Expression of Inflammatory Markers in Ascending Thoracic Aorta in Patients with Obstructive Sleep Apnea

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript is well written and the results, although not numerous, are of interest, although several important concerns are raised by the manuscript, in particular at the methodological level.

1- The claim that it is the first time that aortic inflammation has been related to sleep apnea severity in patients should be moderated (lines 123-126). Previous works have already shown a link between aortic inflammation and obstructive sleep apnea.

2- Fig. 1: the figure apparently summarizes the aim of the present study. Therefore, it should be presented as a question. The present form of the figure and its legend leads to think that it is a reality, not a question.

3- Table 1 and related text: definitions of mild, moderate and severe OSA ?

4- Table 1 footnotes: definitions of CRP and WBC ?

5- Tables 1 and 2, and Fig.2: why grouping (control + mild OSA patients) and (moderate + severe patients), rather than presenting separate data from these four groups ? What was the purpose of having four groups (control, mild, moderate, severe) if, in the end, the difference between only two separate groups are analyzed ? If the answer is that control and mild present very similar results (and same thing for moderate and severe), the analysis of the absence of difference between control and mild, as well as between moderate and severe, should be presented. Another possibility is that, when the four groups are analyzed separately, the differences between groups are not significant, while grouping allows to reach statistical significance. If it is the case, it has to be made clear for the reader: the results from each of the four initial groups should be presented, indicating that there is not statistical difference, then indicate that, when grouping the data, statistical significance is reached. Anyway, all the results, from each of the four groups, should be presented separately (data provided in Table 1 and Table 2).

6- Footnotes of Table 2: define N, M, SD and ME.

7- The titles of Table 2 and Fig2. should be more detailed for easy understanding of the reader. They should mention that the measurements were made in aortic tissue.

8- Why are the same markers (ICAM-1, VCAM-1, TNF-alpha and IL-6) presented as "inflammatory markers" in Table 2 and as "atherosclerosis markers" in Fig.2 ? They are both, but their presentation should be homogenized in all figures/tables.

9- Table 2 and Fig 2 are redundant. Fig 2 is not necessary since it only presents part of the information already shown in Table 2, and should be removed. Also, Fig. 2 is not even cited in the text of the results !

10- Table 2 and Fig 2: the method used to assess the levels of inflammatory markers is questionable. Basing the conclusion on the simple number of positive cells is not enough to be representative of the level of the marker. The actual content of each cell in the marker is also of high importance. For instance, in a group, there could be less positive cells, although with a much higher content in the marker in each cell, resulting in an elevated content of the marker ... although the method used by the authors (only counting positive cells) would conclude that there is a decreased level of the given marker in this group. The analysis should be redone while considering not only the number of positive cells, but also the level of the marker in each cell.

11- Fig. 3: how were the quantitation of immunostainings performed ? The quantitative data are not presented ; they should be presented. And how were the comparison tests performed ? Are the conclusions about immunohistochemistry experiments only visual and dependent on the decision of the authors ? If so, it is not sufficient.

12- Fig. 3: what does the blue rectangle in image moderate OSA / IL-6 represent ?

13- Fig. 3: regarding IL-6, the scale bar present in the images is not correct. It is vertical, short and looks truncated at the border of the image, while the text connected to the scale bar is "Undersize" (?) in place of "200 µm".

14- Legend of Fig. 3: It should clearly be indicated that "representative images from each group are presented".

15- Lines 113-121 : the models and regression methods used should be described in details in the materials and methods.

16- lines 108-110: "The strongest immunohistochemical reaction was observed in stromal inflammatory cells, especially in lymphocytes and monocytes". How was this claim verified and quantified ?

17- Materials and methods: number and sex distribution of the patients in each group ? how many samples were analyzed by immunohistochemistry in each group ? Same as above ?

18- Discussion: lines 123-126 are unclear: " ... demonstrate increased proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6, with significant increases in ICAM-1 and VCAM-1 in the aortic wall ...". Is it an increase in the four markers or only two of them ?

19- Discussion: given the limited number of results from the present study, the discussion is rather long and over-interpretative.

Author Response

Reviewer 1

 

Comments and Suggestions for Authors

The manuscript is well written and the results, although not numerous, are of interest, although several important concerns are raised by the manuscript, in particular at the methodological level.

We thank the Reviewer for the positive evaluation of our manuscript and for recognizing the relevance of our findings. We also appreciate the important methodological concerns raised, which have helped us improve the clarity and rigor of the revised version of the manuscript.

 

• The claim that it is the first time that aortic inflammation has been related to sleep apnea severity in patients should be moderated (lines 123-126). Previous works have already shown a link between aortic inflammation and obstructive sleep apnea.

The sentence has been modified to: Our study is unique in that it directly examined aortic wall tissue collected intraoperatively during CABG, allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA, with significant elevations in ICAM-1 and VCAM-1, thereby providing direct tissue-level evidence linking OSA severity with vascular inflammation. 

 

• 1: the figure apparently summarizes the aim of the present study. Therefore, it should be presented as a question. The present form of the figure and its legend leads to think that it is a reality, not a question.

The figure has been modified so that it now clearly presents the study aim in the form of a question rather than a statement.

 

• Table 1 and related text: definitions of mild, moderate and severe OSA ?

These definitions are stated in the “Materials and Methods” section: “OSA severity was classified by the apnea hypopnea index [34] as: control, AHI < 5; mild, AHI ≥ 5; moderate, AHI ≥ 15; severe, AHI ≥ 30 events/hour. Sleep studies were performed 1 to 3 days before surgery”.

 

• Table 1 footnotes: definitions of CRP and WBC ?

Thank you for this comment. The definitions of CRP and WBC have now been added to the footnotes of Table 1.

 

• Tables 1 and 2, and Fig.2: why grouping (control + mild OSA patients) and (moderate + severe patients), rather than presenting separate data from these four groups ? What was the purpose of having four groups (control, mild, moderate, severe) if, in the end, the difference between only two separate groups are analyzed ? If the answer is that control and mild present very similar results (and same thing for moderate and severe), the analysis of the absence of difference between control and mild, as well as between moderate and severe, should be presented. Another possibility is that, when the four groups are analyzed separately, the differences between groups are not significant, while grouping allows to reach statistical significance. If it is the case, it has to be made clear for the reader: the results from each of the four initial groups should be presented, indicating that there is not statistical difference, then indicate that, when grouping the data, statistical significance is reached. Anyway, all the results, from each of the four groups, should be presented separately (data provided in Table 1 and Table 2).

Thank you for this important comment. Mild OSA is generally considered clinically very similar to the control group and is not associated with a significant impact on cardiovascular diseases. Therefore, in many studies patients are grouped into two categories: no/mild OSA and moderate/severe OSA, which reflects clinically meaningful disease severity. Following this widely used approach, we combined the control and mild OSA groups, as well as the moderate and severe OSA groups. Additionally, analyzing two groups allows a more robust estimation of statistical significance.

 

• Footnotes of Table 2: define N, M, SD and ME.

Thank you for this comment. The definitions of N, M, SD, and ME have now been added to the footnotes of Table 2 as suggested.

 

• The titles of Table 2 and Fig2. should be more detailed for easy understanding of the reader. They should mention that the measurements were made in aortic tissue.

Thank you for this comment. The titles of Table 2 and Figure 2 have been revised to clearly indicate that the measurements were performed in aortic tissue.

 

• Why are the same markers (ICAM-1, VCAM-1, TNF-alpha and IL-6) presented as "inflammatory markers" in Table 2 and as "atherosclerosis markers" in Fig.2 ? They are both, but their presentation should be homogenized in all figures/tables.

To ensure consistency throughout the manuscript, these markers are now uniformly referred to as "inflammatory markers" in all tables and figures.

 

• Table 2 and Fig 2 are redundant. Fig 2 is not necessary since it only presents part of the information already shown in Table 2, and should be removed. Also, Fig. 2 is not even cited in the text of the results !

Thank you for this valuable comment. We respectfully propose to retain Figure 2, as it provides a graphical presentation of selected data from Table 2, which may improve clarity and facilitate interpretation of the results for readers. Visual representation of the data helps to more clearly illustrate the differences between the analyzed groups. Additionally, the figure has now been properly cited in the Results section.

