JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-14-10 (2014)

Reviewer's report
Title:Concurrent Autoimmune Pancreatitis and Primary Biliary Cirrhosis: a Rare
Case Report and Review of the Literature
Version: 1Date:8 October 2013
Reviewer: Sudeep Khanna
Reviewer's report:
The language needs to be revised a little.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-14-10 (2014)

Reviewer's report
Title:Concurrent Autoimmune Pancreatitis and Primary Biliary Cirrhosis: a Rare
Case Report and Review of the Literature
Version:1Date:18 October 2013
Reviewer: Hideaki Miura
Reviewer's report:
Major compulsory revisions
1. An initial predominant clinical feature in the present case was obstructive
jaundice caused by the enlargement of pancreas due to AIP. Why did the
authors administer UDCA? UDCA has choleretic action and is usually thought to
be contraindication in case of biliary obstruction with hyperbilirubinemia. Did
administration of UDCA start after nasobiliary drainage?
2. As the authors demonstrated, the diagnosis of AIP is undoubtedly right with
reference to diagnostic criteria. However, diagnosis of PBC was made only by
the fact that the patient was serologically positive for AMA when liver dysfunction
due to AIP was overt. Diagnosis of PBC should be made carefully when there is
other disease that causes hepatic cholestasis. This manuscript seems to be too
lack of information about PBC to demonstrate synchronous development of AIP
and PBC. Had liver dysfunction that was diagnostic as typical PBC persisted
before development of obstructive jaundice? Otherwise, a presence of PBC
should be shown histologically.
3. The titer of AMA and the value of AMA (M2) should be described.
4. The authors concluded that there were not extrapancreatic lesions; however,
CT image demonstrated enhancement and wall thickening of gallbladder and
common bile duct, suggesting the presence of some inflammation. Authors say
that these figures are possibly due to obstruction by enlarged pancreas.
However, these pictures also resemble those of gall bladder and bile duct
involvement seen in AIP.
4. The discussion is somewhat too long, and seems like review article in part.
The reviewer suggests the authors to rewrite the discussion focusing on the
importance of this case report.
5. This manuscript is full of misspelled words and wrong terms.
aotuimmune, pruritis, comfirmed, administaed, glutamyltrasferase,
immunocomprised, chinese, fibrilation, asprin, hastory, arythmia, alanine
transaminase, etc. ..................
The authors are advised to a native English-speaking scientific proofreader to
revise their article.
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I declare that I have no competing interest.
Review for 10.1186/1471-230X-14-8 (2014)

Reviewer's report
Title:Telomere shortening correlates to dysplasia but not to DNA aneuploidy in
longstanding ulcerative colitis
Version: 4Date:1 July 2013
Reviewer: Ferenc Sipos
Reviewer's report:
1. Major compulsory revisions
It is an interesting, well-designed and well-presented study about the association
of telomere-shortening, DNA aneuploidy and dysplasia/cancer development in
ulcerative colitis.
The authors have shown that both the increased amount of ultra-short telomeres,
and the shortening of mean telomere length are significantly associated with
dysplasia in longstanding disease, but no such associations were found between
telomere status and DNA aneuploidy.
Based on thier results it seems that the amount of ultra-short telomeres
may be a more sensitive marker of colitis-associated tumour progression than
mean telomere length.
Their results are new and may explain earlier observations about
telomerase-reverse transcriptase (TERT) expression in ulcerative colitis (Sipos F.
et al, Scand J Gastroenterol. 2008 Mar;43(3):289-98.).
2. Minor essential revisions
--
3. Discretionary revisions
A short (1-2 sentence) discussion about the a possible context between TERT
expression in UC and the found results would give a wider functional aspect of to
the discussion, and would enhance the strenght of the manuscript.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-8 (2014)

