JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 0 Date: 06 Oct 2021
Reviewer's report:
This is an interesting topic and I think the study was well performed overall. However, there are
several major issues to be addressed.
1. There are already several studies investigating CD10 and DAS-1 as IM markers. If this study
was to validate the usefulness in clinical application, a larger number of samples should have
been included.
2. This study was aimed to explore the potential of CD10 and Das-1 as biomarkers to subtype
IM. I’m afraid it seems inappropriate to include gene expression analysis of IM in the results.
I suggest authors move it to supplementary data.
3. Authors determined the IM subtype only by histological evaluation. However, it can be hard
even for experienced pathologists because IM often occurs in mixed type or in hybrid type. Thus,
I believe that the determination of IM subtype should be backed up by ancillary studies such as
special stainings or other established IHC markers.
4. Hybrid-type IM is likely to express both CD10 and Das-1, which could confound the results.
I’m wondering whether there were no samples containing hybrid type IM.
5. In the lower panel of fig. 2B, authors claim that it is incomplete type IM, however, it seems
to be mixed type IM and Das-1 positive area is mostly complete IM, whereas incomplete type
IM portion is negative for Das-1.
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 0 Date: 22 Nov 2021
Reviewer's report:
The authors  investigated the utility of CD10 and Das1 to help objective assessment of Intestinal
metaplasia subtype. They performed the staining and  statistics very well. It is a straightforward
study and worth publishing. I have no critical comments.
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 2 Date: 03 Jan 2022
Reviewer's report:
Topic 1: “Innovation”
: Again, I'm afraid that using two markers, CD10 and DAS-1 does not seem very interesting
because they already are well-established markers. Likewise, methodology such as multiple
single gland analysis by digital quantification is not strong enough to make up for the weakness
of the small number of cases, especially if you try to analyze the risk of IM subtype in GC
development.
Topic 2: “Diagnosis of IM subtypes, mixed IM and hybrid IM”
:  "The utility of CD10 and Das1 staining in combination is to group not only subtypes but also
help in risk prediction for progression to gastric cancer."
For the above response from the authors,  I feel that this study does not provide strong evidence
(Again, about 20 cases of GCs and control seems too small to make any conclusion.
I understand the study has been finished and it is impossible to include additional cases and do
it all over again. I feel sorry, but I'm not very convinced about the conclusion of the study.
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 2 Date: 16 Jan 2022
Reviewer's report:
The present study is well-desinged and performed. the issue discussed in this manuscript is
interesting also. The reviewer’s comments were considered well managed and answered in the
present manuscript and the authors‘ reply.  I have no further comments for the manuscript.
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 2 Date: 15 Feb 2022
Reviewer's report:
I read with interest the paper entitled CD10 and Das 1: a biomarker study using
immunohistochemistry to subtype gastric intestinal metaplasia.
I found the paper interesting and the study well conducted. Intestinal metaplasia is an important
step in the evolution of atrophic gastritis versus cancer. Unfortunately, subtyping of complete
and incomplete intestinal metaplasia did not gain universal attention and generally is not
performed for routine assessment of gastric biopsies by histopathologists. I think that new
markers for risk of progression to cancer of intestinal metaplasia merit attention.
I would suggest adding as a limit of the study that the clinical applicability of these markers
seem promising but need to be validated by further studies.
Review for 10.1186/s12876-022-02268-z (2022)

Title: CD10 and Das1: a biomarker study using immunohistochemistry to subtype gastric
intestinal metaplasia
Version: 5 Date: 23 Mar 2022
Reviewer's report:
I'm afraid to say that I'm still not convinced that the methodology used in the study allows you
to reach any reliable conclusion without increasing the number of cases.
Review for 10.1186/s12876-022-02273-2 (2022)

Title: External validation of the BEST-J score and a new risk prediction model for ESD delayed
bleeding in patients with early gastric cancer
Version: 2 Date: 05 Feb 2022
Reviewer's report:
This study is about the prediction of delayed bleeding in ESD for EGC comparing BEST-J score
and new one. I’ve read this study with great interests. This is well designed study, however,
there were some debates as follows;
Major comments
Taking apart BEST-J score, which shows modest prediction value, the significant factors for
delayed bleeding were smoking, tumor size, hemoclip use, multiple tumors and prolonged aPTT.
We can expect that patient factor, humoral factor and procedure related factors are related to a
delayed bleeding. The authors suggested smoking is related to a delayed bleeding, but there was
no sufficient explanation about this.
Second, we can agree that tumor size and multiple tumor would be associated with a delayed
bleeding, However, hemoclip use itself can’t be a significant factor, because it only reflects
intraprocedural bleeding. There are lots of method to control bleeding during procedure, so
hemoclip use means severe intraprocedural bleeding.  Thus, it is appropriate to assess the degree
of bleeding during procedure.
Third, prolonged aPTT was important factor in this study. However, this is not cause of bleeding
tendency but reflect of bleeding tendency. Again, in my knowledge, prolonged aPTT itself is
not associated with bleeding tendency. Thus, this have to be elaborated.
Review for 10.1186/s12876-022-02270-5 (2022)

