Review Reports
- Asma Alonazi 1,*,
- Lena Almasoudi 1 and
- Abdullah Alismail 2,3,4
- et al.
Reviewer 1: Natalia A. Bezdenezhnykh Reviewer 2: Anonymous Reviewer 3: Francisco Epelde
Round 1
Reviewer 1 Report
Comments and Suggestions for AuthorsI reviewed with interest the manuscript by Asma Alonazi et al., "Effects of a Four-Week Combined Respiratory Muscle Training and Breathing Exercise Program on Respiratory Endurance, Functional Performance, Sleep Quality, and Perceived Stress in Healthy University Students." In this article, the authors examined the clinical effectiveness of their proposed respiratory training program in college students. The authors obtained the expected results: improved sleep quality, increased breath-holding time, and decreased stress levels. These changes appear beneficial in the cohort of students studied.
During review, I had the following comments and questions:
1. In their rationale for the study, the authors state that they conducted it in this format (respiratory training) due to the prevalence of a sedentary lifestyle among college students in Saudi Arabia. However, respiratory training alone does not improve students' mobility. It takes time (breathing exercises twice a day), requires additional equipment (to train the inspiratory and expiratory muscles), and requires the participation of a research assistant. I believe that without the latter's involvement, adherence to training would be significantly lower. A logical question arises: might these efforts be better directed toward increasing students' mobility (aerobic exercise, strength training, etc.)?
2. To assess the dynamics of functional mobility, the authors used the Timed Up-and-Go (TUG) and Sit-to-Stand (STS) tests. These tests are widely used in comprehensive geriatric assessments and to identify frail patients (e.g., Ref. 1, see below). Their evaluation in young, healthy individuals appears highly questionable. The improvement observed by the authors on these tests is most likely due to bias, resulting from the same research assistant administering these tests. 3. In the Discussion section, it would be appropriate to consider other possible types of training for students that may affect the state of the cardiorespiratory system (e.g., ref. 2, see below).
4. The objective of the study should be shortened; the last sentence can be placed in the Discussion section.
References:
1. Grgic J, Wazny VK, Kirk B, Poon ET, Valenzuela PL. Reference values for gait speed, five-times-sit-to-stand test, balance, and handgrip strength: analysis of data from the English Longitudinal Study of Aging. Geroscience. 2026 Feb 26. doi: 10.1007/s11357-026-02163-5.
2. Csepregi É, Gyurcsik Z, Veres-Balajti I, Nagy AC, Szekanecz Z, Szántó S. Effects of Classical Breathing Exercises on Posture, Spinal and Chest Mobility among Female University Students Compared to Currently Popular Training Programs. Int J Environ Res Public Health. 2022 Mar 21;19(6):3728. doi: 10.3390/ijerph19063728.
Author Response
Reviewer 1
Comment 1:
I reviewed with interest the manuscript by Asma Alonazi et al., "Effects of a Four-Week Combined Respiratory Muscle Training and Breathing Exercise Program on Respiratory Endurance, Functional Performance, Sleep Quality, and Perceived Stress in Healthy University Students." In this article, the authors examined the clinical effectiveness of their proposed respiratory training program in college students. The authors obtained the expected results: improved sleep quality, increased breath-holding time, and decreased stress levels. These changes appear beneficial in the cohort of students studied.
Response 1:
We sincerely thank the reviewer for the careful evaluation of our manuscript and for the constructive comments. We have revised the manuscript accordingly and believe these changes have strengthened the paper.
Comment 2:
During review, I had the following comments and questions:
In their rationale for the study, the authors state that they conducted it in this format (respiratory training) due to the prevalence of a sedentary lifestyle among college students in Saudi Arabia. However, respiratory training alone does not improve students' mobility. It takes time (breathing exercises twice a day), requires additional equipment (to train the inspiratory and expiratory muscles), and requires the participation of a research assistant. I believe that without the latter's involvement, adherence to training would be significantly lower. A logical question arises: might these efforts be better directed toward increasing students' mobility (aerobic exercise, strength training, etc.)?
Response 2:
We thank the reviewer for this insightful comment. We fully agree that aerobic and resistance exercise remain the cornerstone interventions for improving overall physical fitness and health among university students. Our intention was not to suggest that respiratory training should replace conventional physical activity programs. Rather, we aimed to investigate whether a low-impact, targeted respiratory intervention could serve as a complementary strategy for students who may have limited participation in regular exercise because of academic demands, time constraints, or low adherence to traditional exercise programs.
We have revised the Introduction and Discussion to clarify that breathing exercises and respiratory muscle training (RMT) should be viewed as adjunctive rather than alternative interventions. We also acknowledge that the supervised nature of our intervention may have contributed to the high adherence observed and that future studies should evaluate the feasibility and effectiveness of unsupervised or minimally supervised programs. (P. 10-11, Line 396-411)
Comment 3:
To assess the dynamics of functional mobility, the authors used the Timed Up-and-Go (TUG) and Sit-to-Stand (STS) tests. These tests are widely used in comprehensive geriatric assessments and to identify frail patients (e.g., Ref. 1, see below). Their evaluation in young, healthy individuals appears highly questionable. The improvement observed by the authors on these tests is most likely due to bias, resulting from the same research assistant administering these tests.
References:
1. Grgic J, Wazny VK, Kirk B, Poon ET, Valenzuela PL. Reference values for gait speed, five-times-sit-to-stand test, balance, and handgrip strength: analysis of data from the English Longitudinal Study of Aging. Geroscience. 2026 Feb 26. doi: 10.1007/s11357-026-02163-5.
Response 3:
We appreciate this important observation. Although the TUG and STS tests are frequently used in older adults and clinical populations, they have also been employed in healthy young adults to evaluate functional mobility, movement efficiency, lower-extremity functional performance, and postural control. Our rationale for selecting these tests was based on their simplicity, reliability, ease of administration, and sensitivity to changes in functional performance. Made the editing on Methods section (P. 5, Line 200-202) and Discussion section (P. 10, Line 384-389).
We agree, however, that ceiling effects may occur in healthy populations and that the observed improvements could have been partially influenced by familiarization or assessor-related bias. As correctly noted by the reviewer, all assessments were performed by the same non-blinded assessor. We have strengthened the limitations section to explicitly acknowledge this issue and have moderated our interpretation of the functional outcomes. Made the changes on the Limitaions section (P. 12, Line 494-501).
