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Thank you for revising your manuscript to address the concerns of the reviewers. Reviewer 2 now recommends acceptance and I am satisfied that the comments of reviewer 1 have been addressed. The manuscript is now ready for publication.
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I thank the authors for addressing my comments.
**PeerJ Staff Note:** Please ensure that all review, editorial, and staff comments are addressed in a response letter and that any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate.
In the introduction, the sentence "Ankle proprioception (the sense of ankle position and movement in the absence of visual input) [...]" states a quite simplified definition of proprioception. Proprioception is not only defined as the ability to sense position and movement, but also force, effort, and heaviness, as described in Proske & Gandevia (2012). I suggest the authors use a more appropriate definition of proprioception, or phrase this sentence differently, e.g., "kinesthesia, a sub-modality of proprioception that includes the senses of position and movement, is a contributor to standing balance and walking".
The authors should consider adding more information about the corrections of the voluntary activation to the main manuscript. Indicating that values considered as measurement errors were adjusted to ensure they match physiological values does not make much sense. If the value is a measurement error, the authors do not know what the value would have been without the measurement error. Instead, it might be good to explain why these non-physiological values do not influence the results. The explanation provided in the response to reviewers could be summarized and included in the manuscript directly.
The fact that participants receiving the intervention were not instructed to maintain their level of physical activity represents a bias that should be discussed more, especially since there was no difference between groups in proprioceptive outcomes. The control group performed their usual activities, whereas the intervention group might have replaced their usual activities (maybe aerobic exercise or strength training) with stepping. This does not really compare the effect of the intervention itself and is potentially biased by a change in the participant's lifestyle.
Could the authors perform a secondary analysis to distinguish between people who increased their activity during the intervention vs those who did not? It is possible that people who increased it would show improvements that would not be reflected when taking the whole group into account. Similarly, the intervention differed for all participants since they selected the level of difficulty themselves. Is there a difference between people who increased the task difficulty faster vs people who increased it slower, or between people who played a lot vs people who played the minimum time requested? Without these analyses, it is difficult to conclude on the impact of the exergame on proprioception and other outcomes.
In the introduction, please precise if this meta-analysis is for people with MS or the general population.
Both reviewers have requested major revisions. Please attend to all their comments.
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The study includes multiple outcome measures (e.g., proprioception thresholds, voluntary activation, MVC torque). While this increases the comprehensiveness of the results, there is a risk that multiple tests without proper corrections (e.g., Bonferroni adjustments) could inflate type I errors. It would help if the design included a power analysis to ensure the sample size is sufficient for detecting significant effects across all these outcomes.
Methods for Replication:
More detailed information on
1. A clear description of the smart±step system’s calibration and training intensity settings, including how they were adjusted for participants.
2. The specifics of the movement detection task could be clearer, especially the criteria for “correct” responses and whether participants could improve during the task (i.e., learning effects).
3. A more detailed description of the electromyography (EMG) setup for muscle performance testing, including calibration protocols, would improve transparency and allow replication.
4. A specific description regarding the Proprioceptive training program for the experimental group
First, the data from this study are nested within a larger clinical trial (i-FIMS) and present a few potential concerns and limitations that need to be addressed clearly in the manuscript. When a sub-study is part of a larger trial, there are often implications for data interpretation, statistical power, and focus.
Regarding these significant issues, the authors must emphasize the limitations of their results. Since the current study focuses on secondary outcomes (ankle proprioception and plantar flexor muscle performance), the primary research has not been designed with these specific variables as primary considerations. The intervention may have been optimized for reducing falls but may not necessarily improve proprioception or muscle performance. This could mean that the intervention intensity, duration, or measurement method may not be ideally suited to detect changes in these secondary outcomes.
The first major concern is that the methods and intervention may lack specificity for the secondary outcomes, leading to null findings because the trial wasn’t tailored to these particular outcomes. Also, the intervention description does not specify ankle and foot proprioception training exercises.
This must be emphasized in a limitation section.
Secondly, the manuscript mentions that the study was nested within a larger trial. Still, it doesn’t fully explain how this sub-study is distinct or whether the broader trial’s design might have biased or limited its findings for proprioception and muscle performance. Therefore, I suggest the authors delineate how this sub-study's objectives, design, and outcomes were different or similar to the primary i-FIMS trial. Were any adjustments made to suit this sub-study? If not, how might the parent study’s design limit the findings here?
