Acute Resistance Exercise Temporarily Reduces Circulating Adiponectin in Trained Young Men: A Pilot Study

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thanks for the invitation to review this work.

 

1. The introduction effectively frames the study’s rationale, linking adiponectin’s role in metabolism to resistance exercise and time under tension (TUT). However, the transition between paragraphs 6 (discussing HIIT) and 7 (focusing on TUT) is abrupt. The connection between HIIT-induced metabolic stress and TUT’s potential impact on adiponectin could be strengthened to highlight the study’s novelty.
2. Table 1: The table lists “Percentile ACSM 1RM/BW” with a mean of 88.9, but the unit is unclear. Is this a percentile score or a ratio? Clarifying the variable’s definition (e.g., “ACSM 1RM/BW percentile”) would resolve ambiguity.
3. The description of ETS1 (high TUT) and ETS2 (moderate TUT) is clear, but the text mentions “the time under tension protocol used in ETS1 was designed to elicit greater metabolic stress, primarily through the prolonged eccentric phase” without specifying the cadence for ETS2. Adding the cadence for ETS2 (e.g., “2-1-2-1” as in the abstract) in the methods would improve consistency.
4. The post-hoc power calculation (0.73) is noted as a limitation, but the a priori calculation (requiring 12 participants) is based on a repeated-measures ANOVA with a medium effect size (f=0.4). However, the study uses non-parametric tests (Friedman, Wilcoxon) due to non-normal data. Reassessing power for non-parametric analyses would be more accurate, though this is a minor point.
5. Figure 3: The caption states “plasma adiponectin decreased by approximately 15–20% at 24 hours and by nearly 25% at 48 hours compared to baseline values,” but the figure’s error bars (SD) are large, making the magnitude of change less clear. Adding exact p-values for each time point comparison (e.g., baseline vs. 24h, baseline vs. 48h) in the caption would enhance interpretability.
6. Figure 4: The Western blot images (A and B) show bands for HMW, MMW, and LMW adiponectin, but the densitometric analysis (C and D) does not specify which oligomer(s) are significantly changed. The text mentions “HMW adiponectin oligomers decrease,” but the figure’s statistical markers (**p<0.01, ***p<0.001) should be explicitly linked to HMW in the caption.
7. Figure 5: The VAS data (panel B) is described as showing “a reduction of muscle soreness between 24 and 48 hrs post exercise,” but the figure only plots VAS at 24h. Including 48h VAS data in the figure or clarifying that the reduction is inferred from the text would resolve this discrepancy.
8. The text states “plasma adiponectin showed moderate to strong inverse correlations with CK during recovery,” but the exact correlation coefficients (e.g., r=-0.65 at 24h) are not provided. Reporting these values would strengthen the conclusion about the relationship’s strength.
9. In Discussion. The sentence “the greater post-exercise CK elevations, which is indicative of heightened metabolic and mechanical stress, were moderately to strongly associated with larger reductions in plasma adiponectin” is well-supported, but the subsequent claim “this inverse relationship is consistent with previous evidence showing a reduction in adiponectin under conditions of acute metabolic overload” would benefit from a specific reference (e.g., citing a study where CK and adiponectin correlate inversely).The discussion notes “salivary adiponectin remained unchanged,” but the abstract mentions “salivary adiponectin remained unchanged” without explaining why this is notable. Adding a sentence on the potential implications (e.g., saliva may not reflect systemic adiponectin changes) would improve coherence.

The final sentence (“Future studies that consider long-term resistance training interventions and integrate other molecular markers should clarify the role of adiponectin within the muscle-adipose endocrine axis”) is vague. Specifying which markers (e.g., IL-6, myostatin; Cell Death Dis. 2025, 16, 788) or interventions would be valuable would make the suggestion more actionable.

10. The small sample size is correctly identified, but the study’s focus on male participants is not discussed as a limitation. Acknowledging that results may not generalize to females would be appropriate.
11. Figure 6: The panel labels (A1, A2, etc.) are clear, but the y-axis for “Adiponectin (μg/mL)” in some subpanels is truncated, making it hard to compare baseline values across groups. Adjusting the y-axis range to include all data points would improve readability.

