JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-023-02733-3 (2023)

Title: Comparison of clinical and pathological features between early-stage gastric-type and
intestinal-type differentiated adenocarcinoma: a retrospective study
Version: 1 Date: 17 Jan 2023
Reviewer:  Hon Chi Yip
Reviewer's report:
This is an interesting study investigating the clinicopathological and magnifying endoscopic
features between differentiated gastric type and intestinal type early gastric cancer. The topic is
relevant to the readers of the journal and provided a large volume data on mucin phenotypes of
early gastric cancers. I have the following additional comments:
1. Since magnifying NBI features were one of the main outcomes of the study, please outline
the experience of the endoscopists on interpreting NBI findings, and whether there was photo
documentation and second verification of the findings. Inter-observe variability could be a
limiting factor for ME-NBI findings.
2. One of the limitation of the study is that only endoscopically resected early gastric cancer were
included. It is therefore difficult to conclude that gastric type adenocarcinoma behaved more
aggressively, as the proportion of advanced cancers were not included. Moreover, there could
be a higher difficulty to determine "clinical indication" for ESD in gastric type adenocarcinoma,
thus leading to a higher incidence of non-curative resection. There seems to be a trend of more
depressed lesions than elevated lesions for gastric type cancer, which could translate to a more
difficult determination of ESD suitability. This should be addressed in the discussion part.
3. Although there was a significant difference in the microvascular pattern between GDA and
IGA, the proportion of ILL and FNP in  each group made it difficult to use it as  a meaningful
diagnostic tool. The authors may need to describe the usefulness of differentiating ILL from
FNP or if any additional diagnostic criteria may be helpful.
3. Minor comments
- Japanese ESD guidelines should be properly referenced.
- Reference 17 was incorrect
Review for 10.1186/s12876-023-02736-0 (2023)

Title: Utility of monocyte distribution width in the differential diagnosis between simple and
complicated diverticulitis: a retrospective cohort study
Version: 0 Date: 07 Jan 2023
Reviewer's report:
Thank you for asking me to review the manuscript entitled, ‘Utility of MDW for diagnosing
colonic diverticulitis in the emergency department: a retrospective cohort study’. This is an
interesting study. The authors have studied the MDW in relation to the identification of patients
with complicated diverticulitis. However, I do have some concerns which I have divided in to
major and minor categories. They are as follows:
Major concerns:
1. Sample size- The main concern here is that only 21 cases were defined as complicated
diverticulitis. There is no sample size calculation. Please provide this.
2. Please provide a table of test characteristics (sensitivity, specificity, PPV, NPV) for the
standard cut-off for MDW and their cut off for MDW.
3. From my calculations, it looks like the PPV is low, but the NPV is high. The authors could
play to this strength, if the sample size is adequate.
4. Was there an improvement in test characteristics when the MDW was combined with the
WCC?
5. Please provide the calibration statistic for the multivariate logistic regression model.
Minor concerns:
(i) Title- The title should state ‘diagnosing complicated colonic diverticulitis’ not just
‘diagnosing colonic diverticulitis’.
(ii) Please provide the diagnostic criteria for complicated diverticulitis in the methods section.
(iii) The first paragraph of the discussion should be a summary of the study findings.
(iv) The content of the first two paragraphs of the discussion should probably be in the
introduction.
Review for 10.1186/s12876-023-02736-0 (2023)

Title: Utility of monocyte distribution width in the differential diagnosis between simple and
complicated diverticulitis: a retrospective cohort study
Version: 0 Date: 10 Jan 2023
Reviewer:  Alessandro Iacona
Reviewer's report:
the study highlights the correlation of the mdw with the severity of the pathology.
There is no control group with which to compare the colonic diverticulitis patient population.
From the results it is not possible to say that mdw is useful in the diagnosis of diverticulitis in
the emergency room.
Review for 10.1186/s12876-023-02736-0 (2023)

Title: Utility of monocyte distribution width in the differential diagnosis between simple and
complicated diverticulitis: a retrospective cohort study
Version: 0 Date: 22 Jan 2023
Reviewer:  Murat Taner Gül#en
Reviewer's report:
The study is up-to-date and gives us a practical approach to a common clinical issue. The
introduction and discussion sections of the article are sufficient. However, I would like to address
some issues in the Materials and Methods section:
1) It should be stated whether the tomographies are taken orally or IV, and how the diagnosis
is made radiologically should be briefly explained.
2) The characteristics of complicated and uncomplicated Diverticulitis should be clearly stated.
3) How the cutoff value of MDW is found as 20.38 should be explained in the material and
method section.
4) Is the MDW measured from the patient's blood at the time of admission or from the blood
taken at the later time?
5) How the MDW is obtained and why it has not a unit should be briefly stated.
Review for 10.1186/s12876-023-02736-0 (2023)

Title: Utility of monocyte distribution width in the differential diagnosis between simple and
complicated diverticulitis: a retrospective cohort study
Version: 2 Date: 08 Feb 2023
Reviewer's report:
Thank you for asking me to review the revised manuscript entitled, ‘Utility of MDW for
diagnosing complicated colonic diverticulitis in the ED: a retrospective cohort study’. I wish to
thank the authors for responding to my queries. I have three minor comments:
1) Please use the term ‘multivariable’ instead of ‘multivariate’ in relation to the multivariable
logistic regression model.
2) Page 5, line 90- ‘intravenous (IV) contrast CT’, not ‘intravenous (IV) CT’.
3) Please add the sample size calculation to the manuscript.
Review for 10.1186/s12876-023-02736-0 (2023)