Comment 4:
In the Discussion section, it would be appropriate to consider other possible types of training for students that may affect the state of the cardiorespiratory system (e.g., ref. 2, see below).
References:
2. Csepregi É, Gyurcsik Z, Veres-Balajti I, Nagy AC, Szekanecz Z, Szántó S. Effects of Classical Breathing Exercises on Posture, Spinal and Chest Mobility among Female University Students Compared to Currently Popular Training Programs. Int J Environ Res Public Health. 2022 Mar 21;19(6):3728. doi: 10.3390/ijerph19063728.
Response 4:
We thank the reviewer for this valuable suggestion. We have incorporated discussion of alternative training approaches that may influence cardiorespiratory function and musculoskeletal health in university students. Specifically, we have cited the study by Csepregi et al. and compared our findings with other exercise-based interventions. (P.10-11, Line 401-411).
Comment 5:
The objective of the study should be shortened; the last sentence can be placed in the Discussion section.
Response 5:
We thank the reviewer for this suggestion. We agree that the study objective was unnecessarily lengthy. The objective statement has been revised (P.3, Line 123-130), and the hypothesis regarding inter-correlations and common mechanistic pathways has been moved to the Discussion section as suggested. (P.10, Line 357-360).
Author Response File:
Author Response.docx
Reviewer 2 Report
Comments and Suggestions for AuthorsThank you for the opportunity to review this interesting work. Breathing training is well documented as a promising intervention to alleviate stress in various populations. Taking into consideration that university students face significant stress and anxiety, especially during exam period, this work could be promising. Regarding the enhancement of physical functioning and postural control, this population doesn't usually present significant deficities.
Comments.
- It seems quite difficult to imagine that college students up to 25 years old face balance instability and functional deficities due to diaphragmatix dysfunction. These kind of pathologies linked to the diaphragm are seen in older adults. Thus the rationale of this study is not so convincing.
- Additionally, the authors need to support what benefits will have from breathing exercises and what from RMT, what is targeted by each intervention?
- TUG and STS tests are generally employed in older adults, what the authors expect to find in this young population? There are other tests more appropriate for this age.
- The authors need to provide data to support the sedentary lifestyles of college students in Saudi Arabia in order to strengthen their rationale. Interventions are designed in relation to data on a specific population that explains and supports the methodological design.
- This is also evident in the discussion, as the authors explain their findings in general and not specifically to this population.
- The discussion needs to be enhanced as it is quite superficial and not provide support to evidence.
- What could be the clinical recommendations that derive from this study?
Author Response
Reviewer 2
Comment 1:
Thank you for the opportunity to review this interesting work. Breathing training is well documented as a promising intervention to alleviate stress in various populations. Taking into consideration that university students face significant stress and anxiety, especially during exam period, this work could be promising. Regarding the enhancement of physical functioning and postural control, this population doesn't usually present significant deficities.
Response 1:
We sincerely thank the reviewer for the positive assessment of our work and for the thoughtful comments. We agree that university students generally do not exhibit the same degree of functional impairment observed in older adults and have revised the manuscript to better justify the study rationale, clarify the intended effects of the intervention components, strengthen the discussion, and expand the clinical implications of our findings.
Comment 2:
It seems quite difficult to imagine that college students up to 25 years old face balance instability and functional deficities due to diaphragmatix dysfunction. These kind of pathologies linked to the diaphragm are seen in older adults. Thus the rationale of this study is not so convincing.
Response 2:
We thank the reviewer for this important observation. We agree that healthy university students do not typically present with clinically significant balance impairments or diaphragmatic dysfunction. Our intention was not to imply that this population suffers from pathological deficits. Rather, our rationale was based on evidence suggesting that the diaphragm contributes to both respiratory and postural functions and that improvements in respiratory muscle performance may influence movement efficiency and functional performance even in healthy individuals.
To address this concern, we revised the Introduction (P. 3, Line 110-117) and Discussion to avoid implying the presence of dysfunction in healthy students and instead emphasize optimization of respiratory function and movement efficiency. We also tempered our interpretation of the functional outcomes and acknowledged the possibility of ceiling effects.
Comment 3:
Additionally, the authors need to support what benefits will have from breathing exercises and what from RMT, what is targeted by each intervention?
Response 3:
We thank the reviewer for highlighting this important point. We have expanded the Introduction and Intervention sections to clarify the distinct but complementary roles of breathing exercises and respiratory muscle training. (P. 3, Line 103-109)
Breathing exercises (diaphragmatic and pursed-lip breathing) were primarily intended to improve breathing patterns, promote parasympathetic activation, reduce perceived stress, and enhance relaxation. In contrast, inspiratory and expiratory muscle training were intended to increase respiratory muscle strength and endurance through threshold loading.
Because both interventions were delivered simultaneously, the present study cannot determine the relative contribution of each component. This limitation has been acknowledged.
Comment 4:
TUG and STS tests are generally employed in older adults, what the authors expect to find in this young population? There are other tests more appropriate for this age.
Response 4:
We appreciate this observation and agree that TUG and STS are most commonly used in geriatric and clinical populations. However, these tests have also been applied in healthy adults as simple, reliable measures of functional performance, movement efficiency, and lower-limb function. (P. 5, Line 200-205) and (P. 12, Line 494-501)
Our objective was not to identify mobility impairments but to determine whether improvements in respiratory function could be accompanied by measurable changes in functional performance. Nevertheless, we acknowledge that more challenging performance assessments may have been more sensitive in this population.
Comment 5:
The authors need to provide data to support the sedentary lifestyles of college students in Saudi Arabia in order to strengthen their rationale. Interventions are designed in relation to data on a specific population that explains and supports the methodological design.
Response 5:
We thank the reviewer for this valuable suggestion. We have strengthened the Introduction by adding evidence demonstrating the high prevalence of sedentary behavior and insufficient physical activity among university students globally and within Saudi Arabia. These data provide a stronger rationale for investigating accessible health-promoting interventions in this population. (P. 2, Line 64-73)
Comment 6:
This is also evident in the discussion, as the authors explain their findings in general and not specifically to this population.
