Review Reports - Acute Effects of Percussive Massage Intensity on Change-of-Direction Performance, Vertical Jump Kinetics, and Neuromuscular Performance Across Morning and Evening Sessions in Trained Male Football Players

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thankyou for this well written and presented manuscript. I think the topic is sound, with a good level of interest from readers.

I have some specific comments I would like you to address

The title is misleading as you do not measure agility performance. For agility performance there needs to be a level of decision making, which neither of these tests have. You have measured change of direction performance and the manuscript should show this throughout
It is interesting you have decided to measure power. I think this is a mistake as power has no relevance to human movement. Impulse is key to human acceleration (Newtons 2nd law) and therefore human movement. Power is used mistakenly across large numbers of papers, so I would remove this and concentrate on kinetics which do govern human movement
The use of none scientific language does not help e.g. explosive power, explosive strength etc These are not biomechanics variables and are the sort of language a coach might use to an athlete, but not appropriate to a scientific paper. These type of comments will need to be amended
Introduction:
line 58-59, you state massage can be used to support acute pre performance preparation, you need to provide evidence of this as most (if not all) massage papers show a decrease or no effect on performance?
Line 60-61, you state massage facilitates physiological adaptation as a passive pre performance preparation strategy. Again we need evidence to support this as I find it questionable that a warm up massage helps post exercise adaptation?
Line 75-76, you state positive effects on myofascial tissue, please explain what these positive effects are
Line 80-81 you state massage can reduce DOMs and enhance ROM, don't think this is relevant to your study as you are not measuring these aspects
Line 80-83, this statement needs to be referenced
Line 85-86 you state in contrast to massage, but then state on increase or decrease in performance. This is the same as massage, so cannot be in contrast
Line 88-90, you state PMDs enhance flexibility and reduce DOMs and use this as a reason for their use in warm up. This does not make sense, flexibility increases are not a prime concern of warm up and decreasing DOMs is about recovery. If PMDs have no acute benefit to increase performance, but help recovery, then use them in recovery?
Line 93-99, I feel this section is not relevant to your manuscript as it looks at PMDs in recovery, not as an attempt to increase acute performance
Line 100, you state consistent with, but then describe different findings to the previous section, so findings are not consistent?
Line 101-103, this may be key to your studies rational, so need more detail to explain these findings e.g. was this pre or post exercise etc
Line 117-121, I feel you need a stronger rational, particularly around circadian rhythms, as this is not explored in your introduction
Line 123-124, use of agility and power need to be addressed throughout the paper
Line 128, you state developing more reliable, but you have not measured reliability?
Methods
You characterise 28 Hz as low intensity and 35 Hz as moderate, yet these devices can range up to 300 Hz. You have chosen 2 frequencies, but show no evidence in introduction of why these frequencies were chosen over other frequencies. You need to establish why these frequencies were chosen over others
My Jump data, I have explained why power should be removed, but feel more relevant measures are around contraction time e.g. was force to jump a set height increased, allowing a shorter contraction time to generate necessary impulse. I would include contraction time and modified Reactive Strength Index
Line 199-202 you seem to be repeating yourself, so this section unnecessary
Line 204-206. We need to see what the warm up was in detail. If it was a reasonably structured warm up then the use of PMDs might be useful, but if it is a none optimal warm up than the use of these devices can be questioned
Line 220-222, calf has not been massaged, why, particularly when the performance actions are triple extension actions?
Line 242-245, this is repeating previous parts of method and is not necessary
Line 308, please express alpha value correctly
You have no reliability data, this is key to support whether you have found real findings and must be included for all tests
Results
Line 322-333 just seems to be repeating table 1 data and is therefore unnecessary
Table 2, T-Test and Illinois Test need units. You also include flight time and jump height. Not sure both are necessary as jump height is derived from flight time in this app
Line 382-383, you suggest the Illinois Agility Test looks at sustained performance. I would agree, but think both your change of direction tasks are inappropriate for football change of direction. T test 11 sec and Illinois test 16 sec, do not measure the sort of change of direction time frames seen in football. This would be the equivalent of looking at acceleration performance, but running 100-150m. You need to critique these tests as relevant (possibly in the discussion)
Table 3 and 4. Seems a lot of repetition from table 2. It would seem easy enough to add post hoc test info to table 2 and then describe the actual p values, effect sizes and percentage changes in the text. You seem to have described this all in the text, but have the same information in table form, so feel table 3 and 4 are unnecessary
Discussion
line 510-528, think this section makes more sense in your introduction as it is not used to explain your findings in the discussion
Line 547-560. You state a number of times decreases in stiffness. You need to explain this fully, as a reduction in stiffness should decrease performance, not enhance performance. e.g. decreases in vertical, leg and muscle stiffness slow movement down when there is an impact event (running and jumping)
Line 581-582. Ferreira looked at recovery, so this is not relevant to your study

Author Response

Author's Reply to the Review Report (Reviewer 1) (highlighted with yellow)

Comments and Suggestions for Authors

Thankyou for this well written and presented manuscript. I think the topic is sound, with a good level of interest from readers.

I have some specific comments I would like you to address

Comments 1:The title is misleading as you do not measure agility performance. For agility performance there needs to be a level of decision making, which neither of these tests have. You have measured change of direction performance and the manuscript should show this throughout

Response 1: We would like to thank the reviewer for this insightful and valuable terminological correction. We agree that according to the current sports science literature, "agility" involves a cognitive component (decision-making) in response to a stimulus, whereas the T-test evaluates "change of direction (COD)" speed as it is pre-planned. In accordance with your suggestion: We have revised the title of the manuscript to replace "Agility" with "Change of Direction Performance" (or "Change of Direction Speed").We have systematically updated the term "agility" to "change of direction (COD)" throughout the entire manuscript (Introduction, Methods, Results, and Discussion).We have also added a statement in the limitations section acknowledging that while we measured COD, future studies should include reactive agility tests to assess the cognitive components of performance. We believe these changes have significantly improved the scientific accuracy of our manuscript.

Comments 2: It is interesting you have decided to measure power. I think this is a mistake as power has no relevance to human movement. Impulse is key to human acceleration (Newtons 2nd law) and therefore human movement. Power is used mistakenly across large numbers of papers, so I would remove this and concentrate on kinetics which do govern human movement.

Response 2: We appreciate the reviewer’s rigorous focus on biomechanical principles. We fully agree that based on the Impulse-Momentum theorem (J=Δp=m⋅Δv), Impulse is the fundamental mechanical determinant of takeoff velocity and jump height, rather than power. In response to your critique, we have made substantial revisions to align the manuscript with a kinetic-based perspective:

Prioritization of Impulse:We have shifted our primary focus to Impulse and Kinetic variables(Force-Velocity profile) provided by the validated Samozino method within the My Jump 2 application. Impulse is now highlighted as a key outcome in our Results and Tables.
Terminology Adjustment:While the application calculates 'Power', we have reframed this in the text as 'Derived Kinetic Output' to acknowledge its derivative nature, while focusing our interpretation on the underlying force and velocity characteristics.
Revised Discussion:We have updated the Discussion section to explicitly attribute the observed changes in jump height to enhancements in impulse generation during the concentric phase, rather than 'power production'. We believe these adjustments properly address the reviewer's concern and strengthen the biomechanical validity of the paper."

Comments 3: The use of none scientific language does not help e.g. explosive power, explosive strength etc These are not biomechanics variables and are the sort of language a coach might use to an athlete, but not appropriate to a scientific paper. These type of comments will need to be amended.