Title: Utility of monocyte distribution width in the differential diagnosis between simple and
complicated diverticulitis: a retrospective cohort study
Version: 2 Date: 25 Feb 2023
Reviewer:  Alessandro Iacona
Reviewer's report:
The study demonstrates that mdw is useful in the differential diagnosis between simple and
complicated diverticulitis in a population of patients diagnosed with diverticulitis.
The title and conclusion of the manuscript are not consistent with the content of the manuscript.
The study design is not appropriate to the research objective.
The type of anticoagulant used (K2edta or K3edta) is not specified.
Review for 10.1186/s12876-023-02725-3 (2023)

Title: APC mutation correlated with poor response of immunotherapy in colon cancer
Version: 2 Date: 31 Dec 2022
Reviewer's report:
Authors showed an interesting speculation about APC mutation and the response of
immunotherapy in colon cancer.
However, I think that there are several points to be addressed.
1) It is well known that tumors with microsatellite instable have a lower frequency of APC
mutations, compared with microsatellite stable and CpG island methylator phenotype-low
(many of chromosomal instability phenotype) colorectal cancers.
Authors concluded that the colon cancer patients with APC mutations were associated with poor
response of immunotherapy. I think that they should verify the proportion of the chromosomal
instability phenotype, microsatellite instability phenotype and CpG island methylator phenotype
contained in the group with  APC mutations. I wonder if the response to immunotherapy would
be poor because the MSI phenotype was rarely included.
2) If authors have data about analysis of stroma or microenvironment of tumor, they should
show it. I think that these factors are also deeply involved in the efficacy of immunotherapy.
Review for 10.1186/s12876-023-02725-3 (2023)

Title: APC mutation correlated with poor response of immunotherapy in colon cancer
Version: 2 Date: 18 Jan 2023
Reviewer's report:
Overall, this is an interesting study. Using a computational approach, the authors show that in
colon cancer patients, the presence of adenomatous polyposis coli (APC) mutation correlated
with a less effective immunotherapy outcome. In my opinion, the manuscript is suitable for
publication after the authors have addressed the following questions and comments
1. In Table 1, the authors suggest that there is no correlation between APC mutation and tumor
mutational burden (TMB) while comparing APC mutant and wildtype group in the MSKCC
dataset. However, in Figure 4, the authors show that APC mutation is associated with lower
TMB. How can the authors explain this apparent contradiction in their findings?
2. The authors present interesting findings in Figure 5. However, it would be nice to see if the
computational findings correlate with experimental data. Could the authors stain patient samples
(APC wildtype and mutants) to look at immune cell infiltration?
3. The manuscript is well organized, and it is easy to follow the logical flow of ideas and
the rationale of the study. However, there are several grammatical and typographical errors
throughout the manuscript.  The manuscript needs to be carefully revised to improve the written
content.
Review for 10.1186/s12876-023-02711-9 (2023)

Title: Thiols as a Marker of Inflammatory Bowel Disease Activity: A Systematic Review
Version: 2 Date: 06 Jan 2023
Reviewer's report:
Congratulations to the authors for the detailed review of the topic, which is evidently
heterogeneous and evolving.  The work on the meta-analysis is indeed commendable and
thorough.
However, the studies included in this particular review and meta-analysis are inferior in quality
and are heterogeneous due to a lack of standardization, and different entities of the diseases
concerned. Only a few of the studies have been able to reach a conclusion with statistical
significance, hence the meta-analysis also could not have a significant numerical result. More
studies are obviously needed, with larger sample sizes, with a focus on a single disease (e.g.,
ulcerative colitis) and a particular stage (e.g., remission or activity). The ongoing drug regimens
which have (or have not) achieved remission are also a surrogate marker of the severity. To
summarise, performing a meta-analysis with such a small dataset without choosing a niche
population (e.g. Small bowel Crohn's disease on Biologics, where non-invasive assessment
would make a difference) would be premature and would not have a practice-changing influence
on the current management.
Review for 10.1186/s12876-023-02711-9 (2023)

Title: Thiols as a Marker of Inflammatory Bowel Disease Activity: A Systematic Review
Version: 2 Date: 11 Jan 2023
Reviewer's report:
Introduction : have adequately described the literature involving IBD and need for bio markers.
Objective clearly stated. need to correct grammar at places.
Methodology : have described the database searched, mesh terms used, software used for
automation, eligibility criteria,  data extraction and risk of bias.
The final date when a search was conducted needs to be mentioned. which parameters were
extracted needs to be mentioned.
Reason for exclusion of studies need not be mentioned in the methodology and should be shifted
to results. There appears to be a typing error - "CD" is written as "DC" at places and UC is
written as "RCU".  what is "DII" ?
Results: Methodology and findings of the included studies  described adequately. Different
disease activity indices have been used for patients with UC. combining such studies into one
meta analysis does not appear to be appropriate. the last paragraph of results is about limitation
of the study design. It should be shifted to the discussion.
Discussion : adequate
Review for 10.1186/s12876-023-02711-9 (2023)

Title: Thiols as a Marker of Inflammatory Bowel Disease Activity: A Systematic Review
Version: 5 Date: 15 Feb 2023
Reviewer's report:
The effort to compile all the data on a niche and novel topic is really commendable. However,
this investigation is neither standardized nor reproducible. Hence, the results are heterogeneous,
as expected. This meta-analysis does not guide clinical decision-making. A systematic review
alone would be sufficient to summarise the utility of thiols as markers of IBD activity.
Review for 10.1186/s12876-023-02711-9 (2023)