Response 6:
We agree with the reviewer and have revised the Discussion to better contextualize the findings within a university student population. Specifically, we further discuss the relevance of sleep quality, stress management, academic demands, and the feasibility of implementing respiratory interventions within student wellness programs in the discussion section.
Comment 7:
The discussion needs to be enhanced as it is quite superficial and not provide support to evidence.
Response 7:
We thank the reviewer for this recommendation. The Discussion has been substantially expanded through the addition of relevant literature comparing our findings with previous studies on breathing exercises, respiratory muscle training, autonomic regulation, physical performance, sleep quality, and stress reduction.
Comment 8:
What could be the clinical recommendations that derive from this study?
Response 8:
We appreciate this suggestion. We have expanded the "Practical Implications and Future Research" sections to provide practical recommendations while acknowledging the preliminary nature of the findings.
Author Response File:
Author Response.docx
Reviewer 3 Report
Comments and Suggestions for AuthorsManuscript title: Effects of a Four-Week Combined Respiratory Muscle Training and Breathing Exercise Program on Respiratory Endurance, Functional Performance, Sleep Quality, and Perceived Stress in Healthy University Students
Overall recommendation: Major revision
- Summary of the manuscript and key contributions
This manuscript examines whether a four-week combined breathing exercise and respiratory muscle training program is associated with changes in respiratory endurance, functional performance, sleep quality, and perceived stress among healthy university students in Saudi Arabia. The intervention included diaphragmatic breathing, pursed-lip breathing, inspiratory muscle training, and expiratory muscle training, performed five days per week. The authors assessed outcomes before and after the intervention, including chest expansion, breath-holding time, Timed Up-and-Go, five-times sit-to-stand, Pittsburgh Sleep Quality Index, and Perceived Stress Scale.
The topic is timely and potentially relevant. Breathing exercises and respiratory muscle training are low-cost, accessible interventions that may be attractive for use in young adults, university settings, and preventive health programs. The study is strengthened by its practical intervention, high adherence, inclusion of both male and female participants, and use of several familiar clinical and patient-reported outcome measures. The manuscript may provide useful preliminary data for designing a future randomized controlled trial.
However, in its current form, the manuscript overstates the strength of its findings. The single-arm pre-post design does not allow causal conclusions regarding effectiveness. Several outcomes are vulnerable to learning effects, expectation effects, motivation, repeated testing, and temporal changes unrelated to the intervention. The interpretation of breath-holding time as respiratory endurance is also problematic without additional objective respiratory measures. The manuscript therefore requires substantial revision before it can be considered for further processing.
- Major comments
2.1 Study design and causal interpretation
The main limitation is the absence of a control group, sham intervention, randomization, or blinded assessment. Although the authors describe the study as a pilot pre-post intervention study, several parts of the manuscript appear to imply that the intervention caused improvements in respiratory endurance, functional performance, sleep quality, and perceived stress.
Because all outcomes were measured before and after the intervention in a single group, the observed changes cannot be confidently attributed to the intervention itself. Improvements may reflect learning effects, familiarity with testing procedures, expectation effects, regression to the mean, increased attention from study staff, changes in daily activity, academic workload, sleep schedule, or other unmeasured lifestyle factors during the four-week period.
The manuscript should therefore consistently describe the findings as preliminary within-group changes or associations, not as evidence of efficacy. Terms such as “effectiveness,” “improved,” “resulted in,” or “led to” should be replaced or qualified unless the authors are referring only to within-group changes. The Abstract, Discussion, and Conclusion particularly need revision so that the wording matches the exploratory single-arm design.
2.2 Primary outcome: breath-holding time
The use of breath-holding time as the main indicator of “respiratory endurance” requires stronger justification and more cautious interpretation. Breath-holding time is not a direct measure of respiratory muscle endurance. It is influenced by multiple factors, including motivation, discomfort tolerance, chemoreflex sensitivity, anxiety, prior experience with breath-holding, lung volume at the start of the test, and participant effort.
A single post-inhalation breath-hold trial is especially vulnerable to learning and motivational bias. Participants may perform better after the intervention simply because they are more familiar with the test or more willing to tolerate discomfort. The reported 132% increase is large, but without post-intervention maximal inspiratory pressure, maximal expiratory pressure, spirometry, or an objective respiratory endurance test, it is not possible to conclude that this represents a true physiological respiratory muscle adaptation.
The authors mention that MIP and MEP were used to prescribe training intensity. If these measures were collected at follow-up, they should be reported. If they were not collected, this should be acknowledged as a major limitation. The manuscript should avoid equating breath-holding time with respiratory muscle endurance and should instead refer to it more precisely as “breath-holding time” or “a composite respiratory performance measure.”
2.3 Intervention description and reproducibility
The intervention is clinically interesting, but further detail is required to make it reproducible. The authors state that inspiratory and expiratory muscle training were performed at 40–60% of maximal inspiratory or expiratory pressure, but it is unclear whether the load was progressed during the four weeks, whether MIP and MEP were reassessed during the intervention, and whether participants remained at the same relative or absolute intensity throughout the study.
The authors should clarify:
- how initial training loads were determined;
- whether IMT and EMT loads were adjusted over time;
- whether MIP and MEP were reassessed for progression;
- how adherence was monitored;
- whether sessions were supervised or unsupervised;
- whether adverse events or discomfort were recorded;
- whether all participants completed the same number of sessions.
The intervention is also multimodal, combining diaphragmatic breathing, pursed-lip breathing, inspiratory muscle training, and expiratory muscle training. Because these components were delivered together, the study cannot determine which component, if any, contributed most to the observed changes. This should be stated clearly as a limitation.
2.4 Statistical analysis and reporting
The statistical reporting needs careful revision. The sample size calculation appears to be based on detecting a medium effect in a paired comparison, but the manuscript includes multiple outcomes, multiple correlations, and subgroup comparisons. Although exploratory studies may reasonably avoid formal correction for multiple comparisons, the interpretation must remain cautious.
The correlation analyses are especially vulnerable to overinterpretation. The reported associations are modest and exploratory, and they should not be used to support mechanistic claims. The authors should present these correlations as hypothesis-generating only.
