JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-023-02682-x (2023)

Title: Frequency, outcomes, and need for intervention in stricturing gastrointestinal
tuberculosis: A systematic review and meta-analysis
Version: 1 Date: 08 Aug 2022
Reviewer's report:
The search strategy, by specifying “AND” stricture OR fibrosis OR stenosis, will be biased
towards articles where strictures have been found and so “frequency” should not be included in
the title nor recorded as a result in the abstract and manuscript.  So, the study might be better
titled as “The effect of anti-tuberculosis (TB) treatment on the need for surgical intervention in
gastro-intestinal tuberculosis with strictures…”.
Such a study would then have to exclude those in whom surgery was undertaken immediately
and include only those who had surgery after completing a course of effective TB treatment.
Furthermore, the decision for endoscopic or surgical intervention may be limited by availability
of the two different procedures.  Each included paper should investigate whether the criteria for
each procedure, where both were available, are consistent among the different publications.
If the authors wished to estimate the frequency of stricture formation, then studies of
gastrointestinal TB not requiring surgical intervention might be helpful in providing a lower
limit to the frequency of stricture formation.
Currently, the conclusions are unsafe due to the heterogeneity of the papers and the inclusion
bias.
The inclusion criteria should consider how gastro-intestinal TB was diagnosed, whether by
a positive culture or PCR of gastro-intestinal tissue, concurrent cultures from pulmonary
specimens or merely by histological diagnosis (where Crohn’s disease might remain a possible
diagnosis) with or without concurrent radiological criteria.
As structuring is not an all-or-none phenomenon, especially with regard to symptoms of
diarrhoea or intestinal obstruction, the authors might usefully request individual patient data
from the included papers.  For instance, a >90% stricture might always require surgery, whereas
lesser degrees of stricture formation might be more amenable to treatment.  The authors have
also noted the importance of the site of stricture formation and the number of lesions.
As the authors note in the discussion, the degree of resolution of structuring may well depend
on duration of the disease process and time to diagnosis.  The individual patient data may shed
light on whether this hypothesis is correct.
The search strategy (supplementary Table 1) has been included.  The studies which were
excluded in Supplementary Table 2 includes the 34 papers after eligibility criteria were satisfied.
However, the other three supplementary tables were not available in the download available to
me.
The supplementary figures have not been included in the download available to me.
In view of the high heterogeneity, a random effects model was correctly used.  The limitations
of such a model in this context should be discussed.
Review for 10.1186/s12876-023-02682-x (2023)

Title: Frequency, outcomes, and need for intervention in stricturing gastrointestinal
tuberculosis: A systematic review and meta-analysis
Version: 2 Date: 05 Sep 2022
Reviewer's report:
The submission cannot meet the editorial requirements for publication as the systematic review
is complicated by inherent biases in the publications.  The conclusions are therefore both lacking
in scientific rigour and unsafe for medical practice.
Review for 10.1186/s12876-023-02682-x (2023)

Title: Frequency, outcomes, and need for intervention in stricturing gastrointestinal
tuberculosis: A systematic review and meta-analysis
Version: 2 Date: 09 Sep 2022
Reviewer's report:
Some suggestions on revision of reviewers have not been well answered, please search  more
literatures to improve,  further providing  better references for readers.
Review for 10.1186/s12876-023-02682-x (2023)

Title: Frequency, outcomes, and need for intervention in stricturing gastrointestinal
tuberculosis: A systematic review and meta-analysis
Version: 3 Date: 04 Dec 2022
Reviewer's report:
This paper has high heterogeneity (I2 statistic values above 80-90) and more bias (funnel plot).
This may be related to the difference in the quality of the included studies. The author also
included three Abstracts of articles. But the author made sensitivity analysis with six studies of
good quality.The results of  statistics were reliable.
Review for 10.1186/s12876-023-02681-y (2023)

Title: A descriptive study of abdominal complications in patients with mild COVID-19
presenting to the emergency department: a single-center experience in Japan during the omicron
variant phase
Version: 2 Date: 09 Dec 2022
Reviewer's report:
Compliments to the authors for the study results.
This is a retrospective study with a sufficient number of patients enrolled.
However, the most important problem is the diagnosis, in particular of intestinal hemorrhage,
obtained without an objective endoscopic finding.
It should be better clarified which radiological semiological elements were used to arrive at this
diagnosis and what sensitivity and specificity they have.
Review for 10.1186/s12876-023-02681-y (2023)

Title: A descriptive study of abdominal complications in patients with mild COVID-19
presenting to the emergency department: a single-center experience in Japan during the omicron
variant phase
Version: 2 Date: 02 Jan 2023
Reviewer's report:
Dear authors, congratulations on your paper
The manuscript needs revision in some sections:
The results part is very plain, the statistical analysis part can be mentioned furthermore as text
the tables and figures were ok
Review for 10.1186/s12876-023-02681-y (2023)

Title: A descriptive study of abdominal complications in patients with mild COVID-19
presenting to the emergency department: a single-center experience in Japan during the omicron
variant phase
Version: 3 Date: 22 Jan 2023
Reviewer's report:
I thank the authors for the additions that made the manuscript more complete and understandable.
Review for 10.1186/s12876-023-02681-y (2023)

