JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-01998-w (2021)

Title: Diagnostic yield of esophagogastroduodenoscopy, colonoscopy, and small bowel
endoscopy in Thai adults with chronic diarrhea
Version: 2 Date: 05 Sep 2021
Reviewer's report:
Dear Editors and authors,
I realized that the authors did put the high effort the revise the manuscript. I think this work is
much improved. However, I still have two major concerns as the following;
1. The author changed the definition of chronic diarrhea by adding the time <4 weeks, regarding
to the reviewer 2's suggestion. I totally agreed with the reviewer 2's suggestion. I'm not sure that
why the number of included patients per year was not decreased (50-60 pt. per year) and the
percentage of IBS patients was still high. Because the definition was more concise. the average
number of patients per year  as well as the number of IBS patients should be decreased. Please
re-check the data.
2. From the response to editor No.4, the author said that "The median amount of weight loss
was 0 kg with the interquartile range of 0-3 kg". But these data were different from the data in
Table 1. I'm not sure which one is correct.
Review for 10.1186/s12876-021-01998-w (2021)

Title: Diagnostic yield of esophagogastroduodenoscopy, colonoscopy, and small bowel
endoscopy in Thai adults with chronic diarrhea
Version: 3 Date: 16 Oct 2021
Reviewer's report:
Thank you for the author's explanation. However, I still concern about a very high percentage of
IBS patients in this study (39%).  This maybe from the limitation of retrospective study.  Some
physicians might not strict to the definition of chronic diarrhea (> 4 weeks of persistent watery
diarrhea) and made a wrong diagnosis in IBS patients as a chronic diarrhea.  Please discuss on
this issue and consider mention this uncommon finding in the limitation of this study.
Review for 10.1186/s12876-021-02001-2 (2021)

Title: An Alternative Splicing Signature in Human Crohn’s Disease
Version: 2 Date: 03 Jun 2021
Reviewer's report:
In the validation study, the authors sequenced 8 subjects. The sample size is really small which
made the conclusion is not so robust. The included CD patients all received different medications
including biologics and immunosuppression which may also infect the expression of genes.
Better to include treatment naïve CD patients.
Among the discovered approximately 3,000 unique AS events in CD patients compared to the
healthy controls from a public mRNA-seq data, the authors only validated two AS events which
are STAT3 and IRF1 genes. How about the other genes? Moreover, whether these identified AS
events play a vital role in the pathogenesis of CD, eg, affecting protein diversity or downstream
signaling transduction pathways warrant further study.
There are some grammatical and spelling errors in this manuscript which need to be further
proof-reading by native speakers.
Review for 10.1186/s12876-021-02001-2 (2021)

Title: An Alternative Splicing Signature in Human Crohn’s Disease
Version: 4 Date: 22 Sep 2021
Reviewer's report:
I think the majority of my comments has been answered and the language of the revised
manuscript has much improved. Still the identified two AS events should be validated eg, use
treatment naïve patients or in another cohort, and their possible functions warrant further study.
The tables should not be embedded in the main part of the manuscript, they should be uploaded
separately.
Review for 10.1186/s12876-021-02001-2 (2021)

Title: An Alternative Splicing Signature in Human Crohn’s Disease
Version: 6 Date: 19 Oct 2021
Reviewer's report:
As the authors mentioned, due to the budget limitation and the sample limitation,  a western blot
to validate the impact of 3’UTR change on
protein expression wasn't performed. I hope the authors can continue their work in the future
to further validate these preliminary results. Moreover, this should be listed the as a major
limitation in their manuscript which warrant further study.
Review for 10.1186/s12876-021-02004-z (2021)

Title: Impact of cone-beam computed tomography with automated feeder detection software
on the survival outcome of patients with hepatocellular carcinoma during treatment with
conventional transarterial chemoembolization
Version: 1 Date: 21 Oct 2021
Reviewer's report:
Authors should be commended for their work.
I have the following comments:
1) Usually the main limitation of CT scan after conventional TACE is that it cannot capture
eventual residual viable tumoral areas in the nodule (due to lipiodol stain). How this new
technique overcomes this issue?
2) THe Kaplan Meyer curve should be improved reporting censored and number at risk.
3) Overall survival in HCC patients could be due to other clinical factors that should be
mentioned in the paper. Comment at least these, citing the relevant papers:
- Diabetes (PMID: 23845075)
- Use of eventual post-treatment systemic therapies (for example sorafenib or regorafenib,
PMID: 31877664, or newer immunotherapy ,PMID: 33086471).
Review for 10.1186/s12876-021-01984-2 (2021)

Title: Correlation of MKI67 with Prognosis, Immune Infiltration, and T Cell Exhaustion in
Hepatocellular Carcinoma
Version: 1 Date: 24 Aug 2021
Reviewer's report:
Interesting work.
My only recommendations are about the discussion that should be improved:
1) More insights on the pathogenesis of HCC should be provided. On this regard, cite and
comment the following papers:
- PMID: 29220698 on the molecular mechanisms in the setting of HCC on NAFLD progression
- PMID: 28976021 on fibrosis progression in HCV patients
- PMID: 23845075 on role of metabolic factors and diabetes in immunomodulation in HCC
- PMID: 25974743 on the role of angiotensin pathway in fibrosis progression
Review for 10.1186/s12876-021-01984-2 (2021)