The reported effect size for breath-holding time, r = 1.00, is unusual and should be checked carefully. The authors should clarify the exact formula used for each effect size, ensure that the reported effect sizes are consistent with the statistical tests performed, and use a consistent effect size approach across outcomes. If parametric and non-parametric tests were mixed, the corresponding effect size metrics should be clearly explained.
The Abstract also contains repetitive and unclear correlation reporting. For example, associations involving PSQI/PSS and STS/PSS appear to be repeated. These should be simplified, corrected, and interpreted cautiously.
2.5 Mechanistic interpretation
The mechanistic explanation is currently too speculative. The manuscript suggests that improvements may be mediated by autonomic regulation, reduced sympathetic activity, enhanced parasympathetic tone, or stress modulation. These mechanisms are plausible, but they were not directly tested.
No objective autonomic or physiological markers were measured, such as heart rate variability, resting heart rate, blood pressure, cortisol, catecholamines, actigraphy, sleep architecture, or respiratory gas exchange. Therefore, the manuscript should clearly distinguish between observed findings and possible explanations.
Statements implying that autonomic regulation “mediated,” “underlies,” or “explains” the observed changes should be revised. A more appropriate formulation would be that autonomic regulation is a possible mechanism that should be examined in future controlled studies.
2.6 Functional performance outcomes
The inclusion of Timed Up-and-Go and five-times sit-to-stand provides practical functional measures, but their interpretation in healthy university students requires caution. These tests are commonly used in older adults or clinical populations, where they have clearer functional meaning. In young healthy adults, ceiling effects are likely, and small improvements may not represent clinically meaningful change.
The baseline TUG and STS values suggest that participants were already functioning well. A statistically significant reduction of less than one second in TUG may not be clinically important in this population. The authors should discuss whether the observed changes exceed minimal detectable change or minimal clinically important difference values for comparable healthy young adults. If such thresholds are unavailable, the authors should avoid describing these changes as clinically meaningful and instead present them as statistically significant within-group changes.
2.7 Sleep quality and perceived stress
The sleep and stress findings are interesting, but they should also be interpreted cautiously. PSQI and PSS are self-reported instruments, and both are vulnerable to expectation effects, reporting bias, and temporal changes unrelated to the intervention.
The timing of measurement should be discussed more carefully. The intervention lasted four weeks, and PSQI and PSS refer to recent experiences over a similar period. Depending on the exact timing of post-intervention assessment, the responses may partially reflect both pre-intervention and intervention-period experiences. This overlap should be acknowledged.
The lack of a control group is especially important for stress and sleep outcomes in university students, because these outcomes may vary substantially with academic workload, examinations, holidays, social factors, and sleep routines. The authors should report when the study occurred relative to examinations or other major academic stressors.
2.8 Participant flow and eligibility criteria
The participant flow section requires correction and clarification. The Results reportedly state that participants were excluded for “BMI ≤29.9 kg/m²,” but the inclusion criterion was BMI ≤29.9 kg/m². This appears to be an error, and the authors presumably meant BMI >29.9 kg/m². This should be corrected.
The manuscript should also clarify whether all enrolled participants completed the intervention and post-testing, whether any participants were excluded after enrollment, and whether the analysis included all participants or only those meeting an adherence threshold. Even if no participants were excluded for low adherence, the planned handling of adherence should be described transparently.
2.9 Conclusions
The conclusions should be substantially tempered. The current data support the statement that a four-week combined breathing exercise and respiratory muscle training program was associated with within-group improvements in breath-holding time, selected functional tests, self-reported sleep quality, and perceived stress. However, the data do not establish that the intervention caused these changes, nor do they demonstrate the physiological mechanisms responsible.
The conclusion should emphasize feasibility, adherence, and preliminary signals rather than effectiveness. The authors should recommend future randomized controlled trials with a control or sham group, blinded outcome assessment, objective respiratory measures, objective sleep or autonomic measures, and longer follow-up.
- Minor comments and editorial suggestions
- The Abstract should be rewritten to avoid causal language, repetition, and overstatement. The final sentence is grammatically incomplete and should be corrected.
- The intervention intensity should be reported consistently. The Abstract refers to 40–60% maximal inspiratory pressure, but the manuscript should specify both inspiratory and expiratory loading if EMT was prescribed using MEP.
- The terminology should be standardized throughout the manuscript. The authors should avoid switching between “college students” and “university students,” and should distinguish “breath-holding time” from “respiratory endurance.”
- The tables should be reformatted for readability. Table 2 appears to mix mean ± SD and median/IQR appropriately according to distribution, but the formatting should be clearer.
- The BMI values should be checked across tables and text to ensure consistency.
- Figure 1 is useful, but the caption should be shortened and formatting issues should be corrected.
- All p-value thresholds, correlation labels, symbols, and abbreviations should be used consistently.
- The authors should avoid describing exploratory correlations as evidence of a shared mechanism.
- The manuscript would benefit from careful English-language editing to improve grammar, clarity, and precision.
- Constructive recommendations for improvement
To strengthen the manuscript, the authors should:
- reframe the study as a single-arm pilot feasibility and preliminary signal study;
- revise the Abstract, Discussion, and Conclusion to avoid causal claims;
- justify the use of breath-holding time and avoid presenting it as a direct measure of respiratory muscle endurance;
- report post-intervention MIP, MEP, spirometry, or other respiratory measures if available;
- clarify intervention progression, monitoring, supervision, and adherence;
- correct the BMI exclusion inconsistency and clarify participant flow;
- check and explain all effect size calculations;
- present correlation analyses as exploratory and hypothesis-generating;
- remove or soften unsupported mechanistic claims about autonomic regulation;
- discuss the limited clinical meaning of TUG and STS changes in healthy young adults;
- address the timing and limitations of PSQI and PSS measurement;
- improve the clarity and consistency of tables, figures, terminology, and abstract wording.
- Final assessment
The manuscript addresses a worthwhile and potentially useful topic, and the intervention may be feasible and scalable in university settings. However, the current version requires major revision because the conclusions exceed what can be supported by the design, the primary outcome is vulnerable to bias, objective physiological mechanisms were not measured, and several statistical and reporting issues require correction. With substantial revision and more cautious interpretation, the manuscript could provide useful preliminary evidence to inform a future randomized controlled trial.