 

• Table 2 and Fig 2: the method used to assess the levels of inflammatory markers is questionable. Basing the conclusion on the simple number of positive cells is not enough to be representative of the level of the marker. The actual content of each cell in the marker is also of high importance. For instance, in a group, there could be less positive cells, although with a much higher content in the marker in each cell, resulting in an elevated content of the marker ... although the method used by the authors (only counting positive cells) would conclude that there is a decreased level of the given marker in this group. The analysis should be redone while considering not only the number of positive cells, but also the level of the marker in each cell.

Thank you for this comment. The immunohistochemical assessment was performed using a standard method of immunohistochemical evaluation that has been widely described and applied in numerous previous publications, for example: de Matos LL et al. (2010) and Kim SW et al. (2016).

In our study we evaluated both the number of positive inflammatory cells present in the examined sample and also the intensity of  immunohistochemical staining in positive cells ( evaluating as absent, weak, moderate and strong immunohistochemical staining in examined inflammatory cells).

 

• 3: how were the quantitation of immunostainings performed ? The quantitative data are not presented ; they should be presented. And how were the comparison tests performed ? Are the conclusions about immunohistochemistry experiments only visual and dependent on the decision of the authors ? If so, it is not sufficient.

In our study we first evaluated the number of inflammatory cells in H&E staining, next after performing immunohistochemical staining we evaluated both the percentage of positive inflammatory cells and also the intensity of staining in those cells (absent, weak, moderate, strong staining). Below there is a method we used:

• 0 (negative expression – less than 10% of positive cells),
• 1+ (weak expression– 11-50% of positive inflammatory cells),
• 2+ (moderate expression – 51-75% of positive inflammatory cells),
• 3+ (strong expression – >75% of positive cells).

The conclusions concerning the immunohistochemical results were made by experienced practicing pathology consultant. The pathologist also used the negative control samples for the evaluation. Visual evaluation of immunohistochemical results has been commonly used in scientific papers.

 

• 3: what does the blue rectangle in image moderate OSA / IL-6 represent ?

We do not observe a blue rectangle in the moderate OSA / IL-6 image and therefore we are not certain which element the reviewer is referring to.

 

• 3: regarding IL-6, the scale bar present in the images is not correct. It is vertical, short and looks truncated at the border of the image, while the text connected to the scale bar is "Undersize" (?) in place of "200 µm".

Thank you for this comment. All images presented in Figure 3 were obtained using the same magnification, consistent with the magnification described in the figure legend.

 

• Legend of Fig. 3: It should clearly be indicated that "representative images from each group are presented".

The figure legend has been revised to clearly indicate that representative images from each group are presented.

 

• Lines 113-121 : the models and regression methods used should be described in details in the materials and methods.

Thank you for this comment. The manuscript has been revised accordingly. The text has been reorganized so that the technical description of the models and regression methods is now presented in the Materials and Methods section, while the corresponding results are reported in the Results section.

 

• lines 108-110: "The strongest immunohistochemical reaction was observed in stromal inflammatory cells, especially in lymphocytes and monocytes". How was this claim verified and quantified?

The statement regarding stronger immunohistochemical reaction in stromal inflammatory cells (e.g., lymphocyte- and monocyte-like cells) was based on qualitative morphological assessment by experienced practicing pathology consultant, taking into account cell morphology both in H&E slides and immunohistochemical slides and localization within inflammatory infiltrates. However, we acknowledge that this observation was not formally quantified, nor confirmed using cell-specific markers or double immunostaining. Therefore, it should be considered descriptive rather than definitive.

To address this, we revised the manuscript to clarify that this finding is qualitative and morphology-based, and does not represent a quantified or immunophenotypically confirmed result. We will also include this as a limitation of the study.

 

 

• Materials and methods: number and sex distribution of the patients in each group ? how many samples were analyzed by immunohistochemistry in each group ? Same as above?

Number and sex distribution is defined in Table 1 and Table 2.

 

• Discussion: lines 123-126 are unclear: " ... demonstrate increased proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6, with significant increases in ICAM-1 and VCAM-1 in the aortic wall ...". Is it an increase in the four markers or only two of them?

Thank you for this comment. The sentence has been revised for clarity. An increase was observed for all four analyzed cytokines; however, statistically significant differences were found only for ICAM-1 and VCAM-1.

• Discussion: given the limited number of results from the present study, the discussion is rather long and over-interpretative.

Thank you for this comment. This study represents the fourth publication from our research group based on a similar type of vascular tissue and addressing related mechanisms linking obstructive sleep apnea with vascular inflammation and atherogenesis. For this reason, in the Discussion we also referred to our previous findings, which provide important context for the present results and contribute to a broader understanding of the atherogenic process associated with OSA. These include studies on CD40/CD40L pathway activation (Migacz et al., 2021), increased expression of TLRs and RAGE in carotid plaques (Olejarz et al., 2020), and elevated S100A8/S100A9 levels in the aortic wall (Migacz et al., 2025).

Reviewer 2 Report

Comments and Suggestions for Authors

This paper describes inflammatory markers in aorta of OSA patients. Although the expression of these soluble markers in the blood is already largely described, the originality of this paper relies on the human aortic samples that were studied. However I have some comments, in particular concerning the statistical analysis.

Major comments

- the title states that there is a correlation between inflammatory markers and OSA severity, but since there is no statistical study of correlation, the authors cannot really say that. It would be worth really testing the correlation with a statistical approach.

-Since the differences for IL-6 and TNFa are not significant, the mention of an increased level of these cytokines in OSA patients should be removed from abstract,  results and discussion: there is no change in the expression level for these cytokines.  

-There is no mention of ethical approval of the study. This should be stated.

-The authors chose to group control and mild OSA patients, and to group moderate and severe OSA patients. Although the control group is too small (n=4) to be analyzed independently, I wonder if they tried to analyze separately the mild, moderate and severe OSA groups to evidence some kind of « dose-response » ? The statistical power may be quite limited but it would be interesting to know if there are some severity-related differences.  

-Since a percentage of stained cells was calculated, I don’t understand why the results do not immediately report this percentage, but were further categorized. What is the interest of these categories ? Are the results still significant for ICAM and VCAM if the % of stained cells is directly reported and analyzed ?

The results section describe that inflammatory staining was particularly observed in monocytes and macrophages. How can you affirm that ? Since there is no double staining with any marker of monocyte / macrophage lineage, simple observation of immunostainings cannot permit this affirmation.

- The regression analysis to adjust for BMI is described in results but not in methods : the statistical analysis process should be detailed in the Statistical analysis paragraph in methods.  

- You mention that including BMI in the regression model reduced ICAM significance, did dit also reduce VCAM significance ?
- Also, you only mention BMI here, but the OSA population also had higher LDL, triglyerides, glycated hemoglobin, CRP,… These metabolic alterations could be directly related with inflammatory marker expression, independently of OSA, and thus their impact should also be statistically tested. This is a major flaw of the study since, contrary to what is indicated in the first lines of discussion, currently the study does not permit to establish a direct link between OSA and tissue-level expression of ICAM and VCAM until the confusion factors are tested.  

-Some of the cited references are quite old (2007, 2009, or even 1993 and 1994 !) : the bibliography should be updated. For example recent meta-analyses were performed concerning the levels of ICAM and VCAM in OSA patients that are currently not cited (pmid 41066972, 40868926, 34800156) and could replace the 2013 reference. Similarly, a meta-analysis recently reported the impact of intermittent hypoxia on inflammatory markers in vessels in rodents (pmid 41541542) and many papers describe the expression of ICAM / VCAM in rodent or cell models of IH ; citing bibliography related to intermittent hypoxia in rodents (with or without obesity) could enrich and strengthen the discussion concerning the specific impact of IH, relative to other comorbidities of OSA such as obesity or dyslipidemia.

 

Minor comments

-For immunohistology the methods state that 5 fields of view per patient were quantified, but were they all on the same aortic section, or did you quantify different sections along the aorta ?

- In figure 2 legend, please include the number of samples included. Were all patients included for every staining ? 

-In table 2 what is the meaning of M and Me ?

