JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02607-0 (2022)

Title: Value of abdominal ultrasonography in predicting intestinal resection for premature
infants with necrotizing enterocolitis
Version: 2 Date: 12 Sep 2022
Reviewer's report:
The aim of this study was the assessment of abdominal ultrasound as diagnostic tool for Intestinal
resection in neonates with NEC. The study was performed in three centers. I think is very
important to highlight the role of abdominal ultrasound in NEC. I have some questions that
should be addressed:
1- What are the indications for surgery in these 3 centers? 68 out of 164 who underwent
laparotomy did not need a bowel resection. It feels like a high percentage as the author
commented as well. Why did they require surgery in the first place?
2- To performed diagnostic testing in a retrospective cohort is always risky, as the author
mentioned the risk of selection bias is high: for example the 83 + 26 patients that were not
included in the study ,were they different from the population studied in some way?
3- The indication for surgery can also induce a selection bias of course, maybe there are infants
who died before surgery because of bowel necrosis. It would be better to include all the infants
with verified NEC in the study.
4- In the method is stated: “The included AUS parameters and AR parameters exhibited
significant effects on predicting intestinal resection in the univariate analysis” . What do
“significant effects” mean exactly ? p value <0.05? I might be a sloppy reader but it is unclear
to me how the multivariate regression model is build.
5- There are no data regarding how sick the population studied was. Respiratory supports?
Inotropes?
6- In line 251 it is stated: “These findings should be signs of intestinal perforation, providing an
imaging reference for the selection of clinical treatment options, which was confirmed prior to
pneumoperitoneum, detected by abdominal X-ray examination.”  Which signs?  I suspect that
this line has been moved from another part of the discussion.
7. The references should be double checked. For example n 14 should be Fainglod´s study and
not Han SM, Knell J, Henry O, Riley H, Hong CR, Staffa SJ, Modi BP, Jaksic T. Long-term
outcomes of severe surgical necrotizing enterocolitis. J Pediatr Surg. 2020 May;55(5):848-851.
Review for 10.1186/s12876-022-02607-0 (2022)