Title: Correlation of MKI67 with Prognosis, Immune Infiltration, and T Cell Exhaustion in
Hepatocellular Carcinoma
Version: 1 Date: 24 Aug 2021
Reviewer's report:
Well written study. I recommend only to have the manuscript revised for grammar and clarity
by a native speaker.
Review for 10.1186/s12876-021-01987-z (2021)

Title: Can the Simplified Magnetic Resonance Index of Activity be Used to Evaluate
the Degree of Activity in Crohn's Disease?
Version: 1 Date: 20 May 2021
Reviewer's report:
This is a well-designed and interesting study. However, I've detected a few issues:
In Table 1, please clarify disease location (L) according to Montreal classification.
In Table 2, you are analyzing disease activity. How could you explain 106 terminal ileum
segments while you are analyzing 93 patients? The same with all other segments.
Please indicate the normal range of FC.
Table 3, please indicate what biomarkers values you are writing means (range) or median
(interquartile range)?
The discussion could be more "deeper. "
What are the advantages and differences of your article from this one?
Roseira J, Ventosa AR, de Sousa HT, Brito J. The new simplified MARIA score applies
beyond clinical trials: A suitable clinical practice tool for Crohn's disease that parallels
a simple endoscopic index and fecal calprotectin. United European Gastroenterol J. 2020
Dec;8(10):1208-1216. doi: 10.1177/2050640620943089. Epub 2020 Jul 14. PMID: 32664824;
PMCID: PMC7724527.
Review for 10.1186/s12876-021-01989-x (2021)

Title: Factors influencing failure to undergo interval cholecystectomy after percutaneous
cholecystostomy among patients with acute cholecystitis : A retrospective study
Version: 0 Date: 18 Jul 2021
Reviewer:  Gabriel Sandblom
Reviewer's report:
The manuscript describes an observational study on the decision process in patients having
undergone percutaneous cholecystostomy for acute cholecystitis. This is a patient group with
high co-morbidity and sometimes severe cholecystitis. The decision to insert a percutaneous
drain in the first place, whether this is intended the final therapy or as bridge to surgery, and
whether to carry out a planned cholecystectomy at a later stage requires careful consideration of
the expected natural course of the gallstone disease, the age and co-morbidity of the patient as
well as the patient’s own preference. The paper raises no doubt that the patients in this cohort
were managed in an optimal way and that the right decisions were taken in each individual
case, but the lack of data on the outcome after delayed cholecystectomy versus conservative
management makes the present cohort useless as a model for decision-making in similar
situations.
Major comments
1. Please provide data about treatment failure related to the percutaneous cholecystostomy. I
assume that there were cases of biliary leakage, dislocated drains and need for repeated insertion
of cholecystostomy, which may have affected the subsequent decision to perform surgery.
2. How were the patients followed after the initial treatment? The more active follow-up and
frequent visits, the greater the chance of being offered delayed cholecystectomy.
3. Mortality is a major confounding factor as it is related to age and co-morbidity, which has
a crucial impact on the decision to perform surgery.  The shorter the survival, the shorter the
time period when a delayed cholecystectomy could be carried out, notwithstanding the risk for
perioperative cardiovascular complications. This should be commented in the discussion.
4. How many patients were admitted with a recurrent episode of acute cholecystitis requiring
cholecystostomy? Did this have an impact on the chance of undergoing cholecystectomy as
bridge to surgery?
5. How many patients had liver cirrhosis?
Minor comments
1. What does concomitant AC (page 4, line 80) mean?
2. The manuscript needs language editing.
Review for 10.1186/s12876-021-01989-x (2021)

Title: Factors influencing failure to undergo interval cholecystectomy after percutaneous
cholecystostomy among patients with acute cholecystitis : A retrospective study
Version: 0 Date: 30 Jul 2021
Reviewer:  shridhar Iyer Ganpathy
Reviewer's report:
There is a pertinent clinical question that the authors have tried to address. However there are
serious methodological shortcomings that need to be addressed .
In addition some of the definitions need to be clearer
The grammar and language needs correction
Review for 10.1186/s12876-021-01983-3 (2021)

Title: The analysis of multilevel factors affecting adenoma detection rates for colonoscopies:
A large-scale retrospective study
Version: 1 Date: 16 Jun 2021
Reviewer's report:
I congratulate the authors on the database used for the manuscript. Quality assessment is of
essential importance in colonoscopy. However, the present paper lacks novel findings
Review for 10.1186/s12876-021-01983-3 (2021)

Title: The analysis of multilevel factors affecting adenoma detection rates for colonoscopies:
A large-scale retrospective study
Version: 1 Date: 17 Jun 2021
Reviewer:  Dalbir Sandhu
Reviewer's report:
The authors should be commended on this well written and well conducted study.
Few points:
How did the authors decide to dichotomize senior and junior with the number of 3000
colonoscopies. Did this include colonoscopies done as a trainee?
Why did the authors include ESD in their division of senior and junior endoscopist?
If an endoscopists had done >3000 colonoscopies but did not do ESD - which category were
they placed in?
The authors included serrated adenomas as part of adenoma although sessile serrated polyps is
still not considered as a part of ADR. This should be discussed (as deleting it from the results
may need a great deal of alteration).
The study is from China - it will be worthwhile mentioning if there is a nationwide screening
for colon cancer program in China for the readers of this journal. Also, it will be important to
mention the age at which screening colonoscopies are offered.
What do the authors mean by 'single examiner colonoscopy' and 'dual-examiner colonoscopy'?
If dual examiner means 2 attending proceduralists - how was that information included in the
study?
The authors did not include some important factors for ADR including family history of colon
cancer/polyps, withdrawal time - this should be discussed.
In discussion - page 13 - the authors mention - "Our findings, along with recently published
guidelines (19,20), suggest that individuals with a family history of CRC should have their
first screening colonoscopy at age 45......" I'm not sure which finding in the study corroborates
these societal guidelines of starting screening colonoscopy at age 45 since information on family
history is missing in the current study. In fact on page 15, authors mention information on 'family
history' was not available.
What type of sedation was used - monitored anesthesia care (Propofol), moderate sedation,
general anesthesia or combination?
Review for 10.1186/s12876-021-01986-0 (2021)

