JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-02041-8 (2021)

Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
Version: 10 Date: 23 Aug 2021
Reviewer's report:
Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
I appreciate that in the last version of the revised manuscript the authors deleted the statistical
analysis of TT genotype. However, the statistical analysis and presentation must be improved
throughout the paper and authors should advice a biostatician with expertise in analysing
biometric variables.
1. The whole figure 1 is incorrect. Either you should compare Steatosis (+) vs Steatosis (-) with
each variant (+) or (-) and perform Chi Square test or you should compare the percentages of
patients with steatosis depending on the presence or not of the variant and perform t-test or
Mann-Whitney as appropriate. For instance, in the current form of figure 1, in 1B you present
that 2.9% of patients with hepatic steatosis have no hepatic steatosis!. Please revise.
2. Figure 2 should be revised as well. The illustration of data is not appropriate.
3. Non-parametric continuous variables should be presented as median [interquartile range]
rather than mean (SD). Please revise.
4. The authors present the higher prevalence of AG+GG genotypes of PCSK9 rs505151 vs AA
genotype as OR and subsequently illustrate it as 2 graph bars in Figure 2. That is incorrect. You
should compare the afore-mentioned prevalence as numeric variables performing t-test or Mann-
Whitney as appropriate and then you illustrate those results in the Figure. The logistic regression
analysis is generally presented in a Table with ORs, Cis and p-value and not in a figure.
Minor comments:
The authors should carefully read the whole manuscript for grammatical or syntactic errors. (i.e.
page 9, line 7 “steaosis”).
Review for 10.1186/s12876-021-02041-8 (2021)

Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
Version: 10 Date: 23 Aug 2021
Reviewer:  Nikoletta Maria Tagkou
Reviewer's report:
We thank the authors for thoroughly considering our comments, in order to improve their paper.
Review for 10.1186/s12876-021-02041-8 (2021)

Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
Version: 11 Date: 14 Oct 2021
Reviewer's report:
Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
The authors partially revised the manuscript and the figures in accordance to our comments,
however this was the third revision and they should have been more careful.
More specifically,
1) Although the authors claimed that they have presented non-parametric variables as median
values, they did not encompass this information in “Methods” section as well as they did not
distinguish their presentation from parametric variables. Furthermore, the baseline variables are
presented in Table 2, not in Table 1 as they wrote in the revision letter!
2) The illustration of the data in whole Figure 2 is still inappropriate and it is totally unclear what
comparison has been performed. For instance, in Figure 2A, they showed that patients with CT
+TT genotype with high grade steatosis did not differ significantly from patients with CT+TT
genotype with low grade steatosis? Or with those with CC genotype? And among CC genotype
patients, those with low- or high-grade steatosis? It is totally misleading.
3) In the revision letter, the authors stated that in Figure 2 they compared the prevalence of AA
+AG genotypes in those with “moderate to severe steatosis” versus “mild steatosis”. However,
in the manuscript when they refer to Figure 2, they still use the p-value and ORs derived from
the logistic regression. The comparison between prevalence of 2 different groups should be
performed using Students t-test or Mann-Whitney as appropriate.
4) The overall English language quality is poor.
Review for 10.1186/s12876-021-02041-8 (2021)

Title: Variations in TM6SF2, PCSK9 and PCSK7 genes and risk of hepatic steatosis after liver
transplantation: a cross-sectional study
Version: 13 Date: 21 Nov 2021
Reviewer's report:
As authors made the required changes indicated by the Editor, i recommend for acceptance.
Review for 10.1186/s12876-021-02045-4 (2021)

Title: Hypercortisolism in Patients with Cholestasis is Associated with Disease Severity
Version: 2 Date: 20 Mar 2021
Reviewer's report:
The study is aimed to evaluate the prevalence and the possible causes of hypercortisolism in
patients with cholestasis. Though the sample size is small and the topic has already been studied
in other papers, the presence of a control group of patients without cholestasis is a strength point.
Moreover the paper is well written and clear.
Anyway, I have several comments:
1) In the introduction I suggest to deepen, with a brief explanation, how FXR and, above all,
TGR5 have an action both in enterohepatic circulation and in glucocorticoid metabolism (the last
receptor is just mentioned).  I think it would be more clear for the reader in order to understand
one of the main known mechanisms of cross-talk between cortisol metabolism and cholestasis.
2) Among the exclusion criteria, there are pituitary or adrenal diseases or tumours: how have
you excluded them? Pituitary and adrenal imaging has been performed in all patients?
3) How have you excluded hypercortisolism due to endocrine causes in patients with higher
basal cortisol levels? It would have been correct to evaluate cortisol secretion also at the end of
the acute disease event, for example with the 1 mg dexamethasone suppression test,  in order to
verify that higher levels of cortisol were caused actually by cholestasis and not by other diseases,
at least in few patients.
4) “ (…) patients with cholestasis showed hypercortisolism associated with disease severity as
mirrored by levels of bilirubin. A short duration of disease seems to have more pronounced
effects on cortisol metabolism than long-standing disease”. Regardless of the effects that
levels of bilirubin may have on cortisol metabolism, what could be the clinical implications
of hypercortisolism in these patients? It would have been interesting to evaluate the possible
correlation beetween levels of cortisol and (for example) prognosis, incidence of infections,
duration of hospitalization...
Review for 10.1186/s12876-021-02045-4 (2021)