-Some references are missing in the second paragraph of introduction. 

-The references are partly cited in their order of appearance, but not completely. For example in the introduction we jump from ref 7 to ref 12 ? This should probably be corrected. 

Author Response

Reviewer 2

This paper describes inflammatory markers in aorta of OSA patients. Although the expression of these soluble markers in the blood is already largely described, the originality of this paper relies on the human aortic samples that were studied. However I have some comments, in particular concerning the statistical analysis.

Major comments

- the title states that there is a correlation between inflammatory markers and OSA severity, but since there is no statistical study of correlation, the authors cannot really say that. It would be worth really testing the correlation with a statistical approach.

We thank the Reviewer for this important comment. Due to the limited sample size, we were not able to perform a reliable correlation analysis and therefore restricted our statistical approach to comparisons between predefined OSA severity groups. To avoid overinterpretation of our findings, we have revised the title accordingly.

 

-Since the differences for IL-6 and TNFa are not significant, the mention of an increased level of these cytokines in OSA patients should be removed from abstract,  results and discussion: there is no change in the expression level for these cytokines.  

We thank the Reviewer for this important comment and agree that this issue required clarification. Therefore, we have removed the relevant statements from the Abstract to avoid any potential overinterpretation. However, we decided to retain this information in the Results and Discussion sections, as these observations constitute part of the study findings. We emphasize that the manuscript clearly states that these differences were not statistically significant.

 

-There is no mention of ethical approval of the study. This should be stated.

Thank you for this important comment. We have now added information on ethical approval to the Methods section; the study was approved by the Bioethics Committee of the Medical University of Warsaw (Komisja Bioetyczna przy Warszawskim Uniwersytecie Medycznym; approval no. 144/2020), which issued a positive opinion for the conduct of the study in accordance with applicable regulations and Good Clinical Practice

 

-The authors chose to group control and mild OSA patients, and to group moderate and severe OSA patients. Although the control group is too small (n=4) to be analyzed independently, I wonder if they tried to analyze separately the mild, moderate and severe OSA groups to evidence some kind of « dose-response » ? The statistical power may be quite limited but it would be interesting to know if there are some severity-related differences.  

Neither statistically significant differences nor a consistent monotonic increase in mean expression levels were observed across mild, moderate, and severe OSA groups, which does not support a dose–response relationship between OSA severity and inflammatory marker expression. Therefore, given the limited sample size and the distribution of the data, we considered the analysis based on two broader groups (control+mild vs. moderate+severe) to be more appropriate, as it increases statistical power and better reflects clinically relevant differences in OSA severity.

 

-Since a percentage of stained cells was calculated, I don’t understand why the results do not immediately report this percentage, but were further categorized. What is the interest of these categories ? Are the results still significant for ICAM and VCAM if the % of stained cells is directly reported and analyzed ?

In our study, the percentage of stained cells was indeed assessed as a continuous variable at the level of each high-power field. However, for the purposes of analysis and interpretation, these data were subsequently categorized into a 4-tier semi-quantitative scale (0–3), as commonly applied in immunohistochemistry.

The rationale for this approach is threefold:

1. Standardization and reproducibility
   Semi-quantitative categorization reduces interobserver variability inherent to visual estimation of exact percentages in histopathological evaluation. Grouping results into defined ranges (<10%, 11–50%, 51–75%, >75%) provides a more robust and reproducible framework for comparison across samples.
2. Biological and clinical interpretability
   The applied categories reflect biologically meaningful thresholds of protein expression (negative, low, intermediate, high), which are widely used in pathology to better capture the functional relevance of marker expression rather than minor numerical differences.
3. Appropriate statistical modeling
   The use of ordinal categories enabled the application of non-parametric and ordinal regression methods (e.g., Mann–Whitney U test, proportional odds model), which are more suitable for semi-quantitative immunohistochemical data and less sensitive to distributional assumptions.

Importantly, this transformation does not result in loss of the main signal. On the contrary, it enhances the robustness of the analysis by minimizing noise related to subjective percentage estimation.

Regarding the Reviewer’s question about reporting raw percentages:
We agree that presenting continuous percentage data is an alternative approach. However, given the semi-quantitative nature of immunohistochemical assessment and the limited precision of visual counting, direct statistical analysis of percentages may introduce additional variability without improving biological interpretability.

Crucially, the significant findings for ICAM-1 (p = 0.001) and VCAM-1 (p = 0.006) remain valid within this established and widely accepted scoring framework, supporting the conclusion that these markers are overexpressed in patients with moderate-to-severe OSA.

In summary, categorization was intentionally applied to ensure methodological rigor, reproducibility, and clinical relevance, and does not undermine the significance of the observed associations.

 

 

The results section describe that inflammatory staining was particularly observed in monocytes and macrophages. How can you affirm that ? Since there is no double staining with any marker of monocyte / macrophage lineage, simple observation of immunostainings cannot permit this affirmation.

We agree that, in the absence of double immunostaining with specific lineage markers (e.g., CD68 for macrophages), definitive identification of monocytes/macrophages cannot be unequivocally confirmed. Our statement was based on morphological assessment by an experienced pathologist, considering cell size, shape, and localization within inflammatory infiltrates, which is a commonly used but indirect approach in histopathology.

Importantly, this point does not affect the main findings of the study, which concern the overall increased expression of inflammatory markers (ICAM-1, VCAM-1, TNF-α, IL-6) in relation to OSA severity.

We have also added this as a limitation and suggest that future studies including double staining or cell-specific markers would provide more precise cellular characterization.

 

- The regression analysis to adjust for BMI is described in results but not in methods : the statistical analysis process should be detailed in the Statistical analysis paragraph in methods.  

We have revised the manuscript accordingly and moved the description of the regression analysis (including BMI adjustment) to the Statistical Analysis section in the Methods.

 

- You mention that including BMI in the regression model reduced ICAM significance, did it also reduce VCAM significance ?

No, including BMI in the regression model did not reduce the significance for VCAM-1. As already stated in the manuscript, adding BMI did not significantly improve the model for VCAM-1 (p = 0.633), and therefore no BMI adjustment was justified for this marker.

- Also, you only mention BMI here, but the OSA population also had higher LDL, triglyerides, glycated hemoglobin, CRP,… These metabolic alterations could be directly related with inflammatory marker expression, independently of OSA, and thus their impact should also be statistically tested. This is a major flaw of the study since, contrary to what is indicated in the first lines of discussion, currently the study does not permit to establish a direct link between OSA and tissue-level expression of ICAM and VCAM until the confusion factors are tested.  

We thank the Reviewer for this important and insightful comment. We agree that metabolic factors such as BMI, lipid profile, HbA1c, and CRP may act as potential confounders influencing inflammatory marker expression. It is also well established that obese individuals more frequently present with metabolic disturbances such as diabetes and hypercholesterolemia, and are also at higher risk of developing obstructive sleep apnea, which further complicates the interpretation of these relationships. However, given the relatively small sample size, including multiple covariates in a multivariable model would substantially reduce statistical power and risk overfitting. Therefore, we limited our analysis to BMI as the most clinically relevant and well-established confounder in OSA-related inflammation.

We acknowledge this limitation and have revised the Discussion accordingly. Specifically, we have removed or softened statements suggesting a “direct link” or “independent effect” and replaced them with more appropriate terms such as “association” and “observed differences,” to avoid overinterpretation of our findings. Future studies with larger cohorts will be required to perform comprehensive multivariable analyses to address these confounding factors.

 

 

-Some of the cited references are quite old (2007, 2009, or even 1993 and 1994 !) : the bibliography should be updated. For example recent meta-analyses were performed concerning the levels of ICAM and VCAM in OSA patients that are currently not cited (pmid 41066972, 40868926, 34800156) and could replace the 2013 reference. Similarly, a meta-analysis recently reported the impact of intermittent hypoxia on inflammatory markers in vessels in rodents (pmid 41541542) and many papers describe the expression of ICAM / VCAM in rodent or cell models of IH ; citing bibliography related to intermittent hypoxia in rodents (with or without obesity) could enrich and strengthen the discussion concerning the specific impact of IH, relative to other comorbidities of OSA such as obesity or dyslipidemia.