Comments on the Quality of English LanguageEnglish language must be improved.
Author Response
Reviewer 3
Comment 1:
The topic is timely and potentially relevant. Breathing exercises and respiratory muscle training are low-cost, accessible interventions that may be attractive for use in young adults, university settings, and preventive health programs. The study is strengthened by its practical intervention, high adherence, inclusion of both male and female participants, and use of several familiar clinical and patient-reported outcome measures. The manuscript may provide useful preliminary data for designing a future randomized controlled trial.
However, in its current form, the manuscript overstates the strength of its findings. The single-arm pre-post design does not allow causal conclusions regarding effectiveness. Several outcomes are vulnerable to learning effects, expectation effects, motivation, repeated testing, and temporal changes unrelated to the intervention. The interpretation of breath-holding time as respiratory endurance is also problematic without additional objective respiratory measures. The manuscript therefore requires substantial revision before it can be considered for further processing.
Response 1:
We sincerely thank the reviewer for the thorough and constructive evaluation of our manuscript. We appreciate the recognition of the study's practical relevance, high adherence, inclusion of both sexes, and potential value as preliminary data for future randomized controlled trials. We have carefully revised the manuscript to address all concerns raised.
Comment 2:
2.1 Study design and causal interpretation
The main limitation is the absence of a control group, sham intervention, randomization, or blinded assessment. Although the authors describe the study as a pilot pre-post intervention study, several parts of the manuscript appear to imply that the intervention caused improvements in respiratory endurance, functional performance, sleep quality, and perceived stress.
Because all outcomes were measured before and after the intervention in a single group, the observed changes cannot be confidently attributed to the intervention itself. Improvements may reflect learning effects, familiarity with testing procedures, expectation effects, regression to the mean, increased attention from study staff, changes in daily activity, academic workload, sleep schedule, or other unmeasured lifestyle factors during the four-week period.
The manuscript should therefore consistently describe the findings as preliminary within-group changes or associations, not as evidence of efficacy. Terms such as “effectiveness,” “improved,” “resulted in,” or “led to” should be replaced or qualified unless the authors are referring only to within-group changes. The Abstract, Discussion, and Conclusion particularly need revision so that the wording matches the exploratory single-arm design.
Response 2:
We agree. The absence of a control group prevents causal inference. We have revised the manuscript throughout to consistently describe findings as within-group changes observed following participation in the intervention rather than intervention effects or efficacy. Revised abstract conclusion and discussion.
Comment 3:
2.2 Primary outcome: breath-holding time
The use of breath-holding time as the main indicator of “respiratory endurance” requires stronger justification and more cautious interpretation. Breath-holding time is not a direct measure of respiratory muscle endurance. It is influenced by multiple factors, including motivation, discomfort tolerance, chemoreflex sensitivity, anxiety, prior experience with breath-holding, lung volume at the start of the test, and participant effort.
A single post-inhalation breath-hold trial is especially vulnerable to learning and motivational bias. Participants may perform better after the intervention simply because they are more familiar with the test or more willing to tolerate discomfort. The reported 132% increase is large, but without post-intervention maximal inspiratory pressure, maximal expiratory pressure, spirometry, or an objective respiratory endurance test, it is not possible to conclude that this represents a true physiological respiratory muscle adaptation.
The authors mention that MIP and MEP were used to prescribe training intensity. If these measures were collected at follow-up, they should be reported. If they were not collected, this should be acknowledged as a major limitation. The manuscript should avoid equating breath-holding time with respiratory muscle endurance and should instead refer to it more precisely as “breath-holding time” or “a composite respiratory performance measure.”
Response 3:
We agree and have revised the manuscript accordingly. (P. 5, Line 226-230) and (P. 12, Line 502-516)
Comment 4:
2.3 Intervention description and reproducibility
The intervention is clinically interesting, but further detail is required to make it reproducible. The authors state that inspiratory and expiratory muscle training were performed at 40–60% of maximal inspiratory or expiratory pressure, but it is unclear whether the load was progressed during the four weeks, whether MIP and MEP were reassessed during the intervention, and whether participants remained at the same relative or absolute intensity throughout the study.
The authors should clarify:
- how initial training loads were determined;
- whether IMT and EMT loads were adjusted over time;
- whether MIP and MEP were reassessed for progression;
- how adherence was monitored;
- whether sessions were supervised or unsupervised;
- whether adverse events or discomfort were recorded;
- whether all participants completed the same number of sessions.
The intervention is also multimodal, combining diaphragmatic breathing, pursed-lip breathing, inspiratory muscle training, and expiratory muscle training. Because these components were delivered together, the study cannot determine which component, if any, contributed most to the observed changes. This should be stated clearly as a limitation.
Response 4:
We thank the reviewer for highlighting the need for greater reproducibility. (P. 5, Line 231-233234 and (P. 12, Line 502-507)
Comment 5:
2.4 Statistical analysis and reporting
The statistical reporting needs careful revision. The sample size calculation appears to be based on detecting a medium effect in a paired comparison, but the manuscript includes multiple outcomes, multiple correlations, and subgroup comparisons. Although exploratory studies may reasonably avoid formal correction for multiple comparisons, the interpretation must remain cautious.
The correlation analyses are especially vulnerable to overinterpretation. The reported associations are modest and exploratory, and they should not be used to support mechanistic claims. The authors should present these correlations as hypothesis-generating only.
The reported effect size for breath-holding time, r = 1.00, is unusual and should be checked carefully. The authors should clarify the exact formula used for each effect size, ensure that the reported effect sizes are consistent with the statistical tests performed, and use a consistent effect size approach across outcomes. If parametric and non-parametric tests were mixed, the corresponding effect size metrics should be clearly explained.
The Abstract also contains repetitive and unclear correlation reporting. For example, associations involving PSQI/PSS and STS/PSS appear to be repeated. These should be simplified, corrected, and interpreted cautiously.
Response 5:
We agree and have correct and revised the interpretation accordingly.
Comment 6:
2.5 Mechanistic interpretation
The mechanistic explanation is currently too speculative. The manuscript suggests that improvements may be mediated by autonomic regulation, reduced sympathetic activity, enhanced parasympathetic tone, or stress modulation. These mechanisms are plausible, but they were not directly tested.