Title: Thiols as a Marker of Inflammatory Bowel Disease Activity: A Systematic Review
Version: 5 Date: 21 Feb 2023
Reviewer's report:
Authors have wisely excluded the meta analyses from the study.  line 308, authors have stated
hat thiol levels may act as markers for corticosteroid adverse effects . how was this conclusion
reached ?
I congratulate the authors on a well conducted systematic review. As the studies are
heterogenous, authors have been unable to reach a definitive conclusion. However,  further
studies may expand on the role of thiols in IBD
Review for 10.1186/s12876-023-02699-2 (2023)

Title: Analysis of clinical diagnosis and treatment of intestinal volvulus
Version: 2 Date: 20 Dec 2022
Reviewer's report:
Thank you for the opportunity to review this manuscript.
Dr. Fo and colleagues published their center’s experience in gastro-intestinal volvulus over a
period of 7 years.
The manuscript describes an important problem that requires prompt treatment, however there
are some significant issues that need addressing. Most importantly, this is a small sample size
study that is further split into 3 subtypes of intestinal volvulus.
Major comments:
- The authors describe three subtypes of volvulus: jejunal, ileal and colonic. However, these are
all very different pathophysiological and epidemiological. Lumping these all together into one
retrospective study reduces the clarity of the message of the paper. Similarly, there is a difference
between primary and secondary volvulus (ie adhesional following surgery).
- In this retrospective cohort, all patients underwent surgery. However, there are cases where
conservative therapy can be attempted (as mentioned in the discussion). Are there any other
patients in this time period that underwent conservative therapy? Colonic volvulus, for instance,
can be managed endoscopically with an elective laparoscopic sigmoid resection at a later stage.
- Section 2.4 describes the surgical treatment; however the wording is a bit repetitive and
unclear (including the use of the ‘+’ sign). Instead, the authors should use a table to describe the
operations and provide a clearer overview. Also, did all patients undergo laparotomy, as early
onset cases can be managed laparoscopically?
- In the discussion the authors mention that ‘the occurrence of intestinal necrosis and the
cause of intestinal torsion were not significantly related to the presence or absence of signs of
peritonitis…’. I can only imagine that is due to very small sample size rather than intestinal
necrosis being insignificant for the clinical outcome.
- Regarding diagnostics: abdominal plain film are really obsolete by international guidelines
for acute abdominal pain investigations unless in exceptional circumstances. The gold standard
is CT with oral/rectal contrast if possible. There is no evidence why dual source CT is better
than standard CT in this setting (in contrast to other settings such as evaluating respectability
of borderline malignancies etc.).
Minor comments:
- Instead of ‘anal cessation of exhaust’ it is recommended to use ‘absence of flatus’.
- Some additional revision of language may be appropriate as it is difficult to follow some of the
wording: ’…17 patients with small bowel torsion who were not intestinal necrosis underwent
surgical reduction’.
- In section 2.5: the authors mention skin dehiscence with ‘skin grafts’ being placed under the
incision. It is unclear to me what they mean? Was the wound debrided and skin grafts placed?
How deep was the dehiscence, was it only the skin or did it include the fascia.
- The  methods describe the period from January 2015 unitl December 2022 but this is a typo,
this would mean the last patients had no significant follow-up.
Review for 10.1186/s12876-023-02699-2 (2023)

Title: Analysis of clinical diagnosis and treatment of intestinal volvulus
Version: 2 Date: 24 Dec 2022
Reviewer's report:
In the present form, this article cannot be accepted for publication.
Lot of revision needs to be done with respect to language content, way of writing, sticking to
standard guidelines for writing, proper use of accepted medical terminology. Seems to be a  very
amateur way of writing.
References do not have any pattern of presentation.
Complete article needs to be rewritten, with adherence to journal guidelines.
Review for 10.1186/s12876-023-02699-2 (2023)

Title: Analysis of clinical diagnosis and treatment of intestinal volvulus
Version: 2 Date: 22 Jan 2023
Reviewer's report:
Interesting paper about intestinal volvulus
correct in method section : fischer test not FISH test
add arrows in figures to show the lesions
in the discussion, add if minimally invasive surgery( e.g. laparoscopy has a place)
this systematic review discussed its place (https://www.sciencedirect.com/science/article/pii/
S2667008922000143)
Review for 10.1186/s12876-023-02708-4 (2023)

Title: Correlation between nonalcoholic fatty liver disease and left ventricular diastolic
dysfunction in non-obese adults: a cross-sectional study
Version: 2 Date: 27 Oct 2022
Reviewer's report:
Authors state that....Obesity is related to higher all-cause mortality, so both obese and non-
obese NAFLD patients can benefit from losing weight. For non-obese NAFLD patients, losing
weight by 5-10% through lifestyle intervention can also benefit significantly......but they should
honestly recognise that there are many drugs on the pipeline that are reckoned as good candidates
to cure NAFLD/NASH, and consequently to reduce the burden of  CV diseases  linked to
this very common illness, as evident in various recent papers, for example...Insights into the
molecular targets and emerging pharmacotherapeutic interventions for nonalcoholic fatty liver
disease. Metabolism. 2022 Jan;126:154925. doi: 10.1016/j.metabol.2021.154925. Epub 2021
Nov 2. PMID: 34740573.
Data on visceral adiposity should be presented , such as WC or WHR, to better evaluate its role
in the so-called non-obese subjects (BMI<25), who can be overweight according to cut-offs of
the BMI of the Chinese population.
Data on insulin resistance (such as HOMA or other indices) should be presented to   try
to clarify  the possible mechanisms of the early left ventricular diastolic dysfunction...as
evident in... Early subclinical ventricular dysfunction in patients with insulin resistance. J
Cardiovasc Med (Hagerstown). 2014 Feb;15(2):110-4. doi: 10.2459/JCM.0b013e3283638164.
PMID: 24522082.
Authors should deepen the concept of age that is a risk factor for the progression of both CV
diseases via atherosclerosis and NAFLD , according to their findings, see ORs of the multiple
regression.
Review for 10.1186/s12876-023-02708-4 (2023)

