All reviews of published articles are made public. This includes manuscript files, peer review comments, author rebuttals and revised materials. Note: This was optional for articles submitted before 13 February 2023.
Peer reviewers are encouraged (but not required) to provide their names to the authors when submitting their peer review. If they agree to provide their name, then their personal profile page will reflect a public acknowledgment that they performed a review (even if the article is rejected). If the article is accepted, then reviewers who provided their name will be associated with the article itself.
Dear authors,
You have addressed all reviewers' comments.
I consider that the manuscript is ready for publication.
# PeerJ Staff Note - this decision was reviewed and approved by Mike Climstein, a PeerJ Section Editor covering this Section #]
The review included adjustments in the title, abstract, methods and discussion to adhere to a proof-of-concept study design. In addition, the authors appropriately softened the statements about their results, inferences from them and improved the limitations session. The manuscript is much improved.
above
above
above
The remaining issues within the manuscript are well described by Reviewer 3, specifically soften the message in the basis of your study design as follows: "Although the strict pre vs post comparison has been done, these findings necessitate further empirical verification including a control group."
Further, consider revising the following points:
- line 242, use body mass instead of weight (elsewhere).
- line 250, double dots
- in the introduction, consider including some findings showing alteration on postural adjustments in irregular vs. regular terrain.
- line 211 - consider using main instead of official
- line 305 and final abstract - the term "however" is weird, consider using "Further", or "furthermore".
- limitations - given that the sample size calculation was not done, you cannot infer on that, even claiming a greater sample size. Please, include a sample size calculation in the methods and, on the basis of the output, organize the statement accordingly.
-
-
-
Major comments
I acknowledge the relevance of the study, despite the methodological design being inadequate to demonstrate that a foot exercise program can alter plantar arch dynamics and functional balance. The absence of a control group, lack of blinded assessment, absence of a sample size calculation (the calculation was based on an effect size of 0.66, of which variable? What evidence supports that the SFE changes 0.66 of which outcome?), and the absence of participant randomization are critical limitations. Pre–post studies lack comparative elements, have limited statistical power, and do not adequately control for variables, which can lead to inconclusive or misleading results, making it difficult to determine whether observed changes are due to the intervention or to external factors.
Even if the intention was to assess the acute effect of an intervention, the ultimate goal remains to evaluate its effectiveness. The methodological design that provides the highest level of evidence will always be a randomized controlled trial.
I understand the authors’ arguments in their rebuttal letter about assessing whether any functional change could be observed after a single 2-hour SFE session. Nevertheless, this constitutes a proof-of-concept study rather than a study evaluating the effect of an intervention. Based on the data presented and the authors’ explanations, I can make an effort to frame this work as a proof-of-concept attempt—testing whether even a single session could promote functional changes in foot performance and balance—while recognizing that it remains unknown whether such acute, purely functional effects would persist over time or what impact they would have on the practiced sport (trail running).
Considering that redesigning the methodology would require discarding all current results and initiating a new study, the decision to publish should, at a minimum, be accompanied by a more explicit and thorough statement of the methodological limitations in the discussion—particularly the limitation of testing an intervention without using the appropriate method (i.e., a randomized controlled trial, which is more than simply having a control group). This limitation was addressed only superficially (“the long-term effects of the SFE could not be assessed, and the study lacked a control group”). In addition, the manuscript should clearly identify this as a proof-of-concept study rather than a quasi-experimental one, explicitly stating “proof-of-concept” in the title, abstract, methods, and discussion.
It is inappropriate to claim (lines 346–351) that the present findings are similar to those reviewed in Wei et al. (2022), given that the studies in that systematic review all employed appropriate designs for making such inferences, which is not the case here. Chronic use of the short foot exercise in a systematic training program may indeed lead to increased strength of the intrinsic foot muscles, but this is not what was investigated in the present study. Similarly, it is inappropriate to state that “SFE may represent both mechanical and neural adaptations” (lines 355–356), as no evidence measured in the current study supports such a claim. The change observed in the dynamic balance test is unlikely to result from potential adaptations induced by a single session of short foot exercise.