Reviewer's report
Title:Telomere shortening correlates to dysplasia but not to DNA aneuploidy in
longstanding ulcerative colitis
Version: 4Date:10 October 2013
Reviewer: Junko Aida
Reviewer's report:
Major Compulsory Revisions
In order to examine telomere biology in preneoplastic lesions from patients with
long-standing ulcerative colitis (UC), the authors analyzed multiple biopsy
specimens from colectomy materials harboring dysplasia and DNA aneuploidy.
They assessed the amount of ultra-short telomeres using the Universal STELA
method, and the mean telomere length using q-PCR, and were able to
demonstrate associations between ultra-short telomeres and neoplastic
development in UC. However, the approach employed by the authors has four
inherent problems related to examination of telomere length in the context of
human disease.
(1) There is no way of specifying the type of cell used for telomere measurement,
because the authors used specimens of the entire colonic mucosa, which is
constituted by many cell types. Thus, the mean telomere length would depend on
the relative ratios of the various types of cells present. Therefore I wonder
whether it is meaningful to make comparisons between the cases that have
different cell constitution ratios.
(2) Did the authors evaluate the degree of inflammation in UC cases? Infiltration
of many inflammatory cells effects on mean telomere length of the tissue.
(3) Telomeres shorten with aging. Therefore there is a need to consider age of
the patients from whom the tissue samples were taken.
(4) The telomere lengths of tissue or cells, or chromosomes, vary and show a
non-normal distribution. From a statistical standpoint, it can be considered that
the median or modal value would be more suitable than the mean value for
estimation of telomere length. Did the authors consider using the median or
modal value?
Minor Essential Revisions
(i) p.4, l.1: ‘ROS’ is the abbreviation for ‘reactive oxygen species’, and not
‘oxidative stress’; ‘ROS’ is used only twice in the manuscript. So I think that there
is no need to use the abbreviation ‘ROS’ in the manuscript.
(ii) p.8, l.23: What does the abbreviation ‘T/S ratio’ stand for?
(iii) Is ‘scg’ on p.9, l.3 and l.7 the same as ‘SCG’ on p.17, l.23? This abbreviation
is not defined at first mention in the text.
(iv) p.18, l.23: There is no need to use the abbreviation ‘BFB’ for
breakage-fusion-bridge.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-8 (2014)

Reviewer's report
Title:Telomere shortening correlates to dysplasia but not to DNA aneuploidy in
longstanding ulcerative colitis
Version:5Date:6 December 2013
Reviewer: Rosana Risques
Reviewer's report:
The authors have successfully addressed most of the comments. Only a few
minor revisions remain.
Minor Essential Revisions
1. The fact that all aneuploid samples except two included only 5-10% aneuploid
cells is crucial and should be specifically mentioned in the Discussion. Currently
it just talks about admixture of diploid cells, but this admixture is actually 90 or
95% diploid cells!
2. The authors might want to review this suggestion in discussion: “ultra-short
telomeres might develop independently from the shortening mean telomere
length”. Most likely oxidative damage shortens telomeres, which leads to
ultra-short telomeres as well as to a decrease of the mean telomere length.
However, because the mean is a composite measure of all the telomeres, it does
not capture that well the presence of one or a few critically short telomeres. The
STELA technique does and, thus, it is a more accurate estimator of the
progression towards dysplasia and cancer, which appears to occur when
critically short telomeres fail to cap the end of the chromosomes, leading to
cycles of bridge-breakage-fusion and chromosomal instability.
Discretionary revisions
1. In Discussion, an alternative explanation for the ‘rather surprising finding of no
significant difference in mean telomere length between progressors and non
progressors’ might be the small number of patients coupled with a rather high
coefficient of variation for mean telomere length measurement with either of the
single control genes (10.5% and 11.3%). Typical CV for Q-PCR telomere length
is between 6-7% (see for instance PMID: 21824912). A potential reason for high
CV in this study is the use of a 7900HT Fast Real-Time PCR System, which
appears to have a plate position effect that might increase variability, especially
in samples run in the edges of the plates.
2. The results and parts of the discussion are still somehow difficult to follow due
to so many comparisons. Additional figures or tables summarizing the results
would be helpful, but not essential.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Review for 10.1186/1471-230X-14-8 (2014)

Reviewer's report
Title:Telomere shortening correlates to dysplasia but not to DNA aneuploidy in
longstanding ulcerative colitis
Version:5Date:9 December 2013
Reviewer: Junko Aida
Reviewer's report:
In spite of the examination had a limits in the points I commented, but the authors
replied my questions well and revised the manuscripts..
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-7 (2014)