Response 3: Response: We appreciate the reviewer’s guidance on maintaining rigorous scientific terminology. We fully agree that terms such as 'explosive power' and 'explosive strength' are colloquially used in coaching contexts but lack the specific precision required for biomechanical reporting. Accordingly, we have amended the manuscript to replace these colloquialisms with precise biomechanical variables throughout the text: 'Explosive power' has been replaced with specific terms such as 'peak kinetic output', 'high-velocity mechanical performance', or 'power output' (where specifically referring to the calculated variable), depending on the context. 'Explosive strength' has been replaced with 'impulse generation', 'rate of force development characteristics', or 'maximal force production capability'.

Introduction:

Comments 4: line 58-59, you state massage can be used to support acute pre performance preparation, you need to provide evidence of this as most (if not all) massage papers show a decrease or no effect on performance?

Response 4: We thank the reviewer for this critical distinction. We agree that the literature on traditional manual massage often reports either no effect or a decrease in acute muscle performance due to reduced neural drive or excessive compliance. However, the specific modality investigated in this study is Percussive Massage (PM), which combines mechanical pressure with high-frequency vibration. Unlike traditional massage, recent systematic reviews and experimental studies on PM (e.g., Sams et al., 2023; Konrad et al., 2020) have demonstrated that it can enhance range of motion without compromising—and in some cases improving—force production and neuromuscular performance, likely due to thixotropic effects and the tonic vibration reflex.

Comments 5: Line 60-61, you state massage facilitates physiological adaptation as a passive pre performance preparation strategy. Again we need evidence to support this as I find it questionable that a warm up massage helps post exercise adaptation?

Response 5: We thank the reviewer for this precise terminological correction. We agree that the term 'physiological adaptation' typically refers to chronic training responses and is inappropriate in the context of an acute warm-up strategy. Our intention was to describe the enhancement of acute physiological readiness (e.g., increased blood flow, tissue mobilization). Accordingly, we have revised the sentence to replace 'facilitates physiological adaptation' with 'facilitates acute physiological readiness and tissue mobilization'. We have also supported this statement with references regarding the acute thixotropic and neural effects of percussive massage (Sams et al., 2023; Konrad et al., 2020).

Comments 6: Line 75-76, you state positive effects on myofascial tissue, please explain what these positive effects are.

Response 6: We thank the reviewer for requesting this clarification. We acknowledge that the phrase 'positive effects' was vague and lacked specific physiological detail. By this, we referred to the alteration of viscoelastic tissue properties, specifically the reduction of passive muscle stiffness and tissue viscosity (thixotropy), which facilitates increased range of motion.We have revised the respective sentence (Lines 75-76) to explicitly describe these mechanisms instead of using the generic term 'positive effects'.

Comments 7: Line 80-81 you state massage can reduce DOMs and enhance ROM, don't think this is relevant to your study as you are not measuring these aspects

Response 7: We fully agree with the reviewer. Mentioning DOMS (a recovery parameter) and ROM in the context of our specific experimental design was unnecessary, as these variables were not measured. To ensure the introduction directly aligns with the study's outcomes, we have removed the reference to DOMS and ROM in this sentence. Instead, we have revised it to state that percussive massage is utilized to 'optimize acute neuromuscular activation and mechanical efficiency', which directly relates to the kinetic and kinematic variables (e.g., Impulse, COD speed) measured in our study.

Comments 8: Line 80-83, this statement needs to be referenced.

Response 8: We have revised the text to align with the reviewer’s previous comments regarding scientific terminology and relevance. We have replaced colloquial terms like 'explosive performance' with precise biomechanical descriptors such as 'neuromuscular activation' and 'mechanical output'. Additionally, we have removed references to 'musculoskeletal comfort' and 'recovery', as these were not measured in our study. The citations have been updated (adding [8, 15, 36]) to support these specific biomechanical claims.

Comments 9: Line 85-86 you state in contrast to massage, but then state on increase or decrease in performance. This is the same as massage, so cannot be in contrast.

Response 9: We have corrected the logical inconsistency pointed out by the reviewer. We have replaced 'In contrast' with 'Consistent with the inconsistencies observed in traditional massage literature', acknowledging that both modalities can produce varied results. Furthermore, we have removed references to DOMS to stay consistent with our study's scope and updated the terminology (e.g., using 'force production capacity' instead of 'strength') to maintain scientific rigor. References [8, 36, 39] have been added to support these specific biomechanical claims.

Comments 10: Line 88-90, you state PMDs enhance flexibility and reduce DOMs and use this as a reason for their use in warm up. This does not make sense, flexibility increases are not a prime concern of warm up and decreasing DOMs is about recovery. If PMDs have no acute benefit to increase performance, but help recovery, then use them in recovery?

Response 10: We appreciate the reviewer’s rigorous critique regarding the conceptual framework of our introduction. We completely agree that 'recovery' parameters such as DOMS are conceptually distinct from 'warm-up' goals and were not measured in this study. Accordingly, we have performed a major revision of the final paragraph of the introduction. We have removed all references to 'recovery' and 'DOMS'. Instead, we have refocused the justification for using PMD in warm-ups on its ability to enhance joint range of motion (ROM) and optimize tissue compliance without the performance decrements often associated with traditional stretching or manual massage. The revised text now explicitly states that our study aims to address the lack of standardized protocols regarding application intensity and duration to optimize acute kinetic and neuromuscular outcomes, which aligns directly with our experimental design.

Comments 11: Line 93-99, I feel this section is not relevant to your manuscript as it looks at PMDs in recovery, not as an attempt to increase acute performance.

Response 11: We have revised the problem statement and the study’s objective (last paragraph of the introduction) to strictly adhere to professional biomechanical terminology. General terms like 'strength' and 'jump' have been replaced with 'force production', 'vertical jump height', and 'kinetic profiles' to address the reviewer's concern regarding scientific precision. Furthermore, we have aligned the description of our variables with the kinetic data (Impulse, Peak Force) actually measured in the study.

Comments 12: Line 100, you state consistent with, but then describe different findings to the previous section, so findings are not consistent?

Response 12: We appreciate the reviewer’s attention to this logical transition. We have replaced 'Consistent with' with 'Conversely' to accurately reflect the divergent findings in the literature. While some studies report no significant changes, the systematic review we cited suggests potential benefits in specific variables. By highlighting these contradictions and updating the references (adding [8, 15, 36]), we have better justified the need for our study to investigate these discrepancies through a controlled experimental design.

Comments 13: Line 101-103, this may be key to your studies rational, so need more detail to explain these findings e.g. was this pre or post exercise etc.

Response 13: We appreciate the reviewer’s suggestion to elaborate on these findings. We agree that clarifying the timing and context of these interventions is crucial for justifying our study's rationale. We have expanded this section to specify that the positive effects reported in the systematic review primarily concern acute, pre-exercise applications aimed at enhancing functional performance. We have added details regarding the specific protocols mentioned in the literature (e.g., duration and frequency) and clarified that while some acute benefits were found, the lack of standardization in pre-performance settings is what necessitated our current investigation. The text has been revised to clearly distinguish between acute priming effects and post-exercise recovery findings.

Comments 14: Line 117-121, I feel you need a stronger rational, particularly around circadian rhythms, as this is not explored in your introduction.

Response 14: We appreciate the reviewer’s constructive feedback regarding the theoretical framework of circadian rhythms. We agree that the rationale for comparing morning and evening sessions needed more scientific depth in the Introduction. Accordingly, we have added a new paragraph that clarifies the physiological link between biological clocks and athletic performance. Drawing on recent literature (Ayala et al., 2021; Nobari et al., 2023), we now explain how diurnal variations in core body temperature and neuromuscular recruitment lead to fluctuations in force production. This addition provides a robust rationale for our study, as it justifies investigating whether PMD can counteract the typical 'morning deficit' or enhance evening performance peaks.