Title: Value of abdominal ultrasonography in predicting intestinal resection for premature
infants with necrotizing enterocolitis
Version: 5 Date: 17 Nov 2022
Reviewer's report:
Minor comments:
Clarify lines 233-235 as it remains unclear what this sentence is referring to.
Lines 284-287: consider removing given that this information was stated earlier (lines 242-246).
Line 313: Clarify this sentence.  Perhaps - "AUS may be 'used'  in conjunction..."?
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 3 Date: 05 Mar 2022
Reviewer's report:
The manuscript “Serum soluble T-cell immunoglobulin mucin domain-3 as an early predictive
marker for severity of acute pancreatitis” by Wang et al. is well written and potentially
interesting, however there are several concerns.
Major
• The reviewer could not understand what was being compared in Table 1 and Table 2. What
do the P-values mean? Is SAP compared with MAP + MSAP? If so, a sentence “the length of
hospital stay was longer in patients with MSAP and SAP” on the 3rd-4th lines on page 6 dose
not make sense. Please specify.
• The reviewer could not understand a sentence “the concentration of IL-10 cytokine was not
different significantly among various group” on the 7th-8th lines on page 6 because the P-value
was 0.012 described in Table 2.
• According to Table 2, significant differences (p<0.001) were also shown in white blood cell
count, CRP, Creatinine, and IL-6 not only in sTIM3 and severity scores. Why were they omitted
from subsequent analysis?
• The reviewer could not understand model2 and model3 of multivariable linear regression
analysis. Why were heart rate, respiratory rate, and white blood cell count were adjusted? They
are the factors included in the APACHE II score.
• The reviewer thinks it is necessary to calculate the optimal cutoff value for sTim3 to diagnose
SAP. And the sensitivity and specificity of sTim3 to diagnose SAP should be compared with
those of other markers and severity scores.
Minor
• A sentence “AP or pregnancy induced by trauma” does not make sense on the 6th line on page 4.
• Please specify how many hours taken on admission on average after the onset of AP.
• Please specify when the vital signs listed in Table 1 were measured.
• It is not stated what * means in Figure 1.
• In Figure 1A, the vertical axis is not “SCORE”.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 3 Date: 30 Mar 2022
Reviewer's report:
The authors performed an analysis of sTIM-3 on the patients with acute pancreatitis. Some
comments about the study:
1. The title “Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive
Marker for Severity of Acute Pancreatitis” was supposed to investigate the effect of serum
soluble T-cell immunoglobulin (X or the independent variable) on the result of the severity of
acute pancreatitis (Y or the dependent variable). However, the model used the sTIM-3 as the Y
and AP severity as the X, and readers could not evaluate how sTIM-3 affects the AP severity in
the regression model. Therefore, the authors may consider regressing the sTIM-3 level (with a
cut-off) on the presence of SAP (binary outcome) in logistic regression.
2. To determine the performance of a biomarker, we usually need to know the area under the
curve (AUC) in the receiver operating curve (ROC) of the sTIM-3 for important outcomes (e.g.
SAP or 30-day mortality). For biomarkers to be helpful in a clinical scenario, we can determine a
cut-off on the ROC. Once we have the cut-off level, you can evaluate this biomarker’s sensitivity
and specificity. We can also put the biomarker as a binary covariate together with APACHE#or
other covariates in the regression model to predict SAP or mortality in logistic regression(1).
3. In the abstract on page 2, line 9, “After adjustments for potential mediators,…”. The term
“mediators” needs to be revised. In the regression model, we usually adjust confounders or
covariates. Adjustment of “mediators” should be cautious and usually are avoided because the
inappropriate adjustment could eliminate the actual effects of interested factors and result in
misinterpretation.
4. In the discussion section, the authors will be more persuasive to mention the most significant
finding of this study in the initial paragraph.
The major limitation of this study is the lack of detailed performance of the biomarker
and reasonable multivariate regression. The authors did however has a nice material for the
retrospective analysis. The manuscript can be re-evaluated if the above comments are addressed.
1. Li YM, Li Y, Yan L, et al. Assessment of serum Tim-3 and Gal-9 levels in predicting the risk
of infection after kidney transplantation. International Immunopharmacology 2019;75:105803.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 4 Date: 08 May 2022
Reviewer's report:
1. The authors need to mention the primary outcome and how long the outcomes are followed.
For example, the primary outcome is SAP and we followed every individual data until discharge
or up to 30 days. If the follow-up period is only 48 hours for outcomes, insufficient follow-up
time should be mentioned in the limitation.
2. On page 5, line 21, the statistical analyses: “ …the measurement data with skewed distribution
were expressed by M (Q1-Q3)”. So I guess it meant median. Please show the full term.
3. On page 6, line 4, the authors mentioned the usage of GLM with a logit link. However,
according to table 3, the authors used multivariate linear regression (not logistic regression).
In your methods, the dependent variable (response vector) is still a continuous variable (e.g.
APACHE II, sTIM-3). So it is not a logit link GLM (logistic regression) in which the dependent
variables are of the binomial distribution (e.g. 0 or 1, SAP or not). If you insisted to use the
APACHE II or the sTIM-3 as the dependent variable (the Y variable) in your regression model,
that is fine. Just need to be careful if you adjusted too many covariates in the model to end
in overfitting. In a cohort of up to 80 patients, eight covariates are the maximum number of
covariables to be appropriate. If the authors want to perform logistic regression on the outcomes
(SAP or not), please consult the statistician.
4. In Table 2, the mean and SD of the direct bilirubin were much higher than the total bilirubin.
Total bilirubin value equals direct plus indirct bilirubin. Logically, the mean + s(standard
deviation) of total bilirubin is higher than that of the direct bilirubin.
5. In the first paragraph of the discussion, “Additionally, compared with the BISAP, APACHE
II, and MCTSI score, the predictive value of sTim-3 did not weaker.” Suppose the authors