Reviewer's report
Title:Digital image analysis is helpful in diagnosing gastric mesenchymal tumors
Version: 1Date:9 September 2013
Reviewer: Neven Ljubicic
Reviewer's report:
REPORT TEMPLATE
Reviewer's report
-----------------------
- Major Compulsory Revisions
The authors wished to analyze the efficacy of digital image analysis (DIA) in
differentiating gastric mesenchimal tumors, which is a novel method and the
similar papers on this matter are scarce. The authors have found that this
method is valuable in differentiating GIST from other benign tumors. However,
we believe that the difference between those tumors is obvious on EUS without
using DIA. Differentiation between benign and malignant GIST is challenging,
and the authors found that DIA is not helpful on this matter. The authors
presented the results as positive; however those “positive” results add little to
clinical practice. Additionally, the number of patients with tumors other than GIST
is too small to draw any conclusions. The real strength of the study lies in the fact
that the authors used novel method in differentiating benign and malignant GIST.
Although the results are negative, they should be published if presented in that
way.
The title should be modified in a way that emphasizes that DIA is not useful in
differentiation of malignant and benign GIST.
In Table 1, T value for benign and malignant should be presented separately.
The abstract, discussion and conclusions should be also modified in this way.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
- In the past five years I did not receive reimbursements, fees, funding, or salary
from an organization that may in any way gain or lose financially from the
publication of this paper
- I do not hold any stocks or shares in an organization that may in any way gain
or lose financially from the publication of this paper
- I am not currently applying for any patents relating to the content of the
manuscript and I have not received reimbursements, fees, funding, or salary from
an organization that holds or has applied for patents relating to the content of the
manuscript
- I do not have any other financial competing interests
- I do not have any non-financial competing interests in relation to this paper
Review for 10.1186/1471-230X-14-7 (2014)

Reviewer's report
Title:Digital image analysis is helpful in diagnosing gastric mesenchymal tumors
Version:1Date:6 December 2013
Reviewer: Masayuki Kitano
Reviewer's report:
This article reports usefulness of objective (quantitative) analyses for diagnosis of
gastric mesenchymal tumors. The content of the manuscript is well written with
detailed methods and appropriate analyses of outcomes. The strength of this
article is the first report about utility of rational measurements of parameters of
EUS images for gastric mesenchymal tumors. The weakness of this article is
retrospective analyses of recorded images.
1. (Title) Authors should include this report is about image analysis of “EUS” in
the title.
2. Standardization in this article is skillful using anechoic center and outer
hyperechoic rim in the recorded images. Ideal standardization should be an
unified setting of ultrasonography, including gain, contrast, frequency and so on,
in the prospective study. Authors should discuss this.
3. Authors should describe the detail of the unit of brightness (Tmean and TSD).
Is the maximum value is 130 or 100? Is the minimum value is 0?
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Review for 10.1186/1471-230X-14-7 (2014)

Reviewer's report
Title:Digital image analysis is helpful in diagnosing gastric mesenchymal tumors
Version:1Date:8 December 2013
Reviewer: christian jenssen
Reviewer's report:
1. Is the question posed by the authors well defined?
yes
2. Are the methods appropriate and well described?
yes
3. Are the data sound?
yes, taking into account the discussed limitations of the study.
4. Does the manuscript adhere to the relevant standards for reporting and data
deposition?
yes
5. Are the discussion and conclusions well balanced and adequately supported
by the data?
yes.
However I miss a discussion
1) of the clinical consequences of the data: is there any relevance of digital
image analysis for the decision to operate (or to biopsy) a respective
mesenchymal gastric tumor?
2) are there data on any other noninvasive diagnostic tools to characterize
mesenchymal gastric tumors (elastography, contrast enhanced EUS)?
6. Are limitations of the work clearly stated?
yes, however the problem of selection was only touched.
I propose to add data on how many gastric subepithelial tumors have been
examined in the respective time period of the study. Which gastric subepithelial
tumors have not been operated on in this time period, and which criteria were
used to decide on operation? The authors only mention in their discussion, that
patients were selected for surgery according to the clinical
opinions and decisions of the medical doctors.
7. Do the authors clearly acknowledge any work upon which they are building,
both published and unpublished?
yes
8. Do the title and abstract accurately convey what has been found?
yes
9. Is the writing acceptable?
yes
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
No, I dont have any competing interests with regard to the article.
Review for 10.1186/1471-230X-14-6 (2014)

