helpful. In Figures 3 and 5, it may be useful to just state what the shaded areas indicate. In Figure 4, it would be helpful to state what the error bars represent, as well as what the horizontal lines indicate. Are these the results of specific post-hoc comparisons? For example, is the energy cost of Normal walking significantly different from the cost of Stabilized walking, as appears to be indicated in Figure 4C?
• The authors state in the Discussion that trunk mechanics explain over 60% of the variance in ML foot placement (lines 219-220). I think it would be worthwhile to be a little more specific with this statement – this is only the case for trunk mechanics near the end of the gait cycle.
• While not necessary, I would find it valuable if the authors would briefly speculate why they observed an increased energy cost during stabilized locomotion. They are absolutely correct that the results from other groups have been equivocal, but I’m not aware of a previously reported increase.
• In line 120, “trial” instead of “trail”
• Add the intended reference to lines 142-143
• The “first” in line 186 seems out of place. Maybe I’m reading this sentence incorrectly.
• In line 284, I think this would be clarified by “…and others reported no effects…”
There is an over-emphasis on "hypothesis" testing throughout the manuscript that is unwarranted and diminishes the credibility of the manuscript. This work is primarily exploratory in nature. This is perfectly fine, but the manuscript presents all of this work as being "hypothsesis" driven, which it mostly was not. For example, Lines 91-100: For "hypothesis" (2), the proposed "higher aforementioned correlations in walking" cannot be predicted a priori. Likewise, "hypotheses" (4) and (5) are purely conjecture. This comes across as "HARK-ing" (the unscientific process of contriving hypotheses after the results are known). This unwarranted over-emphasis on "hypotheses" continues throughout the Results and Discussion sections in particular. As the dependent measures addressed here have not yet been assessed in running, an exploratory study to determine how running is similar/different from walking is perfectly legitimate, but the manuscript must be written to present the work as such.
The research question being addressed (lateral balance control during running) is original and is of modest relevance to the scientific field.
There are a number of technical and study design issues that need to be addressed, however, outlined below:
Sample Size -- Line 103: No a priori power analysis presented for sample size of N=10. Here, this is an issue as it was raised by the authors (Line 69-70) pointing to a paper of theirs (Ref. #[20]) that is currently under review titled "Small sample size impedes reproducibility..." and yet the sample tested here (N=10) is as small or smaller than prior similar studies cited previously. Thus, the sample size needs to be fully justified and increased as needed to ensure rigorous and reproducible findings.
Experiment -- Line 127: No justification given for using stiffness of 1260 N/m. In Ijmker et al 2013, with same experimental setup, that study tested stiffnesses up to 1820 N/m. It seems entirely likely the present negative results could easily have been due to not providing enough lateral stabilization.
Incorrect Calculation -- Lines 149-161: Calculations are either not correct, or not properly described (see also Fig. 2 etc.). The goal of the regression is to estimate subsequent foot placement based on prior COM state within each *step*. Thus, (Lines 149-150) time normalizing data to 0-100% of the full gait cycle (i.e., one full stride = 2 complete steps) is not correct here, and makes no sense! This subsequently makes the Results largely indecipherable, as representing these calculations across "0-100% of the gait cycle" is inconsistent with the nature of these analyses.
Statistical Analyses -- Section 2.6: Two assumptions appear not justified. First, Supplement Fig, 1 does show significant differences between left & right legs, especially near 50% gait cycle. While Fig. 1B pools across both running and walking, the significant difference appears clearly driven by the walking data as shown in Fig. 1A. The SPM analysis should therefore be run separately for the walking and running data sets to identify what specific differences occurred within walking itself. However, pooling across limbs may still be justifiable if these differences do not represent a primary aim of this study. Otherwise, the authors should choose one limb or the other to analyze.
Second (and more importantly), whether pooling across limbs or not, the lack of speed differences across running speeds does not justify pooling or averaging these data across all running speeds because you cannot also average across multiple speeds for the walking trials. This creates "apples to oranges" comparisons of 1 walking speed to the average of multiple running speeds. The legitimate approach would be to choose one running speed (maybe 9 km/h?) as "representative" and then compare to the one walking speed.
The major concern over the validity of the findings is the issue of increased metabolic cost while being laterally stabilized.