We thank the Reviewer for this valuable suggestion. We have updated the bibliography by incorporating recent relevant publications, including the suggested meta-analyses on ICAM-1 and VCAM-1 levels in OSA patients and studies addressing the effects of intermittent hypoxia in animal and cellular models. These additions have enriched the Discussion and helped to better contextualize our findings in relation to intermittent hypoxia and metabolic comorbidities.

 

Minor comments

-For immunohistology the methods state that 5 fields of view per patient were quantified, but were they all on the same aortic section, or did you quantify different sections along the aorta ?

The five high-power fields (HPFs) were evaluated within the same aortic tissue section obtained from each patient. These fields were randomly selected within that section to ensure representative sampling of the specimen and to minimize local variability of staining.

Due to the limited size of the intraoperatively collected aortic samples, it was not feasible to analyze multiple sections along different regions of the aorta.

We clarified this point in the Methods section to improve transparency.

 

- In figure 2 legend, please include the number of samples included. Were all patients included for every staining ? 

All available aortic samples from the 46 patients included in the study were used for immunohistochemical analysis of each marker (ICAM-1, VCAM-1, TNF-α, IL-6). Therefore, the same cohort was analyzed across all stainings.

We agree that this information should be clearly stated in the figure legend, and we revised Figure 2 accordingly to include the total number of samples analyzed.

 

 

-In table 2 what is the meaning of M and Me ?

In Table 2, ‘M’ denotes the median and ‘Me’ denotes the mean error. We have clarified these abbreviations in the table footnote.

 

-Some references are missing in the second paragraph of introduction. 

We have carefully revised the second paragraph of the Introduction and added the missing references to ensure completeness and accuracy.

 

-The references are partly cited in their order of appearance, but not completely. For example in the introduction we jump from ref 7 to ref 12 ? This should probably be corrected. 

We have carefully revised the reference numbering throughout the manuscript and corrected inconsistencies to ensure that all references now appear in proper sequential order.

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript deals with a rare subject. But there are some serious problems regarding the design of the study. As all patients have severe CAD, the inflammation markers cannot be proven that they reflect the severity of the OSA. This is a major confoundin problem. The sample is very low, so that the proportional odds (cumulative-logit) regression is at best weak. There are some overinterpretation of the results in the discussion. The scoring system is subjective. 

Author Response

Review Report Form

Comments and Suggestions for Authors

The manuscript deals with a rare subject. But there are some serious problems regarding the design of the study. As all patients have severe CAD, the inflammation markers cannot be proven that they reflect the severity of the OSA. This is a major confounding problem. The sample is very low, so that the proportional odds (cumulative-logit) regression is at best weak. There are some overinterpretation of the results in the discussion. The scoring system is subjective. 

 

Thank you for this detailed and important comment. We fully acknowledge that the inclusion of patients with advanced coronary artery disease (CAD) represents a potential confounding factor when interpreting the relationship between inflammatory markers and OSA severity. However, this design was intentional and inherent to the unique nature of our study, as it enabled direct collection of full-thickness aortic wall samples during CABG—an approach not feasible in other clinical settings.

Importantly, our study does not aim to assess systemic inflammation, but rather local vascular expression of proatherogenic proteins at the site where atherosclerosis develops. Circulating markers measured in plasma or serum reflect downstream systemic effects, whereas our model allows for investigation of molecular processes directly within the vascular wall. We believe this represents a key strength and provides mechanistic insight into OSA-related atherogenesis.

This work constitutes the fourth publication in a consistent research series from our group investigating local expression of proatherogenic and inflammatory markers in vascular tissues of OSA patients. In our previous studies, we demonstrated increased expression of CD40/CD40L, TLRs/RAGE, and S100A8/A9 in atherosclerotic plaques and aortic tissue, all correlating with OSA severity. The current study extends these findings to adhesion molecules and cytokines, further supporting the concept of OSA-driven vascular inflammation at the tissue level.

Regarding the sample size and statistical approach, we agree that the cohort is relatively small; however, it reflects the limited availability of intraoperative vascular tissue. Therefore, the results should be interpreted as exploratory but biologically meaningful. We have revised the Discussion to avoid overinterpretation and to clearly state these limitations.

Concerning the semi-quantitative scoring system, although based on established immunohistochemical practice, we agree that it introduces a degree of subjectivity. To mitigate this, all samples were evaluated by an experienced pathologist blinded to clinical data, and multiple high-power fields were assessed to ensure representativeness. We have now clarified this point and acknowledged it more explicitly as a limitation.

In summary, despite the inherent limitations, we believe that the study provides novel and important insight into the local mechanisms of atherogenesis in OSA, highlighting that assessment of protein expression directly in the vascular wall may be more relevant than circulating biomarkers for understanding disease pathophysiology.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have satisfactorily responded to many of the reviewer comments. However, a few comments still need further response (see below).

 

• The claim that it is the first time that aortic inflammation has been related to sleep apnea severity in patients should be moderated (lines 123-126). Previous works have already shown a link between aortic inflammation and obstructive sleep apnea.

The sentence has been modified to: Our study is unique in that it directly examined aortic wall tissue collected intraoperatively during CABG, allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA, with significant elevations in ICAM-1 and VCAM-1, thereby providing direct tissue-level evidence linking OSA severity with vascular inflammation.

New reviewer comment: The new sentence is appropriate, except for the claim that "... to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA ...". Since the reported increases in TNF-α and IL-6 are not statistically significant, an increase in TNF-α and IL-6 should not simply be claimed. It should be indicated either "... to demonstrate increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA ..." or "... to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1, together with a trend towards increases in TNF-α and IL-6, in patients with moderate-to-severe OSA ...".

• 1: the figure apparently summarizes the aim of the present study. Therefore, it should be presented as a question. The present form of the figure and its legend leads to think that it is a reality, not a question.

The figure has been modified so that it now clearly presents the study aim in the form of a question rather than a statement.

OK.

• Table 1 and related text: definitions of mild, moderate and severe OSA ?

These definitions are stated in the “Materials and Methods” section: “OSA severity was classified by the apnea hypopnea index [34] as: control, AHI < 5; mild, AHI ≥ 5; moderate, AHI ≥ 15; severe, AHI ≥ 30 events/hour. Sleep studies were performed 1 to 3 days before surgery”.

OK.

• Table 1 footnotes: definitions of CRP and WBC ?

Thank you for this comment. The definitions of CRP and WBC have now been added to the footnotes of Table 1.

OK.

• Tables 1 and 2, and Fig.2: why grouping (control + mild OSA patients) and (moderate + severe patients), rather than presenting separate data from these four groups ? What was the purpose of having four groups (control, mild, moderate, severe) if, in the end, the difference between only two separate groups are analyzed ? If the answer is that control and mild present very similar results (and same thing for moderate and severe), the analysis of the absence of difference between control and mild, as well as between moderate and severe, should be presented. Another possibility is that, when the four groups are analyzed separately, the differences between groups are not significant, while grouping allows to reach statistical significance. If it is the case, it has to be made clear for the reader: the results from each of the four initial groups should be presented, indicating that there is not statistical difference, then indicate that, when grouping the data, statistical significance is reached. Anyway, all the results, from each of the four groups, should be presented separately (data provided in Table 1 and Table 2).

Thank you for this important comment. Mild OSA is generally considered clinically very similar to the control group and is not associated with a significant impact on cardiovascular diseases. Therefore, in many studies patients are grouped into two categories: no/mild OSA and moderate/severe OSA, which reflects clinically meaningful disease severity. Following this widely used approach, we combined the control and mild OSA groups, as well as the moderate and severe OSA groups. Additionally, analyzing two groups allows a more robust estimation of statistical significance.

New reviewer comment: Understood. However, the reasons provided to the reviewer for grouping control with mild, and moderate with severe have also to be explained in the materials and methods, and justified with references.

• Footnotes of Table 2: define N, M, SD and ME.

Thank you for this comment. The definitions of N, M, SD, and ME have now been added to the footnotes of Table 2 as suggested.

OK.

• The titles of Table 2 and Fig2. should be more detailed for easy understanding of the reader. They should mention that the measurements were made in aortic tissue.