Reviewer's report
Title:Osteonecrosis of the jaw in a Crohn's disease patient following a course of
Bisphosphonate and Adalimumab therapy: a case report.
Version: 2Date:20 September 2013
Reviewer: Charles N Bernstein
Reviewer's report:
Major compulsory revisions
This paper needs English language editing.
My problem with this case report is the authors making the connection between
using a bisphosphonate in 2004-2009 and developing osteonecrosis of the jaw in
2013. The authors would need to cite literature from elsewhere that have also
shown markedly delayed osteonecrosis after cessation of bisphosphonate
therapy.
The authors attempt to make the case that anti TNF therapy has exacerbated
this condition but they also gloss over the fact that the patient had “oral” Crohn’s
disease. What type of oral disease? In fact the involved bone had a
granulomatous reaction-so was the bone lesion Crohn’s disease related?
Even if the authors ignore the bisphosphonate use from 5 years previous and
want to report this as a new complication of anti TNF treatment the confounder
remains the oral Crohn's disease
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I have consulted to Abbvie Canada maker of Adalimumab
Review for 10.1186/1471-230X-14-6 (2014)

Reviewer's report
Title:Osteonecrosis of the jaw in a Crohn's disease patient following a course of
Bisphosphonate and Adalimumab therapy: a case report.
Version: 2Date:11 October 2013
Reviewer: Allauddin Siddiqi
Reviewer's report:
The authors should consider extending the treatment section (treatment provided
and outcomes) along with an image of the healed site.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-14-5 (2014)

Reviewer's report
Title:Oral bisphosphonates do not increase the risk of severe upper
gastrointestinal complications: a nested case-control study
Version: 1Date:6 May 2013
Reviewer: Kazumasa Miyake
Reviewer's report:
Comments
This is a nested-control study, having clinical significance, suggesting that the
use of bisphosphonates unlikely is causally associated with the onset of serious
GI complications.
But I think this paper needs “Major Compulsory Revisions”.
- Major Compulsory Revisions
# Although this study indicated the risk of bisphosphonates for serious GI
complications using a number of sensitivity analyses, the details in numbers of
factors such as UGIC, current or past exposures of BPs, seem not to be enough.
# Current exposure was defined as the last day of coverage of BPs therapy
within 30 days prior the index date. However, in evaluating drug-associated GI
complications, the period within 30 days seems to be too long and invalid as
“Current exposure”. Was the period justified on what grounds or evidences?
# Gastroprotective agents should consist of some types, such as proton pump
inhibitors, histamine H2 receptor antagonists, prostaglandins.
In addition, it has been reported that nitrogen-containing bisphosphonates
increase gastric damage with depends on higher pH through acid supressants in
the rat.
1)Aliment Pharmacol Ther 14#1215#1223, 2000
2)J Gastroenterol Hepatol 19#512#520, 2004
How were gastroprotective agents defined?
# In “Results”, Figure 4 seems to be needed further explanation.
# This study did not offer the risk for UGIC associated with not only BPs but also
even antithrombotic agents and BPs co-therapied with NSAIDs.
Does this mean that routine clinical practice in your country has adequately
avoided the risks for any drugs-associated UGIC, but not these drugs do not
increase the risk.
# Ref [38] should have indicated the increase in the risk for gastroduodenal
ulcers with co-administration of BPs in patients on long-term NSAIDs therapy, but
not a positive association between use of BPs and the risk of gastroduodenal
ulcers.
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-14-5 (2014)

Reviewer's report
Title:Oral bisphosphonates do not increase the risk of severe upper
gastrointestinal complications: a nested case-control study
Version: 1Date:14 May 2013
Reviewer: Ezgi Gulmez
Reviewer's report:
- Overall comments:
This is a well-written and interesting article evaluating use of oral
bisphosphonates and the risk of severe upper gastrointestinal complications, in a
nested case-control study in the Healthcare Utilisation Databases of the 13
Italian territorial units (four regions & nine local health authorities) participating at
the AIFA-BEST Project.
- Minor Essential Revisions
1) Background page 6: the acronym UGIC is written the first time, add “upper
gastrointestinal complications”.
2) Please provide more information about the HCU databases in Italy.
3) Please provide some more information about the AIFA-BEST project. Is it
conducted only in the mentioned 13 territorial units or is this a nationwide project
and data presented in the manuscript are from 13 territorial units? This then,
could explain a further question: Since there are only four regions participating to
the BEST project, in other words, the project is limited to specific geographical
areas, are the results adequately representative for Italy?
4) Please provide explanation for the different chosen periods for the cohort entry
(1 July 2003 – 31 December 2005) and the cases (hospitalization for UGIC until
2007).
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-5 (2014)

Reviewer's report
Title:Oral bisphosphonates do not increase the risk of severe upper
gastrointestinal complications: a nested case-control study
Version: 1Date:16 May 2013
Reviewer: Olivier Lamy
Reviewer's report:
The design of these nested case-control study is interesting. Only patients with
severe fractures were included. These patients have co-morbidities and take
many medications. The number of patients who were hospitalized and who take
bisphosphonates were very low, only 38. It is difficult to give any conclusion with
this small number. An important bias is the number of patients taking
gastroprotective agents in the “case patients”.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-14-5 (2014)