concluded that the sTim-3 was not inferior to APACHE II or MCTSI. Then, it will be perfect
for comparing the AUC of ROC between sTIM-3 and APACHE II or MCTSI in the statistical
test and show the P-value.
6. On page 13, lines 7-8, the author suggests a cut-off of APACHE II of more than 12 to
determine SAP. How did the authors acquire the cut-off value? By regression model or other
methods (e.g., Younden index on ROC)? The authors need to describe it in the statistical analyses
in the methods.
7. In the conclusion section, “In summary, the serum sTIM-3 was an objective, quantitative, and
more sensitive parameter…”. The author should be more specific to inform readers of the kind of
outcome (e.g., SAP or mortality or local complications?) sTIM-3 outperformed other measures.
8. Please also check some spelling and grammar details in this article. For example there was
“a” significant difference; in IL-6 cytokine level“s” between SAP and MSAP patients
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 5 Date: 20 Jun 2022
Reviewer's report:
Thank you for your modifications. Although there is a disagreement about the analysis method
still remained, I think it is OK because the ROC curve, sensitivity and specificity for the
prediction of severe AP have been added and well discussed.
Now there are a couple of minor revisions required.
• Please describe the clinical significance about the utility of serum sTim-3 as an indicator of
severity in the early phase of AP not only as an early predictor for SAP in discussion section.
• On line 8 of the discussion section, please delete ‘and more accurate’. The presented data did
not show that predictive value of serum sTim-3 was more accurate as compared with those of
BISAP, APACHE II, and MCTSI score.
• There are two different abbreviations for soluble T-Cell immunoglobulin mucin domain-3 in
the text, sTIM-3 and sTim-3.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 5 Date: 21 Jun 2022
Reviewer's report:
The authors did a nice revision for the retrospective analysis.
1. All the mentioned questions have been addressed.
2.  In Table 3, the title will be better to be revised as "Univariate and multivariable linear
regression analysis for the severity of pancreatitis".
3. In Table 4, the title will be better to be revised as "Diagnostic value for different scoring
systems versus sTim-3 in SAP".
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 8 Date: 11 Jul 2022
Reviewer's report:
Thank you for the modifications. The manuscript is now ready for publication in BMC
Gastroenterology.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 8 Date: 23 Jul 2022
Reviewer's report:
1. In table 4, the authors reported cut-offs of sTIM-3, BISAP, APACHE-II, MCTSI to predict
SAP. How did the authors acquire the cut-off values? By regression model or other methods
(e.g., Younden index on ROC)? The authors need to describe it in the statistical analyses in the
methods.
2. On page 14, lines 8-9, in “BISAP…, while meta-analysis display it has low sensitivity for the
prediction of AP”, did the authors mean to predict the SAP rather than AP? Prediction of AP is
not needed while only patients with AP were included.
3. The sentence on page 14, lines 13-15, the sentence “However, peri-pancreatic necrosis and
pseudocysts are not generally present in the early stage of AP, which may delay the early
diagnosis of AP by the MCTSI scoring system.” What does the word,  "which', mean? Did it
mean “early stage of AP”? The sentence should be rewritten. Did the authors mean that MCTSI
mainly consists of pancreatic necrosis and pseudocysts as scoring elements, underestimating the
severity of AP in the early stage of the disease?
4. On page 15, lines 19-23, “There are also several limitations… We attempted to minimize
these limitations by using strict inclusion and exclusion criteria.” The authors need to explain
why strict inclusion and exclusion criteria can compensate for the specific limitation of sample
size. Or just reallocate the strict inclusion criteria to a new paragraph to show the “strength”
of this study.
5. On page 15, lines 21-23, “In addition, … exclude confounding factors.” This is the strength
and did not complement any of the mentioned limitations. Please consider relocating this content
to a strength paragraph (e.g., This study has strength…).
6. In the conclusion section, “…, the serum sTIM-3 was an objective, reliable, convenient, and
more sensitive parameter, which had different levels among MAP, MSAP, and SAP patients.”
This study did not confirm the utility of sTIM-3 in other hospitals and other countries, thus
limiting its validity as a “reliable” biomarker. In addition, unless the sTIM-3 could be efficiently
and economically tested within 12 hours (e.g., CRP, procalcitonin) instead of an ELISA kit, the
word “convenient” may not be literally true for sTIM-3.
The word “comparable” is more suitable because this biomarker was comparable with CRP,
procalcitonin, and BISAP scores.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 10 Date: 12 Aug 2022
Reviewer's report:
There are several incomprehensible sentences due to changes not pointed out by the reviewer
before.
1) On page 1, lane 21: ‘Early prediction of acute pancreatitis (AP)’ does not make sense. Instead,
‘Early prediction of severe acute pancreatitis (SAP)’ makes sense.
2) On page 3, lane 11: ‘the early prediction for AP is important for severity assessments and
treatment decision’ does not make sense. Instead, ‘the early prediction for SAP is important for
treatment decision’ makes sense.
3) On page 3, lane 21: ‘serum sTIM-3 could represent an early indicator of AP’ does not make
sense. Instead, ‘serum sTIM-3 could represent an early indicator of the severity of AP’ makes
sense.
4) On page 4, lane 13: When did patients have the opportunity to refuse participation in this
retrospective study?
5) On page 15, lane 11-12: ‘Early detection of the tendency toward AP’ does not make sense.
Instead, ‘Early detection of the tendency toward SAP’ or ‘Early prediction of SAP’ may make
sense.
6) On page 15, lane 18-19: ‘The association between these indicators and the severity of AP is
controversial in previous reports.’ Reference papers should be added.
7) Retrospective nature should be listed as one of the limitations of this study.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 10 Date: 14 Aug 2022
Reviewer's report:
This article is revised and prepared for publication.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 11 Date: 25 Aug 2022
Reviewer's report:
Thank you for your corrections. The manuscript is now ready for publication.
Review for 10.1186/s12876-022-02537-x (2022)

