Early Cardiovascular and Metabolic Benefits of rhGH Therapy in Adult Patients with Severe Growth Hormone Deficiency: Impact on Oxidative Stress Parameters

Round 1

Reviewer 1 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

The topic of the paper is interesting and the manuscript is improved with respect to previous version. Nevertheless, there are important issues that have to be addressed before considering the paper for publication. For details see an attached file.

Comments for author File: Comments.pdf

Author Response

Responses to Reviewer 1's Comments

 

We would like to sincerely thank Reviewer 1 for their thorough evaluation of our manuscript and for the constructive comments and valuable suggestions. Below we provide detailed responses to each point raised. All changes in the manuscript have been clearly marked in red for ease of review.

1). The topic of the paper is interesting and the manuscript is improved with respect to previous

version. Nevertheless, there are important issues that have to be addressed before considering

the paper for publication. For details see below. The first problem is the title of the paper. Term “Adult-onset growth hormone deficiency (AO-GHD)” seems to be used improperly, as only 3 out of 15 patients had no childhood-onset GHD(CO-GHD) in their history (as reported in Table 4), while 12 fulfilled the criteria of persistentsevere CO-GHD. It seems impossible that all these patients recovered from CO-GHD and gotGHD again as adults. There is no information, if the patients with CO-GHD were previouslytreated with rhGH and how long they remained untreated. Moreover, according to currentrecommendations, a patient P8, with isolated AO-GHD, described as idiopathic, should havetwo GH stimulation tests performed to confirm the diagnosis (especially as before treatment hehad higher IGF-1 than the mean value in the whole group after 6 months of rhGH therapy).The authors should also explain, while in the title of the paper they wrote about 6 months oftreatment, while the analysis is conducted for 6 and 12 months, with relevant results for both timepoints.

We acknowledge the reviewer's concern regarding the use of the term "Adult-onset growth hormone deficiency (AO-GHD)." As noted, the majority of our study group consisted of patients with persistent severe childhood-onset GHD (CO-GHD). In response, we have revised the title and relevant sections of the manuscript to clarify this distinction. We have also provided additional information regarding the prior treatment with rhGH and treatment-free intervals for CO-GHD patients. Furthermore, the case of patient P8 has been clarified with respect to current diagnostic criteria and IGF-1 levels. The discrepancy regarding the treatment duration mentioned in the title has also been addressed by ensuring consistency with the time points analyzed in the results (6 and 12 months).

2).It should be clarified, what is reported in the Tables (median and interquartile range or min-max range, or nonoutlier range?), it’s impossible to interpret the results without such explanation.

Data in the table are expressed as the median along with the minimum and maximum values (MIN–MAX range). In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity.

3) It should be also noticed that the Authors in the Abstract write about TOC and TAC, while in the main text they report TAS/TAC and TOS/TOC. Moreover, in section 5.2. (Biochemical Measurement), only measurement of PerOx (TOC/TAC) is described (lines 361-364). Finally, in section 4.2 Biochemical measurement, the correlations of “TOC capacity” and “TAC capacity”with IGF-1 and with other parameters are reported. These discrepancies should definitely be explained.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity (section Biochemical Measurement).

4)Please note that “Ca2+” suggests measurements of ionized calcium, while both description in Table 1 (Ca) and the reported concentrations seem relate to total calcium – this issue must be clarified.

 

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity.

5)Glucose concentrations are not commented, if there were measured at fasting state, some

patients could have diabetes. As only uncontrolled metabolic diabetes (HbA1c > 7%) is listed

among exclusion criteria of rhGH therapy, it should be reported, what was the number of such

patients and how they were treated. The Authors should consider that both diabetes and its

therapy might influence the obtained results and have effects on the risk of CVD.

Two male patients, aged 18 and 25 years, had a history of type 1 diabetes diagnosed 6 months prior, treated with intensive functional insulin therapy using human insulin analogs, achieving normal metabolic control (HbA1c < 6.5%). Due to the short disease duration and adequate metabolic control, no influence on cardiovascular complications is observed. In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity (section Studied population).

6)Vitamin D concentrations are provided in Table 1 but not included in the analyses and not

commented anywhere.

Vitamin D values have been removed from Table 1, in line with the reviewer's note that they were not discussed or analyzed in the manuscript.

7).Please explain, why HOMA is included in section Results (line 95) as the authors decided to use VAI as a marker of insulin resistance and have not reported any data on insulin concentrations or values of HOMA in the patients.

The aim of the study was to use the VAI index for assessment, for the calculation of which insulin levels are not required. Therefore, data related to the HOMA-IR index and insulin concentrations have not been included in the manuscript. The VAI values have been added to Table 2, while the correlations of the VAI index with individual parameters have been added to Table 3.

8)In Table 3, correlations with “Tissue mass” are reported, while such parameter is not shown in Table 2 and not defined anywhere. Instead, “Tissue fat %” is reported in Table 2 but not included in correlations. Please clarify this inconsistency.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity.

9) I wonder, what is the significance of detailed information of advised physical activity (lines 337-

341), if real activity of the patients was not assessed, there is also missing data concerning the

patients’ diet and caloric intake, while some of them were obese.