 

Author Response

Comment 1: The introduction effectively frames the study’s rationale, linking adiponectin’s role in metabolism to resistance exercise and time under tension (TUT). However, the transition between paragraphs 6 (discussing HIIT) and 7 (focusing on TUT) is abrupt. The connection between HIIT-induced metabolic stress and TUT’s potential impact on adiponectin could be strengthened to highlight the study’s novelty.

Response 1: The authors appreciate the reviewer’s observation regarding the structure of the Introduction. Consequently, they have revised the text to establish a stronger conceptual link between these modalities.

Location: Page 2, lines 83-90

Comment 2: Table 1: The table lists “Percentile ACSM 1RM/BW” with a mean of 88.9, but the unit is unclear. Is this a percentile score or a ratio? Clarifying the variable’s definition (e.g., “ACSM 1RM/BW percentile”) would resolve ambiguity.

Response 2: Thank you for noting this ambiguity. We confirm that the reported value refers to the normative percentile rank derived from ACSM normative data for adult men, based on the participants’ relative strength ratio (1RM/body mass) for the leg press exercise. To eliminate any potential confusion between a percentile score and a ratio, we revised the Table 1 row label and added a clarifying footnote defining the metric and its unit (percentile rank, 0–100).

Location: Page 4, Table 1

Comment 3: The description of ETS1 (high TUT) and ETS2 (moderate TUT) is clear, but the text mentions “the time under tension protocol used in ETS1 was designed to elicit greater metabolic stress, primarily through the prolonged eccentric phase” without specifying the cadence for ETS2. Adding the cadence for ETS2 (e.g., “2-1-2-1” as in the abstract) in the methods would improve consistency.

Response 3: The authors agree that specifying the exact cadence in the method description improves clarity and consistency between the abstract and the main text. The description of the experimental sessions has been amended to explicitly include the cadence codes for both protocols.

Location: Page 5, lines 175-178

Comment 4: Reassess power for non-parametric analyses instead of the ANOVA-based a priori calculation.

Response 4: Thank you for this comment. We agree that the ANOVA-based a priori sample size calculation was used as a planning benchmark and does not directly correspond to the rank-based inferential analyses used in the final manuscript. Accordingly, we removed the post-hoc power statement and added sensitivity analyses (GPower 3.1.9.6) to quantify minimum detectable effects given n = 9. Specifically, we report (i) the minimum detectable within-session omnibus time effect across four repeated measures (f = 0.42, under stated assumptions) and (ii) the minimum detectable paired between-protocol effect for the four ETS1 vs ETS2 comparisons at matched time points (baseline, 15 min, 24 h, 48 h), using a conservative familywise α = 0.0125 (0.05/4), which yielded d_z = 1.39 (α = 0.05 yields d_z = 1.07). We also clarify that non-parametric tests were applied due to departures from normality. The methods section regarding the statistical analysis performed has been rewrite.

Location: Page 6, Section 2.6 Statistics

Comment 5: Figure 3: The caption states “plasma adiponectin decreased by approximately 15–20% at 24 hours and by nearly 25% at 48 hours compared to baseline values,” but the figure’s error bars (SD) are large, making the magnitude of change less clear. Adding exact p-values for each time point comparison (e.g., baseline vs. 24h, baseline vs. 48h) in the caption would enhance interpretability.

Response 5: We thank the reviewer for this suggestion. To improve interpretability, we revised the Figure 3 caption to report the exact two-tailed Conover post hoc p-values for baseline contrasts at each time point and added the corresponding effect sizes (matched rank-biserial correlation, r_rb). We also report the omnibus Friedman statistics and Kendall’s W for completeness.

Location: Page 7, lines 261-275

Comment 6: Figure 4: The Western blot images (A and B) show bands for HMW, MMW, and LMW adiponectin, but the densitometric analysis (C and D) does not specify which oligomer(s) are significantly changed. The text mentions “HMW adiponectin oligomers decrease,” but the figure’s statistical markers (**p<0.01, ***p<0.001) should be explicitly linked to HMW in the caption.

Response 6: The authors thank the reviewer for highlighting this ambiguity. They have revised the caption for Figure 4 to explicitly state that the statistical significance markers refer specifically to HMW.