Title: Both the serum AFP test and AFP/GPC3/SALL4 immunohistochemistry are beneficial
for predicting the prognosis of gastric adenocarcinoma
Version: 2 Date: 10 Jun 2021
Reviewer's report:
Wang et al investigated that  gastric adenocarcinoma cases with definite sAFP levels and then
analyzed their clinicopathological characteristics and immunohistochemical results of AFP,
GPC3, and SALL4. They determined the value of sAFP and A/G/S-IHC in the diagnosis and
treatment of gastric adenocarcinoma.  The manuscript is well illustrated that the conclusions
supported by the evidence presented and the methods sufficiently described to allow the study
to be repeated.
Review for 10.1186/s12876-021-01986-0 (2021)

Title: Both the serum AFP test and AFP/GPC3/SALL4 immunohistochemistry are beneficial
for predicting the prognosis of gastric adenocarcinoma
Version: 2 Date: 06 Sep 2021
Reviewer:  Nikolaos Charalampakis
Reviewer's report:
This manuscript describes the results of a retrospective analysis of patients with rare gastric
adenocarcinoma subtypes that express AFP or manifest with primary enterocyte phenotype. The
authors separated patients into two groups based on preoperative measurements of AFP. Patients
in the operable group were further divided according to AFP expression or GAPEP phenotype
positivity. The authors of this study should be praised for touching on a rare tumor subtype,
which is usually associated with negative prognosis. The manuscript is well written, in a proper
and concise manner and study methods lead to clear and logical conclusions.
The strongest point of this study is the clear association between high AFP expression and
GAPEP phenotype, which is indicative of the fact that these tumors might represent a distinct
entity in gastric cancer, with clear and identifiable molecular and clinical characteristics.
The study has a few minor weaknesses, which should be discussed more clearly in the
manuscript:
1. AFP is a serum value that can be elevated in a variety of pathological conditions, such as liver
disease. Although patients with acute hepatitis were excluded from the study, the authors do not
mention possible comorbidities in patients with high AFP.
2. AFP expressing gastric cancer and GAPEP are rare tumors, resulting in disparities in subgroup
populations that hinder statistical analysis. Over 90% of patients included in this study did not
express AFP or GAPEP phenotype.
3. Group B included patients based on the expression of AFP alone, regardless of subsequent
treatment. The value of the findings in this subgroup is not adequately explained. There is an
association of increased AFP with worse prognosis, but as mentioned in the text, the majority
of patients in this subgroup had liver metastases. A previous study by Hirajima et al. (2013)
concluded that increased AFP could not be used as an independent prognostic marker in
AFP-producing gastric cancer and that the only independent factor was the presence of liver
metastases. Moreover, as mentioned by the authors, there was no comparator arm in group B.
4. In Group A, patients with high AFP or GAPEP, on average, presented with more advanced
disease, which is an independent negative prognostic factor. Although the PSM analysis showed
a statistically significant difference in outcomes for AFP-high patients when other factors were
taken into consideration, unequal distribution of patients between the comparator groups might
have confounded the outcomes.
5. In the paper, it is mentioned that 7 patients with high levels of preoperative AFP were
monitored afterwards and AFP dropped after surgery and within the next year. It would be
interesting if survival data of these patients were available.
Review for 10.1186/s12876-021-01986-0 (2021)

Title: Both the serum AFP test and AFP/GPC3/SALL4 immunohistochemistry are beneficial
for predicting the prognosis of gastric adenocarcinoma
Version: 3 Date: 09 Oct 2021
Reviewer:  Nikolaos Charalampakis
Reviewer's report:
The authors revised the major points suggested by peer-reviewers and the article and the
manuscript should be accepted for publication.
Review for 10.1186/s12876-021-01985-1 (2021)

Title: Heat sink effect of underwater polypectomy in a porcine colon model
Version: 1 Date: 09 Jun 2021
Reviewer:  Benedict Kjaergaard
Reviewer's report:
The issue is relevant and may under some circumstances be used in the human clinic after further
studies.
It seems unclear in the text if there were used only colons from two pigs with seven polyps in
each, so the total number of polyps were 14. Please specify this.
Under limitations you mention that it will be difficult to perform the experiment in humans, but
I suggest that you write that it could be possible to perform studies in living pigs as the next step.
I find the article well written.
Very best
Benedict Kjaergaard
Review for 10.1186/s12876-021-01985-1 (2021)

Title: Heat sink effect of underwater polypectomy in a porcine colon model
Version: 1 Date: 19 Jul 2021
Reviewer:  Yanan Yang
Reviewer's report:
First of all, the manuscript study a new polypectomy method through experiment, the
contribution is valuable.
Several comments:
a.the water temprature can be obtained in the future
b. the heat sink certainly have an impact on the polypectomy while the water is filled in. In the
future, the intensity of temperature change also can be stuidied.
c. the location of the temperature measurement point needs to be described in detail
Review for 10.1186/s12876-021-01958-4 (2021)