 

Before inclusion in the study, each patient received training on the principles of healthy nutrition, and in cases of obesity — also on the use of a calorie-reduction diet and the impact of physical activity on body weight reduction, which in turn may lead to a decreased risk of cardiovascular complications associated with obesity. However, it should be emphasized that the analysis of these data was not the subject of the present study. In accordance with the reviewer’s suggestion, information regarding the principles of the reduction diet has been added in the "Studied population" section (highlighted in red).

10).Mathematical equations in lines 350-352 should be re-written according to the source formulas,as in their current form they lead to different results than proper equations. Namely, squarebracket should include round bracket(s), not conversely. The equation for women, recorded as:VAI = (waist circumference/36.58 + [1.89 × BMI]) × (TG/0.81) × (1.52/HDL) is definitely not equivalent to its original form in the cited paper:;the same relates to the equations for men. So, the authors should clarify this and ensure that all calculations of VAI in their study were made using the correct formulas.

 

Corrected according to the reviewer's recommendations. All VAI calculations were performed using the correct formulas.

 

11). Conclusion concerning personalized rhGH therapy is not supported by the results as such study

should include detailed information about the effects of individual adjustment of rhGH doses on

the assessed parameters. Moreover, as stated before, the majority of patients had severe,persistent CO-GHD, not AO-GHD.

In accordance with the suggestion, the text has been clarified to indicate that the majority of the studied patients had severe, persistent childhood-onset growth hormone deficiency, rather than AO-GHD. Details regarding the personalized individual dose of rhGH can be found in Table 4.

12). The Discussion has been improved with respect to its previous version, as really existing papers

are cited. Nevertheless, some of references have no direct relation to the results presented in

the study. Moreover, there are some discrepancies between the content of cited papers and

their description in the manuscript under review. Namely, in Ref. [39], there is no clear statement that “IGF-1 acts as an anti-inflammatory agent by modulating immune cell activity and reducing the production of pro-inflammatory cytokines, such as interleukin-6 (IL-6) and tumor necrosis factor-alpha (TNF-α)”, while there is some data on the effect of IL-6 and TNF-α on IGF-I.

 

According to the reviewer’s suggestions, Citation 39 has been corrected (Zhang X, Hu F, Li J, et al. IGF-1 inhibits inflammation and accelerates angiogenesis via Ras/PI3K/IKK/NF-κB signaling pathways to promote wound healing. Eur J Pharm Sci. 2024;200:106847. doi:10.1016/j.ejps.2024.10684).

13)The sentence “In the opposition to our study, other researchers have observed higher IGF-1

concentrations in individuals with GHD only after one year [41,42]” in lines 192-193 is not true,

as in the Ref. [42], it is clearly stated that . “Serum IGF-1 was significantly elevated from the

baseline at each follow-up visit, with the increase being most pronounced within the first month

of treatment” (see Fig. 1 and comment to this Figure).  The Ref. [41] is cited improperly, as the

cited paper refers to children treated with long-acting pegylated GH.

 

The conclusion of the paper has been revised. Reference number 41 has been corrected: Lanes R, Jakubowicz S. Is insulin-like growth factor-1 monitoring useful in assessing the response to growth hormone in growth hormone-deficient children?. J Pediatr. 2002;141(5):606-610. doi:10.1067/mpd.2002.127662.

14). Please clarify the statement in lines 221-222. Have the authors really observed “decreased TOC

concentrations” after 6 and 12 months of therapy (with respect to what reference data?) or the

decrease of TOC concentrations with respect to baseline. Only the latter statement could be

supported by the presented results, however only indirectly, as data on “TOC concentrations”

are not provided in the manuscript.

 

In accordance with the suggestion, the text has been clarified. In our study group, we observed a significantly decreased TOS/TOC concentration after 6 months of therapy compared to baseline, followed by a clinically significant increase after 12 months compared to the initial values (p=0.2 vs p=0.04, respectively).

15). Subsection 2.1 in section Results should be re-written or shifted to the section Discussion.

Results should be presented like “A strong negative correlation between VAI and HDL (p=///,

R=///) was observed together with strong positive correlation between VAI and TG (p=///, R=///).

Moreover, section 3 is entitled “Correlations”. The results from section 2.1 should be presented

there (with appropriate p- and R-values provided), until the section is a part of Results. If the

Authors have not presented their own results in 2.1, this text should be placed in the

Discussion, with appropriate References.

 

As per the reviewer's suggestion, the section has been moved to the Discussion. Additionally, the results in the "Correlations" section have been described, and Table 3 has been revised.

 

16). In Results there is no need to write “in a group of AO-GHD patients”, as according to the title ofthe paper and the study design, there were no other patients subjected (however in fact the term AO-GHD is appropriate for 3 cases only).

 

As per the reviewer's suggestion, this formulation has been removed.

17). Please explain the units of “TAS/TAC” and “TOS/TOC” in Table 1, as such the records suggest

that there are proportions ????/? ???/?, not concentrations.

 

Commercial kits were used in the study to assess oxidative and antioxidative status. The aforementioned units are used in the literature and are considered to represent oxidative and antioxidative capacity, expressed in μmol/L.

 

18). Please provide units for BMC and BMD in Table 2.

As per the reviewer's suggestion Table 2 has been revised.