Title: A descriptive study of abdominal complications in patients with mild COVID-19
presenting to the emergency department: a single-center experience in Japan during the omicron
variant phase
Version: 3 Date: 14 Feb 2023
Reviewer's report:
Dear authors, congratulations on your good paper.
The manuscript is good and several comments have raised by other reviewers and they were
addressed clearly. Now, the manuscript is looking better
Thank you for the opportunity to review this paper.
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 1 Date: 24 Nov 2021
Reviewer's report:
General comment
HCC represents one of the most frequent cancer-related death worldwide and, despite the
advances in HCC management, prognosis is still poor due to the diagnosis at advanced stage.
Sorafenib has dominated the field of systemic therapy for HCC for more than a decade  but,
since its approval, no markers predicting of response has bee identified. The paper by Yao et
al. evaluate the role of a family of sialic acid-recognition protein (Siglec) into predicting the
response to therapy. Despite this, there are several lines of information which are missing and
preclude to appropriately evaluate the manuscript.
Major issues
1) A role for siglec in predicting overall survival has been described for HBV-related HCC.
Additional clinical information about aetiology of liver disease, presence of cirrhosis, alpha-
fetoprotein values, tumor burden etc should be added in the text to confirm the role of Siglec
for HCC patients who are started of sorafenib.
2) Authors describe results of overall survival, RFS and PFS. First of all, a definition for all these
endpoint should be added in the statistical analysis paragraph. Moreover, if patients are started
on sorafenib they are not free from CC and recurrence free survival is not a good endpoint to
be evaluated.
3) Which role could SIglec play in predicting the response to new first lines of therapy
(atezolizumab+bevacizumab)?
Minor issues
1) All abbreviations used in the text should be explained as in table and figure legends
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 1 Date: 08 Dec 2021
Reviewer's report:
In the current manuscript Senbang Yao et al, evaluates the functional significance of SIGLECs
family in HCC . The study use TCGA and GEO database for data analysis and the scientific
message is interesting; however I would raise some concerns:
MAJOR CONCERNS:
1) The authors evaluate mRNA levels in HCC and normal patient of the different SIGLECs
family member, but the results are not so clear. The figures and the text do not specifically
define which member of SIGLECs is differentially expressed. This part of the study should be
improved.
2) The authors make a correlation between the different expression of SIGLECs family with
T cells and B cells infiltration levels in HCC. The paragraph seems to be completely separate
from the other part of the study. The authors should explain better the correlation in the text,
especially in the discussion paragraph.
3) The different expression of SIGLECs family members between differ grade and stage of
tumor is an important feature, but it is very difficult to demonstrate statistically significance of
SIGLECs and tumor grade/stage. Number of samples analyzed for the different groups should
be reported.
4) It is also difficult to accept the definition from the title in which is written “predictive role of
SIGLECs family in HCC patients undergoing sorafenib”. The authors analyze data from patient
with HCC and normal patients. How the authors evaluate the predictive role. This part should
be better explained.
5) Discussion paragraph should be improved.
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 1 Date: 15 Dec 2021
Reviewer's report:
The study is really complex and hard to read and this is mainly because the authors used data from
various electronic database and it is not always clear were analyzed data come from. Moreover
many abbreviations are not always spelled at their first appearance in the text.
It is not easy to understand how many patients and controls (or histological samples) have been
analyzed and if the various analyzes have been performed on the same patients or on different
patients from different databases.
Methods are not clear and difficult to follow.
A concise table reporting the number of enrolled patients for various analysis could help.
Regarding survival analysis more information regarding this analysis must be reported as mean
follow-up time, mean treatment duration. Moreover also other potential factors affecting survival
should be evaluated such as CHILD and MELD score or AGE.
There are various typographical and typos. English needs to be improved in addition to the
aforementioned need to make abbreviations explicit when they first appear in the text. Some
abbreviations are reported differently in the text (example both SIGLEC and Siglec are used
in the text)
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 4 Date: 17 Mar 2022
Reviewer's report:
The exposition of the data extraction, analysis and interpretation process remains complex,
difficult to understand and follow.
For the above reasons it is not always clear how analyzed data support authors' conclusions.
Some abbreviations are not explicit (for example GTEx in line 89).
English can be further improved.
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 4 Date: 21 Mar 2022
Reviewer's report:
In my opinion in their replies, the authors have satisfactorily addressed the issues raised by
myself and the other reviewers.
For this reason I am happy to recommend the manuscript for publication.
Review for 10.1186/s12876-023-02672-z (2023)

Title: A comprehensive computational analysis to explore the importance of SIGLECs in HCC
biology
Version: 7 Date: 05 Nov 2022
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
No - there are minor issues
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
No - there are major issues
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
No - there are minor issues
STATISTICS - Is the use of statistics in the manuscript appropriate?
No - there are issues with the statistics in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
No - there are major issues
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Maybe - with major revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: In the files that I received, I did not have a copy of the authors
responses to the issues raised. However, in the marked manuscript they have introduced a
number of changes as recommended but seem not to have edited anything down. I still have
reservations about the emphasis of the manuscript.
REQUESTED REVISIONS:
I really don't think the point of the manuscript is to highlight the use of SIGLECs expression as
a biomarker for sorafenib response. Especially when that observation is based on n=22 patients,
from what I can see in the supplementary data.
For me a better title to use is ""A comprehensive computational analysis to explore the
importance of SIGLECs in HCC biology and prognosis"" this is a sentence of the authors from
the introduction.
Abbreviation use and definition is better but please be consistent, so check your manuscript
again, including your legends and how you label any figures.
Thank you for Figure 1, it was helpful.
Remember part of revision is editing things down too.
Review for 10.1186/s12876-023-02668-9 (2023)