Title: Hypercortisolism in Patients with Cholestasis is Associated with Disease Severity
Version: 2 Date: 06 Apr 2021
Reviewer's report:
The authors examined if cholestatic liver disease changed glucocorticoid metabolism.  They
included 36 patients with cholestasis of different etiologies and 32 patient from the same hospital
without cholestasis.
Baseline Se-cortisol was higher in the cholestatic group than in controls, while ACTH levels
were similar. The responses to a 1µg  ATCH test were similar in the two groups. They conclude
that the effect of cholestasis was not mediated via the pituitary gland but  rather from increased
adrenal synthesis of glucocorticoids or reduced hepatic or renal elimination.
The paper is well written, experimental procedures easy to understand and well chosen for
the purpose. The finding of hypercortisolism in these patients will surprise many. I have some
concerns that I think should be addressed.
Major concerns
1. Based on previous findings in their own lab and reports from others, where supranormal
concentrations of bile acids stimulated adrenal cortisole production,  they expected that baseline
cortisol would correlate to bile acid concentrations. That was however not the case. Nevertheless
they use most of the discussion to infer that their findings actually supported their prior
hypothesis.  That conclusion is not supported by the data, and I think they should rewrite their
discussion accordingly.
2. Bilirubin concentrations did in fact correlate with cortisol concentrations. They could
speculate whether that could be a direct effect. However since we are dealing with a cross
sectional study,  they cannot explore cause-and-effect questions.
Minors
Abstract. Don’t use the term “delta cortisol” in the abstract, it is not explained until later in the
paper. Rewording or explanation needed.
Page 4. The publications suggesting a “hepato-adrenal syndrome” were based on patients with
cirrhosis. They may still be valid, since the patients in this study  did not yet have cirrhosis (at
least most of them did not). If the authors think the old hypothesis is refuted by their data they
should explain why.
Page 5. Important to mention if the cholestatic patients were hospitalized (like the
control group).
Page 14 . UCDA was clearly elevated in the Cholestatic group. How many were treated with
UDCA and could that affect the findings ?
Review for 10.1186/s12876-021-02045-4 (2021)

Title: Hypercortisolism in Patients with Cholestasis is Associated with Disease Severity
Version: 2 Date: 07 Apr 2021
Reviewer's report:
It is suggested that studies of this background in patients with chronic cholestasis may yield
valuable results.
1. Adrenal insufficiency is found in patients with liver cirrhosis. This condition terms “hepato-
adrenal syndrome”. I wonder the possible pathogenesis which helping to establish association
between hypercortisolism and cholestasis.
2. The sample size is small. The author did not detail how the patients were recruited.
3. The author should explain the reasons why 1 ug ACTH was given in cholestatic patients with
hypercortisolism.
4. Several causes, including DILI, PSC, cancer, and autoimmune pancreatitis, was identified
in cholestatic patients. I wonder whether these causes had some effects on glucocorticoid
metabolism. In addition, cholestatic patients without definite causes were excluded from this
study?
5. The author also should detail the clinical diagnosis of patients without cholestasis, who served
as control in this study.
6. The results show that patients with chronic cholestasis have higher TB levels than patients
with acute cholestasis. This might be not true because of the small sample. I prefer the author
compared the baseline cortisol and ATCH levels between with severe cholestasis and mild
cholestasis.
7. The authors state that “Baseline cortisol was significantly higher in the carcinoma group”.
This indicates the influence of cancer on cortisol levels. It is greater to enroll cholestatic patients
with causes influencing cortisol levels, such cholestatic infants.
Review for 10.1186/s12876-021-02045-4 (2021)

Title: Hypercortisolism in Patients with Cholestasis is Associated with Disease Severity
Version: 3 Date: 27 May 2021
Reviewer's report:
The paper, aimed to evaluate the prevalence and the possible causes of hypercortisolism in
patients with cholestasis, after a first revision has been modified adequately and the required
elements have been added.
However, there is one point I would like to focus on, already underlined in the previous revision:
an unknown hypercortisolism with endocrine basis has never really been excluded: in addition
to have examined only the absence of adrenal or pituitary diseases in the anamnesis without
having investigated the finding of increased basal cortisol, no further assessments were carried
out at the end of the acute event to verify that the basal hypercortisolism was really related to
the cholestatic pathology. I agree to cite the Endocrine Society Guidelines for the diagnosis of
Cushing's syndrome and I understand that none of the patients had any characteristics that could
suggest true overt endocrine hypercortisolism, but these guidelines are used in clinical practice,
in patients without already reported increased cortisol levels. Being in this case a clinical study
aimed at evaluating the presence of hypercortisolism related to cholestasis, and having been
found an increase in basal cortisol, I believe it was of primary importance to exclude other
causes of hypercortisolism, not only based on the anamnestic absence of adrenal and/or pituitary
diseases, but also by performing targeted imaging and, possibly, suppression test or urinary free
cortisol. Not having done so, I think it is important to add it within the limits of the study.
Also considering that often the features of hypercortisolism can be very nuanced (subclinical
hypercortisolism) and have not yet caused consequences in terms of physiognomy and/or long-
term complications, making it difficult to apply Endocrine Society Guidelines.
Review for 10.1186/s12876-021-02036-5 (2021)