Title: Homogeneous and heterogeneous risk and prognostic factors for lung metastasis in
colorectal cancer patients
Version: 0 Date: 20 Dec 2021
Reviewer's report:
The results of this paper were judged to be reliable in that they were not significantly different
from the results that have been reported in many other papers. There are no new findings, but
the paper has value in that it confirms previous publications.
Review for 10.1186/s12876-022-02270-5 (2022)

Title: Homogeneous and heterogeneous risk and prognostic factors for lung metastasis in
colorectal cancer patients
Version: 2 Date: 02 Mar 2022
Reviewer's report:
The authors have addressed almost all the earlier comments.
However, they did not incorporate the analysis for stages III-IV patients into the revision (they
only added it in the response). They should add it as a supplementary material and also comment
on it in the revision that the results were comparable when the sample was restricted to stages
III-IV patients. This is an important information and should be added to the manuscript.
Review for 10.1186/s12876-022-02276-z (2022)

Title: Survival after Curative Resection for Stage I Colorectal Mucinous Adenocarcinoma
Version: 1 Date: 14 Sep 2021
Reviewer's report:
The authors answer an interesting question and do this with a large cohort. I think the conclusions
and methods are sound. No big concerns on my behalf.
1. The authors use OS as an endpoint, but have already excluded patients that have died of non-
CRC causes. Then this is more like cancer (disease) specific survival. In my opinion CSS is
good to use, but then don't exclude patients who die of other causes, but just censor them in
survival analyses. Easy to do. Or then use the true overall survival.
2. Figures and tables need some polishing, but this is a small thing.
3. Reference 15 that should explain about the MMR IHC methods, but the referenced article
does truly talk about it. Could a another reference be better?
4. Some grammatical problems and misspelled words are in the results section, please check
them.
Review for 10.1186/s12876-022-02276-z (2022)

Title: Survival after Curative Resection for Stage I Colorectal Mucinous Adenocarcinoma
Version: 1 Date: 17 Nov 2021
Reviewer:  Jihun Kim
Reviewer's report:
Authors investigated clinicopathologic factors affecting long-term patient outcome in stage
I colorectal cancer (CRC) focusing on mucinous histology. Overall methods look good.
However, there are not so much novel findings here. In addition, there are many awkward
English expressions making this manuscript not suitable for publication. Some suggestions for
improvement are listed below.
Major comments
1. Mucinous adenocarcinoma (MAC) is quite heterogeneous in terms of tumor morphology
and biologic behavior. Some tumors might have well differentiated tumor cell strips lining
mucin pools with scarce tumor cells floating in mucin pools while others might have abundant,
moderately differentiated tumor cell clusters or signet ring cells in mucin pools. I recommend
that authors stratify MACs into two or three groups according to tumor differentiation and/or the
presence of signet ring cells. By doing so, authors may provide useful insights for stage I MAC.
2. Disease recurrence or metastasis that eventually leads to patient death in stage I CRC is
intriguing and prediction of such cases is important for patient management. Detailed analysis
of stage I CRCs that led to aggressive systemic metastases or patient death might be very
informative in this sense. Thus, more detailed investigation of 22 patients who died of stage I
CRC is strongly recommended.
3. Authors did not mention the presence and the grade of tumor budding in this manuscript.
The importance of tumor budding can never be overemphasized. CRCs, that did not have
lymphovascular invasion (LVI) but did recur or metastasize, might have tumor budding in many
cases. Thus, authors should investigate tumor budding and its prognostic impact.
Minor comments
1. Insertion of percentage information in parenthesis is recommended in the Table 1.
2. In the Table 2, Hazard ratio would be much better than the mean OS for univariate analysis.
Also, what does MSI positive mean? Please use MSS vs. MSI-H instead. The same thing applies
to the Table 3.
3. Page 7, Paragraph 2, Line7: “appeared to be found significantly more locate at colon…” ->
“was found to be more frequently located at colon…”
4. “higher MSI status” (Page 8, 1st paragraph of the Discussion section, Line 8) ->” a higher
number of MSI-H status.”
5. Many other awkward expressions throughout the manuscript. Please consult a native English
speaking medical doctor for appropriate English expressions.
Review for 10.1186/s12876-022-02276-z (2022)

Title: Survival after Curative Resection for Stage I Colorectal Mucinous Adenocarcinoma
Version: 5 Date: 04 Mar 2022
Reviewer:  Jihun Kim
Reviewer's report:
Authors resolved most raised concerns well. However, I found a few new major and minor
concerns. Please check and correct them.
Major comments
According to the results, dMMR positive group showed significantly worse overall and disease-
free survivals than dMMR negative group (that is pMMR) in the Table 2 & 3, and Figure 2
& 3. However, in the discussion section (the last paragraph), authors stated that “Our study
revealed that stage I CRC patients with dMMR status showed a much better survival compared
with the pMMR group.” Thus, the results and the discussion do not match. Which side is true?
Although there have been controversies about the prognostic impacts of dMMR status in CRC,
the general trend is that dMMR CRCs behave better than pMMR CRCs in early stage. If the
results are true (dMMR CRCs are more aggressive in stage I CRCs), they contradict the previous
reports. Regarding this, I personally observed that mucinous adenocarcinomas could not benefit
from host immune surveillance probably because host immune cells cannot get access to the
tumor cells due to the intervening mucin pools (thus, dMMR mucinous adenocarcinomas show
aggressive clinical behavior and poor response to immunotherapy). Authors should get this thing
straight (which one is true? Results or Discussion?) and discuss the scientific significance of
the related data.
Minor comments
Page 7, 5th line from the bottom: “There were nearly significantly more LVI in MAC patients
than non-MAC patients.” # “LVI tended to be more frequent in MAC patients than in non-MAC
patients.” (more clear expression about statistically insignificant trends)
Review for 10.1186/s12876-022-02276-z (2022)