No objective autonomic or physiological markers were measured, such as heart rate variability, resting heart rate, blood pressure, cortisol, catecholamines, actigraphy, sleep architecture, or respiratory gas exchange. Therefore, the manuscript should clearly distinguish between observed findings and possible explanations.
Statements implying that autonomic regulation “mediated,” “underlies,” or “explains” the observed changes should be revised. A more appropriate formulation would be that autonomic regulation is a possible mechanism that should be examined in future controlled studies.
Response 6:
We agree. Discussion revised
Comment 7:
2.6 Functional performance outcomes
The inclusion of Timed Up-and-Go and five-times sit-to-stand provides practical functional measures, but their interpretation in healthy university students requires caution. These tests are commonly used in older adults or clinical populations, where they have clearer functional meaning. In young healthy adults, ceiling effects are likely, and small improvements may not represent clinically meaningful change.
The baseline TUG and STS values suggest that participants were already functioning well. A statistically significant reduction of less than one second in TUG may not be clinically important in this population. The authors should discuss whether the observed changes exceed minimal detectable change or minimal clinically important difference values for comparable healthy young adults. If such thresholds are unavailable, the authors should avoid describing these changes as clinically meaningful and instead present them as statistically significant within-group changes.
Response 7:
We agree. Discussion revised
Comment 8:
2.7 Sleep quality and perceived stress
The sleep and stress findings are interesting, but they should also be interpreted cautiously. PSQI and PSS are self-reported instruments, and both are vulnerable to expectation effects, reporting bias, and temporal changes unrelated to the intervention.
The timing of measurement should be discussed more carefully. The intervention lasted four weeks, and PSQI and PSS refer to recent experiences over a similar period. Depending on the exact timing of post-intervention assessment, the responses may partially reflect both pre-intervention and intervention-period experiences. This overlap should be acknowledged.
The lack of a control group is especially important for stress and sleep outcomes in university students, because these outcomes may vary substantially with academic workload, examinations, holidays, social factors, and sleep routines. The authors should report when the study occurred relative to examinations or other major academic stressors.
Response 8:
We agree.
Comment 9:
2.8 Participant flow and eligibility criteria
The participant flow section requires correction and clarification. The Results reportedly state that participants were excluded for “BMI ≤29.9 kg/m²,” but the inclusion criterion was BMI ≤29.9 kg/m². This appears to be an error, and the authors presumably meant BMI >29.9 kg/m². This should be corrected.
The manuscript should also clarify whether all enrolled participants completed the intervention and post-testing, whether any participants were excluded after enrollment, and whether the analysis included all participants or only those meeting an adherence threshold. Even if no participants were excluded for low adherence, the planned handling of adherence should be described transparently.
Response 9:
We thank the reviewer for identifying this error.
Comment 10:
2.9 Conclusions
The conclusions should be substantially tempered. The current data support the statement that a four-week combined breathing exercise and respiratory muscle training program was associated with within-group improvements in breath-holding time, selected functional tests, self-reported sleep quality, and perceived stress. However, the data do not establish that the intervention caused these changes, nor do they demonstrate the physiological mechanisms responsible.
The conclusion should emphasize feasibility, adherence, and preliminary signals rather than effectiveness. The authors should recommend future randomized controlled trials with a control or sham group, blinded outcome assessment, objective respiratory measures, objective sleep or autonomic measures, and longer follow-up.
Response 10:
The conclusion has been revised.
Comment 11:
Minor comments and editorial suggestions
- The Abstract should be rewritten to avoid causal language, repetition, and overstatement. The final sentence is grammatically incomplete and should be corrected.
- The intervention intensity should be reported consistently. The Abstract refers to 40–60% maximal inspiratory pressure, but the manuscript should specify both inspiratory and expiratory loading if EMT was prescribed using MEP.
- The terminology should be standardized throughout the manuscript. The authors should avoid switching between “college students” and “university students,” and should distinguish “breath-holding time” from “respiratory endurance.”
- The tables should be reformatted for readability. Table 2 appears to mix mean ± SD and median/IQR appropriately according to distribution, but the formatting should be clearer.
- The BMI values should be checked across tables and text to ensure consistency.
- Figure 1 is useful, but the caption should be shortened and formatting issues should be corrected.
- All p-value thresholds, correlation labels, symbols, and abbreviations should be used consistently.
- The authors should avoid describing exploratory correlations as evidence of a shared mechanism.
- The manuscript would benefit from careful English-language editing to improve grammar, clarity, and precision.
Response 11:
All the minor comments have been taken into consideration.
Author Response File:
Author Response.docx
Round 2
Reviewer 1 Report
Comments and Suggestions for AuthorsThe authors did a good job of proofreading the manuscript. They also responded to all my comments. I have no other comments.
Author Response
Comment 1:
The authors did a good job of proofreading the manuscript. They also responded to all my comments. I have no other comments.
Response 1:
We sincerely thank the reviewer for the careful evaluation of our revised manuscript and for the positive comments. We appreciate your recognition of our efforts in addressing the previous comments and improving the manuscript.
Reviewer 2 Report
Comments and Suggestions for AuthorsI would like to thank the authors for supporting their rationale and answering to all questions. Yet, the main point remains. This population doesn't present any deficiencies and no respiratory weakness, thus applying an IMT and EMT program of medium intensity raises questions. The design of the study needs to be further supported.
Author Response
Comment 1:
I would like to thank the authors for supporting their rationale and answering to all questions. Yet, the main point remains. This population doesn't present any deficiencies and no respiratory weakness, thus applying an IMT and EMT program of medium intensity raises questions. The design of the study needs to be further supported.
Response 1:
We sincerely thank the reviewer for this important observation. We agree that healthy university students do not typically exhibit respiratory muscle weakness or clinically impaired respiratory function. Our intention was not to evaluate respiratory rehabilitation in a deficient population, but rather to explore whether respiratory muscle conditioning, when combined with breathing exercises, could produce measurable physical and psychological adaptations in healthy young adults.
Similar to resistance or endurance exercise, respiratory muscle training has increasingly been investigated as a performance-enhancing and health-promotion strategy in healthy individuals rather than solely as rehabilitation for respiratory disease. Previous studies have reported improvements in respiratory muscle strength, exercise tolerance, and exercise performance in healthy adults and athletes following threshold-loaded respiratory muscle training.