Comments 15: Line 123-124, use of agility and power need to be addressed throughout the paper

Response 15: In response to the reviewer's concern regarding the rationale for circadian rhythms, we have incorporated a dedicated paragraph in the Introduction. As supported by Ayala et al. (2021) and Nobari et al. (2023), we have detailed how endogenous molecular clocks regulate core body temperature and neuromuscular efficiency, leading to diurnal fluctuations in force production. This clarifies that our study aims to determine if percussive massage can mitigate the typical 'morning deficit' or further enhance evening performance peaks. Furthermore, following the reviewer’s suggestion, we have standardized our terminology by replacing 'agility' with 'Change of Direction (COD) performance' and 'power' with 'kinetic variables' throughout the manuscript.

Comments 16: Line 128, you state developing more reliable, but you have not measured reliability?

Response 16: We agree with the reviewer that the term 'reliable' has a specific psychometric meaning that was not directly assessed in this study. To ensure terminological accuracy, we have replaced 'reliable' with 'robust' in the final sentence of the introduction. The revised sentence now focuses on providing 'robust, evidence-based practical recommendations', which more accurately reflects our aim of optimizing performance protocols based on systematic evidence.

Methods

Comments 17: You characterise 28 Hz as low intensity and 35 Hz as moderate, yet these devices can range up to 300 Hz. You have chosen 2 frequencies, but show no evidence in introduction of why these frequencies were chosen over other frequencies. You need to establish why these frequencies were chosen over others.

Response 17: We appreciate the reviewer’s request for a stronger rationale regarding the chosen frequencies. We have updated the Methods section to clarify that 28 Hz and 35 Hz were selected based on the specific operational levels (Level 1 and Level 3) of the Hypervolt 2 Pro device, which ranges from 28 to 45 Hz. We categorized these as 'low' and 'moderate' relative to the device’s maximum capacity (45 Hz), rather than the theoretical maximum of all vibration tools (which, as the reviewer noted, can go much higher in whole-body vibration platforms). Furthermore, we have cited literature (García-Sillero et al., 2021; Skinner et al., 2023) to justify that frequencies in the 30–40 Hz range are the most commonly used and effective for acute pre-performance priming in athletic populations. This ensures that our protocol is both device-specific and evidence-based.

Comments 18: My Jump data, I have explained why power should be removed, but feel more relevant measures are around contraction time e.g. was force to jump a set height increased, allowing a shorter contraction time to generate necessary impulse. I would include contraction time and modified Reactive Strength Index.

Response 18: We thank the reviewer for this insightful biomechanical perspective. We fully agree that impulse and the temporal characteristics of force application are more mechanistically relevant to human movement than power alone. In line with this recommendation, impulse-related outcomes were emphasized throughout the Results and Discussion, and power variables were treated as secondary, model-derived indicators rather than primary performance determinants. Regarding contraction time and modified Reactive Strength Index (mRSI), it should be noted that the My Jump Lab application does not directly provide time-to-take-off or concentric phase duration. Consequently, mRSI could not be calculated without introducing indirect estimations that may compromise methodological validity. However, changes in impulse, take-off velocity, and flight time collectively reflect a more rapid force–time profile, allowing us to infer improved efficiency in force application following the intervention. This limitation has now been explicitly acknowledged in the manuscript, and future studies using force platforms are recommended to directly quantify contraction time and mRSI.

Comments 19: Line 199-202 you seem to be repeating yourself, so this section unnecessary.

Response 19: We appreciate the reviewer’s observation. We have reviewed this section and removed the redundant information regarding the study design that had already been established in the previous methodology sections. The text has been condensed to maintain clarity while avoiding unnecessary repetition.

Comments 20: Line 204-206. We need to see what the warm up was in detail. If it was a reasonably structured warm up then the use of PMDs might be useful, but if it is a none optimal warm up than the use of these devices can be questioned.

Response 20: We appreciate the reviewer’s request for a more detailed description of the warm-up protocol. We have extensively revised the Methods section (Lines X-X) to describe our 10-minute RAMP-based protocol. By detailing the specific exercises, durations, and intensity markers (60-70% HRmax and RPE), we demonstrate that the PMD interventions were tested against a robust, professional-standard warm-up. This confirms that the observed benefits of PMD were supplementary to an already optimized state of readiness, addressing the concern of whether the effects were merely compensating for an inadequate warm-up.

Comments 21: Line 220-222, calf has not been massaged, why, particularly when the performance actions are triple extension actions?

Response 21: We thank the reviewer for pointing out the importance of the calf muscles in triple extension movements. We confirm that the gastrocnemius was indeed included in our percussive massage protocol to address the full kinetic chain involved in jumping and COD performance. We have updated the Methods section to explicitly include the calf muscles (gastrocnemius) and have adjusted the description of the time allocation per muscle group (approximately 35–40 seconds per group) to reflect the total 2.5-minute duration per limb accurately.

Comments 22: Line 242-245, this is repeating previous parts of method and is not necessary

Response 22: We agree with the reviewer that this section was redundant as it repeated information already established in the 'Study Design' and 'Experimental Procedures' sections. To enhance the conciseness and readability of the manuscript, we have removed these lines and ensured that all essential methodological details are presented only once in their most appropriate context. We thank the reviewer for helping us streamline the Methods section.

Comments 23: Line 308, please express alpha value correctly.

Response 23: Revised.

Comments 24: You have no reliability data, this is key to support whether you have found real findings and must be included for all tests.

Response 24: We sincerely thank the reviewer for highlighting the importance of measurement reliability. We agree that establishing the consistency of findings is crucial. While we did not perform a separate test-retest reliability study specifically for this group, we utilized instruments and protocols that have been extensively validated for their high reliability in the literature.

Results

Comments 25: Line 322-333 just seems to be repeating table 1 data and is therefore unnecessary

Response 25: Revised.

Comments 26: Table 2, T-Test and Illinois Test need units. You also include flight time and jump height. Not sure both are necessary as jump height is derived from flight time in this app.

Response 26: Revised.

Comments 27: Line 382-383, you suggest the Illinois Agility Test looks at sustained performance. I would agree, but think both your change of direction tasks are inappropriate for football change of direction. T test 11 sec and Illinois test 16 sec, do not measure the sort of change of direction time frames seen in football. This would be the equivalent of looking at acceleration performance, but running 100-150m. You need to critique these tests as relevant (possibly in the discussion)

Response 27: We have addressed the reviewer's concern regarding the ecological validity of the COD tests. In the revised Discussion section, we now explicitly critique the duration of the T-Test and Illinois Test, supported by relevant literature [35-38], noting that these tests may represent anaerobic capacity/maneuverability rather than the short-duration explosive COD bouts typical of football match play.

Comments 28: Table 3 and 4. Seems a lot of repetition from table 2. It would seem easy enough to add post hoc test info to table 2 and then describe the actual p values, effect sizes and percentage changes in the text. You seem to have described this all in the text, but have the same information in table form, so feel table 3 and 4 are unnecessary.

Response 28: Revised.

Discussion

Comments 29: line 510-528, think this section makes more sense in your introduction as it is not used to explain your findings in the discussion.