The Introduction (Lines 67-70) makes misleading statements. Refs. [3], [9], [10], and [18] all found consistent and significant reductions in energetic cost. Ref. [19] found small reductions that were not statistically significant, but also was comparing healthy subjects to trans-tibial and trans-femoral amputees and stated that "one outlier in the energy cost data considerably influenced the significance of these results"... Ref. [20] is still "under review" so cannot be assessed. Thus, the balance of evidence (while not "unanimous") does strongly support the idea that lateral stabilization does reduce energetic cost. The only inconsistent findings are those that have been produced by the authors' own lab. The subsequent Discussion (Lines 280-291) just repeats the same misleading statements. The only studies to report equivocal findings are those (like this one) from the authors' own lab. This suggests the possible alternative real reason for such equivocal findings may well be within that specific experimental setup and/or with how the processes and procedures were conducted within those experiments that may have led to the discrepancies.
Secondly, the Discussion is largely speculative, but not presented as such. In multiple places, statements are made as if they were "conclusions" but the statements themselves are not supported by the results presented in the study. For example:
Lines 238-244: Likewise, emphasis on "active control" over "passive dynamics" here is no supported by the data. This is conjecture / speculation. The authors' intuition may well be correct, but the analyses presented do not and cannot address the question of which (active or passive) is the underlying *cause* of these correlations. Both possibilities should be discussed and addressed from an unbiased point of view.
Discussion, In General: Likewise, multiple statements throughout the Discussion refer to what these results imply about maintaining (mediolateral) "stability". All of these statements are conjecture and none are supported by the results because no measures of "stability" were computed or presented. All discussion and conclusions should remain within the scope of the actual results themselves. Any speculation for what implications these results may or may not have for other issues should be very clearly labeled as speculation. Indeed, statements made in the Introduction (Lines 71-83) also seem to strongly argue for quantifying ML Margins of Stability, as this measure directly relates to the changes described. It is not clear why this was not done in this study.
Additional Comments:
Lines 53-54: Yes, both passive dynamics and active control will occur... But the correlation analyses presented here cannot disentangle which is which...
Lines 86-87 (and throughout the manuscript): All measures should be reported in standard SI units - Thus, speeds in m/s, not km/h.
Lines 85-88: The sentence, as phrased, is again misleading - It implies different results from the two different studies, when in fact, both studies report consistent results for the same speeds: i.e., no difference b/t 1.0, 1.2, & 1.4 m/s in Wang 2014 & no differences at 1.0 & 1.2 m/s in Stimpson 2018.
Line 127: No justification given for using stiffness of 1260 N/m. In Ijmker et al 2013, with same experimental setup, that study tested stiffnesses up to 1820 N/m. It seems entirely likely the present negative results could easily have been due to not providing enough lateral stabilization.
Lines 155-157: Referring to the regression equation as a "model" is, while technically "correct", still somewhat misleading. This is simply a statistical regression, to compute a correlation. There are no "cause-effect" relationships defined here. Many readers will assume the authors are referring to some mechanistic model (e.g., a dynamic model of actual walking), which is not the case here.
Line 177: More description and definition of "the SPM method" is required.
Lines 193-194: "Highly correlated" is not defined in this context. R^2 = 0.6 is far from R^2 = 1.0. Additionally, R^2 ranges from very low (< 0.1) to higher values approaching 0.8, depending where in the gait cycle you look. So there is both (1) no a priori definition or expectation of 'how high' (R^2 magnitude) and (2) no apriori expectation of where in the gait cycle such correlations should exist. These results are thus exploratory (which is fine), but are not specifically hypothesis-driven as implied.
Lines 220-223 & Line 228: These statements are not supported by the results. Yes, results show correlations of COM state with subsequent foot placement. But correlations do not constitute causation. No conclusions can be drawn about the extent to which these correlations may or may not reflect "active control" or simply passive dynamics.
Lines 238-244: Likewise, emphasis on "active control" over "passive dynamics" here is not supported by the data. This is conjecture / speculation. The authors' intuition may well be correct, but the analyses presented do not and cannot address the question of which (active or passive) is the underlying *cause* of these correlations. Both possibilities should be discussed and addressed from an unbiased point of view.
