JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03264-1 (2024)

Title: Medical radiation exposure in inflammatory bowel disease: an updated meta-analysis
Version: 4 Date: 11 May 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: In this last versione of the manuscript, the authors responded
adequately to my previous concerns
They made changes in the manuscript accordingly
This version of the paper sounds definitely better
ADDITIONAL REQUESTS/SUGGESTIONS:
no
Review for 10.1186/s12876-024-03254-3 (2024)

Title: Sex difference in the associations among risk factors with gastroesophageal reflux disease
in a large Taiwanese population study
Version: 1 Date: 20 Feb 2024
Reviewer's report:
This study mainly studied the prevalence and related risk factors of GERD in Taiwan, and further
analyzed the gender differences among GERD patients, and also proved that gender was not an
independent factor affecting the occurrence of GERD. It was a large sample and comprehensive
study, and I appreciate the authors the how they prepare the study. But the manuscript still has
some shortcomings.
1. The first paragraph of the introduction, lines 11-13, "Symptoms of GERD... More than in
females "citation was missing.
2. Please check the citations 7 and 8 were quoted correctly
3. In the results part, it was found that there was no age difference between the sexes in GERD
patients, but in the discussion section, how do you come to the conclusion "as women tend to
live longer than men, this may explain the higher prevalence of GERD."? so please check again
the casual inference in the discussing part was right.
4. Your manuscript needs careful editing and particular attention to English grammar, spelling,
sentence structure and punctuation mark.
Review for 10.1186/s12876-024-03254-3 (2024)

Title: Sex difference in the associations among risk factors with gastroesophageal reflux disease
in a large Taiwanese population study
Version: 1 Date: 20 Feb 2024
Reviewer's report:
1. Please add China behind Taiwan.
2. Introduction. The authors described that “Gastroesophageal reflux disease (GERD) is a
common global health issue, with a prevalence of approximately 10% to 20% in Western
countries and less than 5% in Asia”. In general, the reported prevalence of GERD in Asia
is lower that of western countries, but not all are below 5% (i.e. a meta-analysis showed the
rate being 12.5% in China [doi: 10.3877/cma.j.issn.1674-6899.2015.01.011]), please make a
comprehensive search and provide the accurate rates range.
3. Introduction.  The authors described that “Symptoms of GERD such as heartburn,
regurgitation, belching, fullness sensation affect females more than males, while pathologic
changes are more common in males than in females”. The citation is missing, please also
described the accurate data.
4. Introduction. The authors should shorten or delete the second paragraph since it is unrelated
to GERD.
5. Introduction. The third paragraph. The authors described that “Nevertheless, few studies
have investigated sex differences in the risk factors associated with GERD”. Please provide
the detailed results and limitation of these studies to validate your further study on the same
direction.
6.Materials and methods. Please describe the method for the choose of study population for the
Taiwan Biobank and your GERD study. In which time period and how many cases are included
in the Taiwan Biobank? How do you choose participants from the Taiwan Biobank for the GERD
study? Please also provide your detailed GERD questionnaire and make a clear definition of
questionnaire-based GERD.
7. Statistical analysis. Why symptoms are not be compared and included for multivariable
analysis?
8. Discussion. The first paragraph. The authors described that “Furthermore, there were sex
differences in the risk factors associated with GERD, and older age, DM, smoking history, and
low HDL-C were more closely related to GERD in the females than in the males”. It is a little
bit different from Table 5, please modify your description accordingly.
9. Discussion. The second paragraph. The authors described that “Therefore, as women tend to
live longer than men, this may explain the higher prevalence of GERD”. According to Table
3, there is no significant difference for age between male and female, the description needs to
be modified.
10. Discussion. The interpretation for the relation of older age, DM, smoking, and low HDL-
C level with GERD is farfetched. Please describe more carefully and, if possible, provide some
actual analysis.
Review for 10.1186/s12876-024-03254-3 (2024)

Title: Sex difference in the associations among risk factors with gastroesophageal reflux disease
in a large Taiwanese population study
Version: 2 Date: 07 Mar 2024
Reviewer's report:
Thanks for your efforts in revising this manuscript, the concerns I proposed were all properly
addressed. but there are still has two problems:
1. one p value in table 4 was missing, please complete the form.
2.Please indicate the table utilized in "Association of factors with GERD in different sex using
multivariable logistic regression analysis "of the result part.
At last, please conduct a comprehensive review of the article, ensuring the coherence of its logic,
accuracy of citations, and conciseness of the language.
Review for 10.1186/s12876-024-03254-3 (2024)