Title: Correlation between HDL2, HDL3 and serum ferritin levels with fatty liver and NAFLD
Activity Score (NAS) in liver histology of organ donors
Version: 2 Date: 10 Jul 2021
Reviewer's report:
I have read with interest this well written manuscript by Saman Nikeghbalian, et al. This valuable
study evaluated the correlation between HDL subtypes and serum ferritin levels with evidence
of NAFLD in liver histology of organ donors. They found that lower HDL2 values and HDL2/
HDL3 ratio were associated with increased NAFLD activity score, and higher levels of ferritin in
organ donors may be associated with increased AST and ALT 24 hours after liver transplantation
in the organ recipient. I look forward to future clinical applications, however there are several
issues that need attention.
Comments:
1. I feel that the introduction is a bit redundant, so please summarize it. The explanation of
the NAFLD activity score may be more appropriate in the materials and methods section or
discussion section.
2. Please describe present key elements of study design.
3. Result section: “Serum levels of HDL2, HDL3 and ferritin were measured and recorded in
all cases. In addition, the same pathologist examined all biopsies of donated livers for NAFLD
activity score (NAS).” ##Please describe it in the method section.
4. Result section: “To investigate the relationship between serum levels of HDL2, HDL3 and
ferritin with NAS, all participants in the study were divided into two groups:
Group 1: cases with NAS #1.
Group 2: cases with NAS >1.” ##Please describe it in the method section.
In addition to the above, other contents that should be written in the method are written in the
result.
5. #Kowdley et al. found that ferritin >450 ng/ml was associated with higher levels of NAS,
AST, ALT and increased hepatic fibrosis [17].
##What is the rationale for binarizing at 1000 in this study? Also, what is the cutoff value in
this study?
6. What would be the result if the cases with possible elevated ferritin as an acute inflammatory
response are excluded?
7. How about multivariate analysis to examine factors associated with NAS>1?
8. Discuss limitations of the study, taking into account sources of potential bias or imprecision.
Review for 10.1186/s12876-021-01958-4 (2021)

Title: Correlation between HDL2, HDL3 and serum ferritin levels with fatty liver and NAFLD
Activity Score (NAS) in liver histology of organ donors
Version: 4 Date: 22 Sep 2021
Reviewer's report:
Unfortunately, I cannot find any reply from the author. As I informed the secretariat before,
there is only a reply to the other reviewer.
Review for 10.1186/s12876-021-01991-3 (2021)

Title: Quantitative splenic embolization possible-Application of 8Spheres conformal
microspheres in partial splenic embolization(PSE)
Version: 0 Date: 02 Aug 2021
Reviewer:  Nobuo Waguri
Reviewer's report:
In this manuscript, the authors presented a very easy-to-understand study in which partial splenic
artery embolization with microspheres was performed in a unified manner in a large number of
cases to investigate the differences in the effects and complications depending on the diameter
of the microspheres. However, there are some problems to be confirmed.
Major comments
1. First, the cases are divided into two groups that are so neatly similar, and PSE is performed by
a unified method. The authors state that the shortcoming of this study is retrospective fashion,
but is it really a retrospective study?
Isn’t it a prospective controlled study?
2. As a PSE procedure, it is stated that the entire amount of 1 vial of microspheres was injected
from a microcatheter placed at the splenic hilum. However, the details of the injection procedure
are insufficient.
Minor comments
2-1. Most interventional radiologists usually perform embolization after selectively inserting a
microcatheter into the upper or lower pole branch of the splenic artery to clarify the area to be
embolized. We do not see the benefit of injecting embolic material throughout the spleen.
2-2. How is the microsphere diluted before injection? If the microspheres are not diluted
sufficiently, they will aggregate and embolize the proximal artery as large masses, and the
original size of the microspheres will not be utilized.
2-3. The microsphere injection must be performed so that it does not backflow from the tip of
the microcatheter. Can the authors always inject the entire volume of one microsphere vial?
2-3. Have the authors confirmed that microspheres flow from the peripheral branches of the
splenic artery to the branches that go out of the spleen (stomach, pancreas, omentum, etc.)?
Review for 10.1186/s12876-021-01991-3 (2021)

Title: Quantitative splenic embolization possible-Application of 8Spheres conformal
microspheres in partial splenic embolization(PSE)
Version: 0 Date: 20 Sep 2021
Reviewer's report:
My congratulations to the authors for their interesting article.
It may be reconsidered for publication after the authors revise the following aspects:
1 - Hypersplenism is not secondary splenomegaly and both different diseases cannot be
considered together.
2 - Authors put together true hypersplenism due to an unknown disease of the spleen, which
destroy the blood elements, with congestive splenomegaly due to portal obstruction, which
prserve the blood elements and release them to the blood flow if necessary.
3 - It is not correct to write secondary hypersplenism, considering this is by definition a primary
hematologic uncknown disease.
4 - Leukopenia and thrombocytopenia due to congesstive splenomegaly is not a problem because
if the patient requires the blood elements the spleen release them. Therefore a leukopenia as
small as 800  leukocytes rise to 12,000 in presence of an appendicitis, for example. No patients
with less than 50,000 platelets present cloat disorder in presence of congestive splenomegaly.
Otherwise, in presence of hypersplenism, the patient present hemorrhages with 100,000 platelets
and the 7,000 leukocytes do not rise in presence of severe infection.
5 - Patients wihich were not included cannot be excluded.
6 - The results must be completely rewritten. Data from tables must be removed from the text.
The authors must write only relevant informations of tables in the text without repeating tables.
7 - The number of blood elements is not the most important, but the efficacy of those elements.
8 - The authors should not repeat method and results in discussion, but only make comments
about what is relevant.
9 - Red and white pulps are not the only zones of the spleen.
10 The authors repeat the same data in tables, results and discussion. It does not make any sense.
11 - Conclusion is a poor summary of method and results without any conclusion.
I suggest the authors to study hypersplenism and to look for a researcher to teach them how to
write a scientific paper.
Review for 10.1186/s12876-021-01991-3 (2021)