Location: Page 8, line 293

Comment 7: Figure 5: The VAS data (panel B) is described as showing “a reduction of muscle soreness between 24 and 48 hrs post exercise,” but the figure only plots VAS at 24h. Including 48h VAS data in the figure or clarifying that the reduction is inferred from the text would resolve this discrepancy.

Response 7: Thank you for highlighting this discrepancy. The VAS panel (Figure 5B) includes both 24 h and 48 h data; however, the caption did not explicitly state the 48 h time point, which could lead to confusion. We have revised the Figure 5 caption to specify that VAS was assessed at 24 h and 48 h in both ETS1 and ETS2 and we added the exact paired-comparison statistics, including P values and effect sizes (r_rb with 95% CI) for the 24 h vs 48 h contrasts. In addition, we expanded the caption notes to define χ²F, Kendall’s W, and r_rb to ensure interpretability.

Location: Page 9, lines 305-318

Comment 8: The text states “plasma adiponectin showed moderate to strong inverse correlations with CK during recovery,” but the exact correlation coefficients (e.g., r=-0.65 at 24h) are not provided. Reporting these values would strengthen the conclusion about the relationship’s strength.

Response 8: We sincerely thank the reviewer for this crucial observation, which prompted us to re-evaluate our correlation data in detail. Upon performing the specific calculations to provide the requested coefficients, we identified that the statement in the original manuscript was incorrect. Spearman’s rank correlation analysis revealed no significant linear associations between plasma adiponectin and CK concentrations (all p > 0.05). The original sentence was likely a drafting error, inadvertently attributing the significant correlations observed with VAS (Figure 7) to CK.

We have therefore corrected the manuscript to accurately reflect these findings. We removed the claim of a "moderate to strong inverse correlation" from the Abstract, Discussion, and Conclusions (line 448).

We clarified that while acute resistance exercise triggers both a significant CK increase and an adiponectin decrease at the group level, the magnitude of muscle damage (CK) does not linearly predict the extent of adiponectin reduction at the individual level. We believe this correction provides a more precise physiological interpretation of the data, suggesting that adiponectin downregulation is a systemic threshold response rather than a dose-dependent effect of muscle damage.

Location: Page 1, lines 32-42. Page 9, lines 338-321. Page 10, lines 354-357. Page 11, lines 394-400

Comment 9: In Discussion. The sentence “the greater post-exercise CK elevations, which is indicative of heightened metabolic and mechanical stress, were moderately to strongly associated with larger reductions in plasma adiponectin” is well-supported, but the subsequent claim “this inverse relationship is consistent with previous evidence showing a reduction in adiponectin under conditions of acute metabolic overload” would benefit from a specific reference (e.g., citing a study where CK and adiponectin correlate inversely).The discussion notes “salivary adiponectin remained unchanged,” but the abstract mentions “salivary adiponectin remained unchanged” without explaining why this is notable. Adding a sentence on the potential implications (e.g., saliva may not reflect systemic adiponectin changes) would improve coherence.

The final sentence (“Future studies that consider long-term resistance training interventions and integrate other molecular markers should clarify the role of adiponectin within the muscle-adipose endocrine axis”) is vague. Specifying which markers (e.g., IL-6, myostatin; Cell Death Dis. 2025, 16, 788) or interventions would be valuable would make the suggestion more actionable.

Response 9: The authors appreciate these constructive suggestions. As requested, a specific reference has been added to the Discussion to support the inverse relationship between metabolic overload and adiponectin reduction. The text now explicitly clarifies that saliva may not serve as a reliable indicator of systemic changes in adiponectin following resistance exercise. The concluding sentence has been refined to be more actionable and has incorporated the recommended citation.

Location: Page 1, lines 36-42. Page 11, lines 401-405

Comment 10: The small sample size is correctly identified, but the study’s focus on male participants is not discussed as a limitation. Acknowledging that results may not generalize to females would be appropriate.

Response 10: The authors agree with the reviewer that the inclusion of male participants limits the generalizability of the findings. Accordingly, they have revised the "Limitations" to explicitly acknowledge this constraint. The text now specifies that the results cannot be extrapolated to female populations.

