JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03401-w (2024)

Title: Netrin-1-CD146 and S100A9-CD146 are associated with early stage of lymph node
metastasis in colorectal cancer
Version: 1 Date: 15 Jul 2024
Reviewer's report:
In this manuscript, the authors presented netrin-1-CD146 and S100A9-CD146 were associated
with early stage of lymph node metastasis in colorectal cancer (CRC), providing a novel
therapeutic target for lymphatic metastasis. Their approach that focused on sentinel lymph
nodes is interesting, but I would suggest that additional information is required to make their
conclusions more reliable.
(1) The authors demonstrated that netrin-1 highly expressed in CRC patients with lymphatic
metastasis, especially N1a+1b, compared to patients with N0 and N2. They also showed positive
correlations between netrin-1/CD146 and CD146/S100A9 and mentioned that netrin-1/CD146
and CD146/S100A9 axis might be related to lymph metastasis in CRC. They cited references
and described that these genes have been shown to be upregulated in various cancers, including
CRC, and involved in malignant behavior. However, no differences were observed in CD146
and S100A9 expression levels themselves in their results. Also, netrin-1 and CD146 levels were
not associated with CRC stage, survival, and recurrence.
As they mentioned, netrin-1 could be a potential therapeutic target to prevent the initiation of
metastasis, but I would say that only their present results may be scant to say that these axes
are related and important for CRC. Please provide some results and comments that support the
above.
(2) In their manuscript and schematic (Supplementary Fig.1), netrin-1 does not seem to play
a key role in the sentinel lymph nodes, but CD146 might be important to drive lymphatic
metastasis in the nodes. Please stain the sentinel lymph node specimens with CD146 and provide
results about expression levels and correlations like Table 5 and 6.
(3) The authors showed that high netrin-1 expression was observed in CRC patients with N1 and
could be related with lymph node metastasis. Please add lymphatic vessel invasion and venous
invasion status based on the staining results in Table 2.
(4) The authors found netrin-1 expression was high particularly in patients with N1. Is it possible
that re-analysis by each N stage would change the S100 A8/A9 results (Table 5)?
(5) How did the authors define and collect the sentinel lymph nodes? Did they use indocyanine
green or something to detect lymph flow and then use the nearest node? Please mention the
detail in method.
(6) I guess that “revealed a possible new mechanism for vascular metastasis” in abstract may be
overstated with their present results. Please modify to appropriate text.
(7) The authors stated in abstract that “The level of netrin-1 protein was positively correlated
with CD146 protein (r=0.414, P=0.001, 60 samples; r=0.430, P=0.02, 29 samples)”. However,
it would be difficult to understand the meaning of those samples from the abstract alone.
Review for 10.1186/s12876-024-03401-w (2024)

Title: Netrin-1-CD146 and S100A9-CD146 are associated with early stage of lymph node
metastasis in colorectal cancer
Version: 2 Date: 29 Aug 2024
Reviewer's report:
The manuscript has been revised almost well.  I recommend that it be accepted for publication.
Review for 10.1186/s12876-024-03404-7 (2024)

Title: Sex differences in Helicobacter pylori infection and recurrence rate among 81,754
Chinese adults: A cross-sectional study
Version: 2 Date: 05 Apr 2024
Reviewer's report:
This study aims to evaluate the prevalence of Helicobacter pylori in Gansu Province, China, and
to compare age differences between men and women in terms of HP infection rate, eradication
rate, and recurrence rate after one year.  41,751# As the authors also describe, this study can
present useful information for HP infection prevention and public health.
1. P.2 and P6. Abstract  and results
“There is a positive linear correlation between HP infection rate and age increase in women.”
Statistical analysis results show a positive correlation, but shouldn't the actual results be limited?
I think the expression be written in an age-limited manner, since at least an increase in infection
rates has not been seen after age 60?
2. P.2 Sex differences is a better keyword than sex.
3. P.5 Statistical analysis
“The variables that were statistically significant (or nearly statistically significant) by univariate
analysis were included in the multivariate logistic regression analysis.”
This is not the correct approach for the multivariate logistic regression analysis. Therefore, it
would be better to check another approach.
4. P.7 Risk factors for HP infection
Is there a correlation between age and BMI?
5. P12. The reasons for the high HP infection rate, low eradication rate, and high recurrence rate
in older females are still unclear.
What is the age of older females?
6. P12. Ohtani and Sipponen et al.
Please state reference number.
7. The sample size for each age group in Fig. 1 should be indicated.
8. Fig. 2 bar chart contains the actual number of patients. This value should be expressed as a
percentage, i.e., the total number of infected subjects in the year should be set as 100 and then
expressed as a percentage.
9. In the first place, the data in Table 1 is unnecessary because it is duplicated in Fig.
10. Please indicate page number on this manuscript.
Review for 10.1186/s12876-024-03404-7 (2024)