Title: Helicobacter pylori infection is associated with reduced risk of Barrett’s esophagus: A
meta-analysis and systematic review
Version: 0 Date: 11 Sep 2021
Reviewer's report:
This study is a meta-analysis and systematic review about the BE and HP infection. The authors
included the published papers and then they performed meta-analysis, including sub-group
analysis. They concluded that  Hp, especially the CagA-positive Hp strain, and BE are inversely
related with considerable heterogeneity. Of course, there have been several meta-analysis about
the similar subjects and they also suggested the similar conclusion. Nevertheless, this study has
strengths such as additional analysis about cagA positivity, length of BE, and HP eradication or
not. Therefore, this study will give a valuable information on understanding the association of
BE and HP infection to clinicians.
Review for 10.1186/s12876-021-02036-5 (2021)

Title: Helicobacter pylori infection is associated with reduced risk of Barrett’s esophagus: A
meta-analysis and systematic review
Version: 0 Date: 26 Sep 2021
Reviewer's report:
The authors have conducted a thorough systematic review and meta analysis into the potential
protective effect on Barrett's esophagus of Helicobacter pylori.
One of the strengths of the study are the relevant subgroup analyses. While there is great
heterogeneity among studies, these subgroup analyses provide us with important information.
I applaud the authors with their effort.
There are only a few minor concerns I would like to address below. I hope the authors are able
to revise the manuscript accordingly.
- While the methods and description of the results are sufficient, I feel the manuscript lacks in
translation of the findings into clinical relevance. The aim of the study should include a brief
discussion on why an inverse relation between HP and BE is clinically relevant.
Why are your findings important for clinical practice? Should it impact decisions on eradication
therapy for HP? This should be addressed in the discussion section. If relevance to clinical
practice is limited, this should also be mentioned.
- The potential protective effect of HP on BE might be explained by decreased acid secretion
due to corpus-predominant gastritis. This could be a plausible pathofysiological mechanism, but
this meta analysis is not able to make statements about causality. Please include a statement that
acknowledges this.
- Please revise the last sentence of the results section on page 9 to a statistically and
grammatically more correct version: "Due to lack of sufficient amount of research, we just could
not discuss single factor with all others controlled."
Review for 10.1186/s12876-021-01993-1 (2021)

Title: Lower testosterone levels predict increasing severity and worse outcomes of hepatitis B
virus-related acute-on-chronic liver failure in males
Version: 1 Date: 20 Mar 2021
Reviewer's report:
This is an interesting and well written paper regarding the impact of testosterone in male patients
with hepatitis B virus related acute on chronic liver failure (HBV-ACLF). The authors evaluated
160 male patients with HBV-ACLF, 151 chronic hepatitis B patients without liver failure (CHB)
and 106 healthy controls (HC) and they found that low serum levels of total testosterone were
associated with increased stage of ascites, hepatic encephalopathy, MELD and HBVB-ACLF
scores, while low testosterone (<142.39 ng/dL) was a risk factor for both the composite outcome
and for death alone within 90 days.
However, there are some issues which should be addressed by the authors
1) SHBG needs abbreviation
2) Declaration of Helsinki needs update
3) The authors stated that the patients underwent artificial liver support system. Can they clarify
better this issue? For how long did they receive this support? How this support can affect their
results?
4) Did the authors have any data regarding the causes of ACLF? Infection, G.I. bleeding etc
5) “MELD and COSSH ACLF were calculated using the most abnormal value”. Is it true? Na
d not at baseline similar to hormones evaluation?
6) MELD score was MELD-Na or original?
7) SPSS version needs update
8) Page 10: SHBG is not a hormone
9) Any data regarding antiviral therapy?
10) Table 1: How did the authors explain that cortisol was lower in early stage that middle and
end-stage of HBV-ACLF? Similar comment for DHEAS
11) Table 3: Estimate? 95%CI?
12) Total testosterone should be excluded from Table 4
13)  In cox regression analysis for the outcome all the variables significantly associated with the
outcome in univariate analysis should be included
Review for 10.1186/s12876-021-01993-1 (2021)

Title: Lower testosterone levels predict increasing severity and worse outcomes of hepatitis B
virus-related acute-on-chronic liver failure in males
Version: 1 Date: 13 May 2021
Reviewer's report:
what is hypothesis on the basis of which the study was designed ?
what is the relationship of testosterone levels with other parenterally transmitted heptotropic
viruses like HCV and HIV?
how does low testosterone levels correlate with MELD score?
what is the reason for low testosterone levels in ACLF patients?
Review for 10.1186/s12876-021-01993-1 (2021)

Title: Lower testosterone levels predict increasing severity and worse outcomes of hepatitis B
virus-related acute-on-chronic liver failure in males
Version: 2 Date: 26 Sep 2021
Reviewer's report:
The paper has been improved. Only 2 comments
1) The original MELD score does not include etiology of liver disease
2) Can the authors clarify better in the text if MELD and COSSH-ACLF were calculated based
on the baseline variables?
Review for 10.1186/s12876-021-02039-2 (2021)