Location: Page 12, lines 424-428

Comment 11: Figure 6: The panel labels (A1, A2, etc.) are clear, but the y-axis for “Adiponectin (μg/mL)” in some subpanels is truncated, making it hard to compare baseline values across groups. Adjusting the y-axis range to include all data points would improve readability.

Response 11: Thank you for this comment regarding the truncated y-axis in Figure 6. We agree that truncated axes can complicate comparisons across panels if not clearly indicated. In our data, baseline plasma adiponectin values were all above ~12 µg/mL (minimum, ETS1: 14,360 µg/mL; ETS2: 14,190 µg/mL), and the axis truncation was applied to improve visual resolution of inter-individual dispersion and the fitted relationships.

To avoid any potential misinterpretation, we have explicitly stated in the figure caption that the y-axis is truncated (with an axis break) and that no observations fall below the lower bound, by adding minimum data for ETS1 and ETS2.

We believe this maintains readability while addressing transparency and comparability.

Location: Page 10, lines 342-343

Reviewer 2 Report

Comments and Suggestions for Authors

This is an interesting research article with adequate novelty. However, some points should be addressed.

• The study population is too short. For this reason, the authors should add int the title that this is a pilot or preliminary study.
• The conclusion section of the abstract includes much repetitions of the results of the study. The authors should try to reduce the conclusion section of the abstract by avoiding repetitions.
• In the introduction section (1st paragraph), the biological role of adiponectin should be more deeply analyzed.
• Before the aim of the study in the last paragraph of the introduction section, the authors should emphasize the literature gap that their study will cover.
• Do some participants be systematically athletes or not? This issue should be reported in section 2.1.
• The mean BMI of the participants is close to overweight cut off. Do the authors select for some reason such a population? This should be discussed.
• The letters of Table 2 should be increased.
• The size and the resolution of figure 3 should be increased to be more easily readable.
• The resolution of figure 4 should be improved.
• Again the size and the resolution of figure 6 should be increased to be more easily readable.
• The sentence in lines 335-337 "Recent studies demonstrated that adipose tissue expresses the transporter of creatine and participates in a creatine-induced cycle that increases thermogenesis and whole-body energy expenditure." needs some references and a more deeply analysis.
• The sentence in lines 344-346 "This hypothesis is in line with previous research showing that adiponectin downreg ulation accompanies early recovery phases characterized by oxidative stress and energetic imbalance." needs some reference and a more deeply analysis.
• Both the strengths and the limitations of the study should be reported at the last paragraph of the discussion.
• The two paragraphs of the conclusion section should be merged into one paragraph.
• The authors should add more proposals concerning what future studies could be performed based on the results of their study.
• English language editing is recommended.

Comments on the Quality of English Language

English language editing is recommended.

Author Response

Comment 1: The study population is too short. For this reason, the authors should add int the title that this is a pilot or preliminary study.

Response 1: The authors accept the reviewer’s suggestion regarding the sample size. They have modified the title to explicitly categorise the work as a "pilot study."

Location: Page 1, line 3

Comment 2: The conclusion section of the abstract includes much repetitions of the results of the study. The authors should try to reduce the conclusion section of the abstract by avoiding repetitions.

Response 2: The authors agree with the reviewer’s observation, and accordingly, they have condensed the abstract conclusion section to avoid restating the results, thereby improving the overall flow of the Abstract.

Location: Page 1, lines 36-42

Comment 3: In the introduction section (1st paragraph), the biological role of adiponectin should be more deeply analyzed.

Response 3: The authors appreciate the reviewer’s recommendation to expand upon the biological background of adiponectin. In the revised Introduction, they have deepened the analysis of adiponectin’s physiological functions.

Location: Page 2, lines 47-65

Comment 4: Before the aim of the study in the last paragraph of the introduction section, the authors should emphasize the literature gap that their study will cover.

Response 4: The authors accept the reviewer’s suggestion to explicitly define the literature gap prior to stating the study's aim. The text now identifies the absence of studies comparing resistance protocols matched for volume but differing in TUT as a critical gap.

Location: Page 2, lines 95-101

Comment 5: Do some participants be systematically athletes or not? This issue should be reported in section 2.1.