Title: Comparison of therapeutic efficacy and treatment costs of Self-Expandable Metal Stents
and Plastic Stents for Management of Malignant Biliary Obstruction
Version: 2 Date: 27 Sep 2022
Reviewer's report:
Thank you for this study on the cost-effectiveness of SEMS versus plastic stents for malignant
biliary obstruction. Unfortunately, I recommend rejection of this submission.
Ultimately, this study attempts to analyze effectiveness of PS vs SEMS but does not account
for indication of use in the efficacy analysis which make the results difficult to interpret
meaningfully, and separately analyzes cost where the three groups are better defined but cost per
month is an unclear outcome. This study does not assess cost-effectiveness – this is a different
concept than examined in this study. If there are patients who received plastic versus metal stents
for each of the 3 indications assessed, this efficacy and cost data could be used as parameter
estimates to create decision tree using a Markov model for a cost-effectiveness analysis.
Please cite data supporting the assertion that the use of plastic stents has not substantially
decreased despite recommendation for SEMS.
Stating that you are conducting a cost-effectiveness analysis implies that a decision tree analysis
to assess an outcome such as life-year gained or death prevented. Here, you simply examine
costs in a single center in a single country. Please explain further how this analysis
You state this was a retrospective study. Did all patients receive treatment following guidelines
only? Were patients who may not have received guidelines-directed therapy for whatever clinical
reason excluded? How can this be controlled for in retrospective inclusion criteria, or was there
a prospective enrollment with these criteria?
What were the dates of the study period?
The use of the word subgroup is confusing – there are 3 groups being compared, but no further
subgroups.
If the indications for plastic (potentially resectable) versus metal stents (potentially unresectable)
are different, how can their cost-effectiveness be compared?
Selectively only including the post-SEMS cost in the sSEMS group is misleading; why is the
initial SEMS cost not relevant?
Please comment on why survival rates
Why does the efficacy analysis not compare the 3 different groups as indicated in the methods for
primary outcomes? How do you account for multiple procedures required by individual patients?
Here, this analysis is flawed due to confounding by indication for type of stent placement.
Does literature support the use of average cost of treatment per month of survival as a way to
control for variable survival time? This seems to yet be another manifestation of confounding
by indication and it is unclear if this is an appropriate way to control for it.
Please comment on the generalizability of cost data to an international audience.
Review for 10.1186/s12876-023-02668-9 (2023)

Title: Comparison of therapeutic efficacy and treatment costs of Self-Expandable Metal Stents
and Plastic Stents for Management of Malignant Biliary Obstruction
Version: 3 Date: 03 Feb 2023
Reviewer's report:
The authors have addressed our concerns with thoughtful due diligence systematically. We have
no further concerns.
Review for 10.1186/s12876-023-02665-y (2023)

Title: Hepatitis C micro-elimination through the retrieval strategy of patients lost to follow-up
Version: 4 Date: 21 Dec 2022
Reviewer's report:
This is a retrospective one-center study reporting the HCV micro-elimination through the
retrieval strategy of patients. It is an interesting study; however, some points have to be clarified.
The authors stated in their conclusion that the call back system can expand our reach to those
unaware or ignoring chronic HCV infection patients and link them to treatment resulting in
improving the goal of HCV micro-elimination. However, most patients did not return for
retrieval, and a huge proportion of the patients were not reached, making the power of this study
weak.
Review for 10.1186/s12876-023-02665-y (2023)

Title: Hepatitis C micro-elimination through the retrieval strategy of patients lost to follow-up
Version: 4 Date: 12 Jan 2023
Reviewer's report:
The authors discussed an important topic regarding HCV elimination and the importance to have
a strong database to follow up patients and to recall them when necessary. I'd like to mention
some points that i hope to be clarified:
Materials and Methods:
-Kindly define: poor medical status
-You mention that each patient received one of the 4 DAAs (elbasvir/grazoprevir, sofosbuvir/
ledipasvir, glecaprevir/pibrentasvir, sofosbuvir/velpatasvir) therapy. Can you define the
selection criteria for each regimen or it was according to the availability?
Results:
-what was the main causes of refusal of therapy and from your point of view how could we
overcome this challenge?
Review for 10.1186/s12876-023-02669-8 (2023)