Title: Total polyunsaturated fatty acid intake and the risk of non-alcoholic fatty liver disease in
Chinese Han adults: a secondary analysis based on a case-control study
Version: 0 Date: 22 Sep 2021
Reviewer's report:
Review of “Total polyunsaturated fatty acid intake and the risk of non-alcoholic fatty liver
disease in Chinese Han adults: a secondary analysis based on a case-control study” (74a6515c-
bb15-4040-abc4-4dafca935660)
This study investigated the association between total polyunsaturated fatty acid intake and the
presence of non-alcoholic fatty liver disease using the data of previously published data. This
study is potentially interesting; however, several problems to be solved.
1. This case-control study is not evaluating the causal relationship between total polyunsaturated
fatty acid intake and incident NAFLD.
2. This study used data from the previous study, and the authors of this study might not know
the detail. However, it is unclear from what population the 1,068 people were selected. This is
a crucial problem.
3. Duplicate description. “NAFLD patients is based on the "Guidelines for the Diagnosis and
Treatment of Non-Alcoholic Fatty Liver Disease: 2010 Update" [21]. Ultrasound examinations
are implemented by experienced ultrasonographists who were unaware of laboratory and clinical
data.”
4. Please add the data of OR of covariates.
Review for 10.1186/s12876-021-02039-2 (2021)

Title: Total polyunsaturated fatty acid intake and the risk of non-alcoholic fatty liver disease in
Chinese Han adults: a secondary analysis based on a case-control study
Version: 0 Date: 24 Sep 2021
Reviewer's report:
This study investigated the effect of total polyunsaturated fatty acid (PUFA) consumption on
the risk of NAFLD in Chinese Han population. The results suggested that PUFA intake could
reduce the risk of NAFLD, and the total PUFA intake ranging betweeen 18.8 and 29.3 g/day
independently characterizes NAFLD. This is an interesting study and provides some useful
opinion to prevent the risk of NAFLD.
1. How to evalute the PUFA intake according to the questionnaire, whether each food contain
the unique concentrations of PUFA? The authors should describe this carefully.
2. What is the meaning of one-onset?
3. The Englishi written should be improved carefully.
4. According to this study, it is obvious that PUFA could reduce the risk of NAFLD, therefore,
the authors should provide some diet guide in the discussion section for the public.
5. In the conclusions in Abstract, “Total PUFA intake ranging between 18.8 and 29.3 g/
day independently characterizes NAFLD”, whether this conclusion could prove the causal
relationship of PUFA intake ranging between 18.8 and 29.3 g/day and the incidence of NAFLD?
Review for 10.1186/s12876-021-02039-2 (2021)

Title: Total polyunsaturated fatty acid intake and the risk of non-alcoholic fatty liver disease in
Chinese Han adults: a secondary analysis based on a case-control study
Version: 2 Date: 25 Oct 2021
Reviewer's report:
Response to reviewer 1’s 2 comment. What this reviewer wanted to say was that it is unclear
how large a sample534 people were drawn from. Therefore, it is not possible to evaluate the
possibility of selection bias. Please mention this point.
Review for 10.1186/s12876-021-02029-4 (2021)

Title: Dietary triggers of gut inflammation following exclusive enteral nutrition in children with
Crohn’s disease: a pilot study
Version: 1 Date: 26 Jul 2021
Reviewer:  Jaroslaw Kierkus
Reviewer's report:
This an important publication. The issue is up to date and very interesting, however the
manuscript needs some minor revision mentioned below
1. The abbreviation CD is used in the first line of the introduction but it isn't mentioned in the
abstarct - no abbreviation is used in the abstract, and then in the text only abbreviations are used
without explaining -please use the abrreviation with term mentioned for the 1st time
2.The list of abbreviations should be placed at the begining of the manuscript
3. In the discussion authors almost do not refer to any publications, since a lot has been published
on the fdield authors should mention more available data in this section
4. Fig 2 is completely unclear, please improve its quality
Review for 10.1186/s12876-021-02029-4 (2021)

Title: Dietary triggers of gut inflammation following exclusive enteral nutrition in children with
Crohn’s disease: a pilot study
Version: 6 Date: 20 Oct 2021
Reviewer's report:
The authors have responded satisfactorily to my comments, and included further analyses and
text that have strengthened the manuscript. I remain curious about the impact of cereal / grain
fiber compared to fruit/veg fiber on FCP post re-introduction. The small SS may not have
sufficient power to separate the nutrient analyses in this manner. Future consideration to this
type of work would advance the field further.
Review for 10.1186/s12876-021-02044-5 (2021)

Title: Detection and characterization of human astrovirus and sapovirus in outpatients with acute
gastroenteritis in Guangzhou, China
Version: 1 Date: 17 Aug 2021
Reviewer's report:
This study determined the incidence of the infection caused by HAstV and SaV in people with
AGE inGuangzhou, China, from September 2013 to January 2016 and characterized the HAstV
and SaV detected according to the genotypes.The results of this study may provide further
epidemiological and molecular information about HAstV and SaV strains causing AGE. This
information may prove useful in the development of vaccines and other preventative therapies
for AGE and related diseases. Totally, the manuscript is well written, but several issues need
to be addressed:
1.Line 107, not “a phylogenetic tree” here, “a” is redundant;
2.Line 110, “The following reference stains and accession numbers were used”. Typo “stains”.
Please elaborate why chose these sequences as references? Did they exhibit different genotypes?
3.Line 134-135. “We also detected three cases of multiple gastrointestinal tract infections.”
Please describe in detail.
4.Line 146-149. What is the distribution of different ages? Please state in sentences or by using
a graph. Then using infection rates for age distribution in HAstV and SaV infections, not just
by case numbers.
5.Line 156-158. “ However, AGE with single HAstV infection is more likely to cause fever and
has been observed in five of the ten cases (50%) compared to infections caused by undetected
pathogens (16.81%)”. Why not use all the HAstV-positive cases here? It’s more reasonable to
use all the HAstV-positive cases here.
6.Line 200-202, “our data also showed that the median age of patients with the single HAstV
infection was higher than that of the patients with other virus infections (P = .0476).” Please
state the potential reason for the phenomenon here.
7.Line 202-204. Why “50% of those with HAstV infection also reported AGE” can “suggesting
that people of all age may be susceptible to HAstV, not just the very young and the elderly”?
Please explain.
8.Line 209-210. “we identified another peak of SaV infection from February to March (41.67%),
indicating the possibility of a high prevalence during early spring months too”, please state the
reason. Is it because of outbreak?
Review for 10.1186/s12876-021-02038-3 (2021)