Title: Sex difference in the associations among risk factors with gastroesophageal reflux disease
in a large Taiwanese population study
Version: 2 Date: 10 Mar 2024
Reviewer's report:
1.Please add China behind Taiwan.
Not revised.
2.Introduction. The authors described that “Gastroesophageal reflux disease
(GERD) is a common global health issue, with a prevalence of approximately
10% to 20% in Western countries and less than 5% in Asia”. In general, the
reported prevalence of GERD in Asia is lower that of western countries, but not
all are below 5% (i.e. a meta-analysis showed the rate being 12.5% in China [doi:
10.3877/cma.j.issn.1674-6899.2015.01.011]), please make a comprehensive
search and provide the accurate rates range.
Revised.
3.Introduction.  The authors described that “Symptoms of GERD such as
heartburn, regurgitation, belching, fullness sensation affect females more than
males, while pathologic changes are more common in males than in females”. The
citation is missing, please also described the accurate data.
Revised.
4.Introduction. The authors should shorten or delete the second paragraph since it is
unrelated to GERD.
Revised.
5.ntroduction. The third paragraph. The authors described that “Nevertheless, few
studies have investigated sex differences in the risk factors associated with
GERD”. Please provide the detailed results and limitation of these studies to
validate your further study on the same direction.
Revised.
6.Materials and methods. Please describe the method for the choose of study
population for the Taiwan Biobank and your GERD study. In which time period
and how many cases are included in the Taiwan Biobank? How do you choose
participants from the Taiwan Biobank for the GERD study? Please also provide
your detailed GERD questionnaire and make a clear definition of questionnaire
based GERD.
Revised.
7.Statistical analysis. Why symptoms are not be compared and included for
multivariable analysis?
Not revised due to the limitation in the design of the study, which is a major loss.
8.Discussion. The first paragraph. The authors described that “Furthermore, there
were sex differences in the risk factors associated with GERD, and older age, DM,
smoking history, and low HDL-C were more closely related to GERD in the
females than in the males”. It is a little bit different from Table 5, please modify
your description accordingly.
Revised.
9.Discussion. The second paragraph. The authors described that “Therefore, as
women tend to live longer than men, this may explain the higher prevalence of
GERD”. According to Table 3, there is no significant difference for age between
male and female, the description needs to be modified.
Revised.
10.Discussion. The interpretation for the relation of older age, DM, smoking, and low
HDL-C level with GERD is farfetched. Please describe more carefully and, if
possible, provide some actual analysis.
Not revised appropriately.
Review for 10.1186/s12876-024-03251-6 (2024)

Title: Risk Factors for Delayed Colorectal Postpolypectomy Bleeding: A Meta-Analysis
Version: 2 Date: 12 Nov 2023
Reviewer's report:
This manuscript showed a meta-analysis of risk factors for delayed colorectal post-polypectomy
bleeding (DPPB).
This manuscript is well argued after meta-analysis, but there are some things to confirm.
Comments are needed on the presence or absence of preventive endoscopic clip closure when
discussing DPPB.
In multivariate logistic regression analysis, “polyp number # 3” were significantly correlated
with an increased risk of DPPB, not “polyp number >3”.
It needs some explanation on this point.
In page 19 line 278, what does the meaning of “protective factor”?
Please add the description of limitation in this manuscript.
In page 2 line 27, it is written as “aspirin (RR=1.46) before surgery”, but “aspirin (RR=1.46)
before polypectomy” is more accurate.
Review for 10.1186/s12876-024-03245-4 (2024)

Title: Hepatic recruitment of myeloid-derived suppressor cells upon liver injury promotes both
liver regeneration and fibrosis
Version: 1 Date: 23 May 2023
Reviewer's report:
Zhang et al. showed that the recruitment of MDSCs, in particular, M-MDSCs during hepatic
inflammation contributed to either proliferation of hepatocytes and activation of profibrotic
HSCs. CD11b+Gr1+ cells are well quantified by flow cytometry using multiple in vivo models
of hepatic inflammation. The authors performed in vitro co-culture of MDSCs and liver tissues
using a transwell to see the effects of MDSC-derived soluble factors to hepatocytes or HSCs.
They suggested that MDSCs promote proliferation of hepatocytes (from co-cultured liver
tissues) via the expression of  TGF-beta, VEGF, IL-10 and HGF.
However, the suggested mechanism is descriptive. While the expression of  TGF-beta and IL-10
by MDSCs are well known, but there is no data showing a direct evidence of VEGF and HGF
expression in MDSCs. The roles of those immunosuppressive cytokines and growth factors
are distinct. Increased proliferation of liver cells by HGF or VEGF is acceptable. However,
it is hard to understand how TGF-beta and IL-10 can enhance hepatocyte proliferation. In the
previous study (PNAS June 1992, Vol 89, 5408-5412), Oberhammer et al. showed that TGF-beta
treatment to hepatocytes induced their apoptosis in vitro. In addition, it is well-known that TGF-
beta-mediated expression of CDK inhibitors reduces cell proliferation. On top of that, IL-10 also
plays anti-fibrotic roles in HSCs (Experimental Cell Research Feb 2022, Vol 411 Issue 2).  I was
wondering how TGF-beta and IL-10 promoted hepatocyte proliferation during the co-culture.
In the co-culture experiments, intracellular staining of VEGF and HGF in MDCSs and flow
cytometry might be a possible experiment to prove the expression of these growth factors by
MDSCs.
Statistic analyses are largely missing in figures (Fig.1, 2, 3, 4D, 5C).
There is a lack of data in Fig. 3C. The authors mentioned that this data is showing M-MDSCs
as a main MDSC population in liver inflammation, which is missing.
Overall, it is difficult to accept the current version of manuscript for publication. The underlying
mechanisms of MDSCs in hepatocytes proliferation and activation of HSCs should be more
thoroughly tested to support the authors' argument.
Review for 10.1186/s12876-024-03245-4 (2024)