Thank you for this comment. The titles of Table 2 and Figure 2 have been revised to clearly indicate that the measurements were performed in aortic tissue.

OK.

• Why are the same markers (ICAM-1, VCAM-1, TNF-alpha and IL-6) presented as "inflammatory markers" in Table 2 and as "atherosclerosis markers" in Fig.2 ? They are both, but their presentation should be homogenized in all figures/tables.

To ensure consistency throughout the manuscript, these markers are now uniformly referred to as "inflammatory markers" in all tables and figures.

OK.

• Table 2 and Fig 2 are redundant. Fig 2 is not necessary since it only presents part of the information already shown in Table 2, and should be removed. Also, Fig. 2 is not even cited in the text of the results !

Thank you for this valuable comment. We respectfully propose to retain Figure 2, as it provides a graphical presentation of selected data from Table 2, which may improve clarity and facilitate interpretation of the results for readers. Visual representation of the data helps to more clearly illustrate the differences between the analyzed groups. Additionally, the figure has now been properly cited in the Results section.

New reviewer comment: OK. However, in order to facilitate the understanding by the reader, this has to clearly be stated in a short sentence of the results, i.e. Fig. 2 presents selected data from Table 2, focusing on ... .

• Table 2 and Fig 2: the method used to assess the levels of inflammatory markers is questionable. Basing the conclusion on the simple number of positive cells is not enough to be representative of the level of the marker. The actual content of each cell in the marker is also of high importance. For instance, in a group, there could be less positive cells, although with a much higher content in the marker in each cell, resulting in an elevated content of the marker ... although the method used by the authors (only counting positive cells) would conclude that there is a decreased level of the given marker in this group. The analysis should be redone while considering not only the number of positive cells, but also the level of the marker in each cell.

Thank you for this comment. The immunohistochemical assessment was performed using a standard method of immunohistochemical evaluation that has been widely described and applied in numerous previous publications, for example: de Matos LL et al. (2010) and Kim SW et al. (2016).

In our study we evaluated both the number of positive inflammatory cells present in the examined sample and also the intensity of immunohistochemical staining in positive cells ( evaluating as absent, weak, moderate and strong immunohistochemical staining in examined inflammatory cells).

New reviewer comment: Understood. However, if the intensity of immunohistochemical level staining in positive cells has also been evaluated, this has to be reported clearly: 1) description of the procedure in the materials and methods, including the method of evaluation of the classification of the number of positive cells and the method of evaluation of the staining intensity (automated ? If so with which sofware ? If not, e.g. only a pathologist doing that, method for rigorously distributing each result in a specific class of intensity (= precise criteria for attribution of a sample to one class or another) ?), 2) these results about staining intensity (new table to add) should also be precisely and extensively reported in the corresponding result section, by adding new columns in table 2 or by adding a new table.

Also, in the title or footnote of Table 2, it has to be made clearer that the "level of inflammatory marker" is a count of the positive cells.

• 3: how were the quantitation of immunostainings performed ? The quantitative data are not presented ; they should be presented. And how were the comparison tests performed ? Are the conclusions about immunohistochemistry experiments only visual and dependent on the decision of the authors ? If so, it is not sufficient.

In our study we first evaluated the number of inflammatory cells in H&E staining, next after performing immunohistochemical staining we evaluated both the percentage of positive inflammatory cells and also the intensity of staining in those cells (absent, weak, moderate, strong staining). Below there is a method we used:

• 0 (negative expression – less than 10% of positive cells),
• 1+ (weak expression– 11-50% of positive inflammatory cells),
• 2+ (moderate expression – 51-75% of positive inflammatory cells),
• 3+ (strong expression – >75% of positive cells).

The conclusions concerning the immunohistochemical results were made by experienced practicing pathology consultant. The pathologist also used the negative control samples for the evaluation. Visual evaluation of immunohistochemical results has been commonly used in scientific papers.

New reviewer comment: See my comments above. The description of the method to evaluate the staining intensity and the method described by the authors in the lines above (number of positive cells) should both be presented in the materials and methods.

• 3: what does the blue rectangle in image moderate OSA / IL-6 represent ?

We do not observe a blue rectangle in the moderate OSA / IL-6 image and therefore we are not certain which element the reviewer is referring to.

OK, it was possibly was a bug in the conversion to pdf by the website. I do not see it in the revised version.

• 3: regarding IL-6, the scale bar present in the images is not correct. It is vertical, short and looks truncated at the border of the image, while the text connected to the scale bar is "Undersize" (?) in place of "200 µm".

Thank you for this comment. All images presented in Figure 3 were obtained using the same magnification, consistent with the magnification described in the figure legend.

New reviewer comment: I understand that all the images have been recorded in the same conditions. However, this does not respond to the comment: the problem with images about IL-6 has not been corrected in Figure 3: vertical and truncated size bars, with the text "Undersize" in place of 200 µm. This has to be corrected in the figure.

• Legend of Fig. 3: It should clearly be indicated that "representative images from each group are presented".

The figure legend has been revised to clearly indicate that representative images from each group are presented.

OK.

• Lines 113-121 : the models and regression methods used should be described in details in the materials and methods.

Thank you for this comment. The manuscript has been revised accordingly. The text has been reorganized so that the technical description of the models and regression methods is now presented in the Materials and Methods section, while the corresponding results are reported in the Results section.

OK.

• lines 108-110: "The strongest immunohistochemical reaction was observed in stromal inflammatory cells, especially in lymphocytes and monocytes". How was this claim verified and quantified?

The statement regarding stronger immunohistochemical reaction in stromal inflammatory cells (e.g., lymphocyte- and monocyte-like cells) was based on qualitative morphological assessment by experienced practicing pathology consultant, taking into account cell morphology both in H&E slides and immunohistochemical slides and localization within inflammatory infiltrates. However, we acknowledge that this observation was not formally quantified, nor confirmed using cell-specific markers or double immunostaining. Therefore, it should be considered descriptive rather than definitive.

To address this, we revised the manuscript to clarify that this finding is qualitative and morphology-based, and does not represent a quantified or immunophenotypically confirmed result. We will also include this as a limitation of the study.

New reviewer comment: I understand. However, because this is a result from the experiments that is reported in the result section, the method used has to also be described, in a few words, in the materials and methods.

• Materials and methods: number and sex distribution of the patients in each group ? how many samples were analyzed by immunohistochemistry in each group ? Same as above?

Number and sex distribution is defined in Table 1 and Table 2.

New reviewer comment: OK, I understand that all the samples from all the patients were studied by immunohistochemistry ? If so, the purpose of the question was that the strongly imbalanced sex ratio in the immunohistochemistry experiments would make difficult to evaluate the difference between men and women. Has there been any sign of a sex-related difference ?

• Discussion: lines 123-126 are unclear: " ... demonstrate increased proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6, with significant increases in ICAM-1 and VCAM-1 in the aortic wall ...". Is it an increase in the four markers or only two of them?

Thank you for this comment. The sentence has been revised for clarity. An increase was observed for all four analyzed cytokines; however, statistically significant differences were found only for ICAM-1 and VCAM-1.

New reviewer comment: same comment as above. The new sentence is appropriate, except for the claim that "... to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA ...". Since the reported increases in TNF-α and IL-6 are not statistically significant, an increase in TNF-α and IL-6 should not simply be claimed. It should be indicated either "... to demonstrate increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA ..." or "... to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1, together with a trend towards increases in TNF-α and IL-6, in patients with moderate-to-severe OSA

• Discussion: given the limited number of results from the present study, the discussion is rather long and over-interpretative.

Thank you for this comment. This study represents the fourth publication from our research group based on a similar type of vascular tissue and addressing related mechanisms linking obstructive sleep apnea with vascular inflammation and atherogenesis. For this reason, in the Discussion we also referred to our previous findings, which provide important context for the present results and contribute to a broader understanding of the atherogenic process associated with OSA. These include studies on CD40/CD40L pathway activation (Migacz et al., 2021), increased expression of TLRs and RAGE in carotid plaques (Olejarz et al., 2020), and elevated S100A8/S100A9 levels in the aortic wall (Migacz et al., 2025).

OK.

Author Response

The authors have satisfactorily responded to many of the reviewer comments. However, a few comments still need further response (see below).