Title: FIB-4, APRI, and AST/ALT ratio compared to FibroScan for the assessment of hepatic
fibrosis in patients with non-alcoholic fatty liver disease in Bandar Abbas, Iran
Version: 1 Date: 14 Jun 2021
Reviewer's report:
Non-alcoholic fatty liver disease (NAFLD) is the leading global cause of chronic liver disease,
estimated to affect approximately 25% of the world’s population. It is not only important to
diagnose MAFLD, but also to distinguish between simple steatosis that can be managed at
primary healthcare level and those with advanced fibrosis (F#2) who need to be referred to
secondary or tertiary levels of care.
Simple point-of-care non-invasive tests (NITs) should be utilized to identify individuals with
advanced fibrosis. APRI (AST-to-platelet) ratio, FIB 4 index and the non-alcoholic fatty liver
disease fibrosis score (NFS) have excellent negative predictive values for advanced fibrosis/
cirrhosis. FIB-4 index is the usual recommended NIT in the absence of a Fibroscan.
Amernia and colleagues compared the FIB-4 index, AST/ALT ratio, and the APRI score with
FibroScan results for the diagnosis of hepatic fibrosis in patients with NAFLD. The APRI score
and FIB-4 were the better indices than the AST/ALT ratio to assess liver fibrosis in NAFLD
patients.
Sensitivity, specificity, positive predictive value, negative predictive value, and accuracy of
APRI at the 0.702 cut-off for the differentiation of F3 and F4 from F2 and F1 were 84.1, 88.2,
66.1, 95.3, and 87.3%, FIB-4 at the 1.19 cut-off were 97.7, 72.7, 49.4, 99.2 and 78%, and AST/
ALT at the 0.94 cut-off were 61.4, 77, 42.2, 87.9, and 73.7% respectively.
In contrast to other published NIT recommendations, the APRI score performed better than
the FIB-4 index with an AUROC curve of 0.923 (95% CI 0.876-0.970) compared to 0.913
(0.868-0.958)
The authors postulate that the difference in the diagnostic performance of NITs (FIB-4 vs
APRI ratio) between previous studies and theirs, is that previous studies used the liver biopsy
as the reference instead of the FibroScan results.  Using the liver biopsy as a reference
has limitations including small sample size, sample not being representative and variable
histological interpretation by histopathologists.
Amernia and colleagues confirm that the non-invasive tests of APRI and FIB-4 had excellent
negative predictive values advanced fibrosis/cirrhosis and these individuals can be managed at
primary care level.
Review for 10.1186/s12876-021-02038-3 (2021)

Title: FIB-4, APRI, and AST/ALT ratio compared to FibroScan for the assessment of hepatic
fibrosis in patients with non-alcoholic fatty liver disease in Bandar Abbas, Iran
Version: 1 Date: 13 Oct 2021
Reviewer's report:
Review from Dr. Mary K. Y. Afihene
The study tried to explore alternative methods in assessing liver fibrosis. Although the study is
important, there are some major issues that needs to be addressed.
Tittle:
1. The tittle of the study did not state where the study was conducted. Study setting should be
included.
2. The study sought to assess hepatic fibrosis and not diagnosis. The authors should revise
appropriately
Abstract
1. line 7 of the abstract background; Please write the tests in the order in which they appear in
the tittle
2. “Aim to” has been repeated in line 7, please delete one
3. Please change the word diagnosis to assessment in lines 2, 9 and 27.
Background
1. it is better to describe NAFLD as a spectrum; NAFLD – steatohepatitis – fibrosis - cirrhosis.
2. The authors gave a global prevalence without recall to the local picture. They should improve
the logical flow of the background (i.e., situation, problem, objective and response).
3. Line 60 – 65; The statement is too long with multiple ideas; I suggest you split them into two
and site each appropriately. Refine the construction of the sentence; remove while and replace
the statement “in close relationship” with “closely related”
4. Line 71; The sentence “Abdominal ultrasonography (US) is the most common imaging
method for the diagnosis of NAFLD with sensitivity and specificity of around 85% and
90%, respectively; however, it has some limitations, including being operator-dependent and
ineffective in patients with central obesity” should precede line 66. Also, I suggest you reference
the second statement concerning the limitations separately.
5. The last paraph of the background failed to describe the burden of the disease in Iran,
availability and cost of fibroscan which should be highlighted in the justification of the study.
Methodology
1. The information on sample size estimation is not sufficient, the authors should provide details
of how they arrived at the sample size of 205 and elaborate data collection tools
2. The study gathered data from human participants. However, there is no statement in the
manuscript on ethical approval from any regulatory authority and inform consent from the
participants.
Results
1. The results is too scanty, Please provide a descriptive analysis of the background
characteristics and laboratory indices
2. Although there is a positive relationship the correlation is a weak one. The authors should
describe the nature of correlation that was found.
3. Mann-Whitney test used is inappropriate. This test is suitable for comparing the difference
in median not means.
Discussion
1. Paragraph one of the discussions should be moved to the background.
2. The first paragraph of the discussion should highlight the major finding of the study. This was
not done in this study. The authors should revise the discussion and relate to current literature.
Review for 10.1186/s12876-021-01988-y (2021)