Title: Correlation between nonalcoholic fatty liver disease and left ventricular diastolic
dysfunction in non-obese adults: a cross-sectional study
Version: 4 Date: 16 Nov 2022
Reviewer's report:
1. Authors of the revised manuscript of Cong et al. “Correlation between nonalcoholic fatty liver
disease and early left ventricular diastolic dysfunction in non-obese adults: a cross-sectional
study”, have tried to implement more complex approach to identify left ventricular diastolic
dysfunction (LVDD).  However, author’s attempt CANNOT be considered adequate. Authors
still use only 2 metrics (E/A ratio and E value), which is insufficient for differentiating normal
from the pseudoformal LV filling. In addition, authors mistakenly call LV diastolic function
normal when 0.850 cm/s (again, more metrics are needed). Reviewer’s opinion here is based on
American and European recommendations (e.g., mentioned in author’s ref 28 ).
2. Authors found NO DIFFERENCE in the prevalence of LVDD in non-obese NAFLD and
control groups (58% vs 54%, P=0.487). In multivariate logistic regression analysis, NAFLD was
not statistically significant factor (P=0.628, Table 7). BUT authors boldly state in the text and
in the conclusion (both abstract and discussion) that “the non-obese NAFLD group had a higher
prevalence of LV diastolic dysfunction” and “non-obese NAFLD is associated with increased
risk of LV diastolic dysfunction”. This is just not right.
3. At best, authors can discuss here only the changes in transmitral flow and its possible
worsening in NAFLD (based on E/A values and prevalence of E/A<1). Suggested conclusion
could be as follows: “Non-obese NAFLD was associated with decrease of E/A, however more
research is necessary to evaluate risk of non-obese NAFLD for LV diastolic dysfunction”. The
title should be also changed.
Review for 10.1186/s12876-023-02708-4 (2023)