Title: Nomogram for predicting the overall survival of underweight patients with colorectal
cancer: A clinical study
Version: 1 Date: 26 Sep 2022
Reviewer:  Xiangpeng Zhan
Reviewer's report:
The author developed a nomogram for predicting OS in underweight patients with CRC and
validated its favorable performance. I have the following concerns to be addressed by the author.
1. The author's language needs to be improved. For example, the recurrence of line 57 is more
appropriate.
2. As the authors say, body mass index has strong and clear evidence for the prognosis of
colorectal cancer. However, in the discussion part, the author's discussion about weight on
prognosis of colorectal cancer seems to be too much redundant. At the same time, I don't seem
to see any discussion on the variables included in the prediction model.
3. I suggest that the author increase the method of model evaluation, such as DCA curve.
4. The model should be used in a simpler way, such as in the form of a web page
5. As the author said, the data obtained are from Korean people, so it may only be applicable to
Korean people. Does the author have data from other countries to verify the applicability of the
model externally. If not, I suggest adding this clause to the limitation
6. The variables included by the author lack more detailed patient information, such as
complications, which also have a great impact on the overall mortality. Therefore, I suggest that
we should re analyze the outcome event, which should be cancer specific death.
7. I don't see the advantages of the research done by the author.
8. 95% confidence interval of AUC in the result part should be added
Review for 10.1186/s12876-023-02669-8 (2023)

Title: Nomogram for predicting the overall survival of underweight patients with colorectal
cancer: A clinical study
Version: 1 Date: 01 Jan 2023
Reviewer:  Zhenhui Li
Reviewer's report:
The author used data from the national registry to investigate the prognosis of underweight
patients and developed a nomogram to predict overall survival (OS) in underweight patients,
which is an interesting study. I have some comments.
1. patients were randomly allocated to the training and validation sets, respectively, at an 8:2
ratio, why?
2. The research should report the calibration of nomogram.
3. The delong test should be used to compare the C-index between the nomogram and TNM
stage system.
4. Underweigh patients have poor prognosis, which is known to all. Hence, the first part of result
is unnecessary.
5. Some mistakes were found in the manuscript, for example “The OS of the underweight group
was significantly worse than that of the non-underweight group (5-year OS, 78.1% vs. 62.9.0%
vs. 78.1%, P<0.001; Figure 1).”
Review for 10.1186/s12876-023-02669-8 (2023)

Title: Nomogram for predicting the overall survival of underweight patients with colorectal
cancer: A clinical study
Version: 4 Date: 03 Feb 2023
Reviewer's report:
The manuscript writing is clearly written. Some expressions still need to be standardized. For
example, on page 2, line 31-44, the description of the statistical data should be consistent.
Sometimes it was described as “… vs. …”, but sometimes as “… versus …”.
Review for 10.1186/s12876-023-02662-1 (2023)

Title: Chronic atrophic gastritis in different ages in South China: a 10-year retrospective analysis
Version: 2 Date: 18 Dec 2022
Reviewer:  Tran Tien Dao
Reviewer's report:
COMMENT SHEET
Article name: Chronic atrophic gastritis in different ages in South China: a 10-year retrospective
analysis
I .  INFORMATION ABOUT REVIEWERS
Full name: Dao Tran Tien
Specialty: Gastroenterologist
Organize: Department of Gastroenterology and Hepatology, Tam Anh Hospital, Ha Noi, Viet
Nam
Email: tiendt1511@yahoo.com/ daotrantien1982@gmail.com
Orcid ID: 0000-0002-4787-6144
II. CRITICAL COMMENTARY
Atrophic chronic gastritis (ACG) is one of the common problems that is associated with the
risk of developing stomach cancer. Therefore, research to identify factors related to atrophic
chronic gastritis such as autoimmune diseases, and H. pylori infection, especially in Asians, has
scientific significance, topical help to predict and have prophylactic methods.
For the research method, the retrospective study had a very large sample size with 24,084 patients
with ACG. However, there is some information that the author should make clear. Firstly,
the author needs to make clear the criteria for the diagnosis of atrophic gastritis in research.
If the diagnosis is based on the OLGA staging system, you should describe the number of
biopsies you take. It is an important factor because it affects the accuracy as well as reliability
of the diagnosis of atrophy gastritis. Although ACG is considered a risk of gastric cancer,
many studies in Japan indicate severe ACG (OGLA grade III, IV) has a high risk of stomach
cancer. So, you need to give detail for this information. Secondly, for patients diagnosed with
autoimmune gastric mucosal atrophy due to pepsinogen reduction or positive intrinsic factor
antibody findings, positive parietal cell antibody findings should be analyzed. We found that
cutoff values of pepsinogen I reduction, or PGI/PGII ratio was different in other studies as well
as race or countries.  Japan takes PGI #70 ng/ml and PGI/PGII # 3 as criteria of ACG, but is
this value consistent with research in China? Thirdly, the criteria for diagnosing and excluding
H. pylori infection only by urease test are not accurate because the sensitivity and specificity
of this method is only about 60-70% and the accuracy of the method is greatly reduced if the
number of biopsy samples is not enough (e.g. 1 biopsy in antrum or body). In addition, urease
testing is also affected by factors such as using antibiotics and PPI drugs. Can the author rule
out these factors? Finally, if stomach cancer is seen in young people < 40 years of age, familial
factors should be evaluated, or it may be that disseminated stomach cancer is hereditary. These
patients need to investigate the factors involved in gene mutations
In conclusion, the research has a large sample size, so the result could influence the population,
however, the author should be made information in the article.
Review for 10.1186/s12876-022-02508-2 (2023)