Title: Hepatic recruitment of myeloid-derived suppressor cells upon liver injury promotes both
liver regeneration and fibrosis
Version: 1 Date: 09 Jun 2023
Reviewer's report:
Qiongwen and colleagues have studied the recruitment of MDSCs to the liver during ongoing
injury. They also assessed the effect of this recruitment on liver regeneration and fibrosis. The
rationale behind the study is well explained and it is an interesting topic. However, there are
several points that need to be addressed to fully concluded on the experiment performed by the
authors.
Major comments:
1. Figure 1A: The H&E seems saturated and the image blurry. Could the authors provide clearer
pictures?
2. Figure 1B: is the percentage of MDSCs on total liver cells or on total immune cells? This
should be specified. Moreover, at which time point is the control analysed?
3. Controls are missing in this study. A control should be provided for each time point for all
the panels in figure 1 and 2, and figure 3B. It is not possible to conclude on the effect of the
different models on MDSCs recruitment if a time matched post injection control is not provided
for each time point.
4. Figure 4C: The authors state that the cells growing out of the liver pieces are hepatocytes. To
be able to conclude this, the authors should provide a staining or a flow cytometry analysis of
these cells with a hepatocyte marker, such as HFN4a for example.
5. Figure 4F: Which maker was used to stain for hepatocytes? It is not indicated in the text
neither in the M&M. To state that hepatocytes were the cells with increased G2/M phase, the
authors need to gate on hepatocyte marker-positive cells. If not, the proliferation could be due
to other cell types.
6. Figure 4G: how can the authors state that the cells growing out of the liver pieces are
hepatocytes if most of them are CK18 negative? Moreover, if the authors see more a-SMA,
which can correlate with liver fibrosis to some extent, it means that some of the proliferative
cells are not hepatocytes but HSC. The authors should revise their statement.
7. Figure 5C: it is puzzling that all the antibodies had similar effects. It means that the full cocktail
of these cytokines is needed to induce the hepatocytes proliferation and that no compensatory
mechanisms exist when one of the cytokines is lost. The authors should discuss this.
Minor comments:
1. Throughout the text, spaces are missing between two words, punctuations are in the wrong
places, and capital letter appear in the middle of a sentence. This should be check thoroughly.
2. The end of the first paragraph of the introduction ends with “extracellular matrix (ECM), ,
and [3-6].” The “, , and” should be removed.
3. The authors need to indicate in the M&M section on the co-culture experiment how they
assessed the growth of liver tissue, although details will be provided in a different section.
4. Overall, the English will need some proofing to increase the readability of the manuscript.
5. In the conclusion, the authors state that TGFb is a pro-inflammatory cytokine. I believe this
is a mistake.
Review for 10.1186/s12876-024-03245-4 (2024)

Title: Hepatic recruitment of myeloid-derived suppressor cells upon liver injury promotes both
liver regeneration and fibrosis
Version: 4 Date: 07 Aug 2023
Reviewer's report:
Qiongwen Zhang and colleagues have studied the recruitment of MDSCs to the liver during
ongoing injury. They also assessed the effect of this recruitment on liver regeneration
and fibrosis.
The authors adressed all the reviewers comments. Their answer are satisfying, however it is
unfortunate that the authors did not performed a single experiment to answer the comments.
More efforts could have been made to answer the comments.
In any case, as the comments were somehow answered, the paper can be published as it is.
Review for 10.1186/s12876-024-03245-4 (2024)