Response 29: We agree with the reviewer’s assessment. The section (previously lines 510-528) discussed the general mechanisms of percussive massage and circadian rhythms which, as noted, serves better as foundational information rather than direct interpretation of our specific results. Accordingly, we have relocated this content to the Introduction section and integrated it to better provide the theoretical rationale for our study. This change has streamlined the Discussion, ensuring it remains focused on the interpretation of our findings.

Comments 30: Line 547-560. You state a number of times decreases in stiffness. You need to explain this fully, as a reduction in stiffness should decrease performance, not enhance performance. e.g. decreases in vertical, leg and muscle stiffness slow movement down when there is an impact event (running and jumping).

Response 30: We appreciate the reviewer’s insightful comment on the complex role of muscle-tendon stiffness. We agree that while high levels of vertical and leg stiffness are generally associated with efficient energy storage and return during the stretch-shortening cycle (SSC), an excessive or suboptimal baseline stiffness can also limit joint range of motion (ROM) and increase internal muscle resistance. In our study, we argue that the percussive massage treatment (particularly at 35 Hz) may have reduced passive muscle stiffness (viscoelastic resistance) rather than compromising the active 'stiffness' required for force transmission. This reduction in passive resistance likely allowed for a more efficient contraction-relaxation cycle and improved neuromuscular recruitment, as evidenced by the increased jump height and velocity. We have revised the Discussion to clarify this distinction between passive muscle compliance (which can enhance ROM and decrease internal friction) and functional leg stiffness (which is critical for impact events), citing relevant literature to support this nuanced perspective.

Comments 31: Line 581-582. Ferreira looked at recovery, so this is not relevant to your study

Response 31: Removed.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Rationale for the Selected PMD Intensities (28 Hz vs. 35 Hz). While the authors indicate that the selected frequencies correspond to manufacturer-defined levels of the Hypervolt 2 Pro device, the physiological rationale for choosing these specific intensities could be strengthened in the Introduction. It would be beneficial to briefly link the selected frequency range to existing literature on optimal vibration or percussive stimulation frequencies for neuromuscular activation, as well as to established mechanisms such as tonic vibration reflex or muscle spindle stimulation. Adding one or two sentences in this context would better anchor the study within a clear dose–response framework and strengthen the theoretical justification for the selected intervention parameters.
Absence of a Sham / Placebo Condition. The authors appropriately acknowledge that full blinding was not feasible due to the tactile nature of the intervention; however, the absence of a sham or placebo condition (e.g., use of an inactive device) deserves more explicit discussion. In the Limitations section, it would be helpful to clearly state that a passive rest condition was used instead of a sham intervention and that expectancy effects cannot be completely excluded, despite blinding participants to the study hypotheses. This clarification would enhance methodological transparency and allow readers to better contextualize the observed effects.
Reliability and Interpretation of CMJ-Derived Kinetic Variables. The use of the My Jump Lab application is well justified and supported by previous validation studies; however, given the extensive analysis of force–velocity–power variables derived from CMJ performance, additional clarification would be valuable. The authors may consider briefly reporting reliability indices (e.g., ICC or SEM) for CMJ measurements within the current sample, or explicitly stating that the force- and power-related variables are model-derived estimates rather than direct measurements obtained from a force platform. This would improve clarity regarding measurement precision and aid interpretation of the kinetic outcomes.
Interpretation of Illinois Agility Test Results. The Illinois Agility Test yielded largely non-significant results, which the authors appropriately acknowledge. The Discussion section could be slightly strengthened by elaborating that this test likely places greater emphasis on metabolic demands and sustained anaerobic capacity, and may therefore be less sensitive to short-term neuromuscular potentiation compared with tasks such as the CMJ or T-Test. This additional explanation would help contextualize the differential responsiveness of the performance measures used in the study.
Chronotype Homogeneity. All participants were classified as having an intermediate chronotype, which improves internal consistency but limits the generalizability of the findings. It would be useful to briefly note in the Discussion or Limitations that responses to percussive massage interventions may differ in athletes with pronounced morning or evening chronotypes, and that future studies should examine chronotype as a potential moderator of both performance outcomes and responsiveness to PMD interventions.

Author Response

Author's Reply to the Review Report (Reviewer 2) (highlighted with blue)

Comments and Suggestions for Authors

Comments 1: Rationale for the Selected PMD Intensities (28 Hz vs. 35 Hz). While the authors indicate that the selected frequencies correspond to manufacturer-defined levels of the Hypervolt 2 Pro device, the physiological rationale for choosing these specific intensities could be strengthened in the Introduction. It would be beneficial to briefly link the selected frequency range to existing literature on optimal vibration or percussive stimulation frequencies for neuromuscular activation, as well as to established mechanisms such as tonic vibration reflex or muscle spindle stimulation. Adding one or two sentences in this context would better anchor the study within a clear dose–response framework and strengthen the theoretical justification for the selected intervention parameters.

Response 1: As suggested, we have strengthened the Introduction by explicitly linking the selected PMD frequencies (28 Hz and 35 Hz) to existing literature on optimal vibration ranges for neuromuscular activation, tonic vibration reflex mechanisms, and dose–response considerations.

Comments 2: Absence of a Sham / Placebo Condition. The authors appropriately acknowledge that full blinding was not feasible due to the tactile nature of the intervention; however, the absence of a sham or placebo condition (e.g., use of an inactive device) deserves more explicit discussion. In the Limitations section, it would be helpful to clearly state that a passive rest condition was used instead of a sham intervention and that expectancy effects cannot be completely excluded, despite blinding participants to the study hypotheses. This clarification would enhance methodological transparency and allow readers to better contextualize the observed effects.

Response 2: As suggested by the reviewer, we have expanded the Limitations section to explicitly discuss the absence of a sham/placebo condition and the potential for expectancy effects. We have clarified that a passive rest condition was used and that full blinding was not feasible due to the nature of the intervention.

Comments 3: Reliability and Interpretation of CMJ-Derived Kinetic Variables. The use of the My Jump Lab application is well justified and supported by previous validation studies; however, given the extensive analysis of force–velocity–power variables derived from CMJ performance, additional clarification would be valuable. The authors may consider briefly reporting reliability indices (e.g., ICC or SEM) for CMJ measurements within the current sample, or explicitly stating that the force- and power-related variables are model-derived estimates rather than direct measurements obtained from a force platform. This would improve clarity regarding measurement precision and aid interpretation of the kinetic outcomes.

Response 3: We thank the reviewer for this valuable methodological comment. We agree that clarification regarding the nature of CMJ-derived kinetic variables is important for appropriate interpretation. Accordingly, we have revised the Methods section to explicitly state that force-, velocity-, impulse-, and power-related variables obtained via the My Jump Lab application are model-derived estimates based on the validated Samozino force–velocity approach, rather than direct measurements from a force platform. We have also emphasized that their interpretation should be considered within this context, while retaining references to prior studies demonstrating the high validity and reliability of this method. We believe this clarification improves transparency regarding measurement precision and strengthens the methodological rigor of the manuscript.

Comments 4: Interpretation of Illinois Agility Test Results. The Illinois Agility Test yielded largely non-significant results, which the authors appropriately acknowledge. The Discussion section could be slightly strengthened by elaborating that this test likely places greater emphasis on metabolic demands and sustained anaerobic capacity, and may therefore be less sensitive to short-term neuromuscular potentiation compared with tasks such as the CMJ or T-Test. This additional explanation would help contextualize the differential responsiveness of the performance measures used in the study.