Title: Survival after Curative Resection for Stage I Colorectal Mucinous Adenocarcinoma
Version: 5 Date: 21 Mar 2022
Reviewer's report:
I thank the authors for their responses and I'm with their responses. I hope they feel my comments
were helpful to improve the manuscript. The material is of good size and provides a nice insight
to the world o stage I CRC.
Review for 10.1186/s12876-022-02262-5 (2022)

Title: Nuclear morphometry and chromatin texture changes in hepatocellular carcinoma samples
may predict liver transplant patients’ outcomes
Version: 2 Date: 14 Feb 2022
Reviewer's report:
Title: Nuclear morphometry and chromatin texture changes in hepatocellular carcinoma samples
may predict liver transplant patients’ outcomes
Authors: Jordan Boeira dos Santos et al.
Reviewer’s comments:
General remarks:
In this manuscript, the authors tried to analyze the nuclear characteristics of hepatocellular
carcinoma in relation to the recurrence rate after liver transplantation. This manuscript is clearly
described and the contents are significant. However, several parts should be dissolved as a
revised manuscript.
Major points:
1. Feret diameter and aspect ratio (AR) or nuclear perimeter are close indicators of nuclear
irregularity. However, either the perimeter or AR did not correlate with patients’ survival after
liver implantation. The authors should discuss the reason why either the perimeter or AR did
not correlate with patients’ survival even though the Feret diameter showed a correlation.
2. I agree that several nuclear factors showed differences in several characteristics (Sex, Age,
MELD score, Recurrence, and survival). However, none of them (nuclear factors) could be
the common factors for each characteristic. If so, why don’t you use discriminant analysis by
combining several factors to predict the difference for each characteristic?
3. I wonder if each HE stained specimen showed different nuclear intensity. Thus nuclear
detection setting for each specimen would be different. However, the authors did not show any
image analysis setting condition for morphometric analysis. This is pretty strange for us. Please
indicate the settings and representative image acquisition findings as new Table and Figure.
Minor points:
1. Please indicate the formula of MELD score in the Materials and Methods part.
2. Please indicate the formula of Aspect ratio (AR) in the Materials and Methods part.
3. Please indicate the definition and meanings of Feret diameter even if the authors take it for
granted in the Materials and Methods part.
4. In Line 176, “carried” is miss-typed as “caried”.
Review for 10.1186/s12876-022-02262-5 (2022)

Title: Nuclear morphometry and chromatin texture changes in hepatocellular carcinoma samples
may predict liver transplant patients’ outcomes
Version: 2 Date: 20 Feb 2022
Reviewer's report:
The study by Jordan Boeira dos Santos et al tries to establish a relationship between
different parameters used to morphometrically assess nuclear and chromatin texture changes in
hepatocellular carcinoma (HCC) tissue samples and the outcome of liver transplant patients.
The authors used the image processing software ImageJ and an add-on for calculating fractal
dimension (FD). The study found several useful parameters  in discriminating between HCC
and surrounding tissue cellular nuclei. From those, only some could be correlated with survival
and survival-related parameters.
Some points that need addressing:
1. The authors state that 34 individuals were included, of whom 19 were male and 12 female,
reaching 100%. Three participants seem to be lost, while percentages still add up to 100.
2. The authors state that 20 samples were excluded as they could cause depletion of the material
stored, two more further excluded due to incomplete data records. Are these supplemental to the
34 included? If so, please provide a workflow diagram in order to understand the selection.
3. Please indicate the scale in figure 1.
4. Please consider adding a figure depicting binarization used for FD calculation. Properly
obtaining the masks by binarization is essential for calculating accurate FDs.
5. Please explain what "20 cores" refers to when stating that it took 40 minutes (per case? in
total?)
6. What is the difference between "hepatocellular" and "neoplastic" nuclei?
7. It is stated that only nuclei "with not sharp nuclear boundaries" were excluded. If one nucleus
was partially obstructed by another, but with a clear boundary, were both included in the
calculation, or only the suprajacent one?
8. Why only one image per case? Selecting an image with a high concentration of nuclei (above
20, as stated) did not introduce an unwanted bias in the analysis?
Review for 10.1186/s12876-022-02262-5 (2022)

Title: Nuclear morphometry and chromatin texture changes in hepatocellular carcinoma samples
may predict liver transplant patients’ outcomes
Version: 4 Date: 11 Mar 2022
Reviewer's report:
Title: Nuclear morphometry and chromatin texture changes in hepatocellular carcinoma samples
may predict liver transplant patients’ outcomes
Authors: Jordan Boeira dos Santos et al.
Reviewer’s comments:
General comment:
I think this manuscript responds appropriately to the reviewer's suggestions. I can't find any
additional indications for the revised form of this manuscript.
Review for 10.1186/s12876-022-02266-1 (2022)