Title: Quantitative splenic embolization possible-Application of 8Spheres conformal
microspheres in partial splenic embolization(PSE)
Version: 2 Date: 09 Oct 2021
Reviewer:  Nobuo Waguri
Reviewer's report:
More details have been added about the PSE method, especially the usage of microspheres. The
reason for injecting the embolic substance at the splenic hilum, consideration for blood vessels
going out of the spleen, and the injection method to prevent backflow were also described in
response to my request. But some concerns remain.
In Japan, even when used for embolization of liver tumors, it is usually diluted several tens of
times and injected so that microspheres do not aggregate.
At a dilution of about 2 to 8 times, agglomeration generally occurs considerably.
It's hard to believe that the 2-fold dilution does not result in microsphere aggregation.
Furthermore, it is hard to believe the authors' explanation that 179 cases of angiography did not
show the omentum branch that goes out of the spleen from inside the spleen.
However, the authors claim that, and further discussion is unproductive.
Review for 10.1186/s12876-021-01979-z (2021)

Title: Physicians’ knowledge, attitude, and prescribing behavior regarding stress ulcer
prophylaxis in China: A multi-center study
Version: 2 Date: 14 May 2021
Reviewer:  Joseph Fadare
Reviewer's report:
Page 9 (starting from " the predictors of high prescribing behaviour in multivariate analysis" to
p=.001) - This segment should be revised - instead of using the statements  ( I agree that SUP
is a prescribing habit), the authors may want to use " respondents who agreed that SUP is a
prescribing habit" etc.
Table 2: This table can be re-formatted using landscape orientation with the statements in the
first column and the options in the other columns. It would make it smarter and easy to follow
Review for 10.1186/s12876-021-01979-z (2021)

Title: Physicians’ knowledge, attitude, and prescribing behavior regarding stress ulcer
prophylaxis in China: A multi-center study
Version: 3 Date: 22 Aug 2021
Reviewer:  Muhammad Eid Akkawi
Reviewer's report:
The main comment:
Again, all guidelines including ASHP, DSAICM and EAST DO NOT recommend SUP in major
surgery except for major burn surgery or organ transplantation. However, the authors stated that
major surgery was considered as a risk factor for stress ulcer in these guidelines, which is not
true. For the Chinese guidelines, I could not retrieve it online, so I am not sure whether major
surgery was stated there or not. Anyway, the whole study depends on considering major surgery
as risk factor for SUP and if there is no evidence/guidelines support this assumption, then the
study results are invalid.
Other comments:
Abstract:
“prescribing behavior of the perioperative patients toward surgeons regarding SUP”: Do patients
prescribe medications for surgeons?! Please give it back to the English proof-reader.
Methods: again delete the word ‘national’.
Introduction:
NMJC is the journal where the Chinese guidelines were published. So, it should be used as a
short name of the guidelines!
“attendance at continuing education programs”: what kind of educational programs? are they
related to the use of PPI as SUP?
Methods and results:
Authors agreed with my comments that the response for some statements should be yes/no
instead of Likert scale. The authors just changed it in the questionnaire but in fact that was not
what had been asked to the physicians. Authors need to mention how they handled the answers
using the original questionnaire. For instance, “I agree that SUP is a prescribing habit” the answer
provided for this statement was ‘a. Always b. Usually c. Sometimes d. Rarely e. Never’ as now
we agreed that the answer should be yes or no, what are answers considered yes and what other
choices considered no?
I suggested to add sex, age, education level and years of experience as variables to the logistic
regression. The authors responded that they did it. But I could not see that in tables 3 & 6!
Review for 10.1186/s12876-021-01979-z (2021)

Title: Physicians’ knowledge, attitude, and prescribing behavior regarding stress ulcer
prophylaxis in China: A multi-center study
Version: 4 Date: 30 Sep 2021
Reviewer:  Joseph Fadare
Reviewer's report:
Thank you for addressing the issues raised by Reviewer 2.
My own comments had been adequately addressed earlier.
Review for 10.1186/s12876-021-01953-9 (2021)