19). Abbreviation “NT-pro-BNP” should be unified, in Table 1 it is now “NT-proBNP”, while in Table 3 NT-pro-BNP, and finally in line 371 “NT-po-BNP”. In Abbreviations section, “NT-pro-BNP” is

explained twice.

 

As per the reviewer's suggestion has been revised.

20). Please unify abbreviation IGF-I (e.g. in Abstract and sections 1 and 2), while IGF-1 (in other

sections).

 

As per the reviewer's suggestion has been revised.

21). Please also check if the abbreviation “FPM” is used anywhere in the text.

As per the reviewer's suggestion has been revised.

22). Lines 100-101 should be rephrased, e.g.: “In the studied group of patients, significantly higher

concentrations of IGF- after 6 and 12 months of therapy were observed comparing to baseline

values …”. In next sentence in lines 102-103, it would be better to write: “We did not observe

statistically significant differences in the concentrations of IGF-1 at 12 months of therapy

compared to 6 months …”; the same relates to line 189. In the last sentence of this paragraph

(lines 103-105), the authors should write about “significantly higher concentrations … after 12

months compared to baseline”. The same relates to other reported “significantly lower (of

higher) concentrations”, “comparing”.

 

As per the reviewer's suggestion has been revised.

23). There is no need to divide section 2.2 for subsections 2.2.1 to 2.2.6, including only single

sentences. The last subsection of Results (2.4.) should be Correlations.

 

As per the reviewer's suggestion has been revised.

 

24). In Table 2 should be listed “Femoral neck” not “Neck” as it is quite different part of the body and such description may be misleading.

 

As per the reviewer's suggestion has been revised.

 

25). In line 166 is an unexplained abbreviation CV. Have the Authors meant CVD? This abbreviation

should be also included in section Abbreviations.

 

As per the reviewer's suggestion has been revised.

26). In References section, reference 45 includes in fact two different references, as a result of

which, next references have double numbers that makes difficult understanding further part of

Discussion. The last Reference in text is [88], relating to the paper of Kim and Park that is listed

with numbers 87 and 88. The authors have to correct this inconsistency before further

processing the Review with respect to the accuracy of References.

 

As per the reviewer's suggestion has been revised.

 

27). An example may be a sentence: “Additionally, there are reports indicating that intravenously

administered ET-1 in healthy men inhibits the increase in GH levels stimulated by growth

hormone-releasing hormone [50].

In accordance with the reviewer's suggestion, the corrections have been made. A new reference has been added:  Vierhapper H. Effect of endothelin-1 in man--impact on basal and stimulated concentrations of luteinizing hormone, follicle-stimulating hormone, thyrotropin, growth hormone, corticotropin, and prolactin with and without pretreatment with nifedipine. Metabolism. 1996;45(5):658-661. doi:10.1016/s0026-0495(96)90039-6

28). Unfortunately, Ref. 49 or 50 is devoted to ET-1 but not to GH, while Ref. 50 or 51 refers to ADMA. The reviewer is not able to verify the Discussion in its present version.

 

As per the reviewer's suggestion has been revised.

29). In Discussion there is no need to repeat exact p- and R-values from the Results. The results

should be commented, while cited only if it is necessary for direct comparisons with the results

of other studies (also cited with similar accuracy).

 

As per the reviewer's suggestion has been revised.

30). Moreover p-values related to the IGF-1 increase repeated in line 188 are different from these in lines 101-102, please verify.

 

Citations of our own results have been removed from the Discussion section in accordance with the reviewer’s suggestion. The data presented in the Results section are correct.

31). Abbreviations used in Tables should be explained below each Table. Especially, both therapies

and diagnoses of the patients in Table 4 are unclear without such explanation directly below the

Table (they are also not described in the main text).

 

As per the reviewer's suggestion has been revised.

 

 

32). Please unify References, with respect to the number of authors listed.  

As per the reviewer's suggestion has been revised.

 

 

Author Response File: Author Response.docx

Reviewer 2 Report (New Reviewer)

Comments and Suggestions for Authors

The original study addresses the effects of rhGH replacement on IGF-1 levels and metabolic benefits. However, adjustments are needed to improve the clarity of the data. 

1) The group of 15 patients is heterogeneous concerning BMI, weakening the article statistically. With 26% of obese volunteers (BMI>30), visceral adiposity may worsen IGF-1 levels. A subanalysis of this group or including a paragraph in the discussion about this relationship is recommended. I would suggest you read the article: 10.1038/s41598-022-23521-1. 

2) In the discussion, including a figure with key data obtained, such as reductions in ET-1, ADMA, and TOC, alongside increases in TAC and IGF-1 would be helpful. These observations suggest decreased cardiovascular risk, improved metabolic balance, and positive effects on body composition. Introducing this figure could increase the number of citations and views of the article.

3) In the limitations of the study, it is worth mentioning that these results may not be reproduced in older patients with GH deficiency (the oldest patient in the population of this study is 60 years old). This is because in the elderly, the benefits of therapy would not have as much impact on body composition. See reference: 10.3389/fendo.2021.635983

4) GH therapy, even at low doses, can cause reactions or side effects, such as joint pain. In the methods, the authors should describe which clinical signs were evaluated in these patients during the segment and whether or not there were any adverse effects. If no such results exist, this should be further explored in the discussion. 