Title: Comparisons of six endoscopy independent scoring systems for the prediction of clinical
outcomes for elderly and younger patients with upper gastrointestinal bleeding
Version: 1 Date: 23 Jan 2022
Reviewer's report:
Dear Editor,
I have reviewed the manuscript submission ID 7c194227-67ed-4694-b134-d67c2d4afe2d
entitled “Comparisons of six endoscopy independent scoring systems for the prediction of
clinical outcomes for elderly and younger patients with upper gastrointestinal bleeding” with
interest. However, there are many major and minor concerns as the following items;
Major concerns
Abstract
1. The authors should provide the AUC data of each comparison rather than only p-value. It is
impossible to understand which scoring system is effective to predict individual outcome in the
current form. Please consider revise.
2. The conclusion was not relevant to the result and too long.  Please consider revise.
Full manuscript
3. The authors stated that “Rebleeding also included cases requiring a second endoscopy,
interventional radiology, or surgery.” This may incorrect as we could not label the patient
underwent second look EGD but did not have additional endoscopic hemostasis with rebleeding.
4. How did the authors know the severity of upper GI bleeding if they did not perform EGD
in the included patients? They stated that “Most patients underwent endoscopy” with unknown
percentage. It would be better to know if the mortality were related to UGIB or not.
5. The authors did not mention about T-score in the introduction part at all. It is difficult for the
readers to follow this study. Please add the background of all assessed scoring system.
6. Why the authors did not calculate the p-value of other baseline characteristic in table 1 eg.
current medication, laboratory testing, endoscopic finding, etc.
7. Please provide the reference in each proper sentence eg. “The incidence of UGIB has declined
dramatically over the past decade.”, “..a mortality rate  4%-10% worldwide” in discussion part,
etc.
8. In table 1, what were the endoscopic findings in “Others”? Please put the details.
9. The major limitation of this study is the scattering, non-focus information. It seems that
the scoring system is helpful in younger patients but not elderly patients but they could not
convey the message to the reader. The authors should re-write the result and discussion part to
demonstrate the benefit of scoring system in each age group.
10. This manuscript is difficult to follow esp. in discussion part. It may need English editing
before re-submission.
Minor concerns
1. Some typing errors were detected, eg. “maligancy” in Table 1.
Review for 10.1186/s12876-022-02266-1 (2022)

Title: Comparisons of six endoscopy independent scoring systems for the prediction of clinical
outcomes for elderly and younger patients with upper gastrointestinal bleeding
Version: 1 Date: 30 Jan 2022
Reviewer's report:
Li et al reported on the comparison of the six endoscopy independent scoring systems for the
prediction of clinical outcomes for elderly and younger patients with upper gastrointestinal
bleeding.
The strength of the study was the relative large numbers of participants (>1000).
I have several comments:
Introduction:
1. Although the main objective of the study was to evaluate the effectiveness to predict the
clinical outcomes in elderly and young patients, the strength and utility  of this predictive
score,  as highlighted in several guidelines, is to rule out high risk patients, eg. GBS score of
<=1. This point should be highlighted, either in introduction or discussion/limitation. Guideline
Recommendations From the International Consensus Group: 'Use of prognostic scales and early
discharge of patients at low risk have the potential to reduce the need for endoscopy, hospital
stays, and associated costs without increasing harms. Sensitivity for detecting high-risk patients
is a critical outcome, because it is important to avoid incorrectly classifying high risk as low
risk when making decisions about early discharge. Specificity is less crucial, because low
specificity results in more low-risk patients being hospitalized but not in high-risk patients being
discharged. '
Methodology:
1. Each scoring system could be described in methodology, including the range of scores. Will
be good to show the parameters used in calculating the various risk scores in supplementary
tables. The readers will have a clearer view in seeing the differences between the various score.
2. Please predefined what score of AUROC represent good, fair or poor accuracy.
Results:
1. In table 1,  why the differences in the usage of medications, relevant variables and scores
components and findings at endoscopy were not analysed statistically? No P value
2. Is there any analysis comparing the accuracy between the different risk scores? Although
ABC's AUROC score numerically appeared better in most outcomes, if there is analysis
comparing different scoring system will be even more convincing.
Discussion:
1. Limitations of the study were not discussed - e.g.. retrospective nature of the study, the
analysis to rule out high risk patients was not done,  other important parameters, including
rehospitalisation and prolonged hospitalisation were not analysed.
Review for 10.1186/s12876-022-02266-1 (2022)

Title: Comparisons of six endoscopy independent scoring systems for the prediction of clinical
outcomes for elderly and younger patients with upper gastrointestinal bleeding
Version: 3 Date: 13 Mar 2022
Reviewer's report:
Dear Editors and authors,
The current version of manuscript is much better. However, the author has not responded to the
Reviewer 1 comment no.4. The authors  should declare the percentage of included patients from
the overall assessment as they excluded patients who did not had EGD result.  This data can
reflex the situation of GI bleeding in this  center.  Moreover, it would be better to know if the
mortality were related to UGIB or not.
Please respond to these concerns.
Review for 10.1186/s12876-022-02264-3 (2022)