Title: Tofacitinib as a maintenance therapy in patients with ulcerative colitis stratified by
OCTAVE Sustain baseline Mayo endoscopic subscore
Version: 2 Date: 15 May 2022
Reviewer's report:
This is a post-hoc analysis of the Octave trials with specific focus on the MES score and how
this relates to patient outcomes. The study is well-conducted and the statistical analyses appear
sound.
The authors have already acknowledged the major deficiencies in the study in the discussion,
and this includes the relatively small sample size which has somewhat limited the analysis
conclusions. Never-the-less the study presents an important finding with implications for
clinical practice. The study suggests that tofacitinib patients should be offered an 8 week
flexible sigmoidoscopy to guide ongoing treatment dose. This provides clinicians and patients
reassurance that  objective disease assessment (rather than relying in clinical reposes alone) is
appropriate before dropping to a 5mg BD dose. As such this study is a valuable contribution
to the field.
Review for 10.1186/s12876-022-02508-2 (2023)

Title: Tofacitinib as a maintenance therapy in patients with ulcerative colitis stratified by
OCTAVE Sustain baseline Mayo endoscopic subscore
Version: 2 Date: 14 Jul 2022
Reviewer's report:
Thanks for this interesting and relevant analysis with potential impact in the use of TOFA in
clinical practice.
My comments to the authors:
- The results are based on the baseline Mayo endoscopisc subscore 0 or 1. As they mention, there
is still no clear agreement in which specific cut-off should be use as remission, but actually,
regardless this fact, the truth is that there can be a bias in the interpretation of Mayo 0 and 1
because of subjective interpretation. Therefore it would be more interesting to base the results on
an histological score. Could the authors comment on this? is there any histological data available
in this sub-analysis?
- The authors focus the results in the baseline Mayo 0-1, but in real life have many patients a
clear clinical response (even remission ) and endoscopic response after induction but still some
activity, like erosions (so still "some" Mayo endoscopic score 2). It would be really interesting
in the clinical practice to know whether this justifies an intensification or extended induction of
TOFA 10mg. Is there any data around this sub-group  from the OCAVE program ?
- Rates of remission at w52 in patients with baseline Mayo 1 are higher in the group of TOFA
10mg than in the group of TOFA 5mg. Can the auhtors comment on this? Would this justify an
intensification of treatment in patients with Mayo 1 under 5mg?
- The AE ratio (p14): any clarification of why is clearly higher in the group of Mayo 1 baseline
from TOFA 5mg as compared to Mayo 1baseline from TOFA 10mg group? the authors justify
this because of higher inflammatory burden in the Mayo 1 group but this is still not explaining
why is higher in the TOFA 5mg. Could the authors comment on this?
- It would be interesting to have data on still longer term FU (at 2y)
- At long term we would also need data on de rate of patients that successfully de-escalate from
10mg to 5mg , depending on the baseline Mayo as well.
Review for 10.1186/s12876-023-02664-z (2023)

Title: Eradication therapy may decrease the risk of immune thrombocytopenia after
Helicobacter pylori infection: A retrospective cohort study in Taiwan
Version: 0 Date: 02 Dec 2022
Reviewer's report:
I have to express my appreciation for the idea which this paper based on
However I have some inquiries
1. The title for me not attractive I think you have to modulate it to be more short and attractive
2. You had a criteria for thrombocytopenia of less than 1000000 however we have a spectrum
of patients from 100 to 150 thousands which may be considered an evolving immune patients,
what about them in yours.
3. Presence a significant differences according to age and CCI  is a considerable weakness for
the results.
4. You stated that there is anemia in comorbidities but in the outcome you excluded any
erythrocytes disorders, explain please.
5. In the results where are results for plts nombers and at what point of time as from the study
design it is not clear the timeline for the patients followup.
6. Did you excluded the antiphospholipid antibodies?
7. In the discussion you tried to explain why females had a lower risk to develop
thrombocytopenia but it is still unclear.
Review for 10.1186/s12876-023-02664-z (2023)

Title: Eradication therapy may decrease the risk of immune thrombocytopenia after
Helicobacter pylori infection: A retrospective cohort study in Taiwan
Version: 0 Date: 11 Dec 2022
Reviewer's report:
In this study the authors retrospectively analyzed the medical records of 1995 adult HP patients
over a 3-year period. After adjusting for other risk factors, the risk of ITP was compared between
patients with HPE and those without HPE. This study showed that adult patients with HP
infection not receiving HPE had a higher risk of developing ITP. There are some additional
points that should be covered prior to publication.
Specific Points
1. More information on which method the authors have used to treat HP and diagnosis of ITP
should be included in the manuscript (specific guidelines, consensus, etc.)
2. Are there any test results for HP in patients after HPE? If HP does not turn negative after
treatment, how to explain the findings of this study?
3. H pylori is recognized as a secondary cause of ITP and the infection may be directly involved
in the pathogenic process. The mechanism may relate to cross-reactive antibodies against platelet
antigens by molecular mimicry. If possible, IgG data from patients with/without HPE who
diagnosed with ITP should be added and analyzed.
4. Please explain the significance of the CCI index analyzed in the results.
Review for 10.1186/s12876-023-02666-x (2023)