Title: Correlation between nonalcoholic fatty liver disease and left ventricular diastolic
dysfunction in non-obese adults: a cross-sectional study
Version: 5 Date: 09 Dec 2022
Reviewer's report:
Authors addressed most of the comments in this revision. To avoid confusions in understanding
of study results, this reviewer considers important to clarify the inadequacy of LVDD grading
by the echocardiographic tools used in this study.
The simplest solution could be the rewriting the corresponding statement in the study limitations
as follows: “….Fifth, we used E/A and E value to evaluate LV diastolic dysfunction. This
approach is unable to identify patients with Grade 2 diastolic dysfunction when E/A is in the
normal range (0.8< E/A <1, pseudonormal filling).[28] Therefore, more accurate methods will
be needed in the future….”
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 1 Date: 01 Nov 2022
Reviewer:  Tarana Gupta
Reviewer's report:
The article prepares a nomogram for prediction of 90-day mortality in HBV-ACLF.
I have few issues.
1. In introduction authors state that HBV-ACLF constitutes 70% of ACLF. I think this is correct
in a regional or few geographical settings. Should be improved.
2. This is a retrospective study. Therefore there would be bias on data collection etc.
3. Is this nomogram other than prediction of mortality has been evaluated for response to
treatment.
4. Authors should also include the management protocol used for HBV-ACLF.
5. The HBV parameters including HBV DNA quantitative levels, IgM anti-HBc levels and
positivity, HBeAg status, HBsAg quantitative levels should be included in formation of any
prediction model for HBV-ACLF.
6. All parameters should be taken into consideration for HBV-ACLF, only then we can say that
this is better for prediction of 90-day mortality as compared to generalised scores like MELD,
CLIF-OF score etc.
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 1 Date: 09 Nov 2022
Reviewer's report:
There are no further comments and can be accepted.
However very minor  queries can be further addressed it will carry more clarity,
1. The external validation was done on 198 HBV cases. But in discussion or conclusion authors
further recommend validating. The reason thereof   can be explained.
2. The probability taken for considering the multivariate logistic analysis.
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 2 Date: 29 Dec 2022
Reviewer's report:
Some issues should be further addressed.
In the Introduction section, aiming at removing confusion, the definitions of “short- and
medium-term” should be presented as you have explained in the file “up point-to-point”.
The sentence “Furthermore, the main causes of disease were hepatitis C and alcohol, rather than
HBV” is inappropriate, where the words “hepatitis C” should be revised as “hepatitis C virus”.
The sentence “ In addition, the COSSH-ACLF also involves multiple parameters and requires
complex organ failure assessments” seems incorrect. “COSSH-ACLF” should be revised as
“COSSH-ACLFs”.
The sentence “Moreover, we compared this nomogram with the aforementioned prognostic
scoring systems to provide guidance for clinical treatment and decision making” is lacking
of logic. As I understand it, the authors compared this nomogram with the aforementioned
prognostic scoring systems in order to demonstrate the clinical predictive value of this
nomogram.
In the Results section, the authors compared predictive abilities between the nomogram and
other scoring systems in a cohort of 181 HBV-ACLF patients. Why not compare predictive
abilities between the nomogram and other scoring systems in the external validation cohort?
The reasons should be explained.
The sentence “The AUC of the nomogram (0.866) was
approximately comparable to that of the COSSH-ACLFs (0.872) and was better than
that of the CLIF-C ACLF (0.825), CLIF-OFs (0.835), and MELD score (0.665)” is
inappropriately expressed due to the absence of statistical comparison. It is possible to compare
the AUC of different prognostic scoring systems.
Details of Figure 1, for example, the inconsistent spacing of letters between one word, should
be further improved.
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 3 Date: 20 Jan 2023
Reviewer's report:
1. In the Comparison of Predictive Abilities Between the Nomogram and Other Scoring
Systems part of the Results section, the sentence “The predictive ability of the nomogram
was approximately comparable to that of the COSSH-ACLFs (AUC 0.866 vs. 0.872), and
significantly better than that of the CLIF-C ACLF (AUC 0.866 vs. 0.825), CLIF-OFs (AUC
0.866 vs. 0.835), and MELD score (AUC 0.866 vs. 0.665)” is inappropriately expressed
due to the absence of statistical comparison. P value should be given. When there is no
statistically significant difference (P > 0.05) between the AUC of this nomogram and the AUC
of the COSSH-ACLFs, the authors can say that “The predictive ability of the nomogram was
approximately comparable to that of the COSSH-ACLFs”.
The issue is an essential one that I have repeatedly referred to but the authors didn’t revise
properly. If the authors cannot resolve this issue, many sentences of this paper are unreasonable,
such as “As observed, the areas under the ROCs of the nomogram and COSSH-ACLFs were
very similar. Hence, it could be considered that the predictive abilities of the nomogram and
COSSH-ACLFs are comparable”, “The nomogram is more accurate than the MELD score,
CLIF-C ACLFs, and CLIF-C OFs...”. Besides, the issue may affect the clinical significance of
this paper. The authors should carefully address this and related issues.
2. In the Discussion section, the sentence “The possible mechanism underlying mechanism
involves the binding of HDL-C particles to lipopolysaccharides” is inaccurate, where the words
“The possible mechanism underlying mechanism” should be revised as “The possible underlying
mechanism”.
3. The authors should check the grammar throughout this paper earnestly.
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 3 Date: 17 Feb 2023
Reviewer:  Tarana Gupta
Reviewer's report:
Authors have improved the manuscript adequately.
Review for 10.1186/s12876-023-02727-1 (2023)

Title: A Novel Nomogram to Predict 90-Day Mortality in Patients with Hepatitis B Virus-
Related Acute-on-Chronic Liver Failure: A Single-Center Retrospective Study
Version: 4 Date: 01 Mar 2023
Reviewer's report:
The manuscript has been revised adequately by the authors.
Review for 10.1186/s12876-023-02722-6 (2023)

Title: Prognostic significance of the Naples prognostic score in colorectal cancer patients
undergoing curative resection: A propensity score matching analysis
Version: 1 Date: 14 Nov 2022
Reviewer's report:
Although several limitations due to the retrospective nature of the research, I think the study
was well conducted, both  in respect of patients selection and statistical methods. The number
of patients was  sufficient and the follow up lenght adeguate.
I have only to highlight the eccessive number of autocitations by the Authors.
Review for 10.1186/s12876-023-02722-6 (2023)

Title: Prognostic significance of the Naples prognostic score in colorectal cancer patients
undergoing curative resection: A propensity score matching analysis
Version: 1 Date: 04 Dec 2022
Reviewer's report:
Dear authors,
Thank you for submitting your report.
This report shows clearly that  NPS is significantly better than other indicators.
Although there were no significant differences between the two groups after PSM in this paper,
it would be better to comprehensively include covariates for PSM that may have an impact on
prognosis (such as TNM) in addition to those that differ between the two groups.
It offers good results, but there are a few things I would like to confirm or question.
#1 Please add the standardized difference in table2 (in order to evaluate propensity score
matching)
Review for 10.1186/s12876-023-02722-6 (2023)

Title: Prognostic significance of the Naples prognostic score in colorectal cancer patients
undergoing curative resection: A propensity score matching analysis
Version: 1 Date: 10 Feb 2023
Reviewer's report:
Thank you for allowing me to review this manuscript. For the most part, the result is clear, and
the interpretation of the data is warranted. I also think that the topic may be of interest to the
field. However, I have found some issues that will improve the manuscript.
1 Because chemotherapy or radiotherapy can affect neutrophils, neoadjuvant treatment cases
should be excluded from the analysis. Additionally, the number of these patients is minimal.
2 Propensity matching should include pT and pN instead of pStage as oncological factors. In
the current analysis, the operative times between the two groups differ even after the propensity
score. This result means that more advanced cancers were present in the HighNPS group.
3 Show the years after surgery when inflammatory markers were compared in the time-
dependent ROC curve.
4 There is no prognostic difference in DFS, which raises the question of whether NPS represents
cancer progression. Discuss this point.
Review for 10.1186/s12876-023-02722-6 (2023)