Title: Sex differences in Helicobacter pylori infection and recurrence rate among 81,754
Chinese adults: A cross-sectional study
Version: 2 Date: 05 Jul 2024
Reviewer's report:
General:
In this study, the authors investigated the sex differences of H. pylori infection rate and 1-year
recurrence rate in Chinese population. Authors showed a positive correlation between H. pylori
infection and age increase in women. This study was well written and may have potential.
Major comments:
1. Because there are many typos, so the manuscript needs to be carefully corrected.
2. Why did risk of H. pylori infection in female differ among generations?
3. The 1-year overall recurrence rate was 3.86%, including 2.82% in males and 5.44% in females.
This rate was too high compared with previous reports. What was the possibility of a false
negative when performing a successful or unsuccessful eradication therapy?
4. Is it common in China to use a urea breath test to diagnose H. pylori infection at health
checkups?
5. Please add information of an UBT kit used.
6. How do you deal with patients who have been examined more than once during the study
period?
7. Please calculate factors involved in re-infection in univariate and multivariate analyses.
8. Very few patients of H. pylori infection diagnosis were performed after one year. Selection
bias is also possible.
9. What causes differences in nutritional markers between with or without H. pylori infection?
10. How did you treat with patients failed eradication therapy?
11. P9: The reason why HP infection rates increase with age is unclear. Correctly, the reasons
why H. pylori infection rates decrease in younger generation is unclear.
12. Is the same result with the reports by Chinese researchers on H. pylori infection rates between
men and women?
Review for 10.1186/s12876-024-03395-5 (2024)

Title: A modified GLIM criteria-based nomogram for the survival prediction of Gastric Cancer
Patients undergoing Surgical Resection
Version: 2 Date: 19 Jul 2024
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors , please address the following points below:
-Could you please provide more clarification on the clinicopathological characteristics?
-The small sample size in this study is not just a limitation; it significantly weakens the
manuscript.
-Additionally, the modification of the GLIM with CRP does not contribute to this study due to
the small sample size."
Review for 10.1186/s12876-024-03395-5 (2024)

Title: A modified GLIM criteria-based nomogram for the survival prediction of Gastric Cancer
Patients undergoing Surgical Resection
Version: 2 Date: 20 Jul 2024
Reviewer:  Mohamed Ibrahim
Reviewer's report:
Thank you for giving me the opportunity to review this Retrospective cohort study on 210
patients undergoing radical resection for gastric cancer, divided into a development cohort (150
patients) and an external validation cohort (60 patients). The following is my main critiques:
1- A small sample size can limit the power of the study to detect significant differences and may
increase the margin of error. In addition, there is a risk of overfitting the model, which may not
perform well in different or larger populations.
2- The 5-year survival rate difference between well-nourished and malnourished patients
(97.78% vs. 85.00%) suggests a significant impact of nutritional status on survival. However,
the lack of details on other potentially influential factors (such as cancer stage, comorbidities,
and treatment variations) makes it hard to attribute differences solely to nutritional status.
3- The inclusion of CRP as an inflammatory marker significantly improved model sensitivity
and specificity. However, the study lacks a comparative analysis of other potential inflammatory
markers, limiting the understanding of whether CRP is the best choice.
Review for 10.1186/s12876-024-03395-5 (2024)

Title: A modified GLIM criteria-based nomogram for the survival prediction of Gastric Cancer
Patients undergoing Surgical Resection
Version: 4 Date: 22 Aug 2024
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
changes are done, accepted for publication
Review for 10.1186/s12876-024-03385-7 (2024)

Title: INCIDENCE AND RISK FACTORS FOR COLORECTAL CANCER IN AFRICA: A
SYSTEMATIC REVIEW AND META-ANALYSIS
Version: 0 Date: 07 Dec 2023
Reviewer's report:
Thank you for the opportunity to review the manuscript entitled “Incidence and risk factors for
colorectal cancer in Africa: A systematic review and meta-analysis”.
The authors sought to evaluate risk factors for colorectal cancer in Africa and to quantify the
incidence rate for colorectal cancer in Africa.
I have several concerns about the validity of the study design, as well as the validity of some
of the assumptions made by the authors:
1. The pooled incidence rate for colorectal cancer (CRC) in Africa is not scientifically
informative. Cancer incidences are reported by country (where possible) or extrapolated using
neighbouring country’s data in the absence of source data within a given country. The pooling of
published CRC incidence has a strong publication bias and it is not informative for continental
Africa. Secondly, African CRC incidence rates are published by the African Cancer Registry
Network and through the International Agency for Research on Cancer (Globocan). It would be
unwise to publish incidence rates without taking into consideration the Globocan data.
2. Regarding the pool incidence rate. At best, the authors can claim that it is the pooled
CRC incidence rate based on publications from Egypt, South Africa, Tunisia, Morocco
and Zimbabwe. However, pooling incidence rates the assumption that the populations are
homogeneous. This assumption is not met. The heterogeneous nature of African populations in
terms of genetics and environmental exposures is vast. Northern Africa and sub-Saharan Africa
can not be grouped together for analysis of this nature. Additionally, South Africa and Zimbabwe
are not representative of sub-Saharan Africa.
3. In terms of statistical methodology, odds ratios and relative risk are not the same measure and
often can not be directly equated.
4. Perhaps would be a better approach to perform the meta-analysis on studies from North
Africa to quantify the pooled incidence rates and then compare the incidence rates reported on
Globocan. Thereafter, meta-analyse the risk factors and report on its findings. However, as it
stands, the findings in this manuscript are misleading. The source data are not representative
and the methodologies are flawed.
Review for 10.1186/s12876-024-03385-7 (2024)