Title: hENT1’s role in adjuvant intra-arterial gemcitabine-based chemotherapy for resectable
pancreatic cancer patients
Version: 0 Date: 09 Dec 2022
Reviewer's report:
In the present study entitled “hENT1’s role in adjuvant intra-arterial gemcitabine-based
chemotherapy for resectable pancreatic cancer patients“, the authors have evaluated the clinical
significance of hENT1 as a prognostic predictor for pancreatic cancer patients. They concluded
that high expression of hENT1 is a positive prognostic factor for adjuvant intra-arterial
gemcitabine-based chemotherapy in resectable pancreatic cancer. The objective addressed here
is relevant and clinically important.
I have several comments for the authors:
1. All patients received gemcitabine for adjuvant chemotherapy, but the dosing regimens were
not consistent among individuals (Page 7). The authors should clarify the dosing regimens in
Table 1. If there were significant differences in the dosing regimens between the high and low
groups, it could be a major bias and contribute to survival.
2. In the multivariate analysis, the authors included some factors that were not significantly
related to survival. The insignificant factors in the univariate analysis should not be included in
the multivariate analysis, because they could lead to wrong results.
Review for 10.1186/s12876-023-02666-x (2023)

Title: hENT1’s role in adjuvant intra-arterial gemcitabine-based chemotherapy for resectable
pancreatic cancer patients
Version: 0 Date: 15 Jan 2023
Reviewer:  Satoshi Kobayashi
Reviewer's report:
The authors retrospectively evaluated the role of hENT1 expression on the efficacy of intra-
arterial infusion chemotherapy using Gem-based regimens. In their study, high expression of
hENT1 protein was associated with good prognosis. It may propose some clinical significance
to readers, and it was well-written in overall. However, there is still some issues to be clarified.
Major.
1. As the authors pointed out in the Introduction section, the role of hENT1 expression on
Gem-based systemic chemotherapy is still under debate because there have been contradict
reports. Therefore, I agree with the authors about the need for verification. However, I could not
understand why it was especially important in regional intra-arterial infusion of chemotherapy
(last 5-7 lines of the Introduction section), which was the core background of this study. Please
explain it carefully.
2. The treatment protocol was described in the Methods section: however, I think how long
they took to administer Gemcitabine was essential to evaluate the hENT1 role.  Based on
the pharmacokinetics, the efficacy and safety of Gemcitabine will change by the time of
administration, and slow administration of Gemcitabine may diminish the effect of hENT1.
Minor.
1. The authors excluded patients who had incomplete clinical data (line 8 of the Methods
section). It might make selection bias, especially when they excluded the patients who were lost
to follow up in earlier period (= they would have a poor prognosis). Therefore, it was better to
clarify the exclusion criteria more precisely.
2. The second paragraph of the Discussion section was just the repetition of the data in the
Introduction section, not discussion of their study results. It was preferable to "discuss" what
was same and different from previous reports as in the next paragraph. Otherwise, the second
paragraph will be shorten.
Review for 10.1186/s12876-022-02625-y (2023)

Title: The expression of SERPINE1 in colon cancer and its regulatory network and prognostic
value
Version: 2 Date: 03 Jun 2022
Reviewer:  Kaibo Guo
Reviewer's report:
Authors analyzed the biological function and regulatory network of SERPINE1, and explored
the biological significance of the ectopic expression of SERPINE1 in colon cancer. This study
might  have some clinical significance and innovation. However, these results were obtained
mainly from the databases and had not been verified in experiments.
Review for 10.1186/s12876-022-02625-y (2023)

Title: The expression of SERPINE1 in colon cancer and its regulatory network and prognostic
value
Version: 2 Date: 18 Jul 2022
Reviewer's report:
The manuscript  by Wang et al. aims to analyse gene expression and patient survival associated
with SERPINE1 expression in colorectal cancer, using different databases.
While the approach is good, there are several shortcomings in the manuscript.
1. In Fig 3A, B and D, the normal (control) samples (n=41) should also be stratified according
to patient's age, gender, race, and compare the COAD samples with the corresponding controls.
The statistical analysis of  the data in Fig 3 is not correct. Instead of t-tests, one-way ANOVA
(or the non-parametric equivalent) should be carried out.
2. In Fig 5B and C, it is not quite clear what the colour codes indicate. In the legend to Fig 6, it
should be clarified what the number of leading-edge genes refer to.
3. In Fig  7, clarification is needed  whether SERPINE1 is regulated by those kinases, miRNA
and transcription factors, or the other way around.
4. In general, the figure legends are very  simplistic,  lacking information of  how the analysis
was done and what the graphs actually show. The statistical analysis performed should also be
added to each figure legend.
5. The formatting of the figures is inconsistent, e.g. Fig 2A vs. B, and Fig 4A,B,C vs. D,E,F.
The formatting of the figures should be consistent throughout.
6. A more extended list of abbreviations is needed. The symbols for genes should be italicized.
7. The title of the manuscript should be amended to refer to the overall survival data (prognostic
value of SERPINE1) too. The manuscript would also benefit from better explanation of the
methods and the results.
Review for 10.1186/s12876-022-02625-y (2023)