Reviewer's report
Title:Oral bisphosphonates do not increase the risk of severe upper
gastrointestinal complications: a nested case-control study
Version:2Date:6 December 2013
Reviewer: Kazumasa Miyake
Reviewer's report:
There are no comments.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-4 (2014)

Reviewer's report
Title:A non-interventional study of the genetic polymorphisms of NOD2
associated with increased mortality in non-alcoholic liver transplant patients
Version: 1Date:6 September 2013
Reviewer: Negar Azarpira
Reviewer's report:
The manuscript is a well written article with detail clinical follow up. Please
consider:
1. What is the other causes of transplant recipients? Why do you divide only to
alcoholic and non-alchoholic patients?
2. what is the allele and genotype distribution of NOD gene in different groups ?
please insert a table and include these results.
3. What is the allele and genotype frequencies of other genes? Why don't you
mention at all your results?
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-14-4 (2014)

Reviewer's report
Title:A non-interventional study of the genetic polymorphisms of NOD2
associated with increased mortality in non-alcoholic liver transplant patients
Version:1Date:10 November 2013
Reviewer: Siew Ng
Reviewer's report:
Potentially clinically relevant study to use NOD 2 SNPs for patient prognosis
Major compulsory revisions
There was no mention of why the authors chose to test in particularly the 13
SNPs in this study.
It is unclear how many subject in total had non alcoholic disease and the sample
size should be justified
Were confounding factors including age, severity etc adjusted for between the
groups?
Minor Essential revisions
The abstract conclusion of the use of pre-operative tracking of NOD 2 SNPs as a
tool for follow-up of patient appear premature as these SNPs need to be
validated I larger cohort
The discussion can be trimmed down and be more focused and targeted at the
results.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I declare I have no competing interests
Review for 10.1186/1471-230X-14-3 (2014)

Reviewer's report
Title:Serum pepsinogen levels are valuable markers for the diagnosis of gastric
diseases in Chinese
Version: 1Date:4 October 2013
Reviewer: Katsunori Iijima
Reviewer's report:
Zhang et al. reported serum pepsinogen level as a valuable marker for the
diagnosis of gastric cancer in Chinese. However, because there have already
been a lot of papers regarding relationship between serum pepsinogen and
gastric cancer risk even from China, I found little interest in the contents of the
paper.
I found the following concerns
1. Combined assessment with pepsinogen and H. pylori infection rather that
pepsinogen alone would be more valuable.
2. It is well-known that serum pepsinogen levels are considerably affected by PPI
intake or H. pylori eradication. Were those subjects excluded from the study.
3. Although the authors discussed the different cutoff values of serum
pepsinogen in different countries, they need to be cautious about considerably
differing measured serum PG values between Western and Eastern kits (Iijima K,
et al. World J Gastroenterol. 2009; 21;15(7):853-9. & Miki K, et al. Dig Endosc.
2009 Apr;21(2):134-5).
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
none
Review for 10.1186/1471-230X-14-3 (2014)