5) A minor review in English is necessary 

Best wishes 

Comments on the Quality of English Language

Minor Review. 

Author Response

Responses to Reviewer 2's Comments

We would like to sincerely thank Reviewer 2 for their thorough evaluation of our manuscript and for the constructive comments and valuable suggestions. Below we provide detailed responses to each point raised. All changes in the manuscript have been clearly marked in red or green for ease of review.

1) The group of 15 patients is heterogeneous concerning BMI, weakening the article statistically. With 26% of obese volunteers (BMI>30), visceral adiposity may worsen IGF-1 levels. A subanalysis of this group or including a paragraph in the discussion about this relationship is recommended. I would suggest you read the article: 10.1038/s41598-022-23521-1. 

The reviewer's comments were consulted with a statistician, who advised that subdividing the cohort to isolate individuals with obesity was not methodologically justified due to the small size of this subgroup, which precludes the possibility of obtaining statistically reliable results. Furthermore, in accordance with the reviewer’s recommendations, the necessary revisions have been made. All modifications have been clearly marked in red for ease of reference.

2) In the discussion, including a figure with key data obtained, such as reductions in ET-1, ADMA, and TOC, alongside increases in TAC and IGF-1 would be helpful. These observations suggest decreased cardiovascular risk, improved metabolic balance, and positive effects on body composition. Introducing this figure could increase the number of citations and views of the article.

In accordance with the reviewer's suggestion, the appropriate figures (Fig. 1, Fig 2) has been added to the manuscript.

3) In the limitations of the study, it is worth mentioning that these results may not be reproduced in older patients with GH deficiency (the oldest patient in the population of this study is 60 years old). This is because in the elderly, the benefits of therapy would not have as much impact on body composition. See reference: 10.3389/fendo.2021.635983

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity.

4) GH therapy, even at low doses, can cause reactions or side effects, such as joint pain. In the methods, the authors should describe which clinical signs were evaluated in these patients during the segment and whether or not there were any adverse effects. If no such results exist, this should be further explored in the discussion. 

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in red for clarity.

5) A minor review in English is necessary 

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented.

All modifications have been highlighted in green for clarity.

 

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Dear Authors,

thank you for making the corrections and clarification. The manuscript is improved with respect to both its previous versions, however it still requires major revision. In my opinion, the following issues should be resolved:

1. Despite the fact that the Title is definitely improved, now there is no information that the paper describes adult patients with severe GHD – either in the Title or in the Abstract. Such information should be added as this clinical context is completely different from the situation of children with partial GHD who are also treated with rhGH.
2. Please clarify what is exactly described as TOS/TOC and TAS/TAC, as – according to your explanation – probably there are no ratios of total oxidative status to total oxidative capacity and of total antioxidant status to antioxidant capacity. In literature there are most frequently reported only TOS and TAC, e.g. in the paper of Buczynska et al. https://doi.org/10.1038/s41598-023-40898-9. Have you measured here other markers of OS here than in that study? Note that in Discussion (in lines 272-273) and in Conclusions you still write about TOC and TAC (line 440), not about TOS/TOC and TAS/TAC, please explain this inconsistence.
3. In Table 1, the authors provide the data on significant increase of values of TOS/TOC after 12 months of treatment with respect to baseline (457.3 at baseline vs. 589.5 at 12 mth), the same is repeated in Fig. 2. Unfortunately, these results are commented (in lines 98-99) as “significantly lower concentrations of TOS/TOC after 6 and 12 months (p=0.02 vs p=0.04; respectively)”, while in Discussion as “In our study group, we observed a significantly decreased TOS/TOC concentration after 6 months of therapy compared to baseline, followed by a clinically a significant increase after 12 months compared to the initial values”. This discrepancy must be clarified before publication, with appropriate comment concerning the increase of TOS/TOC after 12 months of treatment added. Such observation is also not in line with the Conclusions (see line 440).
4. The authors should provide data on “a reduction of TAS/TAC status” in Results if they use this finding as an argue in Discussion (lines 275-277). In my opinion, speculations on the relationships between lipids and TAS/TAC are too far-reaching with respect to the presented results.
5. The authors should explain in Introduction, why data on calcium levels are important, as they decided to provide them in the paper. Please note that point 2.1. IGF-1 measurements and Ca should be in fact 2.1.1. If only IGF-1 and Ca are considered by the authors as biochemical markers, there is probably no need to add two names of the same subsection. However, this is not in line with Table 1 in which much more biochemical parameters is reported.
6. In response to my previous review, the authors have stated that “Therefore, data related to the HOMA-IR index and insulin concentrations have not been included in the manuscript”. Nevertheless, in lines 166-167 and in Table 3, the authors give the data on correlation between VAI and HOMA-IR, while there is no other data concerning HOMA or insulin levels, e.g. it’s missing in Table 1. Please clarify this inconsistency.
7. The same relates to correlation of TAS/TAC vs DNA/RNA in Table 3, as there is no explanation of the variable DNA/RNA anywhere in the manuscript. Moreover, this correlation is not provided for timepoint “After 12 months”. Please clarify this issue.
8. In my opinion, it would be better to show median and interquartile range instead of MIN-MAX as the latter one may be biased by even a single outlier in the group. Please consider this.
9. Please also introduce the abbreviation Ca at its first use (this should be done in Introduction) and rephrase the title of this point: “IGF-1 and Ca measurements”.
10. Please unify writing of units, e.g. “mL” (in Table 1) while “ml” (in line 360 of present version).
11. Please rephrase a sentence in line 87, as differences may be statistically significant but levels of hormones may be “significantly higher”, so it should be: “In the studied group of patients significantly higher concentration of IGF-1 …”. Next sentences in this paragraph are OK.
12. There is no need to write in titles of the Tables “in the GHD group” as there is no other group included in this study. If descriptions of V0, V1 and V2 were provided, they should be used in Tables, to unify the descriptions of timepoints with Figures.
13. Information concerning the incidence of obesity should be provided in Renaults, not just in Discussion. The same relates to the information about the cut-off for decreased IGF-1, however, the incidence of decreased IGF-1 has not been reported in the manuscript.
14. In Conclusions, you should also clarify that the study shows the effects of rhGH “for adult patients with severe GHD” (line 438), not in all cases of GHD in any age group.
15. Why the authors included section 6. Patents” that provides no information about patents?
16. Please remove doubled “d” in the word “noted” (line 133) and doubled “Statistically significant differences” (in lines 133-134). Please correct “TASTAC” to “TAS/TAC” in line 257. Please do not leave “minus” at the and of line 143.
17. Please move heading of Table 2 and title of Table 4 to the same page as the whole Table.