Title: INCIDENCE AND RISK FACTORS FOR COLORECTAL CANCER IN AFRICA: A
SYSTEMATIC REVIEW AND META-ANALYSIS
Version: 0 Date: 06 Jan 2024
Reviewer:  Alfred Jatho
Reviewer's report:
The study was appropriately designed, conducted and analyzed using a suitable meta-analysis
model – the DerSimonian and Laird method of random-effects model that accounts for the
heterogeneity across the included studies. The authors compared their findings well with the
current findings in the field suggested the implications of the findings for future colorectal cancer
research and discussed the potential applications. The study conclusion is supported by the data
presented and stated some of the major limitations of the study.
However, in the method, the authors stated that the odds ratio was considered as an estimate of
relative risk for the CRC risk factors and the Meta-analysis was performed to report proportion,
relative risk, and their respective pooled estimate. Also, in table two showing characteristics of
all studies investigating RFs of CRC, lower-evidence studies such as cross-sectional studies, and
studies that may not report odds ratio or relative risk such as case series and others that had no
study design stated were included. In this situation the authors need to clarify in the data analysis
section which specific study designs were considered for computing the pooled estimate of the
CRC incidence, and which specific study designs were considered for computing the pooled
estimate of the CRC RR / ORs. This is because the difference in the strength of evidence and
which study designs are appropriate for estimating incidence or RRs/ORs may grossly affect
the overall effect size. Case-control studies cohort studies and RCTs are more suitable for the
inclusion of meta-analysis to provide the pooled RR. For cross-sectional studies to be included
in the meta-analysis, it is better if it was an analytical cross-sectional study.
Finally, minor English language editing is needed. For example, the authors need to remove the
full stop in the title of the study and correct the spelling of “DerSimoniane” to “DerSimonian”,
among others.
Review for 10.1186/s12876-024-03385-7 (2024)

Title: INCIDENCE AND RISK FACTORS FOR COLORECTAL CANCER IN AFRICA: A
SYSTEMATIC REVIEW AND META-ANALYSIS
Version: 0 Date: 12 Jan 2024
Reviewer's report:
The paper is well written, and I suggest that it should be accepted for publication after some
editorial work has been done on the manuscript.
Review for 10.1186/s12876-024-03400-x (2024)

Title: Genetic estimation of causalities between educational attainment with common digestive
tract diseases and the mediating pathways
Version: 2 Date: 04 Jul 2024
Reviewer's report:
1.  The study primarily used data from European ancestry populations, which may limit the
generalizability of findings to other ethnic groups.
2. After applying the Benjamini-Hochberg adjustment for multiple testing, some of the estimated
causal effects (e.g., WHR on peptic ulcer and fasting insulin on cholelithiasis) became only
borderline significant. This suggests that these specific findings may be less robust and require
further validation.
3. The direct impact of education on non-alcoholic fatty liver disease (NAFLD) weakened
towards null when adjusting for intelligence and cognition. However, the authors note this
could be due to limited sample size, as the combined sample for NAFLD was less than 4,000
individuals .
4. Inability to account for all potential confounders; While Mendelian randomization helps
minimize confounding, it cannot completely rule out all potential confounding factor
Review for 10.1186/s12876-024-03400-x (2024)

Title: Genetic estimation of causalities between educational attainment with common digestive
tract diseases and the mediating pathways
Version: 2 Date: 05 Jul 2024
Reviewer's report:
Review report:
The study by Wang et al. aimed to determine the independent causal effects of education on
six digestive tract diseases, while adjusting for intelligence and cognition. Authors employed
Mendelian Randomization (MR) to explore these effects and identified five significant
mediators: BMI, WHR, body fat percentage, fasting insulin, and major depression. The study
utilized large sample sizes from the FinnGen Study and UK Biobank to ensure robustness of
their MR analyses. Their findings demonstrated that education significantly influences digestive
tract health, independent of cognitive factors. Education was shown to have a direct protective
effect on these diseases, with the identified mediators explaining part of this relationship. The
study emphasizes the crucial role of educational attainment in reducing the risk of digestive
tract diseases and suggests that targeting these mediators could further improve gastrointestinal
health outcomes. Overall, this study provides robust evidence supporting the independent role
of education in gastrointestinal health and highlights the importance of addressing educational
disparities as a strategy to mitigate the prevalence and burden of digestive tract diseases. Overall,
the study findings are interesting and adds a significant value to public health research, however
I have few questions and suggestions to improve further on this:
Major comments:
1. Gender-Specific Analysis: Has the analysis been performed in a gender-dependent fashion?
This could reveal gender-specific causality estimates of education on specific disease outcomes.
2. Gastrointestinal Cancers: It would be interesting to examine the causal associations of
education with gastrointestinal cancers, such as stomach, liver, and pancreas cancer.
3. Selection of Modifiable Risk Factors: How did the authors choose the 21 modifiable risk
factors included in the analysis is not well documented in the manuscript.
4. Additional Mediators: Do the authors have information on oral health and food choices as
mediators? Investigating the effect of education on oral health or food preferences could provide
insights into preventive actions for digestive tract diseases, as these lifestyle factors can be
modified to prevent the occurrence of these diseases.
5. The details of various statistical analyses should be explained in simpler terms to simplify
their purpose.
Minor comments:
1. There are spelling mistakes in a few places in the manuscript. Please check and correct them
carefully.
Review for 10.1186/s12876-024-03390-w (2024)