Title: Hepatic recruitment of myeloid-derived suppressor cells upon liver injury promotes both
liver regeneration and fibrosis
Version: 4 Date: 08 Aug 2023
Reviewer's report:
I cannot agree with the authors’ points for my question number 1.
https://pubmed.ncbi.nlm.nih.gov/21980263/
The reference paper that the authors referred to is showing HGF expression in PMN-MDSC. In
this manuscript, the authors clearly showed that M-MDSC are main MDSC recruited by liver
inflammation in Fig.3. Also, in the gated population in Fig.3A, the mean fluorescence intensity
of HGF in 24 h is not higher than 0h control. Based on this result, it is difficult to conclude
that HGF is expressed by hepatitis-related MDSCs. Further experiments are necessary to prove
that HGF is expressed by hepatitis-related MDSCs as well as MDSCs in the authors' co-culture
model.
https://pubmed.ncbi.nlm.nih.gov/31552179/
Thank you very much  for providing this information showing the up-regulation of VEGF in
MDSCs.
https://pubmed.ncbi.nlm.nih.gov/16828470/
I think that the authors misinterpreted this paper. In this reference paper, after 48 h treatment of
TGF-beta, the survival cells were analyzed and those survivors showed resistance to apoptosis.
In the authors’ manuscript, they are testing the effect of TGF-beta during the co-culture which
is more similar to the paper by Oberhammer et al. in PNAS.
https://pubmed.ncbi.nlm.nih.gov/26839553/
In this reference paper, the authors treated TGF-beta to hepatic progenitor cells (12 or 48 h),
then performed co-culture with HSCs. The experimental method is not the same as the authors
did in this manuscript.
Overall, it is hard to accept the authors’ rebuttals including the following.
We interpret these findings as possible evidence of context-dependent effects of TGF-,
depending on factors such as concentration and duration of exposure. In our co-culture study, we
propose that MDSCs promote the activation of HSCs via a cocktail of different cytokines, which
include TGF- and IL-10. Further study is needed to fully elucidate these intricate interactions
and their implications for liver repair.”.
Revision experiment is needed to accept this manuscript. The author mentioned that the cocktail
of different cytokines including TGF-beta and IL-10 promoted activation of HSCs. I was
wondering whether the treatment of TGF-beta plus IL-10 to hepatocytes or HSCs will promote
their proliferation. Or the cocktail of TGF-beta, IL-10, VEGF and HGF will activate HSCs?
The current version of the manuscript requires further supporting data to be published.
Review for 10.1186/s12876-024-03234-7 (2024)

Title: Long-term prognosis after endoscopic submucosal dissection for esophageal cancer in
older adult patients
Version: 1 Date: 21 Feb 2024
Reviewer's report:
Thank you for giving me the opportunity to review your valuable paper.
This is a very interesting paper that discusses the safety and efficacy of ESD performed in elderly
patients with esophageal squamous cell carcinoma.
This is a very valuable report showing that ESD in the elderly patients is safe and that the rate
of local control of esophageal cancer is high regardless of the presence or absence of additional
treatment after ESD.  The high-risk group without additional treatment had a lower overall
survival rate than the others, and there was no significant difference in DSS between the groups,
which was showed that other risk factors than esophageal cancer is significantly related to overall
survival rate. (Fig 1. e, f) I also think this is a very valuable paper showing that in patients
with ASA-PS III, because the low-risk group has better DSS than the high-risk group, and ESD
performed for some patients with ESCC is useful even if they have poor PS. (Fig 1. g, h)
This paper is very well written, but could you please allow me to confirm a few things about
this paper?
(1) Fig1.
The mean age is 73 years old. Why did you divide by 75 years old to investigate OS? Could
you explain me the reason?
(2) Were there different about the size and the depth of the lesion depending on the ASA-PS.
Review for 10.1186/s12876-024-03234-7 (2024)

Title: Long-term prognosis after endoscopic submucosal dissection for esophageal cancer in
older adult patients
Version: 1 Date: 03 Mar 2024
Reviewer's report:
This study demonstrates the benefit and safety of endoscopic resection of ESCC in the elderly.
It is also very useful in suggesting the pros and cons of additional treatment in the case of
noncurative resection.
However, there are some modifications that need to be made, so please answer the following
questions.
Major comments
1. It is noteworthy that in the present study there was no difference in survival in elderly ESCC
patients with ASA 3 or higher, with or without additional treatment. However, it would be an
over-interpretation to argue the need for additional treatment based on the results of this study. It
is well known that many ESCC patients are smokers and heavy drinkers, and that they often have
overlapping cancers of other organs, such as pharyngeal cancer, lung cancer, and bladder cancer.
In fact, in the present study, deaths from cancer of other organs were the most common cause
of death. In this regard, it is important to ask whether the patients in this study were screened
for complications of cancer of other organs prior to the start of treatment. Please provide your
response to this question.
2. Immunostaining is recommended to determine the presence of vascular invasion
pathologically; it may have been difficult to determine the presence of vascular invasion in
the patients treated before 2013. In what year were the patients with T1a-EP who developed
metastatic recurrence in the cervix treated in this study? Please state your answer.
3. The most noteworthy result of this study concerns treatment strategies for elderly patients
with poor ADL. It has been reported that the concept of sarcopenia related to muscle mass is
useful as a prognostic factor in the elderly. In the current study, sarcopenia (e.g., SARC-F, etc.)
was not assessed. Please state the reason.
Minor comments
1. Perforation related to ESD in this study occurred in 19 cases (4%). This may be higher than the
incidence of perforation, a common complication. If there is a reason for this, please describe it.
2. On page 5 of the text, lines 6-7, "For patient with ..." should be stated as "ESD procedure".
Review for 10.1186/s12876-024-03234-7 (2024)