Author Response

1. Despite the fact that the Title is definitely improved, now there is no information that the paper describes adult patients with severe GHD – either in the Title or in the Abstract. Such information should be added as this clinical context is completely different from the situation of children with partial GHD who are also treated with rhGH.

Thank you for your valuable comment. We fully agree that clearly specifying the clinical context of the studied population is essential. Accordingly, we have revised both the Title and Abstract to explicitly indicate that the paper describes adult patients with severe GHD, distinguishing it from the clinical context of children with partial GHD treated with rhGH.

1. Please clarify what is exactly described as TOS/TOC and TAS/TAC, as – according to your explanation – probably there are no ratios of total oxidative status to total oxidative capacity and of total antioxidant status to antioxidant capacity. In literature there are most frequently reported only TOS and TAC, e.g. in the paper of Buczynska et al. https://doi.org/10.1038/s41598-023-40898-9. Have you measured here other markers of OS here than in that study? Note that in Discussion (in lines 272-273) and in Conclusions you still write about TOC and TAC (line 440), not about TOS/TOC and TAS/TAC, please explain this inconsistence.

Thank you for highlighting this important issue and for pointing out the potential confusion in our terminology. Indeed, the assay kits we used refer interchangeably to Total Oxidative Status/Total Oxidative Capacity (TOS/TOC) and Total Antioxidant Status/Total Antioxidant Capacity (TAS/TAC). In our study, we specifically measured Total Oxidative Capacity (TOC) and Total Antioxidant Capacity (TAC), as commonly reported in the literature, including the previously published studies. We agree that using multiple terms may cause misunderstanding therefore, we have clarified throughout the manuscript that our measurements refer exclusively to TOC and TAC. Additionally, to maintain consistency, we revised the Discussion and Conclusions sections accordingly, explicitly using the terms TOC and TAC. Furthermore, we have modified Figure 2.

1. In Table 1, the authors provide the data on significant increase of values of TOS/TOC after 12 months of treatment with respect to baseline (457.3 at baseline vs. 589.5 at 12 mth), the same is repeated in Fig. 2. Unfortunately, these results are commented (in lines 98-99) as “significantly lower concentrations of TOS/TOC after 6 and 12 months (p=0.02 vs p=0.04; respectively)”, while in Discussion as “In our study group, we observed a significantly decreased TOS/TOC concentration after 6 months of therapy compared to baseline, followed by a clinically a significant increase after 12 months compared to the initial values”. This discrepancy must be clarified before publication, with appropriate comment concerning the increase of TOS/TOC after 12 months of treatment added. Such observation is also not in line with the Conclusions (see line 440).

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

1. The authors should provide data on “a reduction of TAS/TAC status” in Results if they use this finding as an argue in Discussion (lines 275-277). In my opinion, speculations on the relationships between lipids and TAS/TAC are too far-reaching with respect to the presented results.

Thank you for your valuable comment. We agree that presenting data clearly is essential. Although our results showed an increase in TAC after 12 months of rhGH therapy, the phrasing "a reduction of TAC status" in the Discussion was misleading. To address your concern, we have corrected the wording in the Discussion to accurately reflect the observed increase in TAC. Additionally, we have moderated our speculation regarding the relationships between lipid profiles and TAC to align more closely with our presented results.

1. The authors should explain in Introduction, why data on calcium levels are important, as they decided to provide them in the paper. Please note that point 2.1. IGF-1 measurements and Ca should be in fact 2.1.1. If only IGF-1 and Ca are considered by the authors as biochemical markers, there is probably no need to add two names of the same subsection. However, this is not in line with Table 1 in which much more biochemical parameters is reported.