Conclusion
A proof-of-concept study is a preliminary investigation designed to determine whether an idea, method, or intervention shows signs of feasibility and potential efficacy before investing in larger, more rigorous trials. These studies are not intended to provide definitive evidence of effectiveness but rather to explore whether the proposed approach is plausible and worthy of further investigation. In the present case, the work can be positioned as a proof-of-concept demonstrating that even a single SFE session may induce short-term functional changes in foot performance and balance. However, the manuscript must be revised to explicitly frame it as such throughout (title, abstract, methods, and discussion) and to clearly communicate that these findings are exploratory, limited in scope, and not conclusive evidence of intervention efficacy.
-
-
Please review all criticism, suggestions, and comments carefully, replying point-by-point and marking the location of your responses within the text. The reviewer raised fundamental points that required a clear response regarding the general rationale of your study. I suggest increasing the background on possible mechanisms supporting these acute improvements and reinforcing that the improvements were observed in specific tests, rather than directly related to trail run performance. Consider all comments of reviewers 1 and 2 as well, and provide a better explanation in all chapters of the paper.
Lines 77 and 78: It appears that references in Vancouver format have been used in both paragraphs. Please correct.
Line 97-106: The connection between paragraphs 2 and 4 is interrupted by the topic addressed in this section of the introduction. The authors correctly describe the importance of the core-foot and the variables related to it from lines 74 to 96, but then abruptly jump to referring to training time as an injury risk. Since injury risk is addressed in paragraph 1, I would recommend moving part of this topic to the beginning if necessary. Not in such an extensive manner, but as one of the factors to consider regarding risk. Additionally, at the end of the introduction, between lines 117-119, the authors state, "We anticipate that runners with higher weekly training will exhibit a greater improvement in arch height index and perform better on the dynamic balance test compared to those with lower training volumes." The basis for this hypothesis should be clarified, as it implies that longer training time has a positive impact, given that this factor has previously been linked to an increased risk of injury.
Line 136: The authors state "invited by phone". Did you mean "invited by phone call"?
Figure 1: The image shows TOE, and the description specifies RTOE. Please fix it.
Line 296: I recommend separating the paragraph after "...Rebolledo, 2016).", since they begin to refer to another variable
Line 161-162: Please specify the length measurement protocol or reference procedure.
Line 213-215: The authors state, "The study sample was analyzed according to sex, age, weight, height, BMI, accumulated kilometers, years of practice, and weekly training volume, using Percentages, frequencies, and standard deviations." Are you referring to the application of a normality test to analyze the sample characteristics? It seems that a subanalysis was performed for each of these categories. Please clarify.
Figures 2 and 3: I recommend adding comparative and statistical significance symbols (*)
The t-test showed differences in the range of the test in all directions between pre- and post-exercise, however, it is not commented on in the initial paragraph of the discussion.
Line 290- 294: The authors state, "Similarly, the load or frequency of the short foot exercise might influence foot mechanics and performance among trail runners, given that fatigue of the IFM is significantly correlated with greater navicular drop (Headlee et al., 2008). This is particularly relevant considering that participants with low training volume did not show changes in the AHI of the foot pre- nd post-SFE." This argument doesn't make much sense. Were the subjects with low training volume fatigued? Was fatigue responsible for the navicular drop? If the short foot exercise was applied under the same prescription in both groups, this couldn't be an argument for the difference observed between high and low volumes.