The present study was therefore designed as a pilot, single-arm feasibility study to generate preliminary effect-size estimates and examine whether this multimodal intervention merits evaluation in future randomized controlled trials. We agree that the absence of respiratory impairment limits the clinical necessity of the intervention and have revised the manuscript to clarify that the rationale is based on optimization of physiological function rather than treatment of respiratory dysfunction. We have also emphasized throughout the manuscript that the findings are exploratory and hypothesis-generating.
Reviewer 3 Report
Comments and Suggestions for Authors
I thank the authors for their detailed responses to my previous comments and for the revisions made to the manuscript. The topic remains timely and relevant, particularly because breathing exercises and respiratory muscle training are low-cost, accessible interventions with potential applicability in young adults, university settings, and preventive health programs. The study is further strengthened by the practical nature of the intervention, the high adherence reported, the inclusion of both male and female participants, and the use of familiar clinical and patient-reported outcome measures.
Overall, the authors have responded constructively to the main concerns raised in the previous review. In particular, they have acknowledged the limitations inherent to the single-arm pre-post design and have revised the manuscript to describe the findings more cautiously as preliminary within-group changes rather than evidence of intervention efficacy. The revised wording in the Abstract, Discussion, and Conclusion appears more consistent with the exploratory nature of the study and appropriately avoids stronger causal claims.
The authors have also addressed the concern regarding the interpretation of breath-holding time. I appreciate that the manuscript has been revised to avoid equating breath-holding time directly with respiratory muscle endurance and to present it more cautiously as a respiratory performance-related measure. This is an important improvement, given that breath-holding time may be influenced by motivation, discomfort tolerance, learning effects, anxiety, lung volume, and participant effort. The manuscript should still ensure that this terminology is applied consistently throughout all sections, including the Abstract, Results, Discussion, tables, and figure captions.
The additional clarification regarding the intervention is also appreciated. The authors indicate that the relevant sections have been revised to improve reproducibility. This is important because the intervention is multimodal, combining diaphragmatic breathing, pursed-lip breathing, inspiratory muscle training, and expiratory muscle training. The revised manuscript should clearly specify how the initial training loads were determined, whether inspiratory and expiratory loads were progressed during the intervention, whether MIP and MEP were reassessed, how adherence was monitored, whether sessions were supervised or unsupervised, whether discomfort or adverse events were recorded, and whether all participants completed the same number of sessions. Since all components were delivered together, the manuscript should also continue to state clearly that the study cannot determine which individual component contributed most to the observed within-group changes.
The revisions to the statistical analysis and interpretation are also noted. The authors have indicated that they corrected and revised the interpretation of the findings. I recommend that the authors ensure that all effect sizes are reported consistently and that the formula used for each effect size is clearly described. The previously reported effect size for breath-holding time should be checked carefully, as a value of r = 1.00 is unusual and may require additional clarification. The correlation analyses should remain clearly framed as exploratory and hypothesis-generating, rather than as evidence of mechanisms or causal pathways.
The Discussion has been improved by tempering mechanistic explanations. The authors appropriately acknowledge that possible mechanisms such as autonomic regulation, reduced sympathetic activity, enhanced parasympathetic tone, or stress modulation were not directly tested. This distinction between observed findings and possible explanations should be maintained throughout the manuscript. Statements suggesting that autonomic mechanisms “mediated,” “underlie,” or “explain” the observed changes should be avoided unless supported by objective physiological measures.
I also appreciate that the authors revised the interpretation of the functional performance outcomes. The use of Timed Up-and-Go and five-times sit-to-stand tests in healthy university students should be discussed cautiously because ceiling effects are likely in this population and small statistically significant changes may not necessarily represent clinically meaningful improvements. The manuscript should therefore avoid overemphasizing clinical relevance unless minimal detectable change or minimal clinically important difference values for comparable healthy young adults can be cited.
The authors have acknowledged the concerns regarding sleep quality and perceived stress. These outcomes remain interesting but should be interpreted cautiously because PSQI and PSS are self-reported measures and may be influenced by expectation effects, reporting bias, academic workload, examinations, holidays, sleep schedules, or other temporal factors. The manuscript would benefit from clearly stating when the study took place in relation to major academic stressors and from acknowledging the overlap between the measurement periods and the intervention duration.
The correction of the participant flow and eligibility criteria is appreciated, particularly the apparent error regarding BMI. The revised manuscript should clearly report whether all enrolled participants completed the intervention and post-testing, whether any participants were excluded after enrollment, and whether the final analysis included all participants or only those meeting an adherence threshold.
Finally, the authors indicate that all minor editorial comments have been taken into consideration. Before acceptance, I recommend a final careful review of the Abstract, terminology, tables, figure captions, p-value reporting, correlation labels, abbreviations, and English-language clarity. The manuscript should consistently distinguish “breath-holding time” from “respiratory endurance,” use either “university students” or “college students” consistently, and avoid presenting exploratory correlations as evidence of a shared mechanism.
In summary, the authors have made meaningful revisions and have addressed the principal conceptual concerns raised in the previous review. The manuscript is now more appropriately framed as a feasibility-oriented, exploratory pilot study that provides preliminary within-group findings rather than evidence of intervention effectiveness. A few minor issues related to consistency, statistical reporting, terminology, and cautious interpretation remain. Therefore, I recommend minor revision.
Comments on the Quality of English LanguageEnglish language must be improved.
Author Response
Comment 1:
The authors have also addressed the concern regarding the interpretation of breath-holding time. I appreciate that the manuscript has been revised to avoid equating breath-holding time directly with respiratory muscle endurance and to present it more cautiously as a respiratory performance-related measure. This is an important improvement, given that breath-holding time may be influenced by motivation, discomfort tolerance, learning effects, anxiety, lung volume, and participant effort. The manuscript should still ensure that this terminology is applied consistently throughout all sections, including the Abstract, Results, Discussion, tables, and figure captions.
Response 1:
Thank you for this important observation. We carefully reviewed the entire manuscript and revised the terminology wherever necessary to consistently describe breath-holding time as a composite respiratory performance measure rather than as a direct measure of respiratory muscle endurance. The Abstract, Introduction, Methods, Results, Discussion, tables, and figure captions have all been checked to ensure consistent terminology throughout the manuscript.