Response 5: The authors agree that defining the training status of the population is essential for the interpretation of the physiological responses. The participants recruited for this study were "recreationally trained" individuals. While they adhered to a systematic training regimen (minimum 2 years of experience, frequency >3 sessions/week), they were not professional or elite competitive athletes at the time of enrolment. This distinction has been clarified in the "Participants’ recruitment" section.

Location: Page 3, lines 109-115

Comment 6: The mean BMI of the participants is close to overweight cut off. Do the authors select for some reason such a population? This should be discussed.

Response 6: The reviewer correctly notes that the BMI values approach the overweight cutoff (≥25 kg/m²). However, in resistance-trained populations, BMI is well-documented to be a poor indicator of adiposity due to the high density of muscle tissue. The participants were selected for their training experience, which naturally correlates with higher skeletal muscle mass. As shown in Table 1, the participants exhibited a low percentage of Fat Mass (14.8%) and a high percentage of Skeletal Muscle Mass (44.5%), confirming that the BMI values reflect muscularity rather than excess adiposity. A clarifying sentence has been added to the Participants section.

Location: Page 3, lines 117-121

Comment 7: The letters of Table 2 should be increased.

Response 7: Following the reviewer suggestion, the letters of Table 2 have been increased

Comment 8: The size and the resolution of figure 3 should be increased to be more easily readable.

Response 8: Following the reviewer suggestion, the size and the resolution of figure 3 have been increased

Comment 9: The resolution of figure 4 should be improved.

Response 9: Following the reviewer suggestion, the resolution of figure 4 has been increased

Comment 10: Again, the size and the resolution of figure 6 should be increased to be more easily readable.

Response 10: Following the reviewer suggestion, the resolution of figure 6 has been increased

Comment 11: The sentence in lines 335-337 "Recent studies demonstrated that adipose tissue expresses the transporter of creatine and participates in a creatine-induced cycle that increases thermogenesis and whole-body energy expenditure." needs some references and a more deeply analysis.

Response 11: The authors have addressed the reviewer’s request to support the statement regarding creatine transport in adipose tissue with appropriate literature.

Location: Page 11, lines 392-396

Comment 12: The sentence in lines 344-346 “This hypothesis is in line with previous research showing that adiponectin downregulation accompanies early recovery phases characterized by oxidative stress and energetic imbalance.” Needs some reference and a more deeply analysis.

Response 12: The authors have addressed the reviewer’s request to substantiate the statement regarding adiponectin downregulation during early recovery.

Location: Page 11, lines 396-400

Comment 13: Both the strengths and the limitations of the study should be reported at the last paragraph of the discussion.

Response 13: The authors accept the reviewer’s recommendation. In the revised Discussion, the final paragraph has been expanded to explicitly report both the limitations and conceptual strengths.

Location: Page 11, lines 410-443

 Comment 14: The two paragraphs of the conclusion section should be merged into one paragraph.

Response 14: We thank the reviewer for his/her suggestion and accordingly we modified the section in the latest version.

Location: Page 12, lines 452-458

Comment 15: The authors should add more proposals concerning what future studies could be performed based on the results of their study.

Response 15: We thank the reviewer for this valuable suggestion. We have expanded the Discussion section to better outline future research directions.

Location: Page 12, lines 444-450

Comment 16: English language editing is recommended.

Response 16: We thank the reviewer for this suggestion. Following the reviewer’s recommendation, the manuscript has undergone a careful and thorough English language revision to improve clarity, consistency, and overall readability.

Reviewer 3 Report

Comments and Suggestions for Authors

Thank you for the opportunity to review this manuscript. The study addresses an important gap in understanding adiponectin responses to acute resistance training. However, several issues should be addressed before publication.