Title: Genetic evidence causally linking gastroesophageal reflux disease to cholecystitis#A two-
sample Mendelian randomization study
Version: 0 Date: 18 Feb 2024
Reviewer's report:
The  paper is quite well written.  The article covers a very interesting and current topic.
Nevertheless, in my opinion, some parts need to be improved, I have some comments:
1) Conclusion: Our study demonstrated a positive correlation between GERD and the likelihood
of developing cholecystitis. These findings may serve as a fundamental basis for comprehending
the intricate interplay between GERD and cholecystitis. However, additional investigations are
warranted to elucidate the precise underlying mechanisms of this plausible causal relationship.
Abstract might be beneficial to include a sentence  that briefly summarizes the key findings of
the study. This can provide readers with a quick overview of the research.
2) In this study, we conducted a two-sample MR study utilizing single SNPs obtained from
genome-wide association studies linked to GERD as IVs, in order to examine the causal impact
of GERD on cholecystitis risk, marking the first such attempt. Please, improve the description
of study aim and underline the novelty of the article.
3) 3. Results
3.1 Detail Information of the Included Instrumental variables (IVs)
This study incorporated a total of 77 independent SNPs from GWASs on GERD as IVs. All
these SNPs were found to be significantly associated with GERD at the genome-wide level
(p<5×10#8) and possessed F-statistics greater than 10, indicating that none of the SNPs were
weak instrumental variables. Supplementary Table S1  ... Please, improve  and clarify this part,
in particular underline the inclusion and the exclusion criteria.
4) 4. Discussion
A two-sample MR analysis was conducted to evaluate the causal association between GERD
and cholecystitis in this study. Our results indicated that genetically predicted GERD was
significantly associated with a higher risk of cholecystitis. The discussion section needs to be
improved.  It could be interesting to record the aim of the study. It is necessary to be more
concise in the presentation of the facts, clarifying the results obtained and comparing them with
previous or similar studies. However, it is interesting to answer the questions that arise from
these results, backed up by published literature.
Review for 10.1186/s12876-024-03390-w (2024)

Title: Genetic evidence causally linking gastroesophageal reflux disease to cholecystitis#A two-
sample Mendelian randomization study
Version: 1 Date: 22 Jun 2024
Reviewer's report:
The topic is interesting and the paper is quite well written.  The article covers a very interesting
and current topic. I think that the manuscript has been improved in agreement with previous
reviewers' comments. In my opinion, several parts  were improved, I have few comments:
1) 5. Conclusions
In summary, our MR analysis establishes a causal relationship between GERD and cholecystitis,
particularly an increased risk of cholecystitis in patients with genetically-predicted GERD.
However, further studies are required to elucidate the fundamental mechanisms underlying this
causal association. I suggest to improve this paragraph and underline the novelty of the sudy
and the possible clinical implications
Review for 10.1186/s12876-024-03390-w (2024)

Title: Genetic evidence causally linking gastroesophageal reflux disease to cholecystitis#A two-
sample Mendelian randomization study
Version: 2 Date: 23 Aug 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: The revised manuscript significantly improved and the authors
efficiently incorporated all the changes and additions required by revisors. The critical revision
and implementation in the Discussion section are pertinent and self-explanatory. The manuscript
is essentially ready for publication (after a few minor cosmetic edits)
ADDITIONAL REQUESTS/SUGGESTIONS:
I would encourage the authors to critically read the abstract one last time and eventually expand
conclusions. The format of the n value is incorrect and should be similar to the text. Ref. nr.47
can be edited to avoid a title in all capital letters.
Review for 10.1186/s12876-024-03397-3 (2024)