Title: A novel method for early detection of colorectal cancer based on detection of methylation
of two fragments of syndecan-2 (SDC2) in stool DNA
Version: 0 Date: 29 Dec 2021
Reviewer's report:
‘A novel method for early detection of colorectal cancer based on detection of methylation of
two fragments of syndecan-2 (SDC2) in stool DNA’. The authors have studied on aberrant DNA
detection in stool for diagnosing colon cancer. There are concerns that authors need to clarify.
Hypermethylation of SDC2 promotor region in development of colorectal neoplasms is a
frequent epigenetic change. How frequent? This is important for the study in context.
How many stool samples were discarded for poor quality or errors in extraction?
Methods need referencing at places. For example- “Following the Clinical Laboratory Standards
Institute (CLSI) guideline about interference testing, EP7-A2, and Guide to interference testing
in clinical chemistry, WS/T 416-2013”- Please enumerate all the references.
Give a figure of study enrolment.
The description of 339 participants under sample collection section should go in results rather
than methods. Also give description of the eighteen patients diagnosed as ‘colitis’. The basis of
diagnosis of advanced and non-advanced adenomas should be mentioned in methods.
What steps were taken for blinding if any? Were consecutive patients taken to avoid selection
bias? This needs to be mentioned
Was there any difference between detection rates based on age? If so, the possible reason needs
to be explained in discussion too.
Review for 10.1186/s12876-022-02264-3 (2022)

Title: A novel method for early detection of colorectal cancer based on detection of methylation
of two fragments of syndecan-2 (SDC2) in stool DNA
Version: 0 Date: 04 Jan 2022
Reviewer:  Suk-Hwan Lee
Reviewer's report:
The authors employed the syndecan-2(SDC2) methylation assay using stool samples from the
Chinese population to evaluate the feasibility of colorectal cancer(CRC) screening. The authors
also employed the two different SDC2 promoter regions for methylation assay to improve the
sensitivity and specificity of the test.
The strength of the study;
SDC2 is a promising biomarker for colorectal cancer screening now. Like other reports, the
authors successfully established the methylation assay using stool samples as small as 2.5 grams.
The sensitivity of the combined methylation assay improved compared to the single methylation
assay.
The weakness of the study;
Ideally, the screening test needs high sensitivity and specificity. But it isn't easy to achieve the
ideal criteria of the test in reality.
The sensitivity for CRC is 87.28% for combined methylation assay, which is improved
compared to a single methylation assay. However, the differences were not statistically
significant. The sensitivity seemed low compared to the commercially available tests as the
authors described in the manuscript. What do you think is the low sensitivity of the test?
As the differences were not significant, the authors should revise the conclusion.
What number of patients tested the methylation assay in the study? Not 100% of the samples
resulted in the success of the methylation assay. Please describe the technical results of the
methylation assays.
Tables 1, 2, and 5 seemed unnecessary because the authors already described the results in the
manuscript.
Besides the staging of the CRC, do the test results differ based on the location of the tumors?
Besides the advanced adenomas defined by the size and histologic criteria, what are the results
of the detection rates for the smaller adenomas in the study?
Review for 10.1186/s12876-022-02264-3 (2022)

Title: A novel method for early detection of colorectal cancer based on detection of methylation
of two fragments of syndecan-2 (SDC2) in stool DNA
Version: 2 Date: 04 Apr 2022
Reviewer:  Suk-Hwan Lee
Reviewer's report:
Thanks for the detailed answers and the revision recommended by the reviewers.
The manuscript is much more improved than the first one.
Review for 10.1186/s12876-022-02257-2 (2022)

Title: Identification and validation of EMT-immune-related prognostic biomarkers
CDKN2A, CMTM8 and ILK in colon cancer
Version: 1 Date: 04 Feb 2022
Reviewer's report:
1. All statistical packages used should be referenced correctly, including  “survival",
"survminer", and "time ROC".
2. It lacks an external experiment or external database to further support the conclusion.
3. English should be improved based on advices from native speakers. For example,
“Introduction Colon cancer(CC) is a major health problem worldwide and the second-leading
cause of cancer-related deaths”#there should be a space between “Colon cancer”and “(CC)”.
4. The R script should be submitted for reproducibility.
Review for 10.1186/s12876-022-02257-2 (2022)

Title: Identification and validation of EMT-immune-related prognostic biomarkers
CDKN2A, CMTM8 and ILK in colon cancer
Version: 4 Date: 31 Mar 2022
Reviewer's report:
Authors addressed all my comments, provided new analyses and listed limitations. The paper is
in a good stand to be shared with the scientific community.
Review for 10.1186/s12876-022-02246-5 (2022)