 

• The claim that it is the first time that aortic inflammation has been related to sleep apnea severity in patients should be moderated (lines 123-126). Previous works have already shown a link between aortic inflammation and obstructive sleep apnea.

The sentence has been modified to: Our study is unique in that it directly examined aortic wall tissue collected intraoperatively during CABG, allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA, with significant elevations in ICAM-1 and VCAM-1, thereby providing direct tissue-level evidence linking OSA severity with vascular inflammation.

New reviewer comment: The new sentence is appropriate, except for the claim that "... to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA ...". Since the reported increases in TNF-α and IL-6 are not statistically significant, an increase in TNF-α and IL-6 should not simply be claimed. It should be indicated either "... to demonstrate increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA ..." or "... to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1, together with a trend towards increases in TNF-α and IL-6, in patients with moderate-to-severe OSA ...".

We thank the Reviewer for this important comment. We agree that the previous wording could overstate the findings regarding TNF-α and IL-6. Therefore, we have revised the manuscript throughout to avoid suggesting increased expression of TNF-α and IL-6 in the absence of statistical significance.

Specifically:

• statements referring to “increased expression” of TNF-α and IL-6 were removed from the Abstract, Results, Discussion, and Conclusions;
• the Results section now states that statistically significant differences were observed only for ICAM-1 and VCAM-1;
• the BMI-adjusted analysis was revised accordingly, and no association between OSA severity and TNF-α or IL-6 expression is claimed.

Abstract:
“This study provides novel evidence of significantly increased ICAM-1 and VCAM-1 expression in the aortic walls of patients with moderate-to-severe OSA. No statistically significant differences were observed for TNF-α and IL-6.”

Results:
“Immunohistochemistry demonstrated significantly increased expression of ICAM-1 (p = 0.001) and VCAM-1 (p = 0.006) in the aorta of the moderate-to-severe OSA group compared with the control and mild OSA group. No statistically significant differences were observed for TNF-α and IL-6.”

BMI-adjusted analysis:
“Adjustment for BMI attenuated but did not abolish the association for ICAM-1. For VCAM-1, the association with OSA severity remained independent of BMI. TNF-α and IL-6 did not show statistically significant associations with OSA severity.”

Discussion:
“Our study is unique in that it directly examined aortic wall tissue collected intraoperatively during CABG, allowing us for the first time to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA, while no statistically significant differences were observed for TNF-α and IL-6, thereby providing evidence linking OSA severity with vascular inflammation.”

We also carefully reviewed the entire manuscript and removed any remaining statements suggesting increased TNF-α or IL-6 expression in the absence of statistical significance.

We appreciate the Reviewer’s careful attention to this issue and believe the revised wording now more accurately reflects the study findings.

 

• 1: the figure apparently summarizes the aim of the present study. Therefore, it should be presented as a question. The present form of the figure and its legend leads to think that it is a reality, not a question.

The figure has been modified so that it now clearly presents the study aim in the form of a question rather than a statement.

OK

• Table 1 and related text: definitions of mild, moderate and severe OSA ?

These definitions are stated in the “Materials and Methods” section: “OSA severity was classified by the apnea hypopnea index [34] as: control, AHI < 5; mild, AHI ≥ 5; moderate, AHI ≥ 15; severe, AHI ≥ 30 events/hour. Sleep studies were performed 1 to 3 days before surgery”.

OK.

• Table 1 footnotes: definitions of CRP and WBC ?

Thank you for this comment. The definitions of CRP and WBC have now been added to the footnotes of Table 1.

OK.

• Tables 1 and 2, and Fig.2: why grouping (control + mild OSA patients) and (moderate + severe patients), rather than presenting separate data from these four groups ? What was the purpose of having four groups (control, mild, moderate, severe) if, in the end, the difference between only two separate groups are analyzed ? If the answer is that control and mild present very similar results (and same thing for moderate and severe), the analysis of the absence of difference between control and mild, as well as between moderate and severe, should be presented. Another possibility is that, when the four groups are analyzed separately, the differences between groups are not significant, while grouping allows to reach statistical significance. If it is the case, it has to be made clear for the reader: the results from each of the four initial groups should be presented, indicating that there is not statistical difference, then indicate that, when grouping the data, statistical significance is reached. Anyway, all the results, from each of the four groups, should be presented separately (data provided in Table 1 and Table 2).

Thank you for this important comment. Mild OSA is generally considered clinically very similar to the control group and is not associated with a significant impact on cardiovascular diseases. Therefore, in many studies patients are grouped into two categories: no/mild OSA and moderate/severe OSA, which reflects clinically meaningful disease severity. Following this widely used approach, we combined the control and mild OSA groups, as well as the moderate and severe OSA groups. Additionally, analyzing two groups allows a more robust estimation of statistical significance.

New reviewer comment: Understood. However, the reasons provided to the reviewer for grouping control with mild, and moderate with severe have also to be explained in the materials and methods, and justified with references.

We thank the Reviewer for this important comment. In response, we have now expanded the Materials and Methods section to explain the rationale for combining the control and mild OSA groups, as well as the moderate and severe OSA groups. Specifically, we clarified that mild OSA is generally considered clinically similar to the control condition and is usually not associated with a substantial increase in cardiovascular risk, whereas moderate-to-severe OSA is considered the clinically significant form of the disease. Therefore, grouping patients into no/mild versus moderate/severe OSA categories reflects commonly used clinical and research practice. Appropriate references supporting this classification approach have also been added to the manuscript.

• Footnotes of Table 2: define N, M, SD and ME.

Thank you for this comment. The definitions of N, M, SD, and ME have now been added to the footnotes of Table 2 as suggested.

OK.

• The titles of Table 2 and Fig2. should be more detailed for easy understanding of the reader. They should mention that the measurements were made in aortic tissue.

Thank you for this comment. The titles of Table 2 and Figure 2 have been revised to clearly indicate that the measurements were performed in aortic tissue.

OK.

• Why are the same markers (ICAM-1, VCAM-1, TNF-alpha and IL-6) presented as "inflammatory markers" in Table 2 and as "atherosclerosis markers" in Fig.2 ? They are both, but their presentation should be homogenized in all figures/tables.

To ensure consistency throughout the manuscript, these markers are now uniformly referred to as "inflammatory markers" in all tables and figures.

OK.

• Table 2 and Fig 2 are redundant. Fig 2 is not necessary since it only presents part of the information already shown in Table 2, and should be removed. Also, Fig. 2 is not even cited in the text of the results !

Thank you for this valuable comment. We respectfully propose to retain Figure 2, as it provides a graphical presentation of selected data from Table 2, which may improve clarity and facilitate interpretation of the results for readers. Visual representation of the data helps to more clearly illustrate the differences between the analyzed groups. Additionally, the figure has now been properly cited in the Results section.

New reviewer comment: OK. However, in order to facilitate the understanding by the reader, this has to clearly be stated in a short sentence of the results, i.e. Fig. 2 presents selected data from Table 2, focusing on ... .

We thank the Reviewer for this suggestion. To improve clarity for the readers, we added a sentence in the Results section indicating that Figure 2 presents selected graphical data derived from Table 2, focusing on the comparison of inflammatory marker expression between the analyzed groups.

• Table 2 and Fig 2: the method used to assess the levels of inflammatory markers is questionable. Basing the conclusion on the simple number of positive cells is not enough to be representative of the level of the marker. The actual content of each cell in the marker is also of high importance. For instance, in a group, there could be less positive cells, although with a much higher content in the marker in each cell, resulting in an elevated content of the marker ... although the method used by the authors (only counting positive cells) would conclude that there is a decreased level of the given marker in this group. The analysis should be redone while considering not only the number of positive cells, but also the level of the marker in each cell.

Thank you for this comment. The immunohistochemical assessment was performed using a standard method of immunohistochemical evaluation that has been widely described and applied in numerous previous publications, for example: de Matos LL et al. (2010) and Kim SW et al. (2016).

In our study we evaluated both the number of positive inflammatory cells present in the examined sample and also the intensity of immunohistochemical staining in positive cells ( evaluating as absent, weak, moderate and strong immunohistochemical staining in examined inflammatory cells).