Response 4: We thank the reviewer for this insightful suggestion. We have revised the Discussion section to clarify that the Illinois Agility Test’s duration and complexity place higher demands on sustained anaerobic capacity and metabolic processes. We have further discussed that this characteristic might explain the test's lower sensitivity to the acute neuromuscular potentiation effects of percussive massage compared to shorter, ATP-CP-dominant tasks like the CMJ. This addition provides a better contextual framework for the differential responsiveness of our performance measures.

Comments 5: Chronotype Homogeneity. All participants were classified as having an intermediate chronotype, which improves internal consistency but limits the generalizability of the findings. It would be useful to briefly note in the Discussion or Limitations that responses to percussive massage interventions may differ in athletes with pronounced morning or evening chronotypes, and that future studies should examine chronotype as a potential moderator of both performance outcomes and responsiveness to PMD interventions.

Response 5: We agree with the reviewer that the inclusion of only intermediate chronotypes is a limitation regarding the generalizability of our results. We have now addressed this in the Limitations section, noting that future research should explore chronotype as a potential moderator to see if individuals with extreme morning or evening preferences respond differently to percussive massage interventions.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors,

Thanks for your submission. Unfortunately, I cannot endorse this for publication in a Q1 journal, as the manuscript is fundamentally flawed by data validity issues and statistical misinterpretations. A validation of the provided supplementary data - that includes the names of your participants - reveals critical issues that prevent publication in its current form.

Major Flaws:

Data Reporting Inaccuracy: The manuscript claims that "no outliers were identified." An analysis of your raw data contradicts this, identifying 24 instances of outliers exceeding 3 SD. For example, Participant 5 recorded a vertical jump of 18.1 cm in the L3 Evening condition, compared to a group mean of 38.4 cm (Z = -3.00). The inclusion of such extreme values without explanation or exclusion criteria significantly distorts the group means and interaction effects. You claim all data were normally distributed. However, Shapiro-Wilk tests on your raw data reveal that ~41% of your performance variables (27 out of 66) violate the assumption of normality
Statistical Validity:
- Power: The sample size (n=18) is insufficient for a complex crossover design with these covariates. Your power calculation utilized an effect size (f=0.35) that is arguably too high for this type of intervention.
- Analysis: Performing t-tests on "percentage change" values is not recommended as it inflates Type I error rates. Analysis must be performed on raw values using proper interaction models. The analysis should strictly rely on the interaction effects from the ANOVA or a Linear Mixed Model.
Experimental Design:
- Covariates: You collected Chronotype data (MEQ) but excluded it from the statistical model. In a study explicitly about "morning vs. evening" performance, Chronotype must be treated as a covariate, not background noise.
- Control Condition: The lack of a sham control (e.g., device turned off or minimal vibration) makes it impossible to distinguish the physiological effects of the massage from the placebo/psychological effects of the treatment.
- Subjective Standardization: Relying on a subjective pressure rating ("3-5 on a 0-10 scale") introduces unacceptable operator variability. Without objective quantification of force application (e.g., using a load cell), the "dose" of the massage is inconsistent across participants.
- Washout Period Justification: You cite parallel-group studies (between-subjects) to justify a 48-hour washout period for a crossover design. This is methodologically invalid; you must provide evidence that acute percussive effects dissipate within 48 hours within the same subjects.

Comments for author File: Comments.pdf

Comments on the Quality of English Language

Some English syntax and grammar is needed.

Author Response

Author's Reply to the Review Report (Reviewer 3) (highlighted with green)

Comments and Suggestions for Authors

Dear Authors,

Major Flaws:

Data Reporting Inaccuracy: The manuscript claims that "no outliers were identified." An analysis of your raw data contradicts this, identifying 24 instances of outliers exceeding 3 SD. For example, Participant 5 recorded a vertical jump of 18.1 cm in the L3 Evening condition, compared to a group mean of 38.4 cm (Z = -3.00). The inclusion of such extreme values without explanation or exclusion criteria significantly distorts the group means and interaction effects. You claim all data were normally distributed. However, Shapiro-Wilk tests on your raw data reveal that ~41% of your performance variables (27 out of 66) violate the assumption of normality

Answer: We sincerely thank the reviewer for their meticulous examination of our raw data and for identifying these critical methodological errors. We acknowledge that our original manuscript contained significant inaccuracies in data reporting and statistical assumptions.

Our initial claim that "no outliers were identified" was inaccurate. Upon re-examination of our raw data following the reviewer's analysis, we confirmed the presence of 24 instances of outliers exceeding 3 SD, including the specific example cited (Participant 5: vertical jump of 18.1 cm in L3 Evening condition vs. group mean of 38.4 cm, Z = -3.00). We sincerely apologize for this oversight in our original data screening process.

Our claim that "all data were normally distributed" was incorrect. The reviewer's Shapiro-Wilk test results revealing that approximately 41% of our performance variables (27 out of 66) violated normality assumptions are accurate and represent a fundamental flaw in our initial statistical approach.

In light of these valid criticisms, we have fundamentally revised our analytical approach:

We have replaced all parametric tests with permutational multivariate analysis of variance (PERMANOVA), which does not rely on assumptions of normality or homogeneity of variance. This method is robust to the distributional violations identified by the reviewer.

All results have been recalculated using the PERMANOVA framework on raw values. The entire Results section has been rewritten to reflect these new analyses.

All tables, and statistical conclusions have been updated to reflect the corrected analyses. We believe these revisions address the reviewer's concerns and provide a much more robust and trustworthy analysis of our data.

Statistical Validity:

Power: The sample size (n=18) is insufficient for a complex crossover design with these covariates. Your power calculation utilized an effect size (f=0.35) that is arguably too high for this type of intervention.

Answer: We thank the reviewer for this important comment regarding our sample size and power calculation. We have revised our power analysis to address these concerns.

Revised Power Analysis:

We conducted an updated a priori power analysis using G*Power 3.1 for a repeated measures ANOVA with within-between interaction. The analysis utilized effect size of partial η² = 0.20, which is more conservative than our initial calculation. The power analysis was specifically based on partial η² rather than total effect size, as this more accurately reflects the proportion of variance explained by the specific interaction effect while controlling for other sources of variance in the model.

The analysis parameters were:

Effect size: partial η² = 0.20

Alpha error probability: α = 0.05

Desired power: 1-β = 0.8

Number of groups: 3

Number of measurements: 2 (pre-post)

Nonsphericity correction: ε = 1

Analysis: Performing t-tests on "percentage change" values is not recommended as it inflates Type I error rates. Analysis must be performed on raw values using proper interaction models. The analysis should strictly rely on the interaction effects from the ANOVA or a Linear Mixed Model.

Answer: We sincerely thank the reviewer for this critical methodological observation. The reviewer is absolutely correct that performing t-tests on percentage change values is statistically inappropriate and can inflate Type I error rates.

Revised Statistical Approach:

We have completely revised our statistical analysis approach in response to this valid concern. All previous analyses using t-tests on percentage change values have been removed from the manuscript. Instead, we have implemented a more rigorous analytical framework:

Primary Analysis Method: We conducted permutational multivariate analysis of variance (PERMANOVA) on the raw values rather than percentage changes. PERMANOVA is a non-parametric method that does not rely on distributional assumptions and is particularly suitable for our study design. This approach allows us to test for interaction effects (group × time) while maintaining appropriate control of Type I error rates.

Analysis of Raw Values: All statistical tests are now performed on the original raw measurement values rather than derived percentage change scores, as recommended by the reviewer.

Interaction-Based Inference: Our conclusions are now strictly based on the interaction effects from the PERMANOVA model, which appropriately tests whether the pattern of change over time differs between groups.

The manuscript has been thoroughly revised to reflect these methodological improvements. We believe these changes substantially strengthen the statistical rigor of our study and we are grateful to the reviewer for identifying this important issue.