Title: Prognostic significance of the Naples prognostic score in colorectal cancer patients
undergoing curative resection: A propensity score matching analysis
Version: 2 Date: 12 Mar 2023
Reviewer's report:
The authors revised the manuscript well according to reviewer’s comments. They described their
topic area and explained the purpose of the study very clearly. I think this original article is well
written and gives useful information for clinicians and scientists. And now, it can be acceptable
for publication in BMC Gastroenterology.
Review for 10.1186/s12876-023-02723-5 (2023)

Title: Comparison of surgery rates in biologic-naïve patients with Crohn’s disease treated with
vedolizumab or ustekinumab: findings from SOJOURN
Version: 2 Date: 22 Nov 2022
Reviewer's report:
The paper addresses the risk of surgery in biologic-naïve CD patients treated with vedolizumab
and ustekinumab.. the number of patients enrolled is remarkable (1,222 included patients)
although described in a retrospective observational study. The main point is about choosing
a treatment for so many patients. The median age of the population is 47 years. the frailty of
the population is indicated only by a higher Charson Comorbidity Index, Patient characteristics
should be more detailed (such as the choice of the two drugs versus for example anti-TNF)
Review for 10.1186/s12876-023-02723-5 (2023)

Title: Comparison of surgery rates in biologic-naïve patients with Crohn’s disease treated with
vedolizumab or ustekinumab: findings from SOJOURN
Version: 4 Date: 13 Feb 2023
Reviewer's report:
Thank you very much for giving me the opportunity to review the "revised" manuscript.
I really think the work addresses an important topic and I appreciate the revised version.
I still think that data on disease history (duration, activity, risk factors) are important to define the
real possibility of comparison between different populations. Therefore, the conclusions should
still refer to this possible bias.
Conflict interest should be clearly stated.
Review for 10.1186/s12876-023-02723-5 (2023)

Title: Comparison of surgery rates in biologic-naïve patients with Crohn’s disease treated with
vedolizumab or ustekinumab: findings from SOJOURN
Version: 4 Date: 15 Feb 2023
Reviewer's report:
This is an important study. While there are numerous methodologic limitations to retrospective,
observational claims data, the authors have addressed the items raised on initial review and
sufficiently stated these limitations in the revised text. The data are intriguing and should lead to
discussion regarding non-TNF post-surgical treatment. Given the revised discussion and clarity
provided by expansion of the supplementary data, all critiques are addressed in this version.
Review for 10.1186/s12876-023-02685-8 (2023)

Title: Whether the Golgi Protein 73 Could Be A Diagnostic Serological Marker in
Hepatocellular Carcinoma: A Meta Analysis
Version: 4 Date: 30 Dec 2022
Reviewer:  Zoe Larghi Laureiro
Reviewer's report:
This is a meta-analysis which aimed to investigate the role of Golgi protein 73  in both  the
diagnosis of Hepatocellular carcinoma and in the differential diagnosis of HCC from liver
cirrhosis.
Overall, the study is very interesting and well conducted.
In my opinion,  it meets all the criteria for publication.
Review for 10.1186/s12876-023-02685-8 (2023)

Title: Whether the Golgi Protein 73 Could Be A Diagnostic Serological Marker in
Hepatocellular Carcinoma: A Meta Analysis
Version: 4 Date: 02 Jan 2023
Reviewer:  Fabio Melandro
Reviewer's report:
I read the paper of Zhang et al. with great interest. in the review and meta analysis, the authors
analyzed article the diagnostic role of Golgi protein 73 marker in the field of hepatocellular
carcinoma and his value for differential diagnosis between HCC and chirrosis
The paper is interesting and well written; the quality of statistical analysis is satisfactory and the
relevant literature is adequately covered in the analysis.
Discussion is very complete.
There are only few suggestions to the authors in order to improve the strength of their study:
1. Could You improve the flow diagram of the research with PRISMA layout and respect
PRISMA guidelines?
2. In the flow diagram could You define the reason for not relevance of the articles (eg. animal
study, letter to editor...)
Thanks
Review for 10.1186/s12876-023-02685-8 (2023)

Title: Whether the Golgi Protein 73 Could Be A Diagnostic Serological Marker in
Hepatocellular Carcinoma: A Meta Analysis
Version: 9 Date: 09 Feb 2023
Reviewer:  Fabio Melandro
Reviewer's report:
The criticisms were addressed. In my opinion, it meets all the criteria for publication.
Review for 10.1186/s12876-023-02685-8 (2023)

Title: Whether the Golgi Protein 73 Could Be A Diagnostic Serological Marker in
Hepatocellular Carcinoma: A Meta Analysis
Version: 9 Date: 18 Feb 2023
Reviewer:  Zoe Larghi Laureiro
Reviewer's report:
The paper by Zhang et al. is a meta-analysis which aimed to investigate the role of Golgi
protein73 in both the diagnosis of Hepatocellular carcinoma and in the differential diagnosis of
HCC from liver cirrhosis.
Overall, the study is very interesting, the analysis is well conducted, and all the small correction
have been assessed.
In my opinion, it meets all the criteria for publication.
Review for 10.1186/s12876-023-02704-8 (2023)