New reviewer comment: Understood. However, if the intensity of immunohistochemical level staining in positive cells has also been evaluated, this has to be reported clearly: 1) description of the procedure in the materials and methods, including the method of evaluation of the classification of the number of positive cells and the method of evaluation of the staining intensity (automated ? If so with which sofware ? If not, e.g. only a pathologist doing that, method for rigorously distributing each result in a specific class of intensity (= precise criteria for attribution of a sample to one class or another) ?), 2) these results about staining intensity (new table to add) should also be precisely and extensively reported in the corresponding result section, by adding new columns in table 2 or by adding a new table.

Also, in the title or footnote of Table 2, it has to be made clearer that the "level of inflammatory marker" is a count of the positive cells.

 

We thank the Reviewer for this valuable comment. We have now clarified in the Materials and Methods section that the immunohistochemical assessment was performed manually by an experienced blinded pathology consultant and was based on semi-quantitative evaluation of the proportion of positively stained inflammatory cells. The evaluation was performed using a standardized four-tier scoring system: 0 (<10% positive cells), 1+ (11–50% positive cells), 2+ (51–75% positive cells), and 3+ (>75% positive cells). The intensity of staining was evaluated qualitatively during microscopic assessment and contributed to the final semi-quantitative interpretation; however, a separate digital image-analysis–based quantification of staining intensity was not performed. We have clarified this limitation in the manuscript. To improve clarity, we also revised the Table 2 legend to explicitly state that the reported values represent semi-quantitative immunohistochemical scores based primarily on the proportion of positively stained cells.

 

• 3: how were the quantitation of immunostainings performed ? The quantitative data are not presented ; they should be presented. And how were the comparison tests performed ? Are the conclusions about immunohistochemistry experiments only visual and dependent on the decision of the authors ? If so, it is not sufficient.

In our study we first evaluated the number of inflammatory cells in H&E staining, next after performing immunohistochemical staining we evaluated both the percentage of positive inflammatory cells and also the intensity of staining in those cells (absent, weak, moderate, strong staining). Below there is a method we used:

• 0 (negative expression – less than 10% of positive cells),
• 1+ (weak expression– 11-50% of positive inflammatory cells),
• 2+ (moderate expression – 51-75% of positive inflammatory cells),
• 3+ (strong expression – >75% of positive cells).

The conclusions concerning the immunohistochemical results were made by experienced practicing pathology consultant. The pathologist also used the negative control samples for the evaluation. Visual evaluation of immunohistochemical results has been commonly used in scientific papers.

New reviewer comment: See my comments above. The description of the method to evaluate the staining intensity and the method described by the authors in the lines above (number of positive cells) should both be presented in the materials and methods.

We thank the Reviewer for this comment. In response, we expanded the Materials and Methods section to include a detailed description of the semi-quantitative immunohistochemical scoring procedure, including both the proportion of positively stained cells and the qualitative assessment of staining intensity. We also clarified that all evaluations were performed manually by an experienced blinded pathology consultant using predefined scoring criteria and negative control samples.

Because staining intensity was assessed as part of the semi-quantitative pathological evaluation and not by separate digital image analysis, these data were incorporated into the overall immunohistochemical scoring description rather than presented as an independent quantitative table.

• 3: what does the blue rectangle in image moderate OSA / IL-6 represent ?

We do not observe a blue rectangle in the moderate OSA / IL-6 image and therefore we are not certain which element the reviewer is referring to.

OK, it was possibly was a bug in the conversion to pdf by the website. I do not see it in the revised version.

• 3: regarding IL-6, the scale bar present in the images is not correct. It is vertical, short and looks truncated at the border of the image, while the text connected to the scale bar is "Undersize" (?) in place of "200 µm".

Thank you for this comment. All images presented in Figure 3 were obtained using the same magnification, consistent with the magnification described in the figure legend.

New reviewer comment: I understand that all the images have been recorded in the same conditions. However, this does not respond to the comment: the problem with images about IL-6 has not been corrected in Figure 3: vertical and truncated size bars, with the text "Undersize" in place of 200 µm. This has to be corrected in the figure.

We thank the Reviewer for pointing out this technical issue. The IL-6 panel in Figure 3 has now been corrected. The incorrect vertical and truncated scale bar, as well as the erroneous “Undersize” label, were removed and replaced with the proper horizontal 200 µm scale bar consistent with the remaining panels.

 

• Legend of Fig. 3: It should clearly be indicated that "representative images from each group are presented".

The figure legend has been revised to clearly indicate that representative images from each group are presented.

OK.

• Lines 113-121 : the models and regression methods used should be described in details in the materials and methods.

Thank you for this comment. The manuscript has been revised accordingly. The text has been reorganized so that the technical description of the models and regression methods is now presented in the Materials and Methods section, while the corresponding results are reported in the Results section.

OK.

• lines 108-110: "The strongest immunohistochemical reaction was observed in stromal inflammatory cells, especially in lymphocytes and monocytes". How was this claim verified and quantified?

The statement regarding stronger immunohistochemical reaction in stromal inflammatory cells (e.g., lymphocyte- and monocyte-like cells) was based on qualitative morphological assessment by experienced practicing pathology consultant, taking into account cell morphology both in H&E slides and immunohistochemical slides and localization within inflammatory infiltrates. However, we acknowledge that this observation was not formally quantified, nor confirmed using cell-specific markers or double immunostaining. Therefore, it should be considered descriptive rather than definitive.

To address this, we revised the manuscript to clarify that this finding is qualitative and morphology-based, and does not represent a quantified or immunophenotypically confirmed result. We will also include this as a limitation of the study.

New reviewer comment: I understand. However, because this is a result from the experiments that is reported in the result section, the method used has to also be described, in a few words, in the materials and methods.

We thank the Reviewer for this comment. In response, we added a brief description in the Materials and Methods section indicating that the identification of stromal inflammatory cells was based on qualitative morphological assessment performed by an experienced pathology consultant using cellular morphology and localization within inflammatory infiltrates on both H&E and immunohistochemical slides.

• Materials and methods: number and sex distribution of the patients in each group ? how many samples were analyzed by immunohistochemistry in each group ? Same as above?

Number and sex distribution is defined in Table 1 and Table 2.

New reviewer comment: OK, I understand that all the samples from all the patients were studied by immunohistochemistry ? If so, the purpose of the question was that the strongly imbalanced sex ratio in the immunohistochemistry experiments would make difficult to evaluate the difference between men and women. Has there been any sign of a sex-related difference ?

We thank the Reviewer for this important observation. All collected vascular samples were included in the immunohistochemical analyses. However, due to the markedly imbalanced sex distribution and the limited number of female participants in the study population, reliable sex-stratified statistical analyses could not be performed. Therefore, no definitive conclusions regarding potential sex-related differences can be drawn from the present study. This limitation has now been acknowledged in the manuscript.

 

• Discussion: lines 123-126 are unclear: " ... demonstrate increased proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6, with significant increases in ICAM-1 and VCAM-1 in the aortic wall ...". Is it an increase in the four markers or only two of them?

Thank you for this comment. The sentence has been revised for clarity. An increase was observed for all four analyzed cytokines; however, statistically significant differences were found only for ICAM-1 and VCAM-1.

New reviewer comment: same comment as above. The new sentence is appropriate, except for the claim that "... to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA ...". Since the reported increases in TNF-α and IL-6 are not statistically significant, an increase in TNF-α and IL-6 should not simply be claimed. It should be indicated either "... to demonstrate increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA ..." or "... to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1, together with a trend towards increases in TNF-α and IL-6, in patients with moderate-to-severe OSA

„We thank the reviewer for this important comment. We agree that the previous wording may have overstated the findings for TNF-α and IL-6. The manuscript has been revised accordingly to report only statistically significant increases in ICAM-1 and VCAM-1, and to describe TNF-α and IL-6 changes as a non-significant trend.”

 

• Discussion: given the limited number of results from the present study, the discussion is rather long and over-interpretative.