Title: Endoscopic Ultrasound Guided Fine Needle Biopsy (EUS-FNB) from Peritoneal Lesions:
A Prospective Cohort Pilot Study
Version: 1 Date: 15 Jul 2021
Reviewer's report:
In this prospective study, the authors evaluated the yield of EUS-FNB for the diagnosis of
peritoneal lesions. The topic is interesting and not fully investigated so far.
Here my comments:
- Please add this reference (PMID: 29941722) after this sentence in the introduction section:
“Nevertheless, it is not practical to use tissue from EUS-FNA for IHC staining due to the
relatively small volume of tissue collected compared to a EUS-guided fine needle biopsy (EUS-
FNB)”.
- In Table 2, please indicate the diagnostic yield of abdominal paracentesis.
- In your study, you used a large bore, side-fenestrated needle (20 gauge). To me, this needle
is not the optimal one for sampling small peritoneal lesions. This point could explain the low
sensitivity you obtained in your study (63%). Moreover, recent studies have demonstrated that
new generation end-cutting needles (e.g., Fork-tip and Franseen) outperformed side fenestrated
ones. Please discuss this point by adding these references
(PMID: 34116031, PMID: 32433914)
- A novel technique for peritoneal sampling has been recently proposed (Moray microforceps).
This tool demonstrated to be able to achieve a definitive diagnosis in more than 70% of cases.
Please discuss this point by adding these references (PMID: 33765374, PMID: 31323232).
Review for 10.1186/s12876-021-01953-9 (2021)

Title: Endoscopic Ultrasound Guided Fine Needle Biopsy (EUS-FNB) from Peritoneal Lesions:
A Prospective Cohort Pilot Study
Version: 1 Date: 17 Jul 2021
Reviewer's report:
The manuscript is interesting, i have just some minor suggestions:
1) Why antibiotic prophylaxis was undertaken before tissue sampling. Current guidelines do not
recommend it anymore.
2) A deeper comment on the available needles for EUS-tissue acquisition should be added to
the discussion, starting with the fields where there is more evidence (i.e., pancreatic masses). In
this regard, cite the following articles:
-  PMID: 29026598
- PMID: 31374187
- PMID: 32014422
- PMID: 34205389
- PMID: 27356212
Review for 10.1186/s12876-021-01982-4 (2021)

Title: Larotinib in Patients with Advanced and Previously Treated Esophageal Squamous Cell
Carcinoma with Epidermal Growth Factor Receptor Overexpression or Amplification: An Open-
Label, Multicenter Phase 1b Study
Version: 0 Date: 19 Jul 2021
Reviewer's report:
Thank you for give me an opportunity for evaluating this prospective study. It seems this study
evaluated risk benefit of esophageal squamous cell carcinoma. We usually call this type of study
as phase 2 study, however authors described phase 1b. Is there any specific reason? Several
concerns are raised before publication.
Major
#1 Statistical procedure, its not clear what is primary endpoint of this study
#2 Why author choose non evaluable cases in this study? What is your purpose?
#3 What is dose-limiting toxicity of this drug?
#4 How about interstitial pneumonitis? Is that related with previous radiation?
#5 Patients characteristics is too simple. Previous surgery is important information.
#6 Why no response were obtained in 300mg larotinib? The explanation is not enough.
Review for 10.1186/s12876-021-01982-4 (2021)

Title: Larotinib in Patients with Advanced and Previously Treated Esophageal Squamous Cell
Carcinoma with Epidermal Growth Factor Receptor Overexpression or Amplification: An Open-
Label, Multicenter Phase 1b Study
Version: 0 Date: 24 Jul 2021
Reviewer's report:
With few treatment options for unresectable, advanced ESCCs, this study appears to be very
useful. This report is intriguing and will meet the criteria of this journal. However, there are
some points that should be addressed.
1. What was the patient's weight or body surface area? I think that the dose of anti-EGFR
antibody is usually determined per body weight or body surface area. Should be specified.
Review for 10.1186/s12876-021-01982-4 (2021)

Title: Larotinib in Patients with Advanced and Previously Treated Esophageal Squamous Cell
Carcinoma with Epidermal Growth Factor Receptor Overexpression or Amplification: An Open-
Label, Multicenter Phase 1b Study
Version: 2 Date: 02 Oct 2021
Reviewer's report:
The authors responded accurately to the reviewer's comments.
Review for 10.1186/s12876-021-01982-4 (2021)

Title: Larotinib in Patients with Advanced and Previously Treated Esophageal Squamous Cell
Carcinoma with Epidermal Growth Factor Receptor Overexpression or Amplification: An Open-
Label, Multicenter Phase 1b Study
Version: 2 Date: 14 Oct 2021
Reviewer's report:
Author described point to point answer. I can understand the study precisely.
Review for 10.1186/s12876-021-01974-4 (2021)

Title: The liver steatosis severity and lipid characteristics in primary biliary cholangitis
Version: 0 Date: 08 Jul 2021
Reviewer:  Vik Meadows
Reviewer's report:
The authors present an interesting study on the lipid levels in various chronic liver diseases in
comparison to PBC patients. They found increased HDL and decreased CAP in PBC patients
which may be indicative of reduced PBC comorbidity of atherosclerosis.
There are some points the authors must address prior to revision for publication:
1. the authors should clarify the rationale for including excessive drinking in the control group
cohort. Alcohol consumption increases hepatic steatosis and may be why PBC patients had
higher HDL compared to healthy control.
2. correlation analysis should be performed to further understand the role of HDL and PBC-
atherosclerosis progression. Did any PBC patients develop atherosclerosis? If so, what were
their HDL levels? Explorations of this nature will improve the manuscript and increase clinical
impact.
3. The authors mention H&E, CK-19, and other stains performed on biopsies of patients. These
were not found in this manuscript. Results of these stains should be detailed in paper or these
methods should be removed from the manuscript.
Review for 10.1186/s12876-021-01974-4 (2021)