Line 303-306: Regarding anterior reach improvements, the authors state, "Our results can be interpreted based on the premise that individuals with lower weekly training volumes are less conditioned. Consequently, their initial adaptation to a functional test like the YBT may result in greater gains following training compared to those with more experience and higher weekly training volumes". The authors identify among their anthropometric variables the years of practice of the discipline, establishing that subjects in the low training volume group have approximately 4 years, versus 2.9 years in the high-volume group. This contrasts with the idea that they are less adapted subjects. In other sports disciplines, the anterior reach of the Y-BALANCE test has been related (albeit poorly) with the risk of lower limb injury (Read et al. 2020. Utility of the anterior reach Y-BALANCE test as an injury risk screening tool in elite male youth soccer players), so it is possible that the authors' findings are more related to those types of factors. The Y-BALANCE test is a multifactorial test, and although short foot training is expected to improve plantar arch positioning, it may not be able to improve overall performance. The authors did not measure joint angles, neuromuscular activity, or proprioception, nor the runners' previous experience in the test, so the justification or hypothesis proposed regarding this variable must be solid. Even more so, considering that it contrasts with the AHI findings discussed previously.
The article is well-structured and written, and is coherent throughout. The topic is interesting for the discipline and has considerable potential for development. It also includes a specific cinematic analysis of the foot, which the authors should emphasize. However, there are some considerations detailed in the comments that must be addressed, as they compromise the argumentative soundness of the document.
The authors should argue in the introduction why there is a need for a sub-analysis based on training volume. The introduction and discussion make it clear why IFM training would improve arch size; however, the arguments associated with training load are ambiguous and inconsistent, given the conflicting results. This would allow them to better substantiate their proposed hypotheses. Additionally, the relationship between exercise and improved plantar arch size is well argued, but this is not the case for the improvements achieved in reaching distance.
In general, the English is clear, unambiguous and professional. However, there are some style issues that could be improved. For example, repetitive adverbs and redundancies (e.g. additionally, furthermore, are repeated in nearby sentences in the same paragraph).
The Introduction and background are clearly written, well structured and informative. However, some statements lack sufficient references. For exemple, In recent years, this sport has experienced remarkable growth in popularity, establishing itself as the leading all-terrain running discipline (Mocanu, 2015). 2015 do not is recent years. Despite this, in general, literature presented is well referenced and relevant.
Structure conforms to PeerJ standards, discipline norm. However, in this section, the authors innapropriately use the Vancouver style of references, in the lines 76 and 78. It is recommended to review and correct this.
As for the 3 figures presented, the first illustrates the experimental procedure and figures 2 and 3 present graphs of results. Although the first figure could be of better quality, since there is a lot of visual pollution in the background, they are in agreement.
An additional figure illustrating the exercises performed for the foot would be very interesting to clarify to the reader how the experimental procedures were applied.
Raw data supplied are in conformity.
This is original primary research within the scope of the journal.
Research question well defined, relevant & meaningful. Moreover, it is stated how the research fills an identified knowledge gap.
The description of the study design is very short, defining the study as quasi-experimental only. The authors could give more details about the study design, for exemple, that is cross sectional, quantitative, ex post facto etc.
Moreover, the authors present part of methods/procedures in this section: Dynamic balance measurements were taken before and after the application of the short foot exercise using the Y-Balance Test (YBT) in the anterior, posterolateral, and posteromedial directions. Additionally, foot kinematics were assessed through the arch height index during the YBT performance.
The above information should be presented in the Procedures section, in my opinion.
It looks like there's a a spelling mistake on line 159: Data such as gender, age, weight, height, BMI, 159 years of running experience, weekly training volume (days per hour of training) and 100 miles per week were recorded in a data sheet. I believe the correct entry would be, in parentheses, hours per day of training, and not days per hour.
The procedures for determining the Arch Index are not sufficiently clear. It is suggested that greater detail be provided on how the kinematic data were used to determine this variable.
The Y-Balance Test (YBT) should be better explained and explored, either with more citations or even with an illustration that facilitates the reader's understanding of the test.
The Short Foot Exercise could be better described. It is a very simple protocol, which should be referenced or at least justified if there is no literature to support it. In addition, it is recommended that the authors clarify which muscles are targeted by this exercise, which agonists and synergists were intended to be exercised. As mentioned previously, a figure would help the reader understand this procedure.