1. The authors report a post-hoc statistical power of 0.73, below the 0.80 needed for 12 participants. This shortfall undermines confidence in the non-significant findings, particularly the lack of differences between the ETS1 and ETS2 protocols. With the current sample size, the study is underpowered to detect potentially meaningful biological differences between the TUT conditions. The authors should explicitly discuss which findings are most affected by insufficient power, whether key conclusions might change with adequate power, and whether results should be considered preliminary pending larger-scale validation. At minimum, null findings for between-protocol comparisons should be framed more cautiously.
2. The authors measure adiponectin and CK but infer metabolic stress responses without directly assessing primary metabolic stressors. The study does not quantify lactate, inflammatory cytokines (IL-6, IL-8, TNF-α), ROS, or oxidative stress markers, yet the central argument attributes adiponectin reductions to “metabolic stress.” Relying on CK alone is problematic, as it primarily indicates muscle membrane disruption rather than metabolic flux. The authors should either include lactate and inflammatory markers in future work, or temper mechanistic claims, presenting the findings as correlational rather than explanatory.
3. The study enrolled only males, yet adiponectin regulation is sex-dependent, influenced by estrogen and testosterone. Women typically have higher basal adiponectin, different inflammatory responses to exercise, and potentially distinct adipokine kinetics during recovery. As such, these findings may not generalize to women, who represent roughly half of resistance-training populations. The authors should acknowledge this as a key limitation and clarify whether the male-only sample was justified mechanistically or purely for practical reasons.
4. Sampling at baseline, 15 min, 24 hr, and 48 hr post-exercise leaves the acute time course poorly characterized. A single 15-min post-exercise measurement may have missed the nadir or important early dynamics in adiponectin mobilization, while the 48-hr endpoint may be insufficient to determine whether levels had recovered, remained suppressed, or continued declining. This limits interpretation of whether changes reflect transient modulation or prolonged systemic effects. The authors should discuss the biological significance of timing and consider more granular sampling in future studies, particularly within the 6–24 hr recovery window.
5. The reported inverse correlations between CK and adiponectin changes, and between salivary adiponectin VAS scores and adiponectin changes in ETS2, are interpreted as evidence that metabolic stress drives adiponectin reduction. However, correlation indicates association, not causation. CK elevation and adiponectin reduction could be independent responses to the same stimulus, and the mechanistic pathway remains unclear. Without interventional data or more detailed biochemical measurements, these findings are suggestive rather than confirmatory. The authors should revise the language to reflect correlational evidence and acknowledge the need for mechanistic validation.
6. The reported dissociation between plasma and salivary adiponectin is described as reflecting “in vivo complexity” but receives minimal mechanistic discussion. Plasma levels declined while salivary levels remained unchanged, which could reflect local oral production, limited transudation from plasma, or assay sensitivity issues. The authors should discuss whether salivary adiponectin is a valid marker of systemic dynamics, cite relevant literature, and justify the choice of salivary versus plasma sampling. While currently regarded as a minor point, this finding has important implications for non-invasive monitoring strategies.

Author Response

Comment 1: The authors report a post-hoc statistical power of 0.73, below the 0.80 needed for 12 participants. This shortfall undermines confidence in the non-significant findings, particularly the lack of differences between the ETS1 and ETS2 protocols. With the current sample size, the study is underpowered to detect potentially meaningful biological differences between the TUT conditions. The authors should explicitly discuss which findings are most affected by insufficient power, whether key conclusions might change with adequate power, and whether results should be considered preliminary pending larger-scale validation. At minimum, null findings for between-protocol comparisons should be framed more cautiously.

Response 1: Thank you for raising this issue. We agree that the small sample size limits precision, particularly for ETS1 vs ETS2 contrasts. We revised the manuscript to frame non-significant between-protocol findings as inconclusive rather than evidence of equivalence and to present the results as preliminary.

The discussion has been revised acknowledging this point, as well as the statistics section of methods.

Location: Page 6, lines 217 – 235. Page 13, lines 410-423

Comment 2: The authors measure adiponectin and CK but infer metabolic stress responses without directly assessing primary metabolic stressors. The study does not quantify lactate, inflammatory cytokines (IL-6, IL-8, TNF-α), ROS, or oxidative stress markers, yet the central argument attributes adiponectin reductions to “metabolic stress.” Relying on CK alone is problematic, as it primarily indicates muscle membrane disruption rather than metabolic flux. The authors should either include lactate and inflammatory markers in future work, or temper mechanistic claims, presenting the findings as correlational rather than explanatory.

Response 2: We thank the reviewer for this important observation. We fully agree that the absence of measurements of primary metabolic stressors (e.g., lactate, inflammatory cytokines, oxidative stress markers) limits the interpretation of our findings.