Title: First Report on Molecular Docking Analysis and Drug Resistance Substitutions to
Approved HCV NS5A and NS5B Inhibitors amongst Iranian Patients
Version: 3 Date: 31 Aug 2021
Reviewer's report:
The fact that the expected phosphorylation amino acids play a critical role in viral replication,
pathogenesis and liver disease should be demonstrated by clinical data and not just affirmed on
the basis of mere hypotheses.
I do not understand the role in the discussino of the issue concerning yeast and E.Coli NS5A
and NS5B protein expression; where does this want to lead?
In general the biochemical part of the discussion is written in very complicated , confusing and
inconclusive way and makes the pathogenetic  aspects  difficult to understand.
The explanation of the great difference between the mutations found by the authors and other
studies must  be discussed in depth. Numerical, geographical, clinical and genetic aspects in
other studies should be evaluated and reported in the discussion not generally suggested.
References in the introduction should be corrected because they are often not relevant (REF 1,
2, 3, 4)
The manuscript needs to be streamlined and made easier to read.
Methods:
What was the detection limit of the test? How many copies of HCV?
Sanger Sequencing methods are not reported
The table two reports the mutations in NS5a and NS5B; mutations at positions 62, 309 and 327
in NS5a are reported in the discussion.
The table seems to show mutations 309 and 327 in NS5B.... Is that so?
The paper must be corrected in typing and English
Review for 10.1186/s12876-021-01988-y (2021)

Title: First Report on Molecular Docking Analysis and Drug Resistance Substitutions to
Approved HCV NS5A and NS5B Inhibitors amongst Iranian Patients
Version: 5 Date: 15 Oct 2021
Reviewer's report:
We are satisfied for the relevant moodifications to the manuscript that is now suitable for
publication
The only very minor modification that we suggest is to add some more recent paper that we
believe should be considered and shortly discussed.
Resistance Associated Mutations in HCV Patients Failing DAA Treatment. New Microbiol.
2021 Jan;44(1):12-18.
Genetic Subtypes and Natural Resistance Mutations in HCV Genotype 4 Infected Saudi Arabian
Patients. Viruses. 2021 Sep 14;13(9):1832.
Review for 10.1186/s12876-021-02031-w (2021)

Title: Risk Factors for Adverse Events Associated with Endoscopic Retrograde
Cholangiopancreatography in Patients with Surgically Altered Anatomy: a Retrospective Study
Version: 1 Date: 15 Sep 2021
Reviewer's report:
Please mention limitations of this study, which are retrospective design, variations of patients/
reconstruction methods and variations of endoscopes.
Please discuss more about higher rate of pancreatitis, 9 patients in BII gastrectomy group.  What
are possible causes? and How to prevent?
In normal ERCP,  balloon dilatation without  sphincterotomy is the one of risk factor for
pancreatitis. Is it compatible with your study result?
Review for 10.1186/s12876-021-02031-w (2021)

Title: Risk Factors for Adverse Events Associated with Endoscopic Retrograde
Cholangiopancreatography in Patients with Surgically Altered Anatomy: a Retrospective Study
Version: 1 Date: 01 Oct 2021
Reviewer's report:
1. Suggest to clarify the definition of multiple cannulation attempts (? >5 attempts or >5 minutes
which are usually used to define difficult canulation).
2. Most of the reconstructed anatomy in this study are Bilroth I and Bilroth II reconstruction
(~80%). This is likely the reason why most ERCP can be performed using conventional
endoscope instead of DAE in this series. The low percentage of patients with Roux-en-Y
anatomy in this series may be one of the reason for high technical success rate.
Review for 10.1186/s12876-021-01951-x (2021)

Title: Age is the only predictor for upper gastrointestinal malignancy in Chinese patients with
uncomplicated dyspepsia: a prospective investigation of endoscopic findings
Version: 0 Date: 28 Aug 2021
Reviewer's report:
Authors aimed to identify the current risk factors predictive of upper gastrointestinal malignancy
or peptic ulcer in China. However, this study is interesting, authors should concern below points.
Major comments.
1. In this study, H. pylori infection was determined by one of positive outcome of rapid urease
test and histology or 13C urea breath test (UBT). Did authors checked history of H. pylori
eradication therapy? Moreover, why gastric atrophy was not examined? Severity of atrophy,
rather than current status of H. pylori infection is important for gastric carcinogenesis. This is
critical.
2. Were the endoscopists known about the patients undergoing EGD are for this prospective
study. If so, this point may cause a slight bias because doctors investigate more carefully than
usual normal screening.
3. Were the found malignant lesions early or advanced gastric cancer? In cancer therapy,
prognosis is a very important factor. Authors should mention detail of the found malignant
lesions more.
4. Authors concluded that age should be considered as the primary indication for malignancy
in Chinese with uncomplicated dyspepsia regardless of the gender and they suggest that EGD
should be performed at age of 56 to identified upper GI malignancy. Can this conclusion apply
for asymptomatic people? Is screening endoscopy meaningless in people younger than 55?
Conclusion of this manuscript can make mislead. Authors should carefully check this point.]
Minor comments.
1.In page6, authors should carefully check below sentence. ‘In those subjects H. pylori infection
was determined by serology, 13C urea breath test and eradication history.’
Review for 10.1186/s12876-021-01951-x (2021)