Title: The expression of SERPINE1 in colon cancer and its regulatory network and prognostic
value
Version: 4 Date: 05 Nov 2022
Reviewer:  Kaibo Guo
Reviewer's report:
The authors have carefully revised the manuscript and I think it is suitable for publication in
BMC Gastroenterology.
Review for 10.1186/s12876-023-02667-w (2023)

Title: Impact of the Body Mass Index on the Retention of the Anorectal Mucosa after Double-
stapled Ileal Pouch-anal Anastomosis for Ulcerative Colitis
Version: 4 Date: 21 Jan 2023
Reviewer's report:
Major problems:
#1:  In this study, anastomosis was performed with a 31 mm circular stapler in all patients. Is it
possible to insert a 31mm circular stapler into the anus of Japanese patients?
#2:  In Table 1, the authors conclude that male-to-female ratio was not a factor related to length of
the retained mucosa. In general, the surgical procedure such as the rectum are easier for women
than men because the pelvis is wider. We would like to know why there was no relevance in
this study.
#3:  The authors should add their considerations about what measures can be taken to reduce
length of the retained anorectal mucosa in patients with high BMI.
Minor problems:
#1:  We can well understand the result of longer retained mucosa on the anterior wall than on
the posterior wall.
Please describe in detail the cases in which retained mucosa more than 5 cm.
#2:  Consider adding items for disease duration and total steroid dose in Table 1.
Review for 10.1186/s12876-023-02667-w (2023)

Title: Impact of the Body Mass Index on the Retention of the Anorectal Mucosa after Double-
stapled Ileal Pouch-anal Anastomosis for Ulcerative Colitis
Version: 4 Date: 26 Jan 2023
Reviewer's report:
Comments to the Author
It was a great pleasure to review your manuscript on Impact of the Body Mass Index on
the Retention of the Anorectal Mucosa after Double-stapled Ileal Pouch-anal Anastomosis for
Ulcerative Colitis.
The report has high clinical significance, as it showed that BMI was the factor most strongly
associated with the retention of a large amount of anorectal mucosa in IPAA.
Only minor comments in order to improve the paper.
1)The ECCO statement states that the maximum length of the anal mucosa from the dentate line
to the anastomosis should not exceed 20 mm. Please specify the reason that you defined having
a retained mucosal length of #30 mm in the anterior or posterior wall. Was it a quantile point?
Or did you quote from previous references?
In addition, since there were only 25 cases of high anastomosis defined as 30 mm or greater,
defining 20 mm or longer as high anastomosis and increasing the number of events may improve
the statistical reliability from the viewpoint of events per variable.
2) In the present results, the frequency of cuffitis was as low as 0.6% and there was no significant
difference between high and low anastomosis. However, a systematic review reported that
cuffitis occured in an estimated 10.2# to 30.1# of pouch patients, and possible risk factors
were rectal cuff length >20 mm, pouch-rectal anastomosis, stapled anastomosis, and J-pouch
configuration 1). I think that this is due to differences in the definition of cuffitis. But, if possible,
please follow the "International Ileal Pouch Consortium guidelines" for the definition 2).
1) Hembree AE, Scherl E. Diagnosis and Management of Cuffitis: A Systematic Review.
Dis Colon Rectum. 2022 Dec 1;65(S1):S85-S91. doi: 10.1097/DCR.0000000000002593. Epub
2022 Aug 25. PMID: 36399769.
2) Shen B, Kochhar GS, Kariv R, Liu X, Navaneethan U, Rubin DT, Cross RK, Sugita
A, D'Hoore A, Schairer J, Farraye FA, Kiran RP, Fleshner P, Rosh J, Shah SA, Chang S,
Scherl E, Pardi DS, Schwartz DA, Kotze PG, Bruining DH, Kane SV, Philpott J, Abraham
B, Segal J, Sedano R, Kayal M, Bentley-Hibbert S, Tarabar D, El-Hachem S, Sehgal P,
McCormick JT, Picoraro JA, Silverberg MS, Bernstein CN, Sandborn WJ, Vermeire S.
Diagnosis and classification of ileal pouch disorders: consensus guidelines from the International
Ileal Pouch Consortium. Lancet Gastroenterol Hepatol. 2021 Oct;6(10):826-849. doi: 10.1016/
S2468-1253(21)00101-1. Epub 2021 Aug 18. PMID: 34416186.
Review for 10.1186/s12876-023-02667-w (2023)

Title: Impact of the Body Mass Index on the Retention of the Anorectal Mucosa after Double-
stapled Ileal Pouch-anal Anastomosis for Ulcerative Colitis
Version: 5 Date: 05 Feb 2023
Reviewer's report:
I really appreciate you that you revised immediately with your kind comments.
The manuscript greatly improved and is definitely a valuable contribution.
Review for 10.1186/s12876-023-02667-w (2023)

Title: Impact of the Body Mass Index on the Retention of the Anorectal Mucosa after Double-
stapled Ileal Pouch-anal Anastomosis for Ulcerative Colitis
Version: 5 Date: 05 Feb 2023
Reviewer's report:
The authors have politely answered my question. The content was very convincing to me.
The authors also made additions and corrections to text and tables.
I consider this paper to be accepted.
Review for 10.1186/s12876-022-02629-8 (2023)