Title: Impact of cholangitis on survival of patients with malignant biliary obstruction treated
with percutaneous transhepatic biliary drainage
Version: 2 Date: 10 Aug 2022
Reviewer's report:
In this study the authors aimed to evaluate the impact of cholangitis on survival of patients with
gastrointestinal cancer and malignant biliary obstruction treated with percutaneous transhepatic
biliary drainage (PTBD).
The study included 588 patients, 258 (43.9%) patients with pancreatic cancer, 222 (37.7%) with
biliary tract cancer, and 108 (18.4%) with metastasis from gastrointestinal cancers. The 30-
day mortality rate was 30.8% for 156 patients with cholangitis before PTBD, 19.5% for 215
patients with cholangitis after PTBD and 25.8% for 217 patients without cholangitis (P=0.039).
The median survival was 1.8 months for patients with cholangitis before PTBD, 3.0 months for
patients with cholangitis after PTBD, and 3.2 months for patients without cholangitis (P=0.002).
After successful PTBD, 54 out of 291 patients received chemotherapy; the median survival was
5.2 months with cholangitis before PTBD, 9.4 months with cholangitis after PTBD and 15.3
months without cholangitis.
They concluded that  In gastrointestinal cancers with malignant biliary obstruction, survival is
poorer if cholangitis occurs before PTBD compared to cholangitis after PTBD.
The study addresses a critical clinical need and is of interest.
My only comment is related to recent literature data that should be discussed to improve the
clinical impact of the manuscript further.
-introduction: the authors should further discuss the Role of Cholangioscopy and EUS in the
evaluation of Indeterminate Biliary Strictures, as recently well addressed in a comprehensive
review (The Role of Cholangioscopy and EUS in the Evaluation of Indeterminate Biliary
Strictures. Gastroenterol. Insights 2022, 13, 192-205.), because differentiating between
malignant and benign biliary strictures remains a clinical challenge.
-also technical aspects of biliary procedures should be recalled as well summarized in a recent
review describing  the techniques, clinical efficacy, and potential pitfalls of advanced ERCP
techniques, percutaneous biliary drainage, and EUS-RV ERCP (Troubleshooting Difficult Bile
Duct Access: Advanced ERCP Cannulation Techniques, Percutaneous Biliary Drainage, or
EUS-Guided Rendezvous Technique? Gastroenterol. Insights 2021, 12, 405-422.).
Review for 10.1186/s12876-023-02704-8 (2023)

Title: Impact of cholangitis on survival of patients with malignant biliary obstruction treated
with percutaneous transhepatic biliary drainage
Version: 2 Date: 19 Dec 2022
Reviewer's report:
In this study Niemela J and colleagues have explored impact of cholangitis on survival
of patients with malignant biliary obstruction undergoing percutaneous transhepatic biliary
drainage. Overall, 588 patients were enrolled; 156 patients had cholangitis before PTBD, 215
had cholangitis after PTBD and 217 patients were without cholangitis. Patients with cholangitis
prior to PTBD had lower survival compared to patients with cholangitis after PTBD or without
cholangitis.
Major concerns:
1. Authors should consider comparing individual groups to find significance like between group
with cholangitis prior to PTBD, without prior PTBD or without cholangitis.
2. Patients with cholangitis prior to PTBD had poorer performance status compared to other two
groups. Whether that was the major contributing factor for overall poor median survival that
should be explored.
3. What were the causes of cholangitis after PTBD should be mentioned in the results like due
to blockage of the PTBD catheter or slippage of PTBD catheter or inadequately drained system.
4. Median time from PTBD insertion to onset of cholangitis should be mentioned.
5. What management was used for management of cholangitis after PTBD should be mentioned
like change of PTBD catheter, upgradation of PTBD catheter or insertion of metallic SEMS.
6. What was the catheter diameter used during PTBD should also be mentioned and whether
metallic stent placement was done during initial setting or subsequent setting should also be
mentioned.
7. Many details of patient’s are mentioned in methodology or discussion section which should
be removed and mentioned in the results section.
8. Tables should be re-arranged at the end of the manuscript not embedded in the results section.
Review for 10.1186/s12876-023-02704-8 (2023)

Title: Impact of cholangitis on survival of patients with malignant biliary obstruction treated
with percutaneous transhepatic biliary drainage
Version: 4 Date: 07 Feb 2023
Reviewer's report:
Authors have addressed the reviewers feedback satisfactorily.
Minor point: Authors should include point no 3 of last review in the limitation of the study.
Review for 10.1186/s12876-023-02690-x (2023)

Title: Eubiotic effect of rifaximin is associated with decreasing abdominal pain in symptomatic
uncomplicated diverticular disease: results from an observational cohort study
Version: 0 Date: 20 Oct 2022
Reviewer's report:
The manuscript is well written and it deals with a hot topic in the research field of Symptomatic
Uncomplicated Diverticular Disease (SUDD). The authors should specify the inclusion criteria
with respect to the exact definition of SUDD. In particular, it is important to report the presence,
the localization and the duration of the abdominal pain, as stated  in multiple conributions in
the literature by Tursi A. et al.
Review for 10.1186/s12876-023-02690-x (2023)