Title: Serum Soluble T-Cell Immunoglobulin Mucin Domain-3 as an Early Predictive Marker
for Severity of Acute Pancreatitis This study was a retrospective analysis
Version: 11 Date: 07 Sep 2022
Reviewer's report:
This manuscript is well prepared for publication.
Review for 10.1186/s12876-022-02619-w (2022)

Title: Lower serum PRL is associated with the development of non-alcoholic fatty liver disease:
A Retrospective Cohort Study
Version: 1 Date: 22 Nov 2022
Reviewer's report:
Th Authors should discuss the importance of endotoxin and oxidant stress, previously shown
alterated in NAFLD. PRL levels should be correlated with markers of oxidant stress, such as
serum sp-NOX2 and urinary 8-iso- PGF2alpha.
Review for 10.1186/s12876-022-02619-w (2022)

Title: Lower serum PRL is associated with the development of non-alcoholic fatty liver disease:
A Retrospective Cohort Study
Version: 1 Date: 25 Nov 2022
Reviewer's report:
Authors correctly state that .... NAFLD comprises extensive histopathologic features ranging
from simple steatosis to steatohepatitis, as well as progressing to liver cirrhosis and
hepatocellular carcinoma eventually- And also, NAFLD significantly increases the risk of
metabolic diseases, including obesity, dyslipidemia and type 2 diabete...but they should add
that there are growing evidence of association between NAFLD and extra hepatic cancers,
such as bladder cancer, mostly frequent among old people, as evident in....Association of
NAFLD and Insulin Resistance with Non Metastatic Bladder Cancer Patients: A Cross-Sectional
Retrospective Study. J Clin Med. 2021 Jan 18;10(2):346. doi: 10.3390/jcm10020346. PMID:
33477579; PMCID: PMC7831331.
Authors should present data and an appropriate figure concerning  a linear regression between
WC and PRL concentrations and  another model of logistic regression adjusted for WC.
Finally, they ought to discuss  at large this aspect.
Review for 10.1186/s12876-022-02619-w (2022)