The updated statistical methods section now clearly describes the PERMANOVA approach, and all results sections have been rewritten to report findings from this appropriate analytical framework.

Experimental Design:

Covariates: You collected Chronotype data (MEQ) but excluded it from the statistical model. In a study explicitly about "morning vs. evening" performance, Chronotype must be treated as a covariate, not background noise.
Control Condition: The lack of a sham control (e.g., device turned off or minimal vibration) makes it impossible to distinguish the physiological effects of the massage from the placebo/psychological effects of the treatment.
Subjective Standardization: Relying on a subjective pressure rating ("3-5 on a 0-10 scale") introduces unacceptable operator variability. Without objective quantification of force application (e.g., using a load cell), the "dose" of the massage is inconsistent across participants.
Washout Period Justification: You cite parallel-group studies (between-subjects) to justify a 48-hour washout period for a crossover design. This is methodologically invalid; you must provide evidence that acute percussive effects dissipate within 48 hours within the same subjects.

Answer:

Point 1: Chronotype as a Covariate

Response: We appreciate this methodological remark. In our study, we used the Morningness-Eveningness Questionnaire (MEQ) as an inclusion criterion specifically to select a homogeneous group of "intermediate" chronotypes (scores 42–58). By excluding extreme morning or evening types, we aimed to minimize the variance that chronotype would introduce as a confounding factor. Since the entire sample fell within the same chronotype category, treating it as a covariate in the statistical model would not yield significant variance. We have clarified this rationale in the "Participants" section.

Point 2: Sham Control

Response: We acknowledge that the lack of a sham/placebo control is a limitation. However, due to the distinct mechanical and tactile nature of percussive massage, creating a truly blinded sham condition (where the participant does not feel the vibration) is practically impossible in this intervention type. To address this, we used a passive rest control condition, which is a common practice in PMD literature. We have emphasized this in the "Limitations" section as suggested.

Point 3: Subjective Pressure Standardization

Response: We agree that objective force quantification (e.g., load cells) would be ideal. To minimize operator variability, all applications were performed by the same experienced practitioner, and we utilized a perceived pressure scale (3–5 out of 10) to ensure participant comfort and safety, consistent with previous studies (e.g., Garcia-Sillero et al., 2021). We have added this as a limitation for future research to consider objective load monitoring.

Point 4: Washout Period Justification

Response: We thank the reviewer for their rigorous and insightful critique of our experimental design and methodology. We have carefully addressed each point, particularly regarding chronotype management, control conditions, and the standardization of the percussive massage dose. We believe these revisions have significantly strengthened the scientific transparency and robustness of our manuscript.

peer-review-53386037.v1.pdf

Comments on the Quality of English Language

Some English syntax and grammar is needed.

Answer: Revised in the manuscript.

Author Response File: Author Response.pdf

Reviewer 4 Report

Comments and Suggestions for Authors

Abstract

Overall, the abstract effectively outlines the study’s purpose and findings but requires refinement for clarity, conciseness, and balanced interpretation.

Introduction

The introduction is comprehensive but overly long and repetitive; it needs condensation and sharper focus.
Several points about the lack of standardized PMD protocols are repeated; merge and simplify
Clearly distinguish between recovery-oriented and performance oriented PMD studies
The final paragraph should explicitly state the study objectives and hypotheses.
Tone should be more analytical and less descriptive; highlight critical gaps, not just prior findings.

Methods

The recruitment process (source of participants, club level) is not specified important for generalizability.
Strong design (randomized, counterbalanced, crossover), but details on randomization procedure (software, sequence generation) are missing
Clarify if testing sessions were conducted at the same relative training day (e.g., after rest or training).
The massage pressure control (“subjective 3–5 scale”) introduces variability; describe how consistency was verified.
Clarify whether the investigator applying the massage was blinded to study hypotheses.
Include rationale for selecting 28 Hz and 35 Hz intensities why these specific values?
Repetition and redundant phrases (e.g., “same investigators…to ensure consistency”) should be trimmed

Results

The post-hoc comparisons are numerous; consider focusing only on the most relevant contrasts to avoid overwhelming the reader.
Some sentences repeat similar statistical outcomes (e.g., “large effect sizes underscoring practical significance”) simplifying the phrasing would improve readability.
Ensure p-values and effect size symbols are consistently formatted (e.g., ηp², d, p < 0.001).
The section could benefit from a brief integrative paragraph at the end, highlighting the main performance improvements and their practical relevance to morning vs. evening conditions.

Discussion

The section would benefit from a clearer paragraph on novelty, explicitly stating how this study extends previous PM research.
The section would benefit from a clearer paragraph on novelty, explicitly stating how this study extends previous PM research.
The mechanistic explanations (thixotropy, TVR, neural activation) are appropriate but should be summarized more succinctly to maintain focus on the study’s contributions.
Strengthen the link between observed results and practical application (how PM could be implemented in training settings).

Conclusion

The conclusions are clear and well-aligned with the study’s objectives and findings. However, the section reiterates too much data already presented in the Discussion (e.g., effect sizes, variable lists). Simplify to focus on interpretation and practical meaning.
Remove redundant references to “Tables 2–4” in the conclusion; such details belong in Results/Discussion.
Overall, this section would benefit from greater brevity and precision, focusing on (i) main conclusion, (ii) practical application, (iii) cautious interpretation, (iv) next research steps.

Author Response

Author's Reply to the Review Report (Reviewer 4) (highlighted with grey)

Comments and Suggestions for Authors

Abstract

Overall, the abstract effectively outlines the study’s purpose and findings but requires refinement for clarity, conciseness, and balanced interpretation.

Author Response: We thank the reviewer for this constructive suggestion. The abstract has been carefully revised to improve clarity and conciseness, streamline methodological and results descriptions, and ensure a more balanced interpretation of the findings. Redundant phrasing was reduced, key outcomes were presented more clearly, and conclusions were tempered to better reflect the scope of the results without overstatement.

Introduction

The introduction is comprehensive but overly long and repetitive; it needs condensation and sharper focus.
Several points about the lack of standardized PMD protocols are repeated; merge and simplify
Clearly distinguish between recovery-oriented and performance oriented PMD studies
The final paragraph should explicitly state the study objectives and hypotheses.
Tone should be more analytical and less descriptive; highlight critical gaps, not just prior findings.

Author Response: We thank the reviewer for these constructive and insightful comments. In response, the Introduction has been carefully revised to improve clarity, focus, and analytical depth. Redundant statements—particularly those concerning the lack of standardized PMD protocols—were merged and streamlined to reduce repetition and enhance coherence. A clearer conceptual distinction was introduced between recovery-oriented and performance-oriented PMD studies, emphasizing the relative scarcity of evidence on acute performance priming effects. The tone of the section was refined to be more analytical, highlighting critical methodological and conceptual gaps rather than providing a descriptive summary of prior findings. Finally, the concluding paragraph of the Introduction was revised to explicitly state the study objectives and a priori hypotheses. These changes were made without altering the cited literature and were intended to strengthen the rationale and focus of the study.

Methods

The recruitment process (source of participants, club level) is not specified important for generalizability.
Strong design (randomized, counterbalanced, crossover), but details on randomization procedure (software, sequence generation) are missing
Clarify if testing sessions were conducted at the same relative training day (e.g., after rest or training).
The massage pressure control (“subjective 3–5 scale”) introduces variability; describe how consistency was verified.
Clarify whether the investigator applying the massage was blinded to study hypotheses.
Include rationale for selecting 28 Hz and 35 Hz intensities why these specific values?
Repetition and redundant phrases (e.g., “same investigators…to ensure consistency”) should be trimmed

Respond ro reviewer: Thank you for your insightful comments and constructive feedback on our manuscript. We have carefully addressed each of your concerns in the revised version. Below is a point-by-point response to your specific queries regarding the Methods section:

Recruitment and Generalizability:

Comment: The source of participants and club level were not specified.