Aditionally, comments on the force exerted, the intensity, and the control of effort or fatigue could be considered. Were these maximal or submaximal contractions? Furthermore, why was the 2-minute interval between contractions determined?
Despite this, the research carried out demonstrated scientific rigor, with adequate technical and ethical standards.
The statistical analysis and validity of the data seemed to me to be in agreement.
Although the results are robust and the analysis adequate, the discussion presents relatively old literature. The balance data could be better discussed, considering postural adjustment mechanisms and the participation of the sensorimotor complex of the feet. Suggest an update of the literature for the discussion section. In addition, it is suggested that the authors carry out a better conception of the balance mechanisms in relation to the intrinsic musculature of the feet.
For example, regarding the argument initiated in line 296: Previous research has shown that short-foot exercise stimulates proprioceptors in the sole of the foot, increasing afferent input to the spinal cord. This, in turn, improves voluntary muscle activation and stability (Newsham, 2010). This would explain the significant changes in dynamic balance in all directions when comparing the pre- and post-SFE periods among the trail runners evaluated.
The authors could seek more references and relate the importance of the intrinsic musculature of the foot and the sensorimotor complex with the arch index and especially with the mechanisms of balance maintenance and recovery that may be related to this variable. It is suggested to deepen this rationale.
Below are some examples with a quick search of up-to-date literature that can be explored in discussing the study results.
Effect of intrinsic foot muscles training on foot function and dynamic postural balance: A systematic review and meta-analysis
Z Wei, Z Zeng, M Liu, L Wang - PLoS One, 2022 - journals.plos.org
HTML] Intrinsic muscles of the foot: Anatomy, function, rehabilitation
JR Jastifer - Physical therapy in sport, 2023 – Elsevier
[HTML] Randomized clinical trial: The effect of exercise of the intrinsic muscle on foot pronation
M Pabón-Carrasco, A Castro-Méndez… - International journal of …, 2020 - mdpi.com
The conclusions are simple but coherent. A more robust discussion could contribute to improving the quality of the study and its conclusions. I reiterate the importance of including in the justification the relationship between the arch index and body stability and the intrinsic musculature of the feet with static and dynamic balance, considering that the balance test used in the research also seeks arguments for the applicability of the results in trail running.
This is a cross-sectional research article with a simple experimental design, but with a contemporary theme. The English language is adequate. The methodology should be more detailed, the discussion should include more information and more current literature. The article is of the quality required for publication, but needs adjustments. Some typing errors are highlighted in the text. Thank you very much for the opportunity. I will remain at your disposal.
Although the authors’ effort in conducting the study and identifying the importance of investigating the effects of specific exercises for the intrinsic foot muscles in the studied population is recognized, it seems unlikely that a single acute intervention would be sufficient to modify functional status, strength, and muscular response of the foot. These muscles are typically underused in individuals who wear conventional, supportive footwear, such as trail runners, who are therefore more likely to exhibit atrophy in this musculature. Thus, the effect of a brief exercise session on muscle trophism, strength, and function under such conditions of disuse would be virtually negligible.
The change observed in the dynamic balance test (Y-Balance Test, YBT) is unlikely to be the result of potential adaptations derived from foot training using the short foot exercise. Even assuming that the short foot exercise stimulates proprioceptors in the sole of the foot, it is difficult to accept that it would acutely enhance voluntary muscle activation and stability to the extent of explaining the significant improvements in dynamic balance observed post-exercise in trail runners.
Chronic use of the short foot exercise in a systematic training program may indeed lead to increased strength of the intrinsic foot muscles (as pointed out by the authors in lines 88–89), thereby contributing to adequate support of the medial longitudinal arch. However, this effect would be expected only with chronic training, as reported in the studies cited by the authors.