Title: Lower serum PRL is associated with the development of non-alcoholic fatty liver disease:
A Retrospective Cohort Study
Version: 3 Date: 13 Dec 2022
Reviewer's report:
The paper was sensibly improved. The Authors answered correctly to all my queries. In my
opinion, the paper is now suitable for publication in its present form.
Review for 10.1186/s12876-022-02615-0 (2022)

Title: Elevated fasting glucose level increases the risk of fatty liver disease: A 10-year study
of 31,154 individuals
Version: 1 Date: 23 Aug 2022
Reviewer's report:
This is a retrospective observational  study aimed to analyze the relationship of elevated fasting
glucose level with FLD.  31,154 patients were  enrolled in the study who were evaluated in the
hospital over a 10 year period.
The study is well designed and evaluates multiple risk factors associated with FLD. However I
will recommend some revisions before acceptance.
1. Introduction mentions that ' This study aimed to analyze the median time-to-onset, cumulative
prevalence and influencing factors for the occurrence of FLD in medical examiners.'  Please
elaborate and answer these questions in the conclusion section
2. Introduction mentions that 'This study aimed to analyze the median time-to-onset, cumulative
prevalence and influencing factors for the occurrence of FLD in medical examiners. ' I think you
meant to say examinees (not examiners). Please edit that
3. Another limitation worth discussing is the confounding factors associated with high FBG
and incidence of FLD. Patients with metabolic syndrome, obesity are at higher risk of both pre-
diabetes, diabetes and FLD.
4. In the results section you have mentioned the median time to onset of FLD was 5.2 years. Is
the 5.2 years after the first diagnosis of elevated FBG ? can you please elaborate.
Similarly when you mention the 1, 3, 5, 7 year prevalence rates, is that the time period from
the first diagnosis of FBG ?
5. Exclusion criteria does not include patients with pre-diabetes and diabetes. These patients are
already at a higher risk of FLD and will alter the results of the study.  It  is a major limitation
of the study and should be mentioned
Review for 10.1186/s12876-022-02615-0 (2022)

Title: Elevated fasting glucose level increases the risk of fatty liver disease: A 10-year study
of 31,154 individuals
Version: 1 Date: 19 Oct 2022
Reviewer's report:
Deng et al conducted a retrospective study to investigate the median time-to-onset, cumulative
prevalence, and the contributing factors for FLD development in patients who underwent routine
screening and evaluation at a large public hospital in China. This is an interesting study but with
the following issues that I included in my comments below:
Major points:
1. In Section 2.2, the authors need to provide an explanation as to how they decided on the
variables to control for. Is it based on prior literature results, biological plausibility, statistical
testing etc?
2. The authors compared several baseline characteristics between the elevated and normal FBG
group, did the authors investigate any other baseline variables? What about comorbidities,
history of alcohol use etc? Variables such as these could certainly confound the results if they
are not accounted for in the model.
3. Could the authors comment on whether they excluded patients with a history of alcohol use?
This needs to be clearly stated or explained.
4. Do the patients in the elevated FBG group have a diagnosis of diabetes mellitus prior to the
routine screening/evaluation? Were they on any anti-hyperglycemic medications?
Minor points:
5. Please make sure that the supplementary material is translated into English.
6. Extensive English language editing is needed to improve readability of the manuscript.
7. The phrase “physical examination” was used throughout the manuscript and is confusing. It
should be changed to “routine screening and evaluation”, which is what I believe the authors
meant.
8. The authors should discuss the limitations in second to last paragraph and state their
conclusions in the final paragraph of the manuscript.
Review for 10.1186/s12876-022-02615-0 (2022)

Title: Elevated fasting glucose level increases the risk of fatty liver disease: A 10-year study
of 31,154 individuals
Version: 5 Date: 11 Nov 2022
Reviewer's report:
The authors have revised their manuscript and responded to my comments.  The supplemental
data has been translated to English. However, I found some of their responses to be inadequate.
1. The authors still did not adequately answer my question about how they selected the variables
to control for. What do the authors mean by "factors most associated with occurrence of FLD"?
This statement is extremely vague.  If this was based on prior literature/knowledge, please
provide citations. This needs to be clearly stated in the methods section.
2. I understand that having a large sample makes data collection difficult, but it should not be an
excuse for not having data such as comorbidities. Please avoid stating "Due to the large sample
size" in the paragraph on limitations.  Please simply state that you don't have these data.
Review for 10.1186/s12876-022-02600-7 (2022)