Title: Long-term prognosis after endoscopic submucosal dissection for esophageal cancer in
older adult patients
Version: 2 Date: 31 Mar 2024
Reviewer's report:
I appreciate for giving me the opportunity reviewing this interesting manuscript.
The point-by-point responses to the reviewers' comments were mostly accepted.
The revised manuscript is very well written.
I think the following points are very important, since high-risk factors in ASA-PS Class III cases
may not affect OS (Figure 1-c, d).
There was no significant difference in disease-specific survival between ASA-PS class I/II and
III cases (Figure 1-d). ASA-PS class III cases had significantly larger tumor diameters, longer
procedure times, a higher proportion of pT1b-SM cases, and a higher proportion of lymphatic
cases compared to ASA-PS class I/II cases (Supplementary Table 3).
Review for 10.1186/s12876-024-03256-1 (2024)

Title: Exploring the Association Between Dietary Fiber Intake and Hepatic Steatosis: Insights
from NHANES
Version: 0 Date: 31 Jan 2024
Reviewer's report:
Comment:
The paper presented analyses the correlation between dietary fibre intake and hepatic steatosis.
The text clearly explains the aim of the study. The methodology applied in the evaluation of
hepatic steatosis is effective for the purpose of the study and the analyses it proposes. The cohort
of patients analysed is large in order to obtain reliable results. Nevertheless, the data on dietary
fibre intake derived from two 24-hour dietary recalls is a major limitation of the study, limiting
its effectiveness. In any case, the study's evaluation is an interesting analysis of fibre's effect on
hepatic steatosis. I suggest acceptance of the manuscript after the following changes.
Major Revisions:
Among the proposed revisions, I suggest expanding the data concerning the demographic
characteristics of the court in the table associated with the study, data such as sex, age and race
are given, but data concerning HDL cholesterol, LDL cholesterol and glycaemia are omitted,
which would be interesting to observe, as well as a clearer analysis of the associated pathologies
other than diabetes and hypertension.
Minor Revisions:
1) I suggest expanding the introductory part of the manuscript with the inclusion of further
information regarding non-alcoholic hepatic steatosis such as the involvement of genetic factors
and microbiota. I suggest the following references: Abenavoli L, Giubilei L, Procopio AC,
Spagnuolo R, Luzza F, Boccuto L, Scarpellini E. Gut Microbiota in Non-Alcoholic Fatty
Liver Disease Patients with Inflammatory Bowel Diseases: A Complex Interplay. Nutrients.
2022 Dec 15;14(24):5323. doi: 10.3390/nu14245323. Elsayed A, Ismaiel A, Procopio AC,
Luzza F, Abenavoli L, Dumitrascu DL.Noninvasive biochemical markers and surrogate
scores in evaluating nonalcoholic steatohepatitis. Minerva Med. 2022 Oct;113(5):864-874.
doi: 10.23736/S0026-4806.22.08185-X. Abenavoli L, Maurizi V, Boccuto L, Di Berardino A,
Giostra N, Santori P, Scarcella ML, Procopio AC, Rasetti C, Scarpellini E. Nutritional Support
in Acute Liver Failure. Diseases. 2022 Nov 18;10(4):108. doi: 10.3390/diseases10040108
Review for 10.1186/s12876-024-03256-1 (2024)

Title: Exploring the Association Between Dietary Fiber Intake and Hepatic Steatosis: Insights
from NHANES
Version: 0 Date: 15 Apr 2024
Reviewer's report:
The authors present data from an observational study, investigating the association between fiber
intake and NAFLD.
The overall rationale is transparent, even though neither methods, topic or findings are novel.
The entire analysis is confirmatory.
Introduction: Fine.
Methods: Fine.
How did you define "high cholesterol levels"? The cut-offs differ by overall CVD risk status.
Results: Fine.
Please use adequate decimals according to raw data precision (e.g. WC with one decimal, liver
enzymes without...).
Discussion: You discovered huge differences of fiber-NAFLD associations between sexes, age
groups and ethnicities, with strata showing linear, inverse quadratic or wave-wise patterns.
Please clarify this heterogeneity more thoroughly.
Review for 10.1186/s12876-024-03253-4 (2024)

Title: A new model of portal vein thrombosis in rats with cirrhosis induced by partial portal
vein ligation plus carbon tetrachloride and intervened with rivaroxaban
Version: 3 Date: 02 Apr 2024
Reviewer:  Dinesh Mani Tripathi
Reviewer's report:
Reply of the comments are not satisfactory.
Authors may read the comments  carefully and may answer the comments with substantial data.
Review for 10.1186/s12876-024-03253-4 (2024)