In Table 1, the mean and SD should be provided with two decimals. The authors should also provide a baseline comparison between groups.
Statistical analysis
1. Add effect sizes for each outcome, along with confidence intervals, to provide a clearer picture of the findings' practical significance.
2. The authors should provide a power analysis for the specific proprioception and muscle performance outcomes to show whether the study had sufficient power to detect meaningful differences.
3. Provide more details on the CACE analysis, including how compliance was assessed and its implications for the results.
4. Discuss how multiple testing was managed, including whether any corrections were applied and their implications for the validity of the findings.
5. To enhance understanding of data distribution, consider including interquartile ranges or other measures of variability for skewed distributions.
6. The confidence intervals frequently cross zero, suggesting null effects. A more thorough interpretation of these null results is needed. The authors should explain whether the study was underpowered or if these null effects truly indicate no difference between the groups. It would also be useful to discuss whether the intervention may have led to positive outcomes in a subgroup of participants more compliant with the training.
The introduction provides a general background on multiple sclerosis (MS) and related impairments in proprioception and muscle performance. However,
1. it lacks a comprehensive theoretical rationale explaining why the specific intervention (the smart±step system) is hypothesized to improve these particular outcomes. Please add information in this regard in the introduction section.
2. Please also add information regarding the mechanism of action behind the intervention, specifically regarding improvements in proprioception and muscle performance.
3. more references should be included related to supporting studies or physiological theories on how step training can specifically target proprioception deficits and muscle performance.
4. the introduction should more clearly specify the knowledge gap the study aims to fill
Conclusions:
1. The data mainly support the conclusions but lack a broader context. Given the null results, the authors should have provided more insight into the potential limitations of the intervention (e.g., low compliance, insufficient training intensity) and suggested how these could be addressed in future studies.
The manuscript is written clearly, with professional English throughout the manuscript. However, the literature references and background information are not sufficient. Here are some suggested improvements:
The introduction is short and non-informative. This section should be more detailed and explain in further detail why the authors think the exergame intervention would improve proprioception and motor performance. For example, the authors mention in l. 74-77 “[…] exercise can improve muscle strength and neural drive to muscles […] exercise training also improves walking and balance […], and mobility […].” It would be interesting to describe the type and modalities of intervention used in the cited studies (e.g., how many times a week, what intensity, duration of the intervention, type of exercise, did they also use exergame, etc.). I suggest the authors rewrite the introduction to provide enough rationale on why it is interesting to investigate this research question and how previous work supports their hypothesis.
Like the introduction, the discussion section is short and non-informative, with only a few references cited. I think the authors could discuss more why they were expecting improvements in their outcome variables, and why they did not observe differences. What are the neural adaptations expected with this type of training? In the first paragraph, the authors discuss the lack of difference of several outcomes between people with multiple sclerosis and healthy controls, only citing their own study. What does literature say about these aspects? How do the authors’ results compare with other studies from other research groups? In the second paragraph, the authors could go deeper in the comparison between the studies cited and their work. The total duration, volume, and intensity of training are major components of a training program. The authors should consider discussing these aspects in more detail, comparing the differences between their training modalities and those shown to improve their outcomes in the literature. Similarly, the authors do not discuss the disparity between the 120-min training goal and the average 60-min training reported. Is 60 min a week sufficient to induce a change? The authors could consider investigating deeper if an effect exists in individuals who train longer (for example, less than 60 min training vs more than 60 min training, or once a week vs 3 times a week). These additional analyses would confirm whether the intervention did not induce a change at all, or if the compliance of participants influenced the results. The use of exergames have been reported to improve motor function in other populations. The authors could consider adding a limitation section, or a perspective section, discussing how future work could improve the effectiveness of type of training to improve their outcomes (what could have been improved in their study to increase the likelihood of observing improvements).
The research question and how it fills an identified knowledge gap could be described more clearly, and the methods section could be more detailed.
I have some questions about the inclusion criteria that could influence the authors' results:
1. Were older adults (aged over 65 yrs) included in this study? If yes, how do the authors control for the potential confounding effect of aging of the results?
2. The authors mentioned that participants had “no apparent cognitive decline”. How was this evaluated?
3. Why did participants need to be able to perform the Choice Stepping Reaction Time test? This test is not reported in the paper.
4. Did the authors control for medication that could influence motor control?
The authors could provide a little bit more details on certain aspects of the intervention that would help the reader understand training modalities better.