Title: Positive association of nap duration with risk of non-alcoholic fatty liver disease in an
occupational population in Guangdong Province, China: A cross-sectional study
Version: 1 Date: 08 Jan 2022
Reviewer's report:
Chang Hong et al. performed a cross-sectional study to investigate association of nap duration
with risk of non-alcoholic fatty liver disease in an occupational population in China. This study
encompasses an interesting finding, but it also includes some methodological problems.
Major comments
1. Authors categorized daytime napping duration as none, <30 min, 30–60 min, and #60 min
per day. Other studies use different categories, for example none, #1 h, and >1 h per day. The
reason to choose that category is not unclear.
2. In this study the definition of daytime napping is not written, for example every day, several
times in a week, and so on. It should be showed How did they ask a question about it.
3. The authors assessed exercise habits but not dietary habits. This is a limitation of this study.
4. Authors explain the relationship between daytime napping duration and the risk of NAFLD,
long daytime napping duration could elevate the level of cortisol in the blood. In general, daytime
napping around 60 minutes could reduce the level of cortisol in the blood. They should show
the reason to consider like that.
5. Supplemental Table 1 shows that lower BMI (<18) is associated with risk of NAFLED.
Authors should explain the reason of the result.
Minor comments
1. In Table 1, there is a spelling mistake. Daytime dapping duration#Daytime napping duration
2. In the abstract, the age of participants is 30–79 years, but in the text that is 25–50 years. They
should unify it in either.
Review for 10.1186/s12876-022-02246-5 (2022)

Title: Positive association of nap duration with risk of non-alcoholic fatty liver disease in an
occupational population in Guangdong Province, China: A cross-sectional study
Version: 1 Date: 17 Jan 2022
Reviewer's report:
The authors showed the positive association of nap duration with risk of non-alcoholic fatty liver
disease in an occupational population in Guangdong Province.
Their study showed that the participants with BMI < 18.5 had a higher OR than that of  BMI >
24. In general, obesity is well known as a risk factor of NAFLD.
The authors should the explain this result in the Discussion section.
About 85% participants have daytime napping duration > 30min. is it common in Chinese? For
example,  is nap time set in each company?
Dose the authors have the data about eating speed, lack of breakfast, and taking snack?
If they have these data, please add the data to multiple analyses.
Review for 10.1186/s12876-022-02248-3 (2022)

Title: Plasma and fecal zonulin are not altered by a high green leafy vegetable dietary
intervention: secondary analysis of a randomized control crossover trial.
Version: 2 Date: 31 Oct 2021
Reviewer's report:
This is an interesting sub-analysis of a randomized controlled trial that measured the response
to high green leafy vegetables on several biological domains. However, this study's statistical
analysis, results, and conclusions need to be substantially revised. Furthermore, I don't think that
it is possible to infer on sex differences in this specific design. Due to the small sample size and
talking account, this was not the pre-defined analysis and/or outcome of this study.
Headline: Sex is written in the headline while gender is being used along the ms.
Introduction:
P2L46-49 It is essential to mention the implication that has been suggested in the mentioned
medical conditions and or disease.
P3L72-76 Several diets have been shown to reduce zonulin levels. It is important to review those
entities and to explain why the current intervention was selected.
Methods:
The methodical part of the intervention is written clearly and allows for replication.
I didn't see any sample size or power calculation (if this is a secondary analysis).
In my opinion, the outline of the intervention (M3G protocol) should move to the main ms.
Statistical analysis:
Accounting for the small size, it is more appropriate to use non-parametric tests instead of t-tests.
It is not clear where Bonferroni correction was used.
Results:
P7L162-169 – Analysis of correlations by sex is inappropriate in this small sample size.
I did not see any description of changes in anthropometric measurement. However, weight loss
has been shown to induce changes in inflammatory markers and microbiome.
Table 1 and 2:
Again, some of the variables are not normally distributed, and it would be better to present them
as medians and IQR.
Figure 2:
Were these correlations corrected for multiple testing? If so, how many comparisons?
Table 3 – same comment as in table 1 and 2.
Discussion:
P11L239-241 – Changes in anthropometric measurements within subjects should be added to
the results.
P11L234-241 – These are strengths and limitations of this study and should be moved to the
relevant section accordingly.
Conclusion:
I think it is not possible to conclude on sex differences in this experimental design
Review for 10.1186/s12876-022-02248-3 (2022)

Title: Plasma and fecal zonulin are not altered by a high green leafy vegetable dietary
intervention: secondary analysis of a randomized control crossover trial.
Version: 2 Date: 14 Nov 2021
Reviewer's report:
With interest, I read the paper by Riviere et al. describing the trajectory of zonulin, inflammatory
markers, and gut microbiota in a subset of 20 participants from a randomized crossover study
in which participants were directed to consume green leafy vegetable consumption or placebo
for four weeks each (with a four week washout period between them).
While some of the results reported in the manuscript are interesting, there are some substantial
concerns and gaps that should be addressed thoroughly before further consideration could be
made:
1. The main problem of the paper is that it lacks a scientific focus.  What is the primary outcome
of this secondary analysis, and what is the STORY that the authors would like to tell??  In
this reviewer's view, the paper should focus on plasma and fecal zonulin trajectory and their
associations with other biomarkers, dietary reporting, and inflammatory state.  Comparison
between sexes is optional based on direct comparisons and not stratification according to sex. If
there is a difference between the sexes, this could be part of the report's central message.
2. How were the participants who were included in this analysis chosen?  Completely randomly?
Was randomization stratified by sex? (since an equal number of men and women are included).
3. Statistical analysis - the use of the Bonferroni method to address multiple comparisons is
appropriate.  Yet, the authors chose to perform T-tests to compare groups with a sample size of
10-20.  The proper way to reach such small groups is by using non-parametric tests.
4. Differences in dietary reportings after the diet should be reported in supplementary material
and not in the main text.
5. The figures are too heavy on the eyes, and all present correlation matrixes. It would be better
to present color figures of heat maps without numbers but with a legend that states the number
range and direction according to color and color strength.
6. How do the authors explain the elevation in inflammatory markers under the LGV diet? Was
this also observed in the main trial?
7. Please consider performing partial-linear correlations to adjust for difference confounders to
assess the relationship between zonulin as a marker of intestinal integrity and other biomarkers.
8. Please remove "further research is warranted" from the abstract's conclusions.
9. Figures 3 and 4 are very general - how do they relate to the hypothesis or aims of the paper??
It is better to thoroughly cover a specific mechanism/biomarker/phenomenon than to describe
a very general concept
10. How were the biomarkers included chosen?  Are other biomarkers relevant and available?
(for example, insulin resistance markers)
Review for 10.1186/s12876-022-02248-3 (2022)