Title: The liver steatosis severity and lipid characteristics in primary biliary cholangitis
Version: 0 Date: 09 Jul 2021
Reviewer's report:
The manuscript submitted by Zhang et al claims to have discussed the use of controlled
attenuation parameter( CAP) as a tool to study steatosis in primary biliary cholangitis (PBC)
patients. The authors present this study in retrospection of the samples collected from the 387 so
patients and measured the different liver marker enzymes to confirm the disease phenotype. They
also performed multivariate analysis for predictors of CAP. Even though the study is claimed
and presented as a novel retrospective analysis of patient samples, it has some concerns that
need to be addressed before it is considered for publication.
1. CAP has been established and published as a non-invasive technique to evaluate steatosis in
NAFLD and autoimmune liver disease previously. Thus this study cannot be claimed as novel
as mentioned in the discussion section by the authors.
2. The explanation provided in support of the experimental data that shows a decrease in hepatic
steatosis is ambiguous. In the introduction and providing the rationale for the study, the authors
claim that PBC is presented with a high risk of atherosclerosis and other cardiovascular events,
however, the data obtained is strikingly opposite to what has set the rationale for the study. The
authors need to revise the discussion section beyond the present data.
3. Since dyslipidemia has been mentioned as a comorbidity of PBC, did the authors consider
looking into the expression of fatty acid metabolism gene expression in the patient samples
collected.
4. Even though predominantly used for grading NAFLD, did the authors consider verifying the
experimental data with NAS score grading for validating the finding obtained by CAP analysis.
5. Since patient biopsy samples were available, did the authors consider performing experiments
that will reveal details about hepatic lipid peroxidation,  fatty acid transport, storage which might
provide a valuable explanation of the results obtained by CAP analysis.
Review for 10.1186/s12876-021-01974-4 (2021)

Title: The liver steatosis severity and lipid characteristics in primary biliary cholangitis
Version: 1 Date: 15 Sep 2021
Reviewer's report:
Some comments previously made were addressed. However, few comments made by the
reviewers received an elusive reply.
1. The liver pathology was entirely taken off from the manuscript. This affects the overall
assessment of the study.
2. It was mentioned that patients'  biopsies were available, However, the data requested by
reviewer #2 could have been included.
Review for 10.1186/s12876-021-01974-4 (2021)

Title: The liver steatosis severity and lipid characteristics in primary biliary cholangitis
Version: 1 Date: 15 Sep 2021
Reviewer:  Vik Meadows
Reviewer's report:
The authors present a succinct and direct story of how CAP analysis of steatosis and HDL can
be prognostic markers in PBC for cardiovascular co-morbidities. The authors have addressed
this reviewers comment and this manuscript would be a welcome addition to the field for
clinicians and researchers alike trying to discover new biomarkers/prognostic markers to prevent
co-morbidities in PBC patients.
Review for 10.1186/s12876-021-01975-3 (2021)

Title: Comparison of Sampling Methods in Assessing the Microbiomefrom Patients with
Ulcerative Colitis
Version: 1 Date: 20 Jul 2021
Reviewer's report:
In this work the authors investigate the microbiome differences in luminal lavage, mucosal
biopsies and stool samples. The addition of luminal lavage is interesting. In general I find the
paper well written without major drawbacks and want to congratulate the authors on their work.
What I would like to see, though, is some more focus on different taxonomic levels and not
just on Phylum which is generally not a very good marker and is generally quite stable without
huge variation.
Also, it would be interesting to see a more explanatory ML approach for the LASSO method to
highlight the factors which are most important. Especially since the stool samples appear to be
performing better than the lavage samples (better AUC).
Also i would suggest the authors cite more recent works which are relevant such as:
https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7160452/
https://pubmed.ncbi.nlm.nih.gov/32328469/
Review for 10.1186/s12876-021-01975-3 (2021)

Title: Comparison of Sampling Methods in Assessing the Microbiomefrom Patients with
Ulcerative Colitis
Version: 1 Date: 06 Aug 2021
Reviewer's report:
Dear Authors,
In this paper you aimed at demonstrating that luminal contents including loosely adherent
luminal bacteria after bowel preparation may be suitable for diagnosing the dysbiosis of UC.
The topic is very interesting, and the manuscript is well written.
On the other hand, I suggest some minor revisions to improve this work.
Minor revisions
INTRODUCTION AND DISCUSSION
Please improve these Sections, citing more studies present in literature about UC and dysbiosis.
Additional reference recommended:
- Weingarden AR, et al. Intestinal microbiota, fecal microbiota transplantation,
and inflammatory bowel disease. Gut Microbes. 2017 May 4;8(3):238-252. doi:
10.1080/19490976.2017.1290757. PMID: 28609251.
- De Sire et al. Microbiota and inflammatory bowel disease: an update. Recenti Prog Med. 2018
Dec;109(12):570-573. doi: 10.1701/3082.30741. PMID: 30667386.
Review for 10.1186/s12876-021-01973-5 (2021)