We have now explicitly this limitation in the Discussion and expanded the Future Directions to highlight the need for studies integrating lactate, inflammatory cytokines (IL-6, IL-8, TNF-α), and oxidative stress markers to better characterize the metabolic and inflammatory milieu underlying adiponectin regulation following resistance exercise.

Location: Page 12, lines 428 – 430. Page 12, line 446-448

Comment 3: The study enrolled only males, yet adiponectin regulation is sex-dependent, influenced by estrogen and testosterone. Women typically have higher basal adiponectin, different inflammatory responses to exercise, and potentially distinct adipokine kinetics during recovery. As such, these findings may not generalize to women, who represent roughly half of resistance-training populations. The authors should acknowledge this as a key limitation and clarify whether the male-only sample was justified mechanistically or purely for practical reasons.

Response 3: We thank the reviewer for highlighting this important point. We agree with the reviewer; the inclusion of only male participants represents a limitation of our study. This aspect has now been addressed in the revised discussion.

The male-only sample was chosen for practical and methodological reasons, including the exploratory pilot nature of the study. However, we agree that these findings cannot be generalized to women, who may exhibit different basal adiponectin levels and recovery kinetics. We have therefore clarified that future studies should include sex-balanced cohorts or specifically address female populations to investigate sex-specific adiponectin responses to resistance exercise.

Location: Page 12, lines 444 – 450

Comment 4: Sampling at baseline, 15 min, 24 hr, and 48 hr post-exercise leaves the acute time course poorly characterized. A single 15-min post-exercise measurement may have missed the nadir or important early dynamics in adiponectin mobilization, while the 48-hr endpoint may be insufficient to determine whether levels had recovered, remained suppressed, or continued declining. This limits interpretation of whether changes reflect transient modulation or prolonged systemic effects. The authors should discuss the biological significance of timing and consider more granular sampling in future studies, particularly within the 6–24 hr recovery window.

Response 4: We thank the reviewer for this insightful comment. In the revised manuscript, we have expanded the Discussion to address the biological significance of sampling timing and to clarify that our findings describe a time-dependent pattern across the measured intervals rather than the complete acute adiponectin time course. We also emphasize that future studies should include more granular sampling, particularly within the 6–24 h recovery window, to better characterize adiponectin dynamics.

Location: Page 12, lines 442-444. Page 13, lines 448-450

Comment 5: The reported inverse correlations between CK and adiponectin changes, and between salivary adiponectin VAS scores and adiponectin changes in ETS2, are interpreted as evidence that metabolic stress drives adiponectin reduction. However, correlation indicates association, not causation. CK elevation and adiponectin reduction could be independent responses to the same stimulus, and the mechanistic pathway remains unclear. Without interventional data or more detailed biochemical measurements, these findings are suggestive rather than confirmatory. The authors should revise the language to reflect correlational evidence and acknowledge the need for mechanistic validation.

Response 5: We thank the reviewer for this important clarification. We fully agree that correlation does not imply causation and that the associations observed between CK, perceived soreness, and adiponectin changes should not be interpreted as evidence of a mechanistic link between muscle damage and adiponectin regulation.

In the revised manuscript, we have carefully re-evaluated the correlation analyses and corrected the text accordingly (see Reviewer 1, point 8). All statements implying a casual or mechanistic relationship have been removed, and the language has been revised to reflect that the reported findings are observational in nature. The manuscript now acknowledges that CK elevation and adiponectin reduction may represent parallel responses to exercise-induced stress rather than a direct cause-effect relationship, and that mechanistic validation will require targeted interventional approaches.

Comment 6: The reported dissociation between plasma and salivary adiponectin is described as reflecting “in vivo complexity” but receives minimal mechanistic discussion. Plasma levels declined while salivary levels remained unchanged, which could reflect local oral production, limited transudation from plasma, or assay sensitivity issues. The authors should discuss whether salivary adiponectin is a valid marker of systemic dynamics, cite relevant literature, and justify the choice of salivary versus plasma sampling. While currently regarded as a minor point, this finding has important implications for non-invasive monitoring strategies.

Response 6: We thank the reviewer for this helpful comment. We agree that the dissociation observed between plasma and salivary adiponectin warrants a more detailed discussion. In the revised manuscript, we have expanded the Discussion to address potential mechanisms underlying this finding, including local oral production, limited transudation of adiponectin from plasma to saliva, and the influence of assay sensitivity.