Title: Plasma and fecal zonulin are not altered by a high green leafy vegetable dietary
intervention: secondary analysis of a randomized control crossover trial.
Version: 4 Date: 20 Jan 2022
Reviewer's report:
The manuscript by Riviere et al. on the effect o a green leafy diet on plasma and fecal zonulin,
inflammatory biomarkers, and the fecal microbiome has been substantially revised and has
dramatically improved.
There are some minor points to be addressed for the article to be improved:
1. Abstract: please omit the abbreviations INT and CON and use the full terms (intervention
or control, respectively). The results section of the abstract needs to be substantially revised
to include baseline correlations of zonulin and inflammation and present the actual biomarkers
changes.
2. Statistical analysis: parametric tests are not appropriate for use in such a small sample size.
Please report only non-parametric tests results. Also, multiple a
3. Table 1: please add more baseline information on study participants - laboratory and
background medical conditions.
4. Please discuss in-depth the clinical significance of zonulin concerning systemic inflammation
and its interaction with the gut microbiome.
5. Why are the analyses between zonulin and inflammatory biomarkers reported across sex
strata? Please report associations first in the entire cohort. If there was an interaction on the
observed associations across sex strata, please state so.
6. Please report CRP in ng/L since this is more acceptable.
7. Title: please revise to highlight that this manuscript deals with plasma and fecal zonulin
changes and their clinical relevance. As reflected from the manuscript, the associations with
systemic inflammation and the gut microbiome were secondary aims.
8. Please also report baseline associations between zonulin and different biomarkers to highlight
the clinical relevance of this biomarker.
9. The manuscript needs to undergo English language editing.
Review for 10.1186/s12876-022-02248-3 (2022)

Title: Plasma and fecal zonulin are not altered by a high green leafy vegetable dietary
intervention: secondary analysis of a randomized control crossover trial.
Version: 4 Date: 07 Feb 2022
Reviewer's report:
First, I would like to thank the authors for improving the manuscript. I feel that it is much
improved. However, I still have some minor concerns, especially regarding the statistical
analysis:
1. A power calculation is obligatory to assess whether this design can explore the hypothesis.
2. I still feel that non-parametric statistics will be more appropriate. However, parametric
statistics might be added to the supplementary.
3. Regarding the anthropometric measurements, I would like to see the actual numbers. The
declaration of no significant changes is insufficient, and data should be shown.
Review for 10.1186/s12876-022-02248-3 (2022)

Title: Plasma and fecal zonulin are not altered by a high green leafy vegetable dietary
intervention: secondary analysis of a randomized control crossover trial.
Version: 6 Date: 29 Mar 2022
Reviewer's report:
The authors have fully addressed all of my previous concerns and inquiries. I congratulate the
authors for their fine work with this manuscript.
Review for 10.1186/s12876-022-02238-5 (2022)

Title: Prevalence and Predictors of Non-alcoholic Liver Disease on MRI among Patients with
Crohn's Disease
Version: 3 Date: 27 Jan 2022
Reviewer's report:
Dear authors,
thank you very much for submitting this paper to BMC Gastroenterology.
The authors should argument more why they thought that there is an association between
NAFLD and Chron's disease in the first place. This should be made clearer in the discussion and
introduction and therefore giving the rationale for this study.
As the only disease-specific factor associated with NAFLD is disease length, the authors should
also expand on the reasons why this association could be happening.
This study illustrates the prevalence of NAFLD and associated risk factors. However, there is
no information on severity (i.e. fibrosis ) and this should be stated as a limitation as fibrosis is
the main clinical predictor in this population.
It would also be good to add in the discussion a paragraph discussing what actions would a
diagnosis of NAFLD prompt in this population and/or if awareness needs to be risen among
IBD specialist
Review for 10.1186/s12876-022-02238-5 (2022)