Title: A new model of portal vein thrombosis in rats with cirrhosis induced by partial portal
vein ligation plus carbon tetrachloride and intervened with rivaroxaban
Version: 3 Date: 03 Apr 2024
Reviewer's report:
Comments to the authors
Abstract
The authors said “49 male SD rats received partial portal vein ligation (PPVL), and 41 survival
rats were divided into 6 groups: PPVL control group; week 4, 6, 8, and 10 model group”. After
the PPVL operation, 44 rats were divided into 6 groups, not 41. Additionally, it is recommended
that the authors include a chart in the article to more clearly illustrate the group distribution of
the model rats as well as the numbers of deaths and survivals.
Materials and methods
The authors said “We took 49 rats to perform PPVL and intraperitoneal injection of CCl4
to establish a rat model of cirrhosis complicated with PVT”. Not all 49 rats received an
intraperitoneal injection of CCl4; the author should clearly describe this point.
The authors said “The rats after PPVL one week later were divided into 6 groups”. Grouping
rats after the PPVL operation could lead to selection bias: the condition of the rats at the time
of grouping might influence which group they are assigned to. For example, rats that are in
better health or have a stronger recovery ability after the PPVL operation are more likely to be
included in the intervention group. This selection bias could affect the study outcomes, including
the observed survival rates and the efficacy of rivaroxaban intervention. The authors need to
explain this problem.
Results
The authors said “Additionally, the expression of fibrinogen and PAI-1 in rivaroxaban-
treated rats was lower than that in rats in the PPVL+CCl4 10w group, as demonstrated by
immunohistochemical staining and western blotting”. It is mentioned here that fibrinogen was
measured, which conflicts with the results in Figure 7C; the authors need to correct this error.
Review for 10.1186/s12876-024-03237-4 (2024)

Title: CORRELATION OF ALANINE AMINOTRANSFERASE LEVELS AND A
HISTOLOGICAL DIAGNOSIS OF STEATOHEPATITIS WITH ULTRASOUND-
DIAGNOSED METABOLIC-ASSOCIATED FATTY LIVER DISEASE IN PATIENTS
FROM A CENTRE IN NIGERIA
Version: 0 Date: 03 Jan 2024
Reviewer:  Giuseppe Guido Maria Scarlata
Reviewer's report:
The study addresses an interesting topic of considerable scientific interest. However, the writing
is unclear due to linguistic and structural errors. To mention a few:
- In the methods section, there is a table without a caption;
- The font used in the captions is inconsistent;
- Most of the captions for the tables are placed at the top;
- "Fischer" is "Fisher."
- Figure 1 in the results shows "15 ([Percenteage)). I think this is a calculation error that needs
to be revised.
- Caption is missing in the table following Figure 3.
Also, two points should be revised:
1. The statistical analysis is unclear. Why did you choose one test over another? This should be
explained in the appropriate section.
2. The diagnosis of MAFLD was made by assessment of dysmetabolic comorbidities such as
obesity, type 2 diabetes mellitus, hypertension, and dyslipidemia, however, there are additional
criteria that are considered but not assessed (e.g., waist circumference, insulin resistance, CRP
Hs). Considering these criteria will increase the sample size. The diagnostic criteria are well
highlighted in this paper doi: 10.3390/ijms22084241
I suggest that the authors review the entire manuscript from the point of view of content and
structure.
Review for 10.1186/s12876-024-03237-4 (2024)

Title: CORRELATION OF ALANINE AMINOTRANSFERASE LEVELS AND A
HISTOLOGICAL DIAGNOSIS OF STEATOHEPATITIS WITH ULTRASOUND-
DIAGNOSED METABOLIC-ASSOCIATED FATTY LIVER DISEASE IN PATIENTS
FROM A CENTRE IN NIGERIA
Version: 0 Date: 11 Jan 2024
Reviewer's report:
1 In  inclusion criteria, the individuals were graded according to the severity of the fatty liver
disease. However, the authors did not explain how to assess the severity of fatty liver disease.
2 This study revealed that  the ALT level does not reflect what occurs in the liver. The author
should discuss the possible reasons in the article.
Review for 10.1186/s12876-024-03237-4 (2024)

Title: CORRELATION OF ALANINE AMINOTRANSFERASE LEVELS AND A
HISTOLOGICAL DIAGNOSIS OF STEATOHEPATITIS WITH ULTRASOUND-
DIAGNOSED METABOLIC-ASSOCIATED FATTY LIVER DISEASE IN PATIENTS
FROM A CENTRE IN NIGERIA
Version: 4 Date: 29 Jan 2024
Reviewer:  Giuseppe Guido Maria Scarlata
Reviewer's report:
Manuscript has been improved after revisions.
Review for 10.1186/s12876-024-03222-x (2024)

Title: The Association between Healthy Eating Index-2015 with Anthropometric,
Cardiometabolic and Hepatic Indices among Patients with Non-alcoholic Fatty Liver Disease
Version: 2 Date: 12 Dec 2022
Reviewer:  Norberto C. Chavez-tapia
Reviewer's report:
I suggest including non-invasive markers of liver fibrosis as part of liver variables to be analyzed.
In tables 3 and 4, P-for-trend should be a better statistical analysis.
Please include the limitations of this study, including the lack of validation in Iranian population.
Review for 10.1186/s12876-024-03222-x (2024)