We also clarified that, based on the present data, salivary adiponectin does not appear to reliably reflect systemic adiponectin dynamics following resistance exercise. Literature has been added to contextualize the use of salivary adiponectin as a non-invasive biomarker, and the rationale for including salivary sampling has been more clearly justified.

Location: Page 1, line 39-42. Page 12, lines 401-405

Reviewer 4 Report

Comments and Suggestions for Authors

This study investigates the acute effects of two resistance-exercise protocols, differing only in TUT, on circulating adiponectin and CK in trained young men. The authors report a transient, time-dependent reduction in plasma adiponectin, specifically its HMWs, 24–48 h post-exercise, independent of TUT modality, and document an inverse correlation with CK. Salivary adiponectin remained unchanged. The authors conclude that the decline reflects acute metabolic stress and subsequent recovery rather than mechanical load per se. The work provides a useful temporal profile of adiponectin oligomers after resistance exercise, but mechanistic insight is limited and several analytical gaps remain.

Comment 1
The mechanistic inference is constrained by the absence of upstream or downstream inflammatory and metabolic signals. 

Comment 2
Without a time-matched resting control, the reported decline in adiponectin cannot be dissociated from circadian phase, acute negative energy balance, or inter-individual glycaemic variability. A non-exercise control day, mirrored for diet and sampling interval, is essential to attribute the observed effect specifically to contractile activity.

Comment 3

Fig 4. The WB module lacks loading integrity and quantitative transparency. Densitometry should be normalized to a total-protein stain run on the same membrane. Alternatively, a plasma-validated housekeeping protein must be demonstrated. Crucially, report the exact n number of independent blots and provide the corresponding quantitative dataset to substantiate the oligomer-specific changes.

Author Response

Comment 1: The mechanistic inference is constrained by the absence of upstream or downstream inflammatory and metabolic signals. 

Response 1: We agree with the reviewer that mechanistic inference is limited by the absence of direct measurements of upstream and downstream inflammatory and metabolic signals. As clarified in the revised manuscript, the present study was designed as an exploratory pilot investigation, and the observed associations should therefore be interpreted as correlational rather than mechanistic. We added this limitation in the Discussion and highlighted the need for future studies integrating inflammatory and metabolic markers.

Location: Page 12, lines 444-450

Comment 2: Without a time-matched resting control, the reported decline in adiponectin cannot be dissociated from circadian phase, acute negative energy balance, or inter-individual glycemic variability. A non-exercise control day, mirrored for diet and sampling interval, is essential to attribute the observed effect specifically to contractile activity.

Response 2: The authors acknowledge the validity of the reviewer’s concern regarding the absence of a time-matched resting control. Consequently, the authors have revised the "Limitations" to explicitly state the lack of time-matched resting controls as a constraint of the study.

Location: Page 12, lines 430-433

Comment 3: Fig 4. The WB module lacks loading integrity and quantitative transparency. Densitometry should be normalized to a total-protein stain run on the same membrane. Alternatively, a plasma-validated housekeeping protein must be demonstrated. Crucially, report the exact n number of independent blots and provide the corresponding quantitative dataset to substantiate the oligomer-specific changes.

Response 3: We agree with the reviewer comment that an internal control would be helpful, but unfortunately, the serum does not contain "housekeeping proteins". Indeed, an appropriate loading control is critical for Western blot analysis. We performed a kind of “normalization” loading equal amounts of total serum and salivary proteins whose concentration was determined in triplicate by Bradford’s assay. In addition, western blotting analysis on each sample was performed three times in triplicate, and the results were averaged for all samples to analyze and compare the data. Furthermore, all samples of sera and saliva have been treated and stored in the same conditions.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have tried to solve the previous concern, and the article is recommended for publication after careful proof check. 

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have significantly revised and improved their manuscript.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have made substantial revisions that address all of my earlier concerns. The study is now appropriately presented as preliminary work, with its limitations clearly acknowledged and future directions well articulated. I look forward to seeing it published.

 

Reviewer 4 Report

Comments and Suggestions for Authors

The authors have satisfactorily addressed all my questions, and I have no more comments.