Thank you for this valuable suggestion. We agree that the rationale for reporting calcium levels needs clearer justification. In the Introduction, we have now explained that calcium homeostasis is relevant in GHD patients because GH and IGF-1 play crucial roles in calcium metabolism and bone health. GH deficiency can influence calcium balance, potentially affecting bone mineral density and cardiovascular risk, hence justifying its inclusion as a biochemical parameter in our study. Furthermore, we corrected the numbering of subsections in the Results (point 2.1.1 instead of 2.1) to ensure clarity and consistency with Table 1, which indeed includes multiple biochemical parameters beyond IGF-1 and calcium.

1. In response to my previous review, the authors have stated that “Therefore, data related to the HOMA-IR index and insulin concentrations have not been included in the manuscript”. Nevertheless, in lines 166-167 and in Table 3, the authors give the data on correlation between VAI and HOMA-IR, while there is no other data concerning HOMA or insulin levels, e.g. it’s missing in Table 1. Please clarify this inconsistency.

In accordance with the reviewer’s recommendation, we have removed the data related to        HOMA-IR.

1. The same relates to correlation of TAS/TAC vs DNA/RNA in Table 3, as there is no explanation of the variable DNA/RNA anywhere in the manuscript. Moreover, this correlation is not provided for timepoint “After 12 months”. Please clarify this issue.

Thank you for pointing out this issue. Indeed, the correlation between TAS/TAC and DNA/RNA was only observed at the 6-month time point and was neither present initially nor after 12 months of therapy. As this finding lacks clinical relevance and consistency across the observation period, we considered it ambiguous and therefore did not discuss it in the manuscript. To avoid confusion, we have now clarified this point by removing the correlation from Table 3.

1. In my opinion, it would be better to show median and interquartile range instead of MIN-MAX as the latter one may be biased by even a single outlier in the group. Please consider this.

Thank you for your suggestion. We agree that presenting median and interquartile range may offer a more robust view of the data distribution, especially in larger cohorts. However, due to the small sample size in our study (n = 15), we decided to report the full range (MIN–MAX) in the tables to provide complete transparency regarding data variability. To address concerns about potential outliers, we also presented the data using box plots with medians, interquartile ranges, and full data spread, which allows for visual assessment of distribution and outliers.

1. Please also introduce the abbreviation Ca at its first use (this should be done in Introduction) and rephrase the title of this point: “IGF-1 and Ca measurements”.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

1. Please unify writing of units, e.g. “mL” (in Table 1) while “ml” (in line 360 of present version).

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented.

1. Please rephrase a sentence in line 87, as differences may be statistically significant but levels of hormones may be “significantly higher”, so it should be: “In the studied group of patients significantly higher concentration of IGF-1 …”. Next sentences in this paragraph are OK.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

 

1. There is no need to write in titles of the Tables “in the GHD group” as there is no other group included in this study. If descriptions of V0, V1 and V2 were provided, they should be used in Tables, to unify the descriptions of timepoints with Figures.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

 

1. Information concerning the incidence of obesity should be provided in Renaults, not just in Discussion. The same relates to the information about the cut-off for decreased IGF-1, however, the incidence of decreased IGF-1 has not been reported in the manuscript.

Thank you for your helpful comment. We agree that relevant clinical characteristics such as the incidence of obesity and the cut-off criteria for decreased IGF-1 should be clearly stated in the Results section. In response, we have now added the incidence of obesity observed in our study group and included the applied diagnostic cut-off value for IGF-1. Additionally, we clarified how many patients presented decreased IGF-1 concentrations at baseline.

1. In Conclusions, you should also clarify that the study shows the effects of rhGH “for adult patients with severe GHD” (line 438), not in all cases of GHD in any age group.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

1. Why the authors included section 6. Patents” that provides no information about patents?

The data were included by mistake and have been removed in accordance with the reviewer's suggestion.

1. Please remove doubled “d” in the word “noted” (line 133) and doubled “Statistically significant differences” (in lines 133-134). Please correct “TASTAC” to “TAS/TAC” in line 257. Please do not leave “minus” at the and of line 143.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented. All modifications have been highlighted in blue for clarity.

1. Please move heading of Table 2 and title of Table 4 to the same page as the whole Table.

In accordance with the reviewer’s recommendation, the necessary revisions have been implemented

 

Furthermore, due to her significant contribution to the revision of the original version of the manuscript, Małgorzata Jacewicz-Święcka has been added as an author.

Author Response File: Author Response.docx

Round 3

Reviewer 1 Report (Previous Reviewer 1)

Comments and Suggestions for Authors

Dear Authors,

thank you for making next corrections. Nevertheless, there are still some issues that should be clarified or corrected:

1. In Abstract (lines 29-30) there are two p-values concerning IGF-1, while only one p-value for ET-1 and for ADMA. Please clarify this difference- proper explanation is in Results. Please note that the information about two timepoints relates only to TOC and TAC.
2. There is still an information that TOC decreased significantly both at 6 and 12 months of rhGH therapy (lines 31-33) that if definitely not true as TOC was the highest at 12 months (see Table 1). This problem was discussed in previous review and should be corrected both in Abstract and in the main text. Are the authors sure that despite this significant increase of TOC at 12 months, all correlations of TOC with both IGF-1 and HDL are negative (please note that both IGF-1 and HDL also increased in 12 months)? What exactly means “clinically” (not statistically) significant increase of TOC after 12 months (line 258). What were the symptoms of increased TOC? Please try to explain the potential consequences of this finding as it seems to speak against long-term benefits of rhGH therapy with respect to one of the main parameters of oxidative stress. This observation must be also addressed in Discussion.
3. Please clarify what exactly means “-2 standard deviations from the age- and sex-matched reference range” (lies 94-95) – is it -2 SD from mean/median/lower limit of reference range?. Please note that IGF-1 concentrations have log-normal distribution that makes calculation of IGF-1 SD score much more difficult than simple assessment of IGF-1 with respect to reference range for the analytical kits. Please also provide the detailed information on the reference data used for calculations of IGF-1 SD scores. If the authors decided to rely on IGF-1 SDS, such information is necessary.
4. Why the authors decided to provide two references [44,45] for the sentence related only to the results of their study (line 229)? First of these references relates to GH-deficient children, while the second one to BMD – so – both are unrelated to the text of this sentence.
5. Have the Authors really observed elevated HDL cholesterol levels (Line 293) or an increase of HDL? “Elevated” suggests that they were over the upper limit of reference range. Moreover, if you measured both TAC and HDL, you should not speculate in Discussion (line 293) about association between TAC and HDL but just make conclusions from the calculated correlations.
6. Please unify brackets in equations for VAI calculations (lines 403 and 405) and provide explanation of abbreviations used in the equations. Please note that TG and HDL used for calculation of VAI, so there is no additional value in findings that VAI correlates positively with TG and negatively with HDL and there is nothing to discuss in this aspect (lines 355-361).
7. Please note that after corrections, abbreviations TAS and TOS are only on the list of Abbreviations, while they are not used in text. Instead, abbreviation WC (used in equations for VAI) is not explained at all.
8. Please try not to move titles of sections of the paper (1. Introduction, 2. Results) tot the bottom of the page, if possible.
9. Please remove empty lines in Table 3.
10. Please give the title of Table 4 at the top of the Table, not below the Table.

Kind regards,

Reviewer

Author Response

1.In Abstract (lines 29-30) there are two p-values concerning IGF-1, while only one p-value for ET-1 and for ADMA. Please clarify this difference- proper explanation is in Results. Please note that the information about two timepoints relates only to TOC and TAC.

We appreciate the Reviewer’s insightful observation regarding the unequal number of p-values reported for IGF-1, ET-1, and ADMA in the Abstract. We agree that the previous wording may have led to confusion. To address this, we have revised the sentence in the Abstract as follows:“IGF-1 concentrations increased significantly following 6 and 12 months of therapy (p = 0.0003 and p = 0.0001, respectively). These changes were accompanied by a significant decrease in endothelin-1 (ET-1) levels at 12 months (p = 0.007), as well as reductions in asymmetric dimethylarginine (ADMA) levels at both 6 and 12 months (p = 0.01 for each time point).” This revised sentence clearly indicates that the statistical significance for IGF-1 refers to two time points, while for ET-1 it refers only to the 12-month mark, and for ADMA, both time points are significant with the same p-value. We believe this updated formulation resolves the concern and aligns with the data presented in the Results section.

2. There is still an information that TOC decreased significantly both at 6 and 12 months of rhGH therapy (lines 31-33) that if definitely not true as TOC was the highest at 12 months (see Table 1). This problem was discussed in previous review and should be corrected both in Abstract and in the main text.

We thank the Reviewer for pointing out this important inconsistency. We fully acknowledge that the previous version of the manuscript incorrectly stated that TOC decreased significantly at both 6 and 12 months of rhGH therapy. As correctly noted by the Reviewer, TOC significantly decreased at 6 months but subsequently increased at 12 months, reaching its highest level during the observation period, as shown in Table 1. This issue has now been corrected in both the Abstract and the main text. The revised wording accurately reflects the observed trend: a statistically significant decrease in TOC at 6 months, followed by a statistically significant increase at 12 months compared to baseline. We appreciate the Reviewer’s attention to this matter and believe the current version presents the findings clearly and accurately.

3.Are the authors sure that despite this significant increase of TOC at 12 months, all correlations of TOC with both IGF-1 and HDL are negative (please note that both IGF-1 and HDL also increased in 12 months)? What exactly means “clinically” (not statistically) significant increase of TOC after 12 months (line 258). What were the symptoms of increased TOC? Please try to explain the potential consequences of this finding as it seems to speak against long-term benefits of rhGH therapy with respect to one of the main parameters of oxidative stress. This observation must be also addressed in Discussion.

We thank the Reviewer for raising this important point. We confirm that, despite the statistically significant increase in TOC observed at 12 months, the correlations of TOC with both IGF-1 and HDL remained negative across all time points. This was verified through statistical analysis and is reflected in the presented correlation data. The observed inverse relationships suggest that higher IGF-1 and HDL levels were associated with lower oxidative status, even though TOC itself increased after 12 months of rhGH therapy. Regarding the term "clinically significant increase" in TOC, we acknowledge that this phrase may have been misleading. No clinical symptoms related to elevated TOC were observed in the study population. We have therefore revised the text to clarify that the increase was statistically significant and may have potential biological relevance, as elevated TOC could indicate a shift toward a pro-oxidative environment. This aspect may suggest possible long-term implications of rhGH therapy on oxidative stress regulation. This observation has now been appropriately addressed in the Discussion section, where we highlight the need for further investigation to determine whether this pro-oxidative shift might offset some of the long-term metabolic benefits of rhGH treatment.