Title: Age is the only predictor for upper gastrointestinal malignancy in Chinese patients with
uncomplicated dyspepsia: a prospective investigation of endoscopic findings
Version: 0 Date: 29 Aug 2021
Reviewer's report:
Dear Authors
Manuscript: Age the only predictor for upper gastrointestinal malignancy in Chinese patients
with uncomplicated dyspepsia: a prospective investigation of endoscopic findings.
This is a nice study done in China, Renji Hospital, Shanghai which is a single center prospective
observational study with a huge number of upper gastrointestinal symptoms patients underwent
esophagogastroduodenoscopy (EGD) with the aim to find the risk factors of major pathological
endoscopic findings in this group of patients.  The aim of this study is quite useful for the reader
in terms of selection appropriate patient to undergo EGD which is common problem in clinical
practice.
Major issues
In abstract at the conclusion, the “indication” should be used for the investigation rather than
for the diagnosis.  So, this should be revised.
In study design for the factor associated with the major lesions: The authors found esophageal
cancer 0.3% (15 cases) which one factor commonly associated with esophageal cancer is head
and neck cancer (5-30%), did the authors have this data which should be analyzed and included
in this study.
In Discussion and conclusion, Main discussion is focusing in upper GI malignancy but not the
peptic ulcer disease which was found more commonly than malignancy.  So, I would suggest to
add the predictors for peptic ulcer disease in discussion and conclusion as well.
Minor issues
The topic of this manuscript as “Age the only predictor”, I suggest to add is after age.  Thus,
it will be: Age is the only…………
Page 4 Line 3, because of dyspepsia should be “because of upper gastrointestinal symptoms”
Page 4 Line 11, with dyspepsia should be “with upper gastrointestinal symptoms”
I recommend language editing
Review for 10.1186/s12876-021-01951-x (2021)

Title: Age is the only predictor for upper gastrointestinal malignancy in Chinese patients with
uncomplicated dyspepsia: a prospective investigation of endoscopic findings
Version: 1 Date: 28 Sep 2021
Reviewer's report:
Thank you for revising this manuscript as suggestions and my opinion for this manuscript is
accepted for publication.
Review for 10.1186/s12876-021-02017-8 (2021)

Title: Risk of Severe COVID-19 and Mortality in Patients with Established Chronic Liver
Disease: A Nationwide Matched Cohort Study
Version: 3 Date: 04 Jun 2021
Reviewer's report:
The findings of this population based study (risk of severe COVID-19 / mortality due to
COVID-19 in CLD patients was not different from that in the general population) are different
from a number of hospital based studies, wherein patients with cirrhosis and COVID-19 had
higher mortality rates compared to controls.
I have the following comments:
1. Did any study patients die due to therapeutic limitation (ie. was death due to lack of availability
of ICU beds)
2. Did any study patient in the control arm have chronic liver disease mentioned as a co-
morbidity.
Review for 10.1186/s12876-021-02017-8 (2021)

Title: Risk of Severe COVID-19 and Mortality in Patients with Established Chronic Liver
Disease: A Nationwide Matched Cohort Study
Version: 3 Date: 07 Jun 2021
Reviewer's report:
I congratulate the authors for their study. I made a few suggestionf to potentially improve the
reporting of their results:
1. How did you select controls? You named them "without recorded CLD" - but based on clinical
or histopathology data? How did you select 5 of them per each case - randomly or by any other
method? This aspect is of paramount relevance and this influences decisively or HR estimates.
2. The cases had higher prevalence of all comorbidities measured at index date (biopsy), many
of them the main risk factors for severe COVID in the general population and some of them
intrinsically related to CLD (e.g. metabolic syndrome); how can we say that this did not have
at least a similar impact on CLD patients and per se increased the risk of COVID complications
further? Don't you think the prevalence of COVID in your sample is just too small (follw-up
from 02 to 07/2020)?
3. Cases showed higher all-cause mortality rate but similar severe COVID rate. Could this
mortality excess be attributable to liver disease only or just no-covid-related factors? Could the
impact of the COVID pandemic on the health system be the driver of this mortality excess or
this difference would be similar in preCOVID era? Are there any other explanations?
4. I would suggest the authors elaborate more on the impact of their findings namely: (1) a
plausible biological explanation for the apparent lack of increased risk of severe COVID among
CLD patients; (2) the lessons for the every-day clinician and for public health authorities for
this and perhaps another viral pandemic.
5. I praise the authors for the space dedicated to the limitations of their study, I fully agree with
them.
Review for 10.1186/s12876-021-02017-8 (2021)

Title: Risk of Severe COVID-19 and Mortality in Patients with Established Chronic Liver
Disease: A Nationwide Matched Cohort Study
Version: 6 Date: 14 Aug 2021
Reviewer's report:
I appreciate the authors' work on revising their manuscript.
My comments have been generally appropriately addressed.
I would recommend including the added references.
Review for 10.1186/s12876-021-02030-x (2021)