Comment 2:
The additional clarification regarding the intervention is also appreciated. The authors indicate that the relevant sections have been revised to improve reproducibility. This is important because the intervention is multimodal, combining diaphragmatic breathing, pursed-lip breathing, inspiratory muscle training, and expiratory muscle training. The revised manuscript should clearly specify how the initial training loads were determined, whether inspiratory and expiratory loads were progressed during the intervention, whether MIP and MEP were reassessed, how adherence was monitored, whether sessions were supervised or unsupervised, whether discomfort or adverse events were recorded, and whether all participants completed the same number of sessions. Since all components were delivered together, the manuscript should also continue to state clearly that the study cannot determine which individual component contributed most to the observed within-group changes.
Response 2:
We thank the reviewer for this helpful suggestion. To improve reproducibility, we expanded the Methods section by providing additional details regarding the intervention protocol. Specifically, we clarified how baseline IMT and EMT training loads were established using MIP and MEP measurements, stated that loads were maintained at 40–60% of baseline values without progression because MIP and MEP were not reassessed, described the supervision of all training sessions, detailed adherence monitoring through attendance records and training logs, specified the predefined adherence criterion (<80%) for exclusion, reported that all participants completed at least 90% of the prescribed sessions, and stated that no adverse events or clinically significant discomfort occurred. We also continue to acknowledge in the Discussion that, because breathing exercises and respiratory muscle training were delivered simultaneously, the independent contribution of each intervention component cannot be determined.
Comment 3:
The revisions to the statistical analysis and interpretation are also noted. The authors have indicated that they corrected and revised the interpretation of the findings. I recommend that the authors ensure that all effect sizes are reported consistently and that the formula used for each effect size is clearly described. The previously reported effect size for breath-holding time should be checked carefully, as a value of r = 1.00 is unusual and may require additional clarification.
Response 3:
Thank you for this observation. We carefully reviewed all statistical analyses and effect size calculations. The statistical analysis section has been revised to clearly specify the formulas used for each effect size. The previously reported breath-holding time effect size has been recalculated and corrected. Effect sizes are now reported consistently throughout the manuscript.
Comment 4:
The correlation analyses should remain clearly framed as exploratory and hypothesis-generating, rather than as evidence of mechanisms or causal pathways.
Response 4:
We agree completely. The Results and Discussion have been revised to consistently describe the correlation analyses as exploratory and hypothesis-generating. Statements implying mechanistic or causal relationships have been modified accordingly, and the Discussion now emphasizes that these associations do not establish underlying physiological mechanisms.
Comment 5:
The Discussion has been improved by tempering mechanistic explanations. The authors appropriately acknowledge that possible mechanisms such as autonomic regulation, reduced sympathetic activity, enhanced parasympathetic tone, or stress modulation were not directly tested. This distinction between observed findings and possible explanations should be maintained throughout the manuscript. Statements suggesting that autonomic mechanisms “mediated,” “underlie,” or “explain” the observed changes should be avoided unless supported by objective physiological measures.
Response 5:
We agree completely. The Results and Discussion have been revised to consistently describe the correlation analyses as exploratory and hypothesis-generating. Statements implying mechanistic or causal relationships have been modified accordingly, and the Discussion now emphasizes that these associations do not establish underlying physiological mechanisms.
Comment 6:
I also appreciate that the authors revised the interpretation of the functional performance outcomes. The use of Timed Up-and-Go and five-times sit-to-stand tests in healthy university students should be discussed cautiously because ceiling effects are likely in this population and small statistically significant changes may not necessarily represent clinically meaningful improvements. The manuscript should therefore avoid overemphasizing clinical relevance unless minimal detectable change or minimal clinically important difference values for comparable healthy young adults can be cited.
Response 6:
Thank you. We have further tempered the interpretation of the Timed Up-and-Go and Sit-to-Stand findings in both the Discussion and Limitations sections. We now acknowledge the possibility of ceiling effects in healthy young adults and emphasize that the clinical significance of the observed changes remains uncertain because minimal clinically important differences have not been established for this population.
Comment 7:
The authors have acknowledged the concerns regarding sleep quality and perceived stress. These outcomes remain interesting but should be interpreted cautiously because PSQI and PSS are self-reported measures and may be influenced by expectation effects, reporting bias, academic workload, examinations, holidays, sleep schedules, or other temporal factors. The manuscript would benefit from clearly stating when the study took place in relation to major academic stressors and from acknowledging the overlap between the measurement periods and the intervention duration.
Response 7:
We agree and have expanded the Discussion accordingly. We now explicitly acknowledge that the PSQI and PSS are self-reported measures susceptible to expectation and reporting bias, and that both questionnaires assess experiences over approximately the preceding month. We also clarify that data collection occurred during a standard academic semester rather than during final examination periods, while acknowledging that variations in academic workload and other external factors may still have influenced participants' responses.
Comment 8:
The correction of the participant flow and eligibility criteria is appreciated, particularly the apparent error regarding BMI. The revised manuscript should clearly report whether all enrolled participants completed the intervention and post-testing, whether any participants were excluded after enrollment, and whether the final analysis included all participants or only those meeting an adherence threshold.
Response 8:
Thank you. The participant flow has been clarified in the Results section. We now explicitly state that all 40 enrolled participants completed the intervention and post-intervention assessments, achieved at least 90% adherence, and were therefore included in the final analyses.
Comment 9:
Finally, the authors indicate that all minor editorial comments have been taken into consideration. Before acceptance, I recommend a final careful review of the Abstract, terminology, tables, figure captions, p-value reporting, correlation labels, abbreviations, and English-language clarity. The manuscript should consistently distinguish “breath-holding time” from “respiratory endurance,” use either “university students” or “college students” consistently, and avoid presenting exploratory correlations as evidence of a shared mechanism.
Response 9:
We appreciate this recommendation. We conducted a comprehensive final review of the entire manuscript. Terminology has been standardized (particularly the distinction between breath-holding time and respiratory muscle endurance), abbreviations have been corrected where necessary, tables and figure captions have been revised for consistency, p-value reporting has been standardized, and the manuscript has undergone an additional round of English-language editing to improve clarity and readability.