Title: Impact of atherosclerosis on the postoperative complications of colorectal surgery in older
patients with colorectal cancer
Version: 1 Date: 26 Sep 2022
Reviewer's report:
Short summary: This is an interesting single-center study where the authors investigate whether
atherosclerosis is associated with postoperative complications of Clavien-Dindo complication
grade 3 or higher.
Major comments:
- It is mentioned several times that CAVI and AAC are 'independent' risk factors for
postoperative complications. In statistics, an independent risk factor should be part of a model
with established risk factors, however you performed only univariate logistic regression on few
parameters. In order to confirm CAVI and AAC as an independent risk factor, a multivariate
model including the risk factors you describe in the discussion (line 188-190, of which many
could be confounders as i.e. smoking, sex and diabetes are associated with athersclerosis) would
need to be part of the model. A model including these, as well as ASA score, hyperlipidemia,
hypertension, ischemic heart disease etc would be very interesting, to see whether CAVI and
AAC would still hold up as independent risk factors.
Otherwise, you might want to amend your description of an 'independent risk factor'.
- The authors conclude (line 253-256) that preoperative atherosclerosis evaluation could help
surgeons perform surgery safely and appropriately tailor postoperative management. While this
may be true, there is nothing in the discussion where it is mentioned how measuring CAVI and
AAC might influence changes in treatment. The atherosclerosis itself is not treatable anymore.
Would you suggest all patients with results over the ROC-cutoff get a stoma? Should they not
undergo surgery? I would reccommend adding to the discussion what the clinical implication
is of doing these measurements.
Minor comments:
- A mean postoperative stay of 16 days +/- 23 days seems very long for colorectal surgery,
especially if this is only elective surgeries. Please discuss this.
- Line 198 - you write that postoperative complications might be caused by atherosclerosis. As
this is an observational study, you might refrain from inferring causation and rather talk about
an 'association' between atherosclerosis and postoperative complications.
Review for 10.1186/s12876-022-02600-7 (2022)

Title: Impact of atherosclerosis on the postoperative complications of colorectal surgery in older
patients with colorectal cancer
Version: 1 Date: 16 Oct 2022
Reviewer's report:
Authors showed the impact of artherosclerosis of the elderly on the postoperative complications
of colorectal surgery by evaluating two biomarkers, CAVI and AAC score. The aim and
conclusions are clear and informative but  the manuscript itself has several major points to be
revised.
1. Some data are statistically incorrect. "Univariate analysis" in Table 2 seems like a result of chi-
square's test. I think these data should be shown as an independent table. In addition, regarding
"logistic regression" in Table 2, is this analysis performed as univariate analysis or multivariate
analysis? Even if there are factors that did not show significance, odds ratio and 95% CI should
be shown.
2. Although the authors are discussing about the types of complications ( Line236-), predicted
underlying mechanism is still unclear. There are some description regarding paralytic ileus, but
how about the infectious complications? Is there any evidence from the aspect of immune system
regarding  artherosclerosis? The sentence from Line242, "...indicating that our result was not a
coincidence", is unclear. Authors  should clarify what you are trying to explain scientifically.
3. Were there any patients who created diverting stoma in anterior resection to avoid anastomotic
leakage? Do you think we should use CAVI/AAC for the decision of creating diverting stoma?
4. Related to the previous comment, authors should discuss about how we can utilize CAVI/
AAC into clinics. What kind of behavior change is expected by measuring these?
Review for 10.1186/s12876-022-02579-1 (2022)

Title: Clustering of pediatric onset inflammatory bowel disease in Finland: A nationwide
register-based study
Version: 2 Date: 16 Jun 2022
Reviewer's report:
Innovative study.
1. how do you explain that FEWER residences are linked to case status?
2. in the abstract and the text, please note that one potential explanation for clustering is that
IBD-interested physicians/IBD-clinics often have a certain catchment area and the risk of being
diagnosed is increased in such areas.
Review for 10.1186/s12876-022-02579-1 (2022)