Title: Efficacy and safety of Endoscopic nasobiliary drainage versus percutaneous transhepatic
cholangial drainage in the treatment of advanced hilar cholangiocarcinoma: a systematic review
and meta-analysis
Version: 6 Date: 27 Apr 2024
Reviewer:  Yang Liu
Reviewer's report:
As a meta-analysis article, this article is well written and the selected literature is convincing.
However, the article still needs to address some underlying logical issues. For example,
why choose the comparison between ENBD and PTCD instead of ERCP, please explain it
appropriately. In fact, during the surgical process of ENBD and ERCP, it is difficult for the
guide wire to pass through the site of the bile duct tumor. The guide wire that can pass through
the tumor will inevitably have friction with the tumor or even penetrate the tumor to drain bile,
which may lead to distant metastasis of the tumor in the future. Of course, this is not related
to this article, it is only mentioned briefly. In addition, some parts of this article are confusing,
such as lines 81-83, where bile should be excreted from the body rather than into. Lines 288 to
292, ENBD leads bile out of the body, so why is it internal drainage?
Review for 10.1186/s12876-024-03397-3 (2024)

Title: Efficacy and safety of Endoscopic nasobiliary drainage versus percutaneous transhepatic
cholangial drainage in the treatment of advanced hilar cholangiocarcinoma: a systematic review
and meta-analysis
Version: 8 Date: 28 May 2024
Reviewer:  Yang Liu
Reviewer's report:
1. Is the author not familiar with PTCD and ENBD? The guide wire of PTCD does not pass
through the tumor, while the guide wire of ENBD needs to pass through the tumor. The author's
description in 233-241 is very confusing and needs to be revised.
2. Why does ENBD expel bile from the body and enter the external collection bag  compared
to PTCD, it may reduce the incidence and severity of postoperative electrolyte imbalance and
digestive function damage in patients? PTCD also has an external collection bag, and the method
of handling bile can be the same as ENBD, such as collecting bile and taking it orally.
Review for 10.1186/s12876-024-03397-3 (2024)

Title: Efficacy and safety of Endoscopic nasobiliary drainage versus percutaneous transhepatic
cholangial drainage in the treatment of advanced hilar cholangiocarcinoma: a systematic review
and meta-analysis
Version: 9 Date: 16 Jul 2024
Reviewer:  Yang Liu
Reviewer's report:
After modification, it can be published
Review for 10.1186/s12876-024-03397-3 (2024)

Title: Efficacy and safety of Endoscopic nasobiliary drainage versus percutaneous transhepatic
cholangial drainage in the treatment of advanced hilar cholangiocarcinoma: a systematic review
and meta-analysis
Version: 9 Date: 27 Jul 2024
Reviewer's report:
1. The description of PTCD in the introduction should not be integrated into the second
paragraph; it should be described separately in a new paragraph.
2. The introduction section's logical flow and language expression need further adjustment and
revision.
3. In the first paragraph of the discussion section, the sentence "In contrast, PTCD is less difficult
to perform, but its success rate is largely dependent on the condition of the bile duct, with higher
success rates when the diameter of the bile duct exceeds 0.4 cm." inaccurately describes the
situation. For HCC patients, the bile ducts are generally dilated, and it is rare for the bile duct
diameter to be less than 0.4 cm. Thus, the description in this sentence is inappropriate.
4. The manuscript describes PTCD as more effective than ENBD, yet in the Conclusions section
(line 55 and 250), the authors state that "there was no significant difference in TBIL change after
drainage between the ENBD group and the PTCD group," which is confusing.
5. The logical flow in some parts of the manuscript is somewhat disorganized; revising the
manuscript for a clearer logical structure is recommended.
6. The language throughout the manuscript needs further refinement.
Review for 10.1186/s12876-024-03397-3 (2024)