4.Please clarify what exactly means “-2 standard deviations from the age- and sex-matched reference range” (lies 94-95) – is it -2 SD from mean/median/lower limit of reference range?. Please note that IGF-1 concentrations have log-normal distribution that makes calculation of IGF-1 SD score much more difficult than simple assessment of IGF-1 with respect to reference range for the analytical kits. Please also provide the detailed information on the reference data used for calculations of IGF-1 SD scores. If the authors decided to rely on IGF-1 SDS, such information is necessary.

We thank the Reviewer for this valuable and precise observation. The phrase “-2 standard deviations from the age- and sex-matched reference range” refers to values below -2 standard deviations from the mean of the age- and sex-adjusted normative population, as provided by the reference data used for the IGF-1 SDS calculation. We fully agree with the Reviewer that IGF-1 concentrations follow a log-normal distribution, which makes the interpretation of absolute concentrations more complex. Therefore, we used standard deviation scores (SDS) for IGF-1 to allow for age- and sex-adjusted comparisons across individuals and timepoints. The IGF-1 SDS values were calculated using the reference data provided by the analytical assay manufacturer (Roche Diagnostics), based on a large normative database stratified by age and sex. We have added this information to the Materials and Methods section to clarify the source and calculation method of SDS values. We appreciate the Reviewer’s suggestion and have revised the manuscript accordingly to ensure that the description of IGF-1 SDS is both accurate and transparent.

5.Why the authors decided to provide two references [44,45] for the sentence related only to the results of their study (line 229)? First of these references relates to GH-deficient children, while the second one to BMD – so – both are unrelated to the text of this sentence.

In accordance with the reviewer’s suggestion, we have revised citation 44 to: "Verhelst J, Abs R, et al. Two years of replacement therapy in adults with growth hormone deficiency. Clin Endocrinol (Oxf). 1997;47(4):485-494. doi:10.1046/j.1365-2265.1997.3041112.x" and 45 to  "McCallum RW, Sainsbury CA, et al. Growth hormone replacement reduces C-reactive protein and large-artery stiffness but does not alter endothelial function in patients with adult growth hormone deficiency. Clin Endocrinol (Oxf). 2005;62(4):473-479. doi:10.1111/j.1365-2265.2005.02245.x", which are studies concerning adult GHD patients over a 6-month treatment period and include the assessment of IGF-1 levels during this time.

6.Have the Authors really observed elevated HDL cholesterol levels (Line 293) or an increase of HDL? “Elevated” suggests that they were over the upper limit of reference range. Moreover, if you measured both TAC and HDL, you should not speculate in Discussion (line 293) about association between TAC and HDL but just make conclusions from the calculated correlations.

Thank you for your valuable comment. In line with your suggestion, we have removed the speculative statements.

7.Please unify brackets in equations for VAI calculations (lines 403 and 405) and provide explanation of abbreviations used in the equations. Please note that TG and HDL used for calculation of VAI, so there is no additional value in findings that VAI correlates positively with TG and negatively with HDL and there is nothing to discuss in this aspect (lines 355-361).

Thank you for your valuable comment. We have unified the brackets used in the VAI equations (lines 403 and 405) to ensure consistency and clarity. Additionally, a brief explanation of the abbreviations used in the equations (WC, BMI, TG, HDL) has been added directly below the formulas. Regarding your observation on the correlation between VAI and TG/HDL: we agree with your point that these parameters are part of the VAI formula, and therefore their correlation with VAI is mathematically inherent. Consequently, we have removed the corresponding discussion from lines 355–361, as it does not provide additional interpretative value.

8.Please note that after corrections, abbreviations TAS and TOS are only on the list of Abbreviations, while they are not used in text. Instead, abbreviation WC (used in equations for VAI) is not explained at all.

Thank you for your observation. The abbreviations TAS and TOS have been removed from the list of abbreviations, as they are not used in the main text. Additionally, the abbreviation WC has now been properly explained in the section where the VAI equations are presented.

9.Please try not to move titles of sections of the paper (1. Introduction, 2. Results) tot the bottom of the page, if possible.

Thank you for your suggestion. We have reviewed the formatting of the manuscript and adjusted the layout to ensure that section titles (e.g., 1. Introduction, 2. Results) do not appear at the bottom of the page. Every effort has been made to improve the visual structure and readability of the document

10.Please remove empty lines in Table 3.

Thank you for your comment. We have carefully reviewed Table 3 and removed all unnecessary empty lines to improve clarity and formatting consistency.

11.Please give the title of Table 4 at the top of the Table, not below the Table.

Thank you for your suggestion. The title of Table 4 has been moved to the top of the table, in accordance with formatting guidelines

Author Response File: Author Response.pdf

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The topic of the paper submitted by Kościuszko et al. is interesting and clinically relevant. Unfortunately, all checked References from [27] are not existing in databases and on source pages of Journals and their titles do not refer to the problems that should be related, according to the text of Discussion. In my opinion, the manuscript should be rejected with no further proceeding.

I decided not to review a paper with a large number of not existing References.