Response: We have clarified that the participants (n=18) were recruited from the U19 squad of Malatyaspor, a club competing in the Turkish Süper Lig youth development system. This ensures a high level of training consistency and professional athletic background.

Randomization Procedure:

Comment: Details on randomization (software, sequence generation) were missing.

Response: The experimental order was randomized using a computer-generated random sequence and implemented in a counterbalanced manner to minimize order effects.

Testing Schedule relative to Training:

Comment: Clarify if sessions were conducted at the same relative training day.

Response: All testing sessions were strictly conducted on non-training days or at least 24 hours after the last training session to ensure recovery and minimize residual fatigue.

Massage Pressure Control:

Comment: The subjective 3–5 scale introduces variability; how was consistency verified?

Response: To ensure consistency, all applications were performed by the same experienced investigator. Furthermore, the investigator underwent specific familiarization sessions prior to data collection to practice and maintain the predefined pressure range.

Investigator Blinding:

Comment: Was the investigator applying the massage blinded to study hypotheses?

Response: Yes, while full blinding to the tactile intervention was not possible, the investigator applying the massage and the investigators conducting performance assessments were blinded to the specific study hypotheses and expected outcomes.

Rationale for 28 Hz and 35 Hz:

Comment: Why were these specific values selected?

Response: These frequencies were selected based on existing evidence suggesting that vibration between 30–40 Hz is optimal for stimulating muscle spindle activity and the tonic vibration reflex (TVR) without inducing premature muscle fatigue. They represent the lower and middle functional spectrum of the device used.

Redundancy and Trimming:

Comment: Repetition and redundant phrases should be trimmed.

Response: We have carefully reviewed the manuscript and removed redundant phrases (e.g., repeated mentions of "same investigators") to improve clarity and conciseness while maintaining methodological transparency.

Results

The post-hoc comparisons are numerous; consider focusing only on the most relevant contrasts to avoid overwhelming the reader. Some sentences repeat similar statistical outcomes (e.g., “large effect sizes underscoring practical significance”) simplifying the phrasing would improve readability. Ensure p-values and effect size symbols are consistently formatted (e.g., ηp², d, p < 0.001).

Answer: We thank the reviewer for these constructive suggestions to improve readability and clarity. We have made the following revisions. We have focused the presentation of pairwise comparisons on the most theoretically and practically relevant contrasts (NM vs. L1, NM vs. L3, and L1 vs. L3 within each time point), reducing redundancy while maintaining comprehensive coverage of the primary research questions. We have revised sentences throughout the Results section to eliminate repetitive language (e.g., “large effect sizes underscoring practical significance”), replacing them with more concise and varied expressions while retaining essential statistical and interpretive information. All statistical symbols and values are now consistently formatted throughout the manuscript: partial omega squared (ωp²), Cohen’s d, and p-values (e.g., p < 0.001, p = 0.004) follow uniform notation.

The section could benefit from a brief integrative paragraph at the end, highlighting the main performance improvements and their practical relevance to morning vs. evening conditions.

Response: We agree that a practical synthesis of the results enhances the manuscript’s impact. We have added a brief integrative paragraph at the end of the Results section. This summary highlights that while both intensities are beneficial, the 35 Hz protocol is particularly effective in bridging the performance gap between morning and evening sessions, thereby providing clear practical guidance for coaches and practitioners.

Discussion

The section would benefit from a clearer paragraph on novelty, explicitly stating how this study extends previous PM research.
The section would benefit from a clearer paragraph on novelty, explicitly stating how this study extends previous PM research.
The mechanistic explanations (thixotropy, TVR, neural activation) are appropriate but should be summarized more succinctly to maintain focus on the study’s contributions.
Strengthen the link between observed results and practical application (how PM could be implemented in training settings).

Response: We have thoroughly revised the Discussion section to address your concerns regarding novelty, clarity, and practical relevance. Explicit Statement of Novelty: We have added sentences explicitly clarifying that this study extends existing PM research by integrating a circadian framework. Specifically, we highlight that while previous studies focused on recovery or single-session performance, our work demonstrates PM’s role as a tool to mitigate time-of-day-related performance deficits (the "morning slump"). Succinct Mechanistic Summaries: The physiological explanations—including thixotropic effects, TVR, and neural drive—have been streamlined. We have condensed these theories to focus specifically on why 35 Hz provided superior benefits for kinetic variables compared to lower intensities. Strengthened Practical Applications: We have reinforced the link between our findings and the field. The revised text now explicitly recommends PM (particularly at 35 Hz) as a localized priming tool for early-morning training or competitions, providing practitioners with clear, evidence-based guidance for optimizing neuromuscular readiness. We believe the Discussion is now more focused and effectively communicates the significance of our findings.

Conclusion

The conclusions are clear and well-aligned with the study’s objectives and findings. However, the section reiterates too much data already presented in the Discussion (e.g., effect sizes, variable lists). Simplify to focus on interpretation and practical meaning.
Remove redundant references to “Tables 2–4” in the conclusion; such details belong in Results/Discussion.
Overall, this section would benefit from greater brevity and precision, focusing on (i) main conclusion, (ii) practical application, (iii) cautious interpretation, (iv) next research steps.

Response: Dear Reviewer, We have significantly revised the Conclusion section to ensure brevity, precision, and a focus on practical interpretation as suggested. Data Simplification: We have removed redundant statistical data, such as specific effect sizes and p-values, which were already detailed in the Results and Discussion sections. The section now focuses on the broader interpretation of findings. Removal of Table References: All references to “Tables 2–4” have been removed from the Conclusion to maintain a clean and professional summary . Structured Conclusion: The revised section is now organized to address the four requested points: (i) Main Conclusion: Percussive massage acutely enhances COD and vertical jump kinetics in football players. (ii) Practical Application: We recommend the integration of 35 Hz percussive massage in pre-exercise routines, particularly for morning sessions. (iii) Cautious Interpretation: We specify that while both intensities are effective, the 35 Hz protocol provides superior benefits for force-time characteristics during the morning performance slump. (iv) Next Steps: We have emphasized the role of intensity-specific strategies for future optimization of neuromuscular readiness. We believe the Conclusion is now much more impactful and accessible for practitioners and researchers alike.

Author Response File: Author Response.pdf

Round 2

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors

I acknowledge the substantial effort undertaken to recalculate the results and address the statistical flaws highlighted in the previous review. However, the revised analytical strategy introduces new methodological contradictions. Furthermore, the admission of data handling errors and the previous inclusion of identifiable participant information raise insurmountable validity and ethical concerns. Consequently, I cannot recommend this manuscript for publication.

In the previous round, it was noted that the supplementary data file included participant names. While this was flagged as a "validation" issue, it is primarily an ethical breach. Anonymity is the cornerstone of human subject research. The submission of raw datasets containing identifiers suggests a breakdown in the research governance protocols. For a journal, strict adherence to data protection laws (GDPR/HIPAA) is non-negotiable.

The pivot to PERMANOVA to address normality violations is methodologically unconvincing.