Title: Efficacy and safety of Endoscopic nasobiliary drainage versus percutaneous transhepatic
cholangial drainage in the treatment of advanced hilar cholangiocarcinoma: a systematic review
and meta-analysis
Version: 9 Date: 28 Jul 2024
Reviewer's report:
The author has made revisions to the relevant issues as required, but the "Conclusion" section
still needs to be improved to highlight its guiding value for clinical practice. At present, the
author only provides a brief summary of the results in the conclusion section, and cannot see
what the  clinical significance is. The main conclusion of meta-analysis is to provide guidance
for the selection and implementation of clinical measures, which is crucial.
I have no other suggestions for revision and suggest publishing this article.
Thank you again for the author's patient response.
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 1 Date: 26 Jun 2024
Reviewer:  Mona Hegazy
Reviewer's report:
1. All the authors in Guangxi University China, and presenting data from NHANES!!!
2. Now its MASLD no  more NAFLD
3. In exclusion; (male average daily drinking > 20g, female average daily drinking > 10g) as
you define, but the MASLD” NAFLD” less than 20gm in women and 30 in men, and between
20-50nin women and 30-60 in men is MetALD, so now with new guidelines must respect those
4. VCTE examination must mentioned using which machine, and the classification built in about
Cap and kpa reading (S0-S3 &F0-F4) not like you mention ( A quick, non-invasive test called
VCTE has proven to be useful in determining the extent of liver steatosis and fibrosis[29]. In the
case of VCTE detection, fibrosis is defined as liver stiffness measurement (LSM) of 8.0 kPa or
above, and steatosis is determined by controlled attenuation parameter (CAP), where a steatosis
threshold is CAP > 274 dB/m [30, 31]) fibrosis considered significant if equal or above 8, but
from 5.8-7.9 had fibrosis but non-significant, some VCTE machine consider above 218 presence
of steatosis, and 274 is S2 not only from274, by this you excluded a lot of MASLD participants
5. I think with the significant role of diabetes and prediabetes on NHR, and the high percentage
of their presence you can’t grantee the pure MASLD role in NHR results
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 1 Date: 01 Jul 2024
Reviewer's report:
The present study is a retrospective analysis of a large data set from a nationally conducted
survey in the US (as authors stated).
The large number of NAFLD patients (4602 patients) and its dependence on VCTE for
diagnosing NAFLD give this study a strong impact. However, few points should be addressed:
Study design:
- Kindly replace "materials and methods" with "Patients and methods".
- It was mentioned that the study is based on a US population surveys and that the data set is
from 2017 - 2020referred as ref. (25). however, this reference is since 2012. Kindly revise.
- Before doing VCTE or any other test for MAFLD, we need an abdominal ultrasound first.
Kindly correct this. Abdominal US is the first step in suspecting the presence of NAFLD.
- In the calculation of the ratio; kindly add that HDL was measured while fasting or not. Also,
what was the reference value of this ratio? and what was meant by the last sentence in this
section?
- In section 2.4 Covariates: If the ration is affected by all these variables it would not be an
accurate test for diagnosis. Also, this should had been stated in the introduction.
Results:
- What is meant by the abbreviation PIR?
- There is a repetition of an error sentence in many areas of the manuscript. Kindly explain and
correct this.
- Suddenly from section 3.2 there is a talk about "models"! there were not mention of these
models before. How were those formed and according to what?
-  Before interpreting these results; validation of this ratio in a normal healthy cohort should be
done. OR, inclusion of a control group without NAFLD. This is important because as stated in
the manuscript this ration can be affected by many other factors and conditions.
Discussion:
Discussion should explain how this ratio can help in the management of NAFLD, and how does
it differ from other scores and ratios present in the literature.
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Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 2 Date: 18 Jul 2024
Reviewer's report:
FOR AUTHORS ,THE IDEA IS GOOD AND COULD SOLVE THE PROBLEM OF MASLD
PREDICTION FROM THE GENERAL POPULATIONS ,IT IS GOOD STUDY
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 2 Date: 26 Jul 2024
Reviewer's report:
Summary:
This is an analysis of NHANES data looking at the association between neutrophil to HDL ratio
(NHR) and MASLD/fibrosis. The authors found a statistically significant positive association
between NHR and MASLD and a U-shaped relationship between NHR and fibrosis. The
association remained significant even after adjustment for covariates.
This manuscript needs substantial editing for language, clarity, and typos.
Comments:
• Editing the English for language and clarity is needed for the entire manuscript.
• Introduction: would avoid the terminology “unhealthy lifestyles” as it is stigmatizing
• Methods: what is the primary outcome? MASLD? MASLD + fibrosis? This should be clearly
stated in the Methods.
• Methods (data and sample source): editing for clarity needed. What does “We excluded the data
lack of NHR” mean? You excluded participants for whom NHR was unable to be calculated?
• Methods (definition of MASLD): probably a typo, but the numbers 1 through 5 are listed twice.
Would proofread carefully.
• Methods: “Liver fibrosis” threshold of 8.2 kPa should be described as “clinically significant
fibrosis” as patients with LSM under this could have fibrosis too.
• Methods (calculation of NHR): “Every blood sample was taken with the stomach empty”
should be revised to “blood samples were obtained after an X hour fast.” You do not need to
say “NHR is the independent variable”—that is clear from the Methods. You do need to specify
your outcomes as above.
• Methods (covariates): would describe PIR categories when you introduce PIR.
• Methods: are you using sex at birth or gender identity? Would change terminology to “sex”
if using sex at birth.
• Table 2: title should read “MASLD” not “NAFLD”
• Table 3: title should read “MASLD” not “MSALD”
• Table 5: title should read “MASLD” not “MSALD”
• Results (subgroup analysis): what is “hepatic fibers”?
• Discussion: would emphasize that one advantage of NHR is the fact that the labs needed to
calculate it are routinely collected in patients with and without liver disease
• Discussion: would expand on the idea that the cross-sectional design is a limitation.  I agree,
mostly for the reason that where NHR would be helpful is in predicting future development of
MASLD. If we are wondering if a patient currently has MASLD, we would do a Fibroscan or
imaging instead of relying on a non-invasive marker that is less accurate. But, if NHR in patients
without MASLD was associated with future development of MASLD, then NHR could have a
role in clinical practice (for example, patients with elevated NHR could be put on a screening
pathway for MASLD).
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 2 Date: 28 Jul 2024
Reviewer's report:
Thank you for addressing all the questions and doing most of the corrections needed. However;
1) The references section in the revised manuscript did not show the corrected ref as stated in
the response letter. Kindly add the corrected ref in the references section.
2) The title should state the country to which these data belong in the title of the work.
3) Authors have to state that these results are based on a health survey of general population, and
without abdominal US one cannot differentiate between advanced stages of fibrosis and frank
cirrhosis, also how can we assess for presence or absence of portal hypertension or ascites. The
primary definition of MASLD is based on the US. This point of weakness should be mentioned
in the discussion and put in the recommendations for further research.
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 3 Date: 15 Aug 2024
Reviewer's report:
IT IS GOOD IDEA , I THINK THIS RATIO IS GOOD INDICATOR AND SIMPLE FOR
APPLICATIONS AND DESERVE A PUBLICATION FOR PHYSICIANS TO APPLY FOR
THEIR PATIENTS
Review for 10.1186/s12876-024-03394-6 (2024)