Title: Risk and characteristics of tuberculosis after anti-tumor necrosis factor therapy for
inflammatory bowel disease: A hospital-based cohort study from Korea
Version: 1 Date: 06 Jul 2021
Reviewer's report:
The message of the paper, that persons with LTBI should be treated before undergoing anti TNF
therapy is not new.  That the incidence of TB increases with age in the study population is also
to be expected, in keeping with the epidemiology of TB in South Korea.
1. The definition of LTBI used in this report (ie. "an abnormal chest X-ray in a patient who had
never completed TB or a positive TST or IGRA")  is unconventional. LTBI is usually defined
as a positive TST or IGRA test in the absence of clinical / radiological signs of active disease.
2. Were the patients on other immunosuppressive treatment besides the anti-TNF-alpha therapy?
If so, this information should have been included in the analysis.
3. Did the patients have other co-morbidities, eg. diabetes, end-stage renal failure, HIV which
also predisposed to TB?  This information should also have been included.
4. It is interesting that 3 cases who tested negative for LTBI and who developed active TB did so
within 2 months of starting anti-TNF therapy. Were they on other immunosuppressive therapy
which might have affected the IGRA performance? Could they already have had active disease
before starting anti-TNF therapy?
5. The patients who developed active TB many years after testing IGRA negative before starting
anti TNF alpha therapy were likely infected after testing negative. This gives support to inclusion
of LTBI testing in the regular surveillance of these persons such that LTBI treatment can be
given (after exclusion of active disease) in those who convert their IGRA test.
Review for 10.1186/s12876-021-01973-5 (2021)

Title: Risk and characteristics of tuberculosis after anti-tumor necrosis factor therapy for
inflammatory bowel disease: A hospital-based cohort study from Korea
Version: 1 Date: 06 Jul 2021
Reviewer:  Tao Li
Reviewer's report:
This study is well designed and analyzed in risk and characteristics of tuberculosis after anti-
TNF therapy for inflammatory bowel disease. The results could be helpful for other researchers
and readers’ practice. The interpretation is clear except few questions need to be further clarified.
Results:
1.“190 patients (96.0%) did not require TB prophylaxis or completed prophylaxis” What’s the
meaning of “did not require TB prophylaxis”, the definition or standard hasn’t been clarified
in the context.
Discussion:
1.The discussion in paragraph 3 seems not in line with paragraph 4. In paragraph 3, authors said
that the relatively lower incidence rate in the current study may benefit from high acceptance and
completion of TB preventive treatment in LTBI group. But in paragraph 4, authors concluded
that no difference for incidence rates in LTBI positive and LTBI negative groups. “The results
of the present study are thus in line with previous studies and confirm that LTBI is not a risk
factor for TB development in patients undergoing anti-TNF therapy who have undergone active
LTBI management.” These were conflicting.
3.“To confirm that the tests were reliable, we checked the HR of TB development in the TST
plus IGRA group and the IGRA-only group; there was no significant difference between the
groups in this regard (HR: 1.170, 95% CI: 0.417–3.284).” The result should be interpreted in
the Results part first before discussion.
Review for 10.1186/s12876-021-01978-0 (2021)

Title: Hepatocellular carcinoma in nonalcoholic fatty liver disease with or without cirrhosis: a
population-based study
Version: 1 Date: 01 May 2021
Reviewer:  Nahum Méndez-sánchez
Reviewer's report:
Hepatocellular carcinoma in nonalcoholic fatty liver disease with or without cirrhosis: a
population-based study
This is an interesting study. Here there is nothing new compare with the results of previous
studies. But the sample size is big. I suggest to improve the discussion section.
Comments
What about other liver function liver tests?
What about the role of gene polymorphisms in for the development of HCC in NAFLD non
cirrhotic patients.
What about the treatment in NAFLD non cirrhotic compare with cirrhotic patients?
What about the mortality in NAFLD non cirrhotic patients?
What about the recurrence in NAFLD non cirrhotic patients?
Review for 10.1186/s12876-021-01978-0 (2021)

Title: Hepatocellular carcinoma in nonalcoholic fatty liver disease with or without cirrhosis: a
population-based study
Version: 1 Date: 05 May 2021
Reviewer's report:
This is an interesting and important study.  However there are some limitations with the dataset.
If these cannot be rectified, they should be acknowledged more specifically in the discussion.
1. Only patients with an established diagnosis of cirrhosis are classified as such.  It is likely that
within the group classed as non-cirrhotic, there are patients with cirrhosis which has not been
reported or detected. This is a limitation, when considering the prevalence of HCC within the
groups.  It may be helpful to include platelet count as a surrogate marker of portal hypertension,
or at least have it shown in the Tables, with the range.  It wasn't clear how the diagnosis of HCC
was made.  Biopsy is required for a diagnosis of HCC in non-cirrhotic patients and may also
provide an opportunity to detect 'asymptomatic' cirrhosis.
2. The alcohol history was not included.  To be more confidant these are NAFLD cases, it may
be relevant to have included searches that would detect alcohol use - either as an exclusion or
as a co-factor.
3. Age analyses are restricted to >65 years for both categories.  What was the age of non-cirrhotic
HCC versus cirrhotic HCC?  I would have liked to see a Table (similar to Table 1) comparing
the characteristics of cirrhotic versus non-cirrhotic HCC cases.
4. This is a comment, rather than something that needs to be further discussed. Obesity was not
an independent risk factor for patients with HCC in patients with NAFLD.  This has also been
seen in genetic studies assessing the risks of HCC in NAFLD.  It is possible that if weight is taken
only at the time of HCC diagnosis, it is lower as a consequence of the cancer and therefore simply
a confounder.  But a lower BMI in NAFLD HCC patients versus NAFLD no HCC patients has
been reported for all stages of cancers.  It may be age related - as older patients get cancers
and weight reduces with age. It is also possible, that fatter NAFLD patients get cirrhosis (plus
cancers)  and thinner ones are less likely to get cirrhosis, but still have a cancer risk with different
biological mechanisms at play. Distinct from the things that promote progression to cirrhosis.
And it takes longer - they are probably older in your cohort.