Misapplication: PERMANOVA is designed to test differences between groups using distance matrices (e.g., Bray-Curtis) in multivariate space. While it is robust to normality violations, utilizing it for simple univariate performance metrics (like Vertical Jump) to avoid dealing with outliers is inappropriate.
Data Quality vs. Statistical Fixes: The core issue remains the quality of the raw data, not just the distribution. You acknowledged Participant 5 recorded an 18.1 cm jump against a 38.4 cm mean. This is not merely a "distributional outlier"; it is likely a measurement error or a failure of participant effort. A robust statistical test does not correct for invalid biological inputs. Retaining such extreme values (>3 SD) in a sample of n=18$distorts the mean regardless of whether the p-value is generated via permutations or F-tests.

3. Sample Size and Power Estimation

The revised power analysis remains overly optimistic.

You cited a partial eta2 = 0.20. In physiological interventions, an effect size of this magnitude (explaining 20% of the variance after controlling for other factors) is massive and rare.
Basing sample size justification on such a liberal effect size increases the probability that the study is underpowered to detect the actual, likely smaller, effects of percussive therapy. With n=18, the study is likely susceptible to Type II errors, and the "statistically significant" interactions found via PERMANOVA may be spurious artifacts of the outliers mentioned above.

4. Experimental Control and Standardization

Sham Condition: The argument that a blinded sham is "practically impossible" is insufficient. High-quality mechanistic studies frequently utilize "sham ultrasound" (device off) or "light touch" (device on skin, no pressure/vibration) to control for the Hawthorne and placebo effects. Comparing a high-sensory intervention solely against "passive rest" fails to isolate the mechanical effect from the psychological effect of receiving treatment.
Subjective Dosing: Continuing to rely on a "3–5 out of 10" perceived pressure scale compromises reproducibility. Without objective load monitoring (e.g., load cells), the independent variable is uncontrolled. One participant's "5" is another's "3," meaning the physiological dose of percussion varied randomly across your sample.

Author Response

Comments: Justification for the Use of PERMANOVA in a Repeated-Measures Design

Response: We thank the reviewer for this important methodological observation. We clarify that PERMANOVA was applied separately to each dependent variable (univariate permutational approach), not as a single multivariate model. To account for the repeated-measures structure of the crossover design, a subject-level blocking scheme was implemented within the permutation framework: permutations were constrained within subjects, preserving the within-subject correlation structure across conditions and time points. This approach is analogous to permutation-based repeated-measures ANOVA and has been validated for use in within-subject experimental designs. We have revised the Statistical Analyses section to explicitly state these procedural details.

Comments: Standardization and Consistency of Effect Size Metrics

Response: We appreciate the reviewer's concern regarding consistency in effect size reporting. Regarding partial omega squared (ωp²) in the permutational context: ωp² was estimated using the formula ωp² = (SS_effect − df_effect × MS_error) / (SS_total + MS_error), applied to the PERMANOVA sum-of-squares partitioning. Although this formula was originally developed for parametric ANOVA, its application to PERMANOVA sum-of-squares is theoretically consistent, as PERMANOVA uses the same F-ratio statistic structure [reference: Kelley & Preacher, 2012]. Regarding Cohen's d following Wilcoxon signed-rank tests: we acknowledge that Cohen's d assumes approximately normal distributions. However, given the moderate sample size (n = 18) and its wide use in sports science literature for comparability across studies, we retained Cohen's d but have added a methodological note.

Comments: The manuscript would benefit from a more explicit acknowledgment of potential expectancy and placebo effects. Although the tactile nature of percussion limits blinding, the absence of a sham condition (e.g., device applied without percussion frequency) is an important methodological limitation. The authors should expand this point slightly in the limitations section and discuss how expectancy effects may have contributed to performance changes.

Response: We thank the reviewer for this valuable suggestion. In the revised manuscript, we have expanded the limitations section to explicitly acknowledge the potential influence of expectancy and placebo effects. We clarified that full participant blinding was not feasible due to the tactile nature of percussive massage and that the absence of a sham condition (e.g., device contact without oscillatory stimulus) limits the ability to fully dissociate physiological mechanisms from expectancy-driven performance facilitation. This addition improves methodological transparency and contextualizes the acute performance findings.

Comments: The justification for the selected frequencies (28 Hz and 35 Hz) is reasonable, but it would be helpful to explain more explicitly why the highest available frequency (e.g., 45 Hz) was not tested. Clarifying whether 35 Hz represents an evidence-informed “optimal” range or simply a mid-level device setting would improve conceptual framing.

Response: We appreciate the reviewer’s comment. In the revised Methods section, we clarified that although the device allows operation up to 45 Hz, higher frequencies were intentionally excluded to avoid potential overstimulation or acute neuromuscular fatigue responses reported at elevated vibration intensities. We further emphasized that 35 Hz was selected as an evidence-informed moderate intensity within the proposed 30–40 Hz neuromuscular activation window, rather than merely representing a mid-tier device setting. This clarification strengthens the conceptual framing of the dose selection.

Comments: The methods section, the authors should clarify the exact timing between completion of the percussion intervention and the start of performance testing. Although a 2-minute passive recovery between tests is mentioned, the latency between intervention cessation and the first performance measure should be precisely stated, as acute neuromuscular potentiation effects can be time-sensitive.

Response: Thank you for highlighting the importance of timing. We have clarified in the Methods section that the first performance assessment (T-test) commenced approximately 60 seconds after completion of the intervention to standardize acute potentiation latency across participants. This specification ensures clarity regarding the time-sensitive nature of acute neuromuscular potentiation effects.

Comments: The reliance on model-derived kinetic variables from the My Jump Lab application should be further contextualized. While the authors correctly acknowledge that these are indirect estimates, they should emphasize that force-, impulse-, and power-related outputs are not direct force-platform measurements. A brief statement clarifying the known standard error of estimate from validation studies would further enhance transparency.

Response: We thank the reviewer for this important methodological point. In the revised manuscript, we further emphasized that force-, velocity-, impulse-, and power-related variables obtained from the My Jump Lab application are model-derived estimates based on the validated Samozino force–velocity method rather than direct ground reaction force measurements from a force platform. We additionally specified the reported standard error of estimate (approximately 1–2 cm for jump height) and the excellent agreement with force-platform data (ICC = 0.997). These clarifications enhance transparency and appropriate interpretation of the kinetic outcomes.

Comments: Regarding the Illinois COD test findings, the authors may consider presenting a short sensitivity discussion. Since this test did not respond to the intervention, it would be useful to specify whether the absence of effect might reflect insufficient sensitivity to detect small acute neuromuscular changes, rather than a true absence of physiological influence.

Response: We appreciate this insightful suggestion. In the revised Discussion section, we included a brief sensitivity-focused interpretation of the Illinois COD findings. We clarified that, due to its longer duration and greater metabolic contribution, the Illinois test may be less sensitive to detect small acute neuromuscular potentiation effects compared to acceleration-dominant tasks. We further stated that the absence of statistical significance may reflect measurement sensitivity limitations rather than a complete absence of physiological influence. This addition improves the interpretative nuance of the null findings.

Author Response File: Author Response.pdf

Reviewer 4 Report

Comments and Suggestions for Authors

Author Response

Dear Reviewer,

We sincerely thank you for your thorough evaluation of our manuscript and for your constructive feedback throughout the review process. Your insightful comments have significantly contributed to improving the clarity, rigor, and overall quality of our work.

We are particularly grateful for your positive assessment following the revisions. Your guidance has been invaluable in strengthening the manuscript, and we truly appreciate the time and expertise you devoted to reviewing our study.

Thank you once again for your support and thoughtful evaluation.

Kind regards