Title: Association between neutrophil-to-high-density lipoprotein cholesterol ratio and
metabolic dysfunction-associated steatotic liver disease and liver fibrosis in the US population:
a nationally representative cross-sectional study using NHANES data from 2017 to 2020
Version: 3 Date: 15 Aug 2024
Reviewer's report:
This article has been revised satisfactorily according to my suggestions. The clarity of the
English has improved.
In the Introduction, there is a typo, "chronic liver worldwide" should read "chronic liver diseases
worldwide."
Would rephrase "with increasing incidence attributed to the proliferation of unhealthy habits
like high-energy diets and lack of physical activity" to "with increasing incidence attributed to
high-energy diets and lack of physical activity."
Review for 10.1186/s12876-024-03386-6 (2024)

Title: Causal relationships between neuropsychiatric disorders and nonalcoholic fatty liver
disease: A bidirectional Mendelian randomization study
Version: 2 Date: 22 Apr 2024
Reviewer:  Fuquan Zhang
Reviewer's report:
The authors performed an MR analysis to explore bidirectional causal associations between
NAFLD and mental disorders. They reported the causal effect of NAFLD on anxiety disorder
and the causal effect of MDD on NAFLD. These findings may help understand the genetic
relationships between NAFLD and mental disorders. I have some recommendations for the
authors:
1. In the abstract, the authors should state clearly which kind of results were reported. Otherwise,
readers have difficulty knowing whether the results were from the discovery stage or the
replication stage. For anxiety disorder, several different names were used, including “anxiety”
and “anxiety disorders”, please unify them into one.
2. Some datasets for mental disorders were not the largest ones available, including
schizophrenia and bipolar disorder. The authors did not include some major mental disorders in
the study, like insomnia. Please discuss the limitations. Please double-check whether the MDD
dataset contained 246,363 patients and 561,190 controls. The publicly available MDD dataset
did not contain the participants from 23andMe, therefore, did not have all these samples.
3. The manuscript can discuss the causal associations between mental disorders and other
diseases, including cardiovascular diseases and diabetes (PMID: 38395927, 36937092,
38490691), since these diseases may partially explain the associations between NAFLD and
mental disorders. Some confounding factors need to be discussed, like education and income,
given that they are vital risk factors for mental disorders (PMID: 38440407, 38007229).
Review for 10.1186/s12876-024-03386-6 (2024)

Title: Causal relationships between neuropsychiatric disorders and nonalcoholic fatty liver
disease: A bidirectional Mendelian randomization study
Version: 2 Date: 18 Jul 2024
Reviewer's report:
The authors attempted to evaluate the association between NAFLD and psychiatric disorders.
There are some concerns that need to be addressed;
1. We need to focus on NAFLD patients as organic diseases, and we need to consider more
confounding factors to improve the robustness of the results. Multivariate MR can be used to
address this issue.
2. page 13 "Genes that predict NAFLD on neuropsychiatric disorders", what does this mean? I
recommended that a professional language editing agency handle the whole text.
3. I noticed that the abstract introduced reverse MR, which I did not find in the results section.
Reverse MR can greatly resolve the direction of causal association.
4. The discussion should provide a detailed discussion of positive/interesting results and analysis
of potential mechanisms.
Review for 10.1186/s12876-024-03386-6 (2024)

Title: Causal relationships between neuropsychiatric disorders and nonalcoholic fatty liver
disease: A bidirectional Mendelian randomization study
Version: 3 Date: 07 Aug 2024
Reviewer:  Fuquan Zhang
Reviewer's report:
The authors have addressed my comments in a satisfactory manner.
Review for 10.1186/s12876-024-03373-x (2024)