Title: Association Between Dietary Phosphorus Intake and Chronic Constipation in Adults:
Evidence from the National Health and Nutrition Examination Survey
Version: 4 Date: 09 Aug 2022
Reviewer's report:
This study examined the association between dietary phosphorus intake and chronic constipation
using NHANES data in the U.S. The relationship of micronutrient intake with intestinal health
has been reported continuously and this work will be of interest to the readers. However, there
are several issues to be improved.
1. Research implications of the study results and suggestions need to be stated more clearly.
There were two diagnostic criteria for chronic constipation used in this study, but evaluation
results of the two did not have the same findings in relation to phosphorus intake.
2. Participant Selection – the reasons for exclusion of participants with phosphorus intake greater
than 4000mg need to be addressed. This sentence seems confusing “… excluded 237 people
with dietary phosphorous deficiency…” Needs rewrite.
3. Did the authors perform an analysis of water and beverage intake? If not, explanations for
this need to be provided.
Review for 10.1186/s12876-022-02629-8 (2023)

Title: Association Between Dietary Phosphorus Intake and Chronic Constipation in Adults:
Evidence from the National Health and Nutrition Examination Survey
Version: 4 Date: 26 Aug 2022
Reviewer's report:
I think this is an interesting topic. However, the biologic plausibility is very weak. No possible
mechanism was discussed. The language is below the level for publication, for example “use
was defined as frequent”, “We set the continuous variables as categorical variables…”,
Specific comments:
1. The sentence is not clear for me, “Dummy variables were used to indicate missing covariate
values”
2. The sensitivity analysis was inconsistent with the main results, “Dietary phosphorus intake
was not associated with these three conditions.”
3. Discussion: More elaboration on the possible mechanisms are expected.
Review for 10.1186/s12876-022-02629-8 (2023)

Title: Association Between Dietary Phosphorus Intake and Chronic Constipation in Adults:
Evidence from the National Health and Nutrition Examination Survey
Version: 4 Date: 20 Sep 2022
Reviewer:  Ioanna Bakogianni
Reviewer's report:
Review
The topic of the paper is very interesting and relevant for the scientific community. It covers a
gap in literature as non many studies have explored the relationship, especially using so extensive
data.
Introduction
The introduction is clear and to the point, describing the importance of the topic as well as the
literature  and relevant scientific concerns.
Methods
The paper methodology is sound and very well described. Various potential confounders were
taken into consideration. The statistical analyses is appropriate and well described.
Results
The study results are clear and thoroughly described also using appropriate tables and figures.
Discussion
The discussion is very well structured and gives a good idea of the relation of the study results
with the existing literature on the topic. Potential limitations are also well described.
Review for 10.1186/s12876-023-02655-0 (2023)

Title: Prognostic significance of serum CA125 in the overall management for patients with
gastrointestinal stromal tumors
Version: 1 Date: 29 Sep 2022
Reviewer's report:
“Prognostic significance of serum CA125 in the overall management for patients with
gastrointestinal stromal tumors”
Interesting topic, research conducted on a large population of patients, the obtained results may
be helpful in clinical practice.
Before publication, it is required to complete:
Lack of a method for determination and a range of reference values of the CA 125 marker,
Explanations of the term "high serum CA 125,
Figures would be clearer after placing the location of the lesion,
In the tables,
I suggest removing the word "reference". After applying the proposed changes, I accept the work
for publication.
Review for 10.1186/s12876-023-02655-0 (2023)

Title: Prognostic significance of serum CA125 in the overall management for patients with
gastrointestinal stromal tumors
Version: 1 Date: 29 Sep 2022
Reviewer's report:
This is a nicely written retrospective study about the predictive value of CA125 in patients
with resected gastrointestinal stromal tumours. The authors found that post operative abnormal
CA125 levels in GIST are associated with poorer outcome and found this to be an independent
prognostic factor.
The rationale for specifically using CA125 as prognostic tumour marker is not completely clear.
Why not CA199 or CEA? The authors mention a 'few studies' that report the association between
CA125 levels and outcome in GIST patient, however there is no reference to this.
The major concern regarding this study is the very small patient numbers within the context of
the retrospective study design. Of the 406patient identified to have a surgical resection, only
46 patients were found to have a CA125 at baseline.  It implies a major selection bias, where
patients with large abdominal tumours with upfront unclear diagnosis were more likely to have
a CA125 at baseline and this would be likely high in these patients. Hence the association with
incomplete resection, rupture, large tumours, tumours with a high mitotic index etc.
What was the cut-off of CA125 values? What was the median and range in the population
described? Could the authors describe this for both the 'low' CA125 group and 'high' CA125
group?
In the design of the study it is not clear when the postoperative CA125 were obtained. If this
concerns a population identified over the course of 10 years, were these patients then asked to
repeat CA125 post hoc? And within this time, would patients have relapsed? At what time points
did the authors obtain a post operative CA125 and in how many patients was this performed
after they have relapsed?
And what proportion of patients was on a TKI at this point?