Title: The Association between Healthy Eating Index-2015 with Anthropometric,
Cardiometabolic and Hepatic Indices among Patients with Non-alcoholic Fatty Liver Disease
Version: 2 Date: 09 Jan 2023
Reviewer's report:
The Authors performed a descriptive analysis on the distribution of HEI quartiles among
different features of NAFLD. A male susceptibility to worse hepatic indices was shown.
This study has several limitations, starting from the language: it is difficult to read and to
understand in several key passages.
About the methods: NAFLD is not defined in the inclusion and exclusion criteria, nor how it
was diagnosed. Most scores are not widely validated and no robust information may be given
(AIP, LAP, CMI, LCI).
A linear regression analysis only describes a correlation (curve in a graph) between two
continous variables. To assess a risk, and a n association, a logistic regression analysis with
odds ratio would be required, also considering that a transformation of the HEI into categorical
variable has already been done in this paper. In addition, the regression models lack critical
information that is included in the NAFLD landscape (diabetes, BMI, transaminases). The
choice of the variable reflects a lack of knowledge in the field.
In addition, almost all findings are not significant. Male sex has been widely addressed as a risk
factor in this field, these results do not add to the current scientific knowledge.
Taken together, the language use, the methodological weakness and the inconsistency of the
results are strong limitations to this paper.
Review for 10.1186/s12876-024-03222-x (2024)

Title: The Association between Healthy Eating Index-2015 with Anthropometric,
Cardiometabolic and Hepatic Indices among Patients with Non-alcoholic Fatty Liver Disease
Version: 3 Date: 31 Jul 2023
Reviewer's report:
The authors tried to address my main concerns but in some cases the issue was simply addressed
as study limitations. Those concerns still remain.
Review for 10.1186/s12876-024-03222-x (2024)

Title: The Association between Healthy Eating Index-2015 with Anthropometric,
Cardiometabolic and Hepatic Indices among Patients with Non-alcoholic Fatty Liver Disease
Version: 4 Date: 12 Mar 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?
No - there are minor issues
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 authors have responded adequately to each of the concerns
raised in the previous evaluation of the manuscript and the changes to reflect their responses
have been made in the revised version of the paper. The overall impression is that the revised
manuscript is improved, specifically by the open acknowledgment of the limitations of the study.
The results reported in this manuscript are still viewed as confirmatory, with the novelty limited
to the population of study.
REQUESTED REVISIONS:
No further revisions are requested.
Review for 10.1186/s12876-024-03252-5 (2024)

Title: Triple-drug combination therapy versus six-month proton pump inhibitor monotherapy
in non-Helicobacter pylori Helicobacter eradication, and hyperacid environment preference of
Helicobacter suis: A clinical study.
Version: 1 Date: 15 Feb 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses a testable research
question(s) (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 technical rigor to allow
confidence in the results?
No - there are minor issues
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?
No - there are minor issues
OVERALL MANUSCRIPT POTENTIAL - Is the current version of this work technically
sound? If not, can revisions be made to make the work technically sound?
Maybe - with major revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: I read the article with interest. Please see my following comments:
1. Page 7, line 20: “After obtaining consent of those who selected the option 2) or 3), we started
eradication therapy in each of them.” This is somewhat confusing statement. Are you trying to
say patients selecting either of the eradication therapy were started based on their preference
and others were followed without treatment who did not consent?
2. Can the authors also give details regarding patients who chose option 1) i.e. follow-up without
choosing any therapy. It would be interesting to know if any of these patients had eradication.
3. In limitations, the authors should also mention the specific type of PPI studies i.e.
esomeprazole, as well as retrospective nature of the study that accounts for bias.
4. In conclusion, the authors should propose a randomized controlled trial comparing PPI
monotherapy to combination regimen for NHPH eradication as the next step to assess the true
efficacy of each therapy.
REQUESTED REVISIONS:
Please see comments above.
Review for 10.1186/s12876-024-03252-5 (2024)

Title: Triple-drug combination therapy versus six-month proton pump inhibitor monotherapy
in non-Helicobacter pylori Helicobacter eradication, and hyperacid environment preference of
Helicobacter suis: A clinical study.
Version: 2 Date: 27 Mar 2024
Reviewer's report:
I am happy with this new version since it improved and fine by me for considering in the journal
Review for 10.1186/s12876-024-03252-5 (2024)

Title: Triple-drug combination therapy versus six-month proton pump inhibitor monotherapy
in non-Helicobacter pylori Helicobacter eradication, and hyperacid environment preference of
Helicobacter suis: A clinical study.
Version: 2 Date: 30 Mar 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?
No - there are issues with the statistics 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?
Probably - with minor revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: I read the revised letter and the authors have answered the queries
to both reviewers except one comment.
In 3.4 they mention that patients were followed annually with EGD who chose not to undergone
treatment, however, they did not provide any actual statistics if there was eradication achieved
for any of these patients. This should be provided.
REQUESTED REVISIONS:
Please see above
Review for 10.1186/s12876-024-03252-5 (2024)