Title: Eubiotic effect of rifaximin is associated with decreasing abdominal pain in symptomatic
uncomplicated diverticular disease: results from an observational cohort study
Version: 0 Date: 28 Oct 2022
Reviewer's report:
This study assessed the effect of cyclic treatment with rifaximin on the fecal microbiota of SUDD
patients. Authors found that Akkermansia was the main bacteria species linked to the SUDD,
since it was inversely correlated with abdominal pain in these patients.
The study on SUDD microbiota are still contradictory and no definite data are available. Thus,
any new study is welcomed. Although this study try to identify some relationship between SUDD
and microbiota, is suffer from too bias to guarantee acceptance.
1. About the inclusion criteria:
a.  the definition of SUDD is not described neither referenced;
b. no description on how the SUDD diagnosis was made was reported;
c. patients with exacerbation of SUDD were enrolled, but it is unclear how this “exacerbation”
was assessed;
d. The severity of abdominal pain was assessed with an arbitrary scale without any validation.
A simple VAS scale would have been much better.
2. About the exclusion criteria:
a. no information is reported about the previous use of systemic antibiotic or probiotics;
b. the “contraindications to the use of rifaximin” have to be clearly listed;
c. the definition “acute complications of diverticular disease during the previous 6 months” is
unclear: are the author talking about acute diverticulitis? Uncomplicated and/or complicated?
And what about the diverticular bleeding?
3. Data about demographics and concomitant medications are lacking;
4. The final study group was too small, since about half of patients were excluded for several
reasons;
5. A control group is lacking: thus, we don’t have any control to confirm the presence of a
different microbiota in  SUDD;
6. Akkermansia was detected in 2 of 12 (16.7%) patients at inclusion, in 7 of 12 (58.3%; p=0.045)
patients at 3 months, and 9 of 12 (75.0% ; p=0.006) patients after 6 months of rifaximin. This
means that Akkermansia appeared during the follow-up, not that it increased during the follow-
up. This is a substantial difference, since increasing or decreasing during the follow-up has to
be assessed by a # Logarithmic scale.
7. As correctly reported by the authors, other studies in SUDD setting found Akkermansia
increased in these patients, with a significant relationship between its abundance and severity of
abdominal pain. Authors have to try to explain the discrepancy between these literature results
and the findings of this study.
Review for 10.1186/s12876-023-02690-x (2023)

Title: Eubiotic effect of rifaximin is associated with decreasing abdominal pain in symptomatic
uncomplicated diverticular disease: results from an observational cohort study
Version: 0 Date: 04 Jan 2023
Reviewer:  Francesco Roscio
Reviewer's report:
The topic is interesting, as it scientifically analyzes the rationale of a therapy too often prescribed
on an empirical basis. Congratulations to the authors for having pursued an observation period
of 6 months.
The paper was quite well written, both the methodology and the statistical analysis are correct.
It just needs some linguistic revisions.
However, I would like to focus on the size of the analyzed cohort.
A series of 12 patients is small. A patient outflow of nearly 50% is significant.
I leave to the Editor the decision whether or not to publish a paper with such low power.
If this aspect does not constitute a limitation, nothing prevents me from publishing it.
Review for 10.1186/s12876-023-02690-x (2023)

Title: Eubiotic effect of rifaximin is associated with decreasing abdominal pain in symptomatic
uncomplicated diverticular disease: results from an observational cohort study
Version: 4 Date: 18 Feb 2023
Reviewer:  Francesco Roscio
Reviewer's report:
Dear Authors, the linguistic form has improved. My judgment does not change and is definitively
positive. If the editor agrees to publish a paper with this case-load, nothing will prevent me from
publishing it. Regards. Francesco Roscio
Review for 10.1186/s12876-023-02716-4 (2023)

Title: Glepaglutide, a novel glucagon-like peptide-2 agonist, has anti-inflammatory and mucosal
regenerative effects in an experimental model of inflammatory bowel disease in rats
Version: 1 Date: 19 Nov 2022
Reviewer's report:
The present paper aims to  investigate the therapeutical benefits of glepaglutide, a long acting
GLP-2 analogue,  in rats with small intestinal inflammation.
I would like to thank the authors for  conducting this study which supports a different approach
to dealing with inflammatory bowel disease. The authors may wish to consider the following
comments
General comments
The paper is well written. However, many sentences are too long making it difficult for the
reader to follow the point.
I am not sure about the value of the long and detailed Table 1 and 2  which are rather confusing
and do not add to the reader’s understanding. Consider deleting or communicating in a more
comprehensive way.
Specific comments
Page 3, line 72-73: Alle IBD therapies aim to improve intestinal barrier function which is usually
evident by histological remission. This is true about Prednisolon (PMID: 33575854), infliximab
(PMID: 22398062) as well as other biologics.
Page 6,  line 148:  Which markers were used to ensure that inflammation was stablished? How
fast can one expect the inflammation would take place after administration of INDO?
Pages 7-8, lines 170-177: Is the method validated? If so, please include a reference.
Page 10,  line 233:  How many rats were used in each arm? Please include a figure with
study design clearly showing each arm, number of rats included, duration of study and study
termination.
Page 10, line 234: Was a dose-dependency test run? Please include a p-value.
Page 10, line 242: Were there any side effects? Or did everything go as planned?
Page 11, line 263, tabel 1: should the unit not be % since it is relative to body weight?
Page 13, lines 300-3001: How can the authoers claim that glepaglutide induced trophicity
7 days after dosing ,all based on intestinal weight? No biopsies were taken and no
immunohistochemistry analyses were performed. Couldn’t it just be an increased intestinal
blood flow resulting in an increased intestinal weight?
Page 15, lines 335-338: GLP-2 is a potent intestinotrophic agent. Should we be concerned (more
than we already are in "healthy" intestine) about its usage in an inflamed environment with a
rapid cell turnover and possibility and risk for mutations and malignancy?
Page 15, lines 347-348: see comment on page 3. Prednisolone is a potent agent inducing mucosal
healing.