Title: Overweight and vitamin D deficiency are common in patients with irritable bowel
syndrome. A cross-sectional study
Version: 3 Date: 16 Jun 2024
Reviewer's report:
1. Please change "Albeit vitamin D supplements in 21.5% of IBS patients, 23.65% had vitamin
D levels <50 nmol/L, compared with 26.0% in controls (p=0.720)" to "Despite 21.5% of IBS
patients taking vitamin D supplements, 23.65% of them had vitamin D levels below 50 nmol/L,
which is similar to the 26.0% observed in the control group (p=0.720)."
2. Please change "dietary supplementals" to "vitamin supplements".
3. The age difference between IBS patients and controls is a confounding factor that might
influence the results. The study does not account for potential seasonal variations in vitamin D
levels, which could confound the results. These are limitations that should be mentioned and
discussed.
4. The presentation of data could be improved by including more visual aids, such as box plots,
to illustrate key findings and dispersion of results.
5. "Other studies have found lower levels of vitamin D in IBS patients compared with non-
IBS patients [64]." - In addition to this, it's relevant to highlight that common environmental
exposures, such as air pollutants and microbial exposure, have also been linked to IBS
development, gut dysbiosis (citation: pubmed.ncbi.nlm.nih.gov/38699957), and reduced levels
of vitamin D and other micronutrients.
6. The conclusion does not seem to follow from the rest of the findings. The authors write
that, "In conclusion, the high degree of comorbidity and extraintestinal symptoms in IBS
may be associated with vitamin D deficiency and/or overweight [23,24,43] and may thus not
solely be directly related to IBS per se." This statement is an overreach as it is suggesting a
causative relationship that is not fully supported by the cross-sectional study design, which
only identifies associations, not causation. Moreover, the conclusion should more accurately
reflect the findings by acknowledging the complexity of IBS and the multifactorial nature of
its symptoms, including the potential contributions of nutritional deficiencies and comorbid
conditions. A more appropriate conclusion would emphasize the need for further research
to explore these associations in greater detail and consider longitudinal studies to establish
causative links.
7. Why are there two clinical registration numbers, "ClinicalTrials.gov, NCT05192603 (Date of
registration 11/29/2021) and NCT03306381 (Date of registration 09/18/2017), respectively"?
Review for 10.1186/s12876-024-03373-x (2024)

Title: Overweight and vitamin D deficiency are common in patients with irritable bowel
syndrome. A cross-sectional study
Version: 5 Date: 10 Jul 2024
Reviewer's report:
1. There are still several instances of language and grammatical errors. E.g., the term
'overweighted' is wrong, "In conclusion, IBS patients were often overweighted or obese with
low vitamin D levels". Instead it should be "In conclusion, IBS patients were often overweight
or obese with low vitamin D levels." Similarly, instead of writing "Participants both patients
and controls completed ...", it should be simply "Both patients and controls completed ..." Please
perform a close copyediting of the entire manuscript.
2. How was the sample size for the control and study group decided? The small control group
(n=50) compared to the IBS group (n=260) reduces the statistical power of the study and
increases the risk of Type II errors. This imbalance also complicates the generalizability of the
findings.
3. "The age (p=0.094), sex distribution (p=0.257), weight (p=0.862), education (p=0.488),
smoking habits (p=0.984), alcohol intake (p=0.661), or physical activity (p=0.636) were equal
between the two IBS cohorts" - Where are these results reported in the tables? How was 'physical
activity' quantified?
4. "We have previously published that several IBS patients have poor dietary habits [62]" - What
about the use of 'self-prescribed' elimination diets?
5. "The small control cohort, with controls from hospital staff and students is a limit ..." - It
should be 'limitation' and not 'limit'.
6. The statement "However, only validated questionnaires were used, to minimize confounding
factors" is problematic for several reasons. The validation of a questionnaire ensures that the tool
measures what it is intended to measure reliably and accurately. However, it does not inherently
minimize confounding factors. Confounding factors are external variables that can affect the
relationship between the independent and dependent variables. To minimize confounding,
proper study design and statistical control methods are required.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 1 Date: 29 May 2024
Reviewer's report:
Thanks for the effort to  take up an important and common problem of liver abscess for further
study. My suggestions  are -
1.  It will be important to add the size of abscess as well at  the time when treatment was initiated
as larger abscess are more likely to cause sepsis and other complication.
2. In the result - provide a table with number of patients who had - septic shock, required ICU
admission,  blood culture  positive and patients who underwent aspiration and drainage
3.  The factors which came positive in multivariate analysis  are obvious factors for severity of
sepsis  or reflect sepsis in any patient .
4. Authors should suggest how these findings can be utilized in  identification of patients with
potential complications and can guide in making management decisions.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 4 Date: 05 Jun 2024
Reviewer's report:
Since the last version the manuscript has been somewhat revised and corrected according to the
reviewers' suggestions.
However  , the title section and abstract still appears to be wrong in some points, since the authors
did not statistically examined the risk factors for developing PLA from a a general population
but they indeed investigated the most relevant risk factors for clinical severity and blood cultures
positivity from a cohort of pts who already had been diagnosed with this infection.
Apart from this minor but essential correction, I suggest the publication of the work in BMC
Gastroenterology journal.
Please you will find the correction highlited in yellow and italic in the text.
I also suggest to the editor to revise the subtitles in the tables since the English seems to be
quite  poor.
Kind regards,
The reviewer