The authors justify their study by stating that “potential acute effects of the short foot exercise on dynamic postural control and foot kinematics have not yet been investigated as a possible strategy for injury prevention in trail runners” (lines 109–111). However, the mere absence of prior studies does not justify the necessity of conducting such research. The research question must be based on plausible rationale, and acutely training a musculature that is likely untrained in the target population does not seem to produce the desired effect. The authors did not present a convincing explanation for why they believe a single session of foot exercise would alter muscle responses, especially given that the references they cite pertain to longer-term, chronic interventions.
Additionally, no theoretical basis was provided to support the hypothesis that runners with higher weekly training volumes would exhibit greater improvements in arch height index or better performance on the dynamic balance test. From this reviewer’s perspective, such a response appears implausible, as meaningful changes in muscle response require, at a minimum, alterations in muscle fiber cellular composition, trophism, and neuromuscular responses—all of which demand an adaptation period of at least 8 to 10 weeks.
It is also important to highlight that the chosen methodological design to address the proposed question was definitely not the most appropriate. In the realm of interventions, the choice between study designs plays a critical role in determining the validity and reliability of findings. When evaluating the effectiveness of an intervention aimed at strengthening foot muscles, employing a randomized controlled trial (RCT) stands out as the gold standard methodology over a pre-post study for several compelling reasons. RCTs ensure higher internal validity by randomly assigning participants, minimizing selection bias and ensuring observed differences are attributable to the intervention. In contrast, pre-post studies lack randomization, making them susceptible to bias and threats to validity.
Furthermore, RCTs are adept at establishing causality between the intervention and outcomes. With controlled conditions and a non-intervention control group for comparison, RCTs enable precise isolation of intervention effects. The inclusion of a control group that does not receive the intervention serves as a crucial benchmark for comparison, enabling researchers to assess the true impact of the intervention by distinguishing between changes attributable to the intervention itself and those resulting from other factors or natural progression over time. In contrast, pre-post studies lack comparative elements, complicating interpretation of whether changes result from the intervention or external factors.
Moreover, RCTs offer greater statistical power and sample size calculation, enhancing reliability and generalizability. By controlling for confounders and randomizing participants, RCTs detect smaller effect sizes with precision, yielding robust conclusions applicable to broader populations. Conversely, pre-post studies often lack statistical power and control over variables, potentially yielding inconclusive or misleading results.
While pre-post studies may offer simplicity and feasibility, they pale in comparison to RCTs in terms of internal validity, causal inference, statistical power, and generalizability. Thus, prioritizing RCTs ensures rigorous methodology, and generates reliable evidence to inform clinical practice effectively.
No comment. Please check item 1.
MINOR ISSUES:
Abstract:
“foot kinematics were measured via the Arch Height Index (AHI) using a 3D motion capture system.” This sentence is somewhat unclear. The authors likely intended to state that they assessed the kinematics of the foot arch using the Arch Height Index (AHI) test, as they did not evaluate foot kinematics in any functional context, but only statically by measuring arch height. When referring to “foot kinematics,” one would typically expect an analysis of joint motion within the foot, not merely changes in arch height. Therefore, I recommend consistently referring to the “kinematics of the foot arch” rather than the “kinematics of the foot.”
Table 1:
- Including both male and female labels in the sex column is redundant. Please include only one, preferably the sex with the largest representation.
- The unit of measurement for “size” should be cm, not “cms.”
- Replace Weight with Body mass. The term “weight” refers to force and should be measured in Newtons.
- Spell out BMI, or define the acronym in a footnote below the table.
Figures 2 and 3:
- The figures should indicate (using an asterisk or similar notation) the presence or absence of statistically significant differences between assessment time points, including the corresponding p-values.
Minor issues:
- Throughout the manuscript, please replace the term “ankle-foot complex” with “foot-ankle complex,” as this is the more universally accepted terminology.
- Line 92: The reported reduction in injury risk in the cited study was 2.42 times, not 2.2.
All text and materials provided via this peer-review history page are made available under a Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.