Title: Patient preferences of healthcare delivery in irritable bowel syndrome: a focus group study
Version: 0 Date: 16 Jul 2021
Reviewer's report:
I would like to congratulate the authors in addressing such an important issue on IBS patients'
preferences.  IBS patients prefer a multidisciplinary team approach, to include a physician
with expertise in the area, specialist nurse, dietitian, and psychologist, thus highlighting the
complexity and multifactorial nature of IBS. Patients focused on communication, information,
expertise and scientific research   IBS patients' problems  should not be addressed by simply
dietary modification or psychological therapies alone but should promote patient empowerment,
education and self-management.  It would be of interest to know whether the authors are planning
to take the results of this study a stage further; i.e. form MDT to include the above expertise
and compare the management of IBS patients in such centres in contrast to the conventional
approach in either primary care, or via dietary modification or psychological therapy  alone
Review for 10.1186/s12876-021-02030-x (2021)

Title: Patient preferences of healthcare delivery in irritable bowel syndrome: a focus group study
Version: 0 Date: 27 Sep 2021
Reviewer:  Greger Lindberg
Reviewer's report:
This is a qualitative study with focus groups of needs for patients with IBS. The authors claim
that multidisciplinary treatment teams, centers of expertise and clear communication are needed
for patients with IBS. Although I sympathize with the unique employment of focus groups for
identifying the needs of patients with IBS there are a couple of issues with the present study that
need clarification or amendments.
1. The concept “centers of expertise” is actually introduced by those performing the interviews.
Isn’t there an obvious risk for bias if you ask “How do you feel about centers of expertise for
IBS care?” and “Which type of healthcare givers would you like to be involved in IBS centers
of expertise?” Do you think centers of expertise would have come up had you not mentioned
them to the participants? Please discuss these matters. Apart from the bias, would you say that
all patients with IBS would benefit from IBS centers of expertise? See also item #2 below.
2. I am uncertain about the representativeness of the 24 subjects included in this study. To
begin with the proportion of people who fulfil the Rome-III or Rome-IV criteria for IBS is quite
substantial and somewhere between 10-20 %. However, the proportion of people who receive the
diagnosis of IBS in primary or secondary care amounts only to 1-2 %. All subjects in this study
had been diagnosed by a doctor, so the participants came from the smaller (1-2 %) population
of people with IBS-like symptoms. Those are the patients who actually seek medical advice
for their symptoms (but the majority do not). So this smaller group consists of those that seek
answers. Some of those, do so because they can never understand, nor accept an explanation.
That is so because they have some variant among the autism spectrum disorders (ASD). In
tertiary care I would say these make up a substantial proportion of patients (perhaps 1/10) that
gastroenterologists can never satisfy. But how many of the participating subjects do you think
might have had ASD?
3. In Discussion the authors write that “we showed” (line 237 and line 271). I think it is more
correct to say “we found”.
4. Reference 30 should read: Gastroenterology 2016;150 (6):1332–1343.
5. The whole concept of IBS is more or less a moving target. Among those we thought had IBS
in the early 1980’s nearly two thirds (2/3) have with time received other diagnoses (e.g. bile
acid diarrhea, microscopic colitis, celiac disease, various carbohydrate malabsorptive disorders,
exocrine pancreatic insufficiency, genetic aberrations and so on. IBS of today is still not a
homogenous group. It is much more likely that it consists of several smaller groups yet awaiting
diagnosis. The term IBS lump them together only on the basis of symptom similarities and
perhaps the fact that we don’t know what causes their symptoms. What is the impact (if any) of
our lack of knowledge with regard to patients’ need for "clear communication"?
Review for 10.1186/s12876-021-02030-x (2021)

Title: Patient preferences of healthcare delivery in irritable bowel syndrome: a focus group study
Version: 2 Date: 03 Nov 2021
Reviewer:  Greger Lindberg
Reviewer's report:
The authors have improved the manuscript. Some uncertainty remains but mainly due to the fact
that we do not understand the pathophysiology of IBS. I have no further questions or comments.
Review for 10.1186/s12876-021-02021-y (2021)

Title: The effect of menopausal hormone therapy on gastrointestinal cancer risk and mortality
in South Korea: a population based cohort study
Version: 3 Date: 05 May 2021
Reviewer's report:
This retrospective cohort study investigates the association between menopausal hormone
therapy (MHT) and gastrointestinal (GI) cancer risks in South Korea. The author concluded that
menopausal hormone therapy was associated with decreased incidence of GI cancer. A dose-
response relationship was identified in the landmark analysis. Overall, the study is interesting
and has significant clinical value. I have only some minor comments.
1. In Figure 2, Figure S2, and Figure 3, some survival curves seem to cross. As the authors
choose Cox proportional hazards regression model to calculate the HR, please examine whether
the proportional hazards assumption was violated.
2. P.12: “The association between MHT use and GC diagnosis hepatobiliary or pancreatic cancer
(HR: 0.847 and HR: 1.163, respectively).” Some words seem to be missing.
3. P.23: “Third, we used Landmark analysis …… to minimize the possibility of lead-time bias.”
Did the authors mean immortal time bias? The lead-time bias and the immortal time bias are
different concepts.