Title: Prevalence and Predictors of Non-alcoholic Liver Disease on MRI among Patients with
Crohn's Disease
Version: 3 Date: 24 Feb 2022
Reviewer's report:
Dr. Qijin Hong et al. have reported prevalence of non-alcoholic fatty liver disease (NAFLD) in
Crohn’s disease (CD). The very interesting point is they develop a nomogram to instruct clinical
practice.
I have some questions and comments, however, that I believe the authors need to address, as
follows:
1. The nomogram created by the authors is very interesting, but the details of how to use it are
unclear. It is unclear what the 'points' in the first factor and the 'Total Points' are. They should
explain the detailed usage of this nomogram.
2. In their discussion, the authors suggest that the dysbiosis of gut bacteria may be involved in
the difference in prevalence of NASH in Crohn's disease, but the rationale for this needs to be
explained in detail.
1. There is no need for "liver" at the beginning of "alcholic liver fatty liver disease" in the third
line of the abstract.
2. They should put (NASH) after 'alcholic liver fatty liver disease' in the second line of the
abstract.
3. On page 2, line 7, 'enterography' should be 'elastograpy'.
4. On page 5, line 18, '86 patients' should be changed to '83 patients'.
5. There are no Figure Legends in this paper, but it would be easier for readers to understand
if you write an explanation for each figure.
Review for 10.1186/s12876-022-02238-5 (2022)

Title: Prevalence and Predictors of Non-alcoholic Liver Disease on MRI among Patients with
Crohn's Disease
Version: 5 Date: 21 Mar 2022
Reviewer's report:
Dr. Qijin Hong et al. have reported prevalence of non-alcoholic fatty liver disease (NAFLD) in
Crohn’s disease (CD). The very interesting point is they develop a nomogram to instruct clinical
practice.
This information is very interesting and important for the clinician.  The authors have clearly
answered all the points that need to be calibrated in several ways. I believe that it is good enough
to accept this manuscript for publication in BMC Gastroenterology.
Review for 10.1186/s12876-022-02265-2 (2022)

Title: Semantic clustering analysis of E3-ubiquitin ligases in gastrointestinal tract defines genes
ontology clusters with tissue expression patterns
Version: 1 Date: 08 Sep 2021
Reviewer's report:
The manuscript entitled ‘Semantic clustering analysis of E3-ubiquitin ligases in gastrointestinal
tract defines genes ontology clusters with tissue expression patterns’ presents semantic cluster
analysis of GIT specific E3 ubiquitin ligases for functional classification and ontology
relationships.
The authors attempt to provide an alternative to commonly used ontological analyses. The
manuscript presents a very short or weak background on the topic. The manuscript lacks strong
arguments for conducting this study. But this study is a good attempt to provide alternative
models for functional annotations.  This work can be accepted after addressing few points below:
The manuscript has grammatical errors and authors should thoroughly check the sentence
structures.
1. The literature presented in the manuscript lacks the scientific motivation to support the
requirement of the present study. What is the significant research gap?
2. Line 53-68: This part needs to properly use literature and explain E3 ubiquitin ligases.
3. Why authors choose E3 ubiquitin ligases for this study?
4. Line 73-79: It is a general statement. Need to focus on the why and how it is relevant. What
is the motivation to conduct this study?
5. Line 78: …’ So, this method provides a more complete picture of functional’…. How can you
say that? Any relevant study or research to support the claim?
6. Use recent references to support the literature. Several classical research articles are available
to explain the ubiquitination mechanisms and their components.
7. Many sentences are lacking proper citations and explanations. Authors need to be specific
and the required information in the sentences should be connected.
8. RNA isolation protocol or appropriate reference needed.
9. What E3-Ub ligase genes, internal controls were used in the study?
10. Line 111-119: Use proper reference, protocol, and citation for clear and complete details.
11. Line 121-155: Use proper references to support the methods and procedures.
12. Does this study differentiate any of the classes of the E3 ubiquitin ligases? If not, why?
13. If possible, authors should predict the classes of the E3 ubiquitin ligases of the upregulated
or downregulated genes with structural information.
14. A flow chart showing stepwise details of the semantic cluster analysis would be useful as it
is difficult to follow the text in the methods and results.
15. Line 340-345: Statement is not clear? What do you want to say?
16. Figure 2 is very difficult to read.
17. Provide more explanation for Figure 3 in the manuscript.
18. It is very difficult to follow/read the ‘Additional file’ which has been frequently cited
throughout the manuscript. Authors should better represent the data.
Review for 10.1186/s12876-022-02265-2 (2022)

Title: Semantic clustering analysis of E3-ubiquitin ligases in gastrointestinal tract defines genes
ontology clusters with tissue expression patterns
Version: 1 Date: 13 Sep 2021
Reviewer's report:
In this manuscript, Iatsiuk et al reported their story about tissue specific gene expression patterns
of ubiquitin ligases in murine gastrointestinal tract (GIT) using a semantic clustering analysis
method. The authors also employed a dextran sulfate sodium (DSS) mouse model to survey cell-
type specific distribution changes of certain ubiquitin ligases. Overall, this is a pretty good story,
since there are some studies of this kind using cell lines, but not at animal level. The authors
basically focused on GIT and provided some valuable data for tissue-specific expression patterns
of ubiquitin ligases, especially in GIT. However, one major disappointment is that the whole
study was based on RNA analysis only. It would be much better to incorporate some verification
data of protein expression for certain ubiquitin ligases using western blots or IHC methods.
Minor concerns:
1. APC2 is one subunit of the APC/C ubiquitin ligase. Therefore, it makes no sense to only
examine one subunit of such a big complex of ubiquitin ligase.
2. BRCC3 (also called BRCC36) is a deubiquitination enzyme, but not ubiquitin ligase.
3. There is a typo in Line 301: Don’t know what is “lexpression”?