Thank you for this comment. This study represents the fourth publication from our research group based on a similar type of vascular tissue and addressing related mechanisms linking obstructive sleep apnea with vascular inflammation and atherogenesis. For this reason, in the Discussion we also referred to our previous findings, which provide important context for the present results and contribute to a broader understanding of the atherogenic process associated with OSA. These include studies on CD40/CD40L pathway activation (Migacz et al., 2021), increased expression of TLRs and RAGE in carotid plaques (Olejarz et al., 2020), and elevated S100A8/S100A9 levels in the aortic wall (Migacz et al., 2025).

OK.

Author Response File: Author Response.docx

Reviewer 2 Report

Comments and Suggestions for Authors

The authors adequately revised my main comments, except for the problem of the non significant difference of expression for TNFa and IL6.

In the last paragraph of the results the authors write that, since model adjustment for BMI does not change significance,  “This suggests therefore that obesity may partly influence the ICAM-1 levels, but not VCAM-1, TNF-α, and IL-6 expression. The expression of these markers is associated with OSA independently from BMI.”

This is not correct, because expression of TNF and IL-6 is NOT associated with OSA severity and this mention should be removed. The overexpression in OSA independently of BMI is only true for VCAM.

Similarly in the first sentence of the discussion they still write “allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA,…”

I insist that this is not correct and should be removed. This is not a result of the study as claimed by the authors, this is an overinterpretation –there is no increase for TNF and IL-6. Mentioning “non significant increases” has no sense.

The paper cannot be accepted as long as these misleading mentions of “increased expression” persist.

 

Minor comments:

Table 2 : In their response the authors said that Me denotes the Mean error, but in the legend of the table it is indicated that Me means Median. Please correct.

Many references were added in the discussion section in the paragraph discussing ICAM and VCAM expression in OSA and rodent models, but they were all grouped ([7;14-19]) at the end of the paragraph. It would be helpful for readers if the authors would cite each reference at the end of appropriate sentence(s).  

In the legend of figure 2, can you please specify what the bars represents (mean and SD ? Median and IQ range ?)

Some typos remain (lack of space between words, extra dot at the end of the sentence,…)

Author Response

Comments and Suggestions for Authors

The authors adequately revised my main comments, except for the problem of the non significant difference of expression for TNFa and IL6.

In the last paragraph of the results the authors write that, since model adjustment for BMI does not change significance,  “This suggests therefore that obesity may partly influence the ICAM-1 levels, but not VCAM-1, TNF-α, and IL-6 expression. The expression of these markers is associated with OSA independently from BMI.”

This is not correct, because expression of TNF and IL-6 is NOT associated with OSA severity and this mention should be removed. The overexpression in OSA independently of BMI is only true for VCAM.

Similarly in the first sentence of the discussion they still write “allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA,…”

I insist that this is not correct and should be removed. This is not a result of the study as claimed by the authors, this is an overinterpretation –there is no increase for TNF and IL-6. Mentioning “non significant increases” has no sense.

The paper cannot be accepted as long as these misleading mentions of “increased expression” persist.

 

We thank the Reviewer for this important comment and fully agree that our previous wording could lead to overinterpretation of the findings regarding TNF-α and IL-6.

In response to the Reviewer’s concern, we have now revised the manuscript throughout to completely remove statements suggesting increased expression or association of TNF-α and IL-6 with OSA severity in the absence of statistical significance.

Specifically, the following changes were made:

Results section:
The sentence:
“This suggests therefore that obesity may partly influence the ICAM-1 levels, but not VCAM-1, TNF-α, and IL-6 expression. The expression of these markers is associated with OSA independently from BMI.”

has been replaced with:

“Adjustment for BMI attenuated but did not abolish the association for ICAM-1. For VCAM-1, the association with OSA severity remained independent of BMI. TNF-α and IL-6 did not show statistically significant associations with OSA severity.”

Discussion section:
The sentence:
“allowing us for the first time to demonstrate increased expression of the proinflammatory markers ICAM-1, VCAM-1, TNF-α, and IL-6 in patients with moderate-to-severe OSA”

has been replaced with:

“allowing us for the first time to demonstrate significantly increased expression of the proinflammatory markers ICAM-1 and VCAM-1 in patients with moderate-to-severe OSA, while no statistically significant differences were observed for TNF-α and IL-6.”

In addition, all remaining mentions suggesting “increased expression”, “higher expression”, or “non-significant increases” of TNF-α and IL-6 have been removed from the Abstract, Results, Discussion, and Conclusions.

We appreciate the Reviewer’s careful evaluation of the manuscript and believe that the revised wording now accurately reflects the statistical findings of the study.

 

 

Minor comments:

Table 2 : In their response the authors said that Me denotes the Mean error, but in the legend of the table it is indicated that Me means Median. Please correct.

We thank the Reviewer for noticing this inconsistency. The abbreviation “Me” has now been corrected and consistently defined as “Median” in the Table 2 footnote and throughout the manuscript.

Many references were added in the discussion section in the paragraph discussing ICAM and VCAM expression in OSA and rodent models, but they were all grouped ([7;14-19]) at the end of the paragraph. It would be helpful for readers if the authors would cite each reference at the end of appropriate sentence(s).  

We thank the Reviewer for this helpful suggestion. The references discussing ICAM-1 and VCAM-1 expression in OSA and experimental models have now been redistributed throughout the Discussion section so that each reference is cited directly in the relevant sentence for improved readability and clarity.

In the legend of figure 2, can you please specify what the bars represents (mean and SD ? Median and IQ range ?)

We thank the Reviewer for this comment. The legend of Figure 2 has now been revised to specify that the bars represent mean values ± standard deviation (SD).

Some typos remain (lack of space between words, extra dot at the end of the sentence,…)

We thank the Reviewer for this observation. The manuscript has undergone additional careful proofreading, and the remaining typographical, punctuation, and spacing errors have been corrected throughout the text.

Reviewer 3 Report

Comments and Suggestions for Authors

Although the authors did some changes and offered some explanations the problems still exists. Local not systemic is not an rational explanation. All the cardiometabolic diseases inflict local changes. So what you measured might not be at all due to OSA. But i understand that you cannot do anything about this right now. Maybe in the future, prepare more carrefully your research design. You should tone a lot down your conclusions that should reflect the independent contribution of OSA to vascular inflammation cannot be achieved only on your results.

Author Response

Comments and Suggestions for Authors

Although the authors did some changes and offered some explanations the problems still exists. Local not systemic is not an rational explanation. All the cardiometabolic diseases inflict local changes. So what you measured might not be at all due to OSA. But i understand that you cannot do anything about this right now. Maybe in the future, prepare more carrefully your research design. You should tone a lot down your conclusions that should reflect the independent contribution of OSA to vascular inflammation cannot be achieved only on your results.

We thank the Reviewer for this valuable comment. We fully agree that the present study design does not allow definitive separation of the independent contribution of OSA from the effects of advanced cardiovascular disease and related cardiometabolic comorbidities. Accordingly, we further revised and substantially toned down the Conclusions and Discussion sections to avoid causal interpretation of the findings. The revised manuscript now emphasizes that the observed results represent an association between OSA severity and local vascular inflammatory changes rather than proof of a direct or independent effect of OSA. We also expanded the Limitations section to explicitly acknowledge the potential influence of underlying atherosclerosis and associated cardiometabolic diseases on the observed inflammatory profile.

In particular, terms suggesting an “independent effect”, “direct contribution”, or “causal role” of OSA in vascular inflammation were removed or replaced with more cautious wording throughout the manuscript.

 

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

The authors adequately answered to all the comments. I think this version is much more rigorous and adequate for publication. 

Author Response

We would like to express our sincere gratitude to the Reviewer for the thorough assessment of our manuscript and for the considerable time and effort devoted to its evaluation. The Reviewer’s valuable comments and suggestions have significantly contributed to improving the quality and clarity of our manuscript. We highly appreciate this constructive feedback and have carefully addressed all points raised.

Reviewer 3 Report

Comments and Suggestions for Authors

Accepted

Author Response

We would like to express our sincere gratitude to the Reviewer for the thorough assessment of our manuscript and for the considerable time and effort devoted to its evaluation. The Reviewer’s valuable comments and suggestions have significantly contributed to improving the quality and clarity of our manuscript. We highly appreciate this constructive feedback and have carefully addressed all points raised.