Supplement: Descriptions given need to be improved. The statements in the Supplement all refer to differences (or lack thereof) for "running". But the figures (Supplement, Figs. 3, 4, & 4) also show data for walking (4.5 km/h). So the statements made do not match the figures shown.
(1) The term "tight" is used in a few places:
- Line 45: "tight" coordination
- Line 87: "tight" coupling
- Line 245: "tight" ML foot placement
and I was not sure what this term meant. Can more specific term(s) be used instead, e.g. does "tight coordination" really just mean a significant correlation between the variables or a stronger correlation compared to some reference case?
(2) Line 28: It would help for clarity and for framing the scope of the paper if the authors could define in the text "stability" or what it means to be "stable" in the context of this research area and their research question. It seemed to me like it would be something like "reject small (internal, step-to-step) perturbations without falling/slowing", something along those lines.
(3) Line 91: It was not clear to me how correlation between these variables reflects "stabilization by active control". The paper would benefit from spending more time in the Introduction developing this relationship. The distinction between "active" and "passive" control does not seem strictly necessary or helpful in this particular paper (unclear how anything concrete on this distinction could be be inferred from these data).
(4) Line 142: Appeared to be a missing reference here
(5) Line 162: Suggest referring to this variable as the "metabolic rate" (or something similar) instead of the metabolic energy expenditure.
Line 99: I didn't understand the basis for hypothesis #5. There is not much about speed in the Introduction. The authors might consider removing this hypothesis to improve the focus of the study on the other more strongly emphasized hypotheses. I didn't think the speed element added much here.
Line 103: Given the relatively small sample size and multiple comparisons, please consider reporting some related statistics e.g. what was the minimum detectable difference or what was the power level for the minimum effect of interest?
Line 158: Why does the model need to include both position and velocity, or if this is not needed, why were both chosen for inclusion? The basis for the model should be briefly explained here beyond just stating what the terms are.
Line 174: I was confused on what was done here with the statistics. How were the R^2 values averaged? They are usually not normally distributed in which case an arithmetic average is probably not appropriate. I had the same concern over using the F-test to test for differences in R^2 values (Line 178); these are typically compared using Fisher's z-transform or something similar, was this done? On Line 176, what is meant by the "R^2 time series"? R^2 is typically just a single number. At a minimum some more detail here is needed. A graphic demonstrating the "flow" of the data analysis might be helpful.
Related to the previous comment, overall I could not tell how the outcome variables were produced. It seems there are a time series of R^2 values, one at each 1% of the gait cycle, but from the description on Line 155 I did not understand how this model produces such data. Earlier text stated (Line 92) stated that the Trunk CoM during swing was being related to the subsequent foot position in stance. How exactly does model do that? It is not clear. This made it very hard to evaluate the paper.
Given the large number of comparisons made in a non-exploratory study, the threshold p-value of 0.05 is not appropriate.
Concerning the estimation of trunk ML CoM, why not just use the force data to calculate the (change in) whole-body CoM? An estimate seemed unnecessary. Or does the framework here require trunk CoM specifically and would not apply to whole-body CoM? It would help to explain this somewhere in the text concerning the choice of outcome variables. I realize trunk is a large fraction of the whole body mass but the notion of whole-body stability seems more relevant to whole-body CoM than trunk CoM.
The interpretation of the results seemed rather subjective and I struggled to understand what results most of the inferences in the Discussion were based on and why. What is it that makes these correlation results "high", "strong", etc.? What are the statistical outcomes supporting these statements? Why are these particular periods of the gait cycle emphasized? What is the basis for the statement on Line 245 that ML placement control is "less tight" in running?
The result of greater energy cost with lateral stabilization needs more Discussion. Previous studies to my knowledge have all either shown a reduction in cost or no change in cost. Are there differences in the equipment that could explain this?
There is good data here, but (with respect to the effort of the authors) I was not able to understand how the main outcome was calculated and the basis on which inferences were made from it on the hypotheses. Overall I thought there was too much here for a single paper. Suggest focusing on a smaller number of outcome variables (e.g. are the step width outcomes needed?) and explaining more clearly how changes in these variables with external stabilization reflects the importance of ML control of foot placement on stability.
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