Title: Clustering of pediatric onset inflammatory bowel disease in Finland: A nationwide
register-based study
Version: 2 Date: 25 Sep 2022
Reviewer:  Mikkel Malham
Reviewer's report:
First of all, thank you to the editors and authors for letting me review this well written paper
elaborating on the increasing incidence of pIBD – more specifically looking at the time and
space clustering. I only have minor comments and no major concerns. However, because I have
not previously worked with the specific statistical tests used, I think this paper should also be
reviewed by someone who has.
In general there are only few language problems, however, the authors should be consisten on
how they punctuate (UK or US and 1000 or 1,000).
Abstract:
- L29P2: “Pediatric inflammatory bowel disease” should be “Pediatric onset inflammatory bowel
disease” as written in the abbreviations section.
- L31P2: Sentence starting with “we evaluated (…)” consider adding “and place of residence
at time of PIBD onset (or diagnosis?)”
- L36P2: I find the sentence starting with “the date of the diagnosis (…)” difficult to understand.
- L37P2: What is a diagnosis address? The subjects address at the time of diagnosis?
Background:
- L70P3: What about the other Nordic countries? The same increasing tendency offers support
for your hypothesis. Consider adding more recent references – maybe “The incidence and
prevalence of paediatric- and adult-onset inflammatory bowel disease in Denmark during a 37-
year period - a nationwide cohort study (1980-2017)” (DOI: 10.1093/ecco-jcc/jjac138).
- L72-3P3: “(…)north than in the south has been reported”. North or south of what? Finland?
Methods:
The good coverage of the Finish SII is well known and well described in the paper. I lack more
knowledge on how the addresses were found and how the coordinates were derived and lastly
how these were translated into distances and compared between cases and controls. In short, I
find it a little difficult to understand the study methodology.
- L91P4The authors state that IBD subtypes are known from 2000 and forth. How was the cases
from 1992-2000 phenotyped?
- L95P4: I would suggest rephrasing the sentence ending with “(…) controls selected for the
case” to “date for the matched controls.”.
- L101P4: I think sex was forgotten in the matching criteria.
- P114P5: I am a little unsure of what the months 2,4,6,12 are a measure of. Time intervals?
Discussion
Generally, I would appreciate a more detailed description of what the study actually found and
why this is important.
- Why does the authors think that only UC should a clustering tendency?
- Can the authors look further into the UC cases where clustering was found – urban or rural
areas?
- Does the authors think the section starting at line 193 is important?
Review for 10.1186/s12876-022-02579-1 (2022)

Title: Clustering of pediatric onset inflammatory bowel disease in Finland: A nationwide
register-based study
Version: 5 Date: 13 Nov 2022
Reviewer:  Mikkel Malham
Reviewer's report:
Thank you for the comprehensive reply to my previous concerns on your otherwise very
interesting study.  Because I also find the results quite intriguing I still lack some deeper
discussion on these results. For instance,  why is the clustering found only in UC?  However,
I do find the paper ready for publication, and I will leave this consideration for the authors.
Congratulations on a well written and interesting paper.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 0 Date: 13 Jul 2021
Reviewer's report:
This manuscript is not solid, and its real outcome is unclear. Some important works are missing
in survey and comparisons. This hinders the quality of this work. For examples, the following
literature is not presented in this manuscript.
Urban, G., Tripathi, P., Alkayali, T., Mittal, M., Jalali, F., Karnes, W., Baldi, P.,: ’Deep Learning
Localizes and
Identifies Polyps in Real Time With 96% Accuracy in Screening Colonoscopy’,
Gastroenterology, 2018, 155(4),
pp. 1069-1078.e8
Misawa M, Kudo S-E, Mori Y, Hotta K, Ohtsuka K, Matsuda T, Saito S, Kudo T, BaBa
T, Ishida F, Itoh H, Oda M, Mori K, Development of a computer-aided detection system
for colonoscopy and a publicly accessible large colonoscopy video database (with video).
Gastrointestinal Endoscopy, first online 2020.
Furthermore, the authors misunderstood the existing work and used it for meta-analysis. The
following works is not the work of polyp detection, the work dedicated for pathological category
decision for the detected polyps. This implies that the authors do not fully read and understand
the papers that they cited.
30. Mori Y, Kudo SE, Misawa M, Saito Y, Ikematsu H, Hotta K, Ohtsuka K, Urushibara
F, Kataoka S, Ogawa Y et al: Real-Time Use of Artificial Intelligence in Identification of
Diminutive Polyps During Colonoscopy: A Prospective Study. Annals of internal medicine
2018, 169(6):357-366.
Moreover, the descriptions and explanations of Figure 3 is limited. What authors to claim is
unclear. Criteria of quality assessment presented in Figure 2 also looks subjective, even though
they used QUADAS-2. The detail descriptions and explanation should be presented.
Thus, unfortunately, I conclude that this manuscript is premature for the journal publication.
Minors:
Figures 2 is a low resolution image.
Figures 3 G,H, I have too small label fonts.
In Figure 2, there is no citation number of papers.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 1 Date: 19 May 2022
Reviewer's report:
General remarks
In this revised version of the manuscript the authors addressed most reviewer questions
satisfactorily. They did a good job with reporting the exclusion and inclusion criteria of
the different studies they analyzed in Table 2 and with reporting machine learning model
performance found in these studies in Table 3. When carefully reading the manuscript, the reader
is now able to extract key information about the different studies from these two tables.
However, some points have not been addressed and need to be clarified.
The major limitation of this manuscript, the fact that only 1 out of 16 studies has external
validation, remains. While the limitation is now mentioned by the authors upon request, the
claims made by the authors have not been adjusted. In particular, the conclusion “AI […] is
expected to improve the performance of young doctors” is not backed up by results.
In summary, the authors did a good job in summarizing 16 machine learning studies, but the
conclusion they draw at the end, which is that AI is expected to improve radiologists, is not
backed up by the results.
Remaining issues
Reporting AUC numbers without additional context has no value. Again, AUC is an abbreviation
for area under the curve. Please report which curve you are talking about. The authors failed to
address this issue in the revision.
One out of 16 studies (1/16 (6 %)) are not “a few” studies, it is just “one”. Using the term “a few”
is misleading. Also, the number of studies which include an external validation cohort is not a
conclusion, it should be reported in the results. The impact which the lack of external validation
has on the conclusions should be discussed in the discussion and mentioned in the conclusion.
Who expects AI to improve performance of radiologists? In the abstract the authors make it
sound like it this is the general opinion of the scientific community. However, in the discussion
the statement is much weaker and phrased as “we speculate” that AI improves the performance
of radiologists. This is misleading the audience and the authors have failed to address this issue
in the revision.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 2 Date: 20 Jun 2022
Reviewer's report:
Some of authors’ feedbacks are off the point.
Modified Tables summarise the details of settings in existing works. However, I couldn’t
confirm valid modification in Figures 3A-F and 4A-C.
Differentiation of detection and classification in Figures are necessary for easy interpretation of
readers. For example, presenting different colour of circles (or different markers) for detection
and classification, respectively, might be effective. Even though the table summarise the details,
it is still hard to understand the full contents from only Figures. Furthermore, in Figure 4A,
which circle express which work? Moreover, what the sizes of circles express in Figures is still
unclear. In Figs 4A-C, how to plot curves from given points as circles. In Figs. 4A-C, the size
of characters is too small. In Fig. 3A, Reference [17] contains an unnecessary space in bracket.
Presentations of the manuscript should be refined for the journal publication.
In Conclusion, the authors describe ‘The lack of external validation may lead to overly optimistic
evaluation of model performance. It is necessary to develop new reporting standards for deep
learning to better evaluate model generalization.’ This is common sense in the field of pattern
recognition and machine learning, and not a new outcome. Furthermore, recent works in polyp
detection (even in a medical journal) reported public datasets for external evaluation. Moreover,
how did the authors introduce Conclusion from their analysis is unclear. Please present clear
logical flow and describe the real outcome of this work.
Please present the definition of ‘external validation’. The current descriptions are unclear.
The authors need English grammatical check over whole the manuscript. There are several
ambiguous and wired sentences.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 2 Date: 01 Jul 2022
Reviewer's report:
In this second revised version of the manuscript the authors addressed the reviewer questions
satisfactorily.
The major methodological limitation of the study, the fact that only 1 out of 16 analyzed
studies is validated externally, is now addressed properly. This limitation significantly lowers
the relevance of the manuscript. Nevertheless, the analysis is now reported in a way that is
accessible for the audience and the study may be of interest to some readers. Also, the weakened
claims now reflect the weaknesses of the individual studies that are part of this meta-analysis.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 5 Date: 04 Sep 2022
Reviewer's report:
1. The author refined the Figures I commented. However, I found miss plotting with incorrect
colour. For example, in Figs.3A, 3B, and 4A, [41] is plotted with red colour, but this work tackles
polyp classification. Please carefully recheck the references and modify the plotting colours.
2. I think the revised conclusions is still out of focus. The authors wrote “Further external
validation of AI and new reporting standards for deep learning is needed.” However, in the field
of Engineering such that Pattern Recognition, Machine Learning, Medical Imaging and Medical
Image Analysis, the external evaluation and reporting style for machine-learning methods
including deep learning have already existed as I commented in the previous round. In other
words, ‘reporting standards for deep learning’ have already exist. I think it means ‘reporting
standards for deep-learning application to the colonoscopy’. Furthermore,  what should be
reported in a new reporting style? Please make this point clear.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 6 Date: 18 Oct 2022
Reviewer's report:
All reviewer questions were already answered satisfactorily in the last revised version of the
manuscript.
The major methodological limitation of the study, the fact that only 1 out of 16 analyzed
studies is validated externally, is now addressed properly. This limitation significantly lowers
the relevance of the manuscript. Nevertheless, the analysis is now reported in a way that is
accessible for the audience and the study may be of interest to some readers. Also, the weakened
claims now reflect the weaknesses of the individual studies that are part of this meta-analysis.
Review for 10.1186/s12876-022-02605-2 (2022)