1. What were the criteria for participants to increase task difficulty of the exergames?
2. How long were participants required to play the two core games every week?
3. How was the 120 min per week goal determined? What were the exact instructions provided to participants regarding practice time (maximum 120 min, exactly 120 min)? Did the authors provide recommendations on the training schedule or was it up to participants (e.g. recommendation for several sessions a week, or one session a week)? Were participants withdrawn if they could not commit to the training goal?
4. The authors mentioned that the control group was instructed to continue their usual activities. Did the intervention group receive the same instructions?
5. I appreciate the thought about providing the educational booklet to the participants but what was the goal of the educational booklet? Were participants of the control group encouraged to follow the exercise mentioned in the booklet?
I have a few comments on the outcome measures included in the study.
1. Why were movement detection threshold and reaction time chosen? What aspect of proprioception does the reaction time evaluate?
2. The term fatigue should be used with caution, especially in the context of multiple sclerosis. The authors should clearly distinguish between fatigue as a symptom experienced by people with multiple sclerosis and performance fatigability assessed in their study. I encourage the authors to adjust their terminology throughout the manuscript to avoid any confusion and clearly state what is assessed. For a review on fatigue vs fatiguability in people with multiple sclerosis: DOI: 10.1177/15459683211046257
3. Why was postural control assessed on a foam mat instead of a rigid surface?
About the setup:
1. What were the consequences for the 5 participants who didn’t wear the same type of shoes in both sessions? Were the data discarded or kept in the analysis?
2. L. 178. Please provide the characteristics of the goniometer used.
3. It is not clear why EMG was recorded during this experiment as none of the results are based on EMG. Why did the authors choose to record the EMG from TA with two electrodes on the muscle, but SOL and GM with a muscle-tendon configuration?
4. It is not clear what the description on l. 187-191 refers to. If this is the setup used for motor performance, the authors could consider moving this section to the section on motor performance.
5. The authors should indicate the characteristics of the motorized footplate used to assess the movement detection threshold and the validity of the device/technique used. What is the sensitivity of the position signal?
6. L. 234. What is the threshold to consider that the MVCs were consistent? L. 240. The authors should consider including some references to justify the use of this specific fatiguing task (2-min MVC). L. 242. What was the delay between the two resting twitches?
7. In my opinion, the authors could report their data on the sense of position, but state clearly that they are using a device that is not validated and mention that these results should be considered with caution. It would be interesting to have the results from two proprioceptive modalities.
8. L. 258. The authors mentioned that the recruitment finished when 66 participants agreed to participate. Did recruitment stop because the authors matched their expected sample size or because no additional participants were willing to participate?
9. I don’t understand how the authors can have voluntary activation values smaller than 0, or greater than 100%. Why were those values altered to fit the physiological range and not excluded from the analysis? A value that is not physiologically plausible does not because plausible by altering it to fit the 0-100% range. I suggest the authors consider these values as not plausible and exclude them from further analysis.
The current version of the manuscript does not allow to fully agree on the validity of the authors' findings. The results of this study could be confounded by several factors, including the modalities of the intervention. Although the goal was 120 min per week, with encouragement for individuals with less than 80 min per week, the authors later report that the mean training time was 60 minutes. In addition, the SD for the practice time is very large. The weekly duration of training and its repartition along the week are important methodological factors that can influence the intervention outcomes. Training once a week for 2 hours is not the same as training 4 times a week for 30 minutes. Was this disparity considered and how can it influence the reported results? The authors should consider providing additional information on the compliance and number of participants who met the 120-min goal, as well as the repartition of the training time on a weekly basis. In addition, as mentioned before, the findings of this study should be compared more to the current literature.
L. 160-161. The authors use the term force, whereas torque is used in the rest of the manuscript. Please homogenize this throughout the manuscript.
L. 350-352. An average of 60.3 (53.5) min, and an average of at least 1h per week is the same.
L. 355. “In summary,” does not summarize the previous paragraph. Please move this sentence to the end of the paragraph. Having the description of the withdrawals after this sentence can make the reader believe these participants withdrawn from the groups of 26 and 28 participants.
L. 358. Lower limb surgery can also impact proprioception. Why were these participants kept for the assessment of proprioception but excluded from the assessment of muscle performance? Are the results different when removing these participants from the analysis?
Data set. What are the negative values for ankle ROM in the excel sheet for controls?
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