Title: Triple-drug combination therapy versus six-month proton pump inhibitor monotherapy
in non-Helicobacter pylori Helicobacter eradication, and hyperacid environment preference of
Helicobacter suis: A clinical study.
Version: 3 Date: 23 Apr 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 authors have revised their manuscripts substantially and
answered all queries raised. The manuscript can be accepted for publication.
Review for 10.1186/s12876-024-03215-w (2024)

Title: Clinico-pathological study of esophageal mucoepidermoid carcinoma: a 10-year survival
from a single center
Version: 1 Date: 08 Sep 2023
Reviewer:  Junya Oguma
Reviewer's report:
I am grateful for the opportunity to review your interesting manuscript entitled: "Clinico-
pathological study of esophageal mucoepidermoid carcinoma: a 10-year survival from a single
center". This report is interesting because it focused on the clinicopathological features of MEC
of the esophagus which is one of the rare histological type of esophageal cancer. However, your
manuscript has several major problems as following.
1. MEC is one of rare malignancy in the esophagus, but I cannot find any novel information
in your manuscript compared to previous reports. We want to know the difference of
clinical characteristics between MEC and SCC. You had better compare clinical features and
postoperative outcomes between these two histological types using propensity score matched
analysis.
2. The average number of resected LN was 11.2, and it was not enough for thoracic esophageal
cancer. I think that sweet approach, which was performed for 42 patients, is not suitable for upper
and middle thoracic esophageal cancer, because sufficient upper mediastinal LN dissection
cannot be undergone during sweet procedure.
3. In your cohort, neoadjuvant chemotherapy was performed for 3 cases and adjuvant
chemotherapy was performed for 17 cases. You should clear the indication of these adjuvant
therapy.
4. You mentioned that 17 patients had LN metastasis. Was histological type of metastatic lesions
MEC or another type?
Review for 10.1186/s12876-024-03215-w (2024)

Title: Clinico-pathological study of esophageal mucoepidermoid carcinoma: a 10-year survival
from a single center
Version: 1 Date: 26 Sep 2023
Reviewer's report:
It was very pleasant to read and review the manuscript titled "Clinico-pathological study of
esophageal mucoepidermoid carcinoma: a 10-year survival from a single center" submitted for
publication in "BMC Gastroenterology".The article is original, well written and the relationship
studies is interesting. However, if you don't mind, I would like to ask for some minor
suggesstions:
A. Please write a specific paragraph concerning the aim of your study instead of including it
in the previous one.
B. Please add the full noun of SPSS
C. 147—174  The author spends a lot of sentences describing how MECE is prone to
misdiagnosis, but how is it related to the clinical pathological studies? It is advised to reduce
some of the explanation content
D. 175—192#The author spends a lot of sentences talking about immune indicators#I hope the
author can consider deleting some of the details.
E. The article only conducted univariate analysis, multivariate analysis also should be
considered.
F. Survival Analysis in different T and N stages should be considered. and the survival curve
was not aesthetically pleasing
I wish the authors good luck.
Review for 10.1186/s12876-024-03215-w (2024)

Title: Clinico-pathological study of esophageal mucoepidermoid carcinoma: a 10-year survival
from a single center
Version: 3 Date: 24 Feb 2024
Reviewer's report:
The word “Introduction” seems  located in a wrong position
Table 5 P =0.000,should be like #0.001
I have no more comments for the reversions.
Review for 10.1186/s12876-024-03246-3 (2024)

Title: Genetically Predicted Gut Microbiota Mediate the Association Between Plasma
Lipidomics and Primary Sclerosing Cholangitis
Version: 0 Date: 14 Apr 2024
Reviewer's report:
The paper used plasma lipidome data from a study involving Finnish population and microbiota
data from a study based on Dutch population and used various statistical tools to try to establish
a relationship between plasma metabolites and gut bacteria in PSC.
The major concern I have is the data heterogeneity (lipid data from a study involving Finnish
population, SNPs from multiple studies and microbiota data from study from Dutch population).
PSC is suggested to have considerable heterogeneity in the geoepidemiology (see publications
listed below). Different diets shape gut microbiome, which would invalidate the approach to
try to establish a relationship between plasma lipids from one population and gut bacteria from
another. The lipid source data investigators used were from short gun lipidomics approach,
which are questionable to annotate lipid to the subspecies level, such as PC(o-16:1_18:1).
Therefore, the association of a nonconfirmed lipid, PC(o-16:1_18:1) levels in PSC and suggested
effect by Eubacterium rectale are not convincing. I regret to inform you of my decision to reject
this work to be published in BMC Gastroenterology.
Tej I. Mehta, et al. Global incidence, prevalence and features of primary sclerosing cholangitis:
A systematic review and meta-analysis. Liver International, 2021.
Palak J. Trivedi, et al. Epidemiology, Natural History, and Outcomes of Primary Sclerosing
Cholangitis: A Systematic Review of Population-based Studies. Clinical Gastroenterology and
Hepatology 2022.