Title: Performance and comparison of artificial intelligence and human experts in the detection
and classification of colonic polyps
Version: 6 Date: 27 Oct 2022
Reviewer's report:
The authors refined Figures 3 and 4, and their captions. These make sense now.
However, the conclusions are still insufficient for the journal publication with the following
reasons.
1. Conclusions is too short.
2. What the authors tackle and what they clarified in this manuscript should be summarised.
3. The authors wrote “We find that AI has a high sensitivity and moderate specificity for polyp
detection and classification, which is similar to that of human experts, and can be used as an
assistant tool,” but this is not coincident to the results shown by Figures and incorrect claim.
3-1. In the refined Figures 4a and 4b, many of blue circles express acceptable middle-accuracy
specificities and inacceptable low-accuracy sensitivities for the detection task.
3-2. The authors should conclude this manuscript by showing their insights obtained from the
results of their survey and comparisons. For example, what is the difference between polyp
classification and polyp detection task in colonoscopy? How difficult these tasks are or how
difficult the construction of AI model of these tasks are? Actually, these tasks result in different
distributions in Figures 4a and 4b.
Review for 10.1186/s12876-022-02551-z (2022)

Title: Diagnostic performance and transportability of fecal Helicobacter pylori antigen test in
Uganda
Version: 1 Date: 16 Sep 2022
Reviewer's report:
It is a region specific study.
The following suggestions are mentioned for improving the manuscript:
1. The language and grammar requires correction at places throughout the manuscript
2. The results and the discussion lacks impact , they need to be conveyed in a more robust
manner . Comparison of similar data  should be done  in the discussion
3. The following references maybe added and discussed:
a.   Segamwenge IL, Kagimu M, Ocama P, Opio K. The utility of the Helicobacter pylori stool
antigen test in managing dyspepsia: an experience from a low resource setting. Afr Health Sci.
2014 Dec;14(4):829-34. doi: 10.4314/ahs.v14i4.9. PMID: 25834490; PMCID: PMC4370061.
b. Safarnezhad Tameshkel F, Karbalaie Niya MH, Kheyri Z, Azizi D, Roozafzai F, Khorrami S.
The Evaluation of Diagnostic and Predictive Values of Helicobacter pylori Stool Antigen Test
in Iranian Patients with Dyspepsia. Iran J Pathol. 2018 Winter;13(1):38-44. PMID: 29731794;
PMCID: PMC5929387.
c. Erzin Y, Altun S, Dobrucali A, Aslan M, Erdamar S, Dirican A, Kocazeybek B.
Comparison of two different stool antigen tests for the primary diagnosis of Helicobacter pylori
infection in turkish patients with dyspepsia. Helicobacter. 2004 Dec;9(6):657-62. doi: 10.1111/
j.1083-4389.2004.00280.x. PMID: 15610080.
d. Sharbatdaran M, Kashifard M, Shefaee S, Siadati S, Jahed B, Asgari S. Comparison of
stool antigen test with gastric biopsy for the detection of Helicobacter Pylori infection. Pak
J Med Sci. 2013 Jan;29(1):68-71. doi: 10.12669/pjms.291.2865. PMID: 24353510; PMCID:
PMC3809175.
Review for 10.1186/s12876-022-02551-z (2022)

Title: Diagnostic performance and transportability of fecal Helicobacter pylori antigen test in
Uganda
Version: 1 Date: 27 Sep 2022
Reviewer:  Seiji Shiota
Reviewer's report:
The authors examined the diagnostic performance of a qualitative stool antigen test (SAT) in
individuals with dyspepsia in rural Uganda. They found that the SAT is a robust diagnostic test
to improve the diagnosis of H. pylori infection in people with dyspepsia. However, there are
several concerns in this study.
Major points
1. In this study, the authors used fifty-nine tested positive for the stool antigen test. The number
of subjects is small to conclude.
2. In this study, PCR method using biopsy specimen from gastric spot was used as gold standard.
However, H. pylori can be negative in the severe atrophy. Therefore, other test such as urea
breath test (UBT) is necessary to conclude.
3. Overall, the findings in this study are not enough for the level of this journal.
Minor comments
1. This manuscript needs native English editing.
Review for 10.1186/s12876-022-02569-3 (2022)

Title: Sex-dependent associations between MAP3K1 gene polymorphisms and soy products
with the gastric cancer risk in Korea: A case-control study
Version: 1 Date: 06 Jul 2022
Reviewer's report:
This paper presents the influence of hormone-dependent effects and the interaction of genetic
factors on the incidence of gastric cancer. It’s a topic of interest to the researchers in the related
areas but the following suggestion can be taken into consideration when revising the paper:
1. In the part1 of the results, whether the intake of soy products in the case group and the control
group of different genders can be considered in the analysis of participant characteristics, and
whether there is statistical difference between the two groups of different genders.
2. Helicobacter pylori infection has been reported in many literatures is a risk factor for gastric
cancer, and in the part1 of results shown in the case group the infection of the Helicobacter pylori
is lower than the control group, and the difference was statistically significant, this contrary to
common sense can discuss appropriately. In addition, in the part2 results shown that overweight
and obesity are protective factors for GC. Is there any similar literature in the past to support
this result?
3. Some terms are not accurate enough, for example, we cannot judge the incidence of diseases
by the OR value.
Review for 10.1186/s12876-022-02569-3 (2022)

Title: Sex-dependent associations between MAP3K1 gene polymorphisms and soy products
with the gastric cancer risk in Korea: A case-control study
Version: 1 Date: 06 Jul 2022
Reviewer's report:
Thank you for the opportunity to review a manuscript entitled “Sex-dependent associations
between MAP3K1 gene polymorphisms and soy products with the incidence of gastric cancer in
Korea: A case-control study” by Jung Hyun Kwak and his colleagues in BMC Gastroenterology.
In this paper, the authors investigated the association between MAP3K1 gene polymorphisms
and GC incidence by sex and whether these associations differ depending on soy product intake.
They made a conclusion that men with the risk allele of MAP3K1 had a significantly increased
risk of GC incidence compared to GG homozygotes and this trend was more pronounced in
those with low intake of soy products. However, the authors collected the participants between
December 2002 and September 2006, almost two decades ago. The behavior and eating habits
have changed dramatically during 20 years worldwide, including Korea undoubtedly. So the
significance of this study has been greatly weakened due to the backwardness of samples.