Reviewer's report
Title:Serum pepsinogen levels are valuable markers for the diagnosis of gastric
diseases in Chinese
Version: 1Date:13 October 2013
Reviewer: Nayoung Kim
Reviewer's report:
This manuscript titled “Serum pepsinogen levels are valuable markers for the
diagnosis of gastric disease in Chinese” has many troublesome points that must
be clarified.
Major comments:
1. Although this is a first study about pepsinogen levels of Chinese Han people in
mid-south China, comparing with previous other studies, the sample size is too
small. Just 82 gastric cancer patients and 34 healthy controls were enrolled and
this is the major limitation of this study. And Furthermore, the authors do not
state about the limitations clearly.
2. The title “Serum pepsinogen levels are valuable markers for the diagnosis of
gastric disease in Chinese” is somewhat conclusive. And all enrolled subjects are
Han people who live in local area of China, Hunan Province, therefore this data
are not represent the whole China population. This is another limitation of this
study.
3. How many subjects underwent gastric biopsy and why the authors do not
check the H. pylori status of the subject?
4. As the authors said in the introduction, pepsinogen levels are affected by
many factors such as the area, race, age, gender, Helicobacter pylori infection
and so on. Why the authors do not take these factors into account?
For example, the result in Table 1 shows that PG I level and PG I/II ratio are
significantly lower in patients with gastric cancer than in the controls and
non-atrophic gastric group. However, the authors do not consider the patient’s
age and H. pylori infection status. Is this a real cancer effect? PG I/II ratio can
also decrease in H. pylori positive patients.
You must present the baseline characteristics of each group before you compare
with each group.
5. It needs correction of English by native speaker.
Minor comments
1. There many spacing errors, typing errors in this manuscript.
1) For example (spacing errors)
In abstract: p<0.001 (x) à p < 0.001 (O)
In Method, Result and Tables 52.3±12.3 (x) à 52.3 ± 12.3 (O)
n=36 (x) à n = 36 (O)
2) For example (Typing errors)
Page 4, line 7, 36 healthy controls à 34 healthy controls
Page 5, line 13, 53 cases of NAG à 55 cases of NAG
2. Please more details descriptions about Figure 1.
3. In the title of Table 2, ‘accuracy’ is not appropriate. Please replace it with
‘frequency’.
4. In Table 2, the sum of subject in # 90 and > 90 are not equal to 142. And the
percentage of the each groups are not correct. Please check it precisely.
Review for 10.1186/1471-230X-14-3 (2014)

Reviewer's report
Title:The value of serum pepsinogen levels for the diagnosis of gastric diseases
in Chinese Han people in midsouth China
Version:2Date:5 December 2013
Reviewer: Marcis Leja
Reviewer's report:
The study design does not allow to eliminate the major draw-back, i.e. the small
sample size, in particular small number of cancer cases. In addition, the PgI/II
cut-off values are sought to discriminate gastric cancer, although this is the
marker for atrophy (linked to risk of cancer).
Otherwise all the remarks have been followed, and the quality of the paper
increased accordingly.
Minor Essential revisions. Although the method has been added to the abstract
(ELISA), this is important to indicate also the manufacturer name there.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
No competing interests
Review for 10.1186/1471-230X-14-3 (2014)

Reviewer's report
Title:The value of serum pepsinogen levels for the diagnosis of gastric diseases
in Chinese Han people in midsouth China
Version:2Date:6 December 2013
Reviewer: Nayoung Kim
Reviewer's report:
Thanks for your kind answer to my comments. I have more comment as follow;
Major comments:
1. As I commented previously, serum pepsinogen levels are affected by many
factors such as age, gender and so on. I understand the author’s opinion that
due to the small sample size, the authors could not analyzed the other factors. If
so, how about adding mean ages and gender distribution of non-GC group, GC
group and healthy control group in tables? How about adding correlation
(correlation coefficient) between pepsinogen values and age?
2. The statistical methods are incorrect.
1) The author said “analyze the differences in patients with gastric disease and
healthy controls by using paired t-test” Paired t-test is estimating the difference
between two matched population means. In this case, Student’s t-test is correct
method.
2) In statistical method section, “P < 0.05 was considered statistically significant”
and “two-sided P value of less than 0.05 was considered statistically significant”
are overlapping sentences.
3) In statistical method section, the authors said “continuous variables were
shown as mean ± SD and non-normal distribution variables were shown as
median and interval.” However, in table 1, all values are presented as mean ±
SD. Which one is non-parametric data?
3. In page 7, “As shown in Table 5, serum PG I level in the patients with gastric
ulcer and those with duodenal ulcer were 147.58 ± 57.81 µg/L (n = 36) and
217.43 ± 51.12 µg/L (n = 31), respectively, significantly higher than in the
subjects with endoscopically normal mucosa (118.39 ± 47.8 µg/L).” This
sentence is more related with ‘Table 1.’ And I think ‘Table 5’ is meaningless data
because the same result already described in ‘Table 1.’ It would better to delete
the ‘Table 5.’
4. In method section, the authors identified the H. pylori status by RUT and
anti-H. pylori IgG test. Please clarify the definition of current H. pylori infection. Is
the author use both of these methods or one of these method?
Minor comments:
1. In abstract, line 3, serum PG levels instead of serum levels.
2. In introduction, page 4, line 3-4, suggest appropriate references, please.
3. In page 5, line 12, correct P as small letter.
4. Please correct all signs of inequality (#, >) in page 7.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-14-2 (2014)

Reviewer's report
Title:Detection of Drug Effects on Gastric Emptying and Contractility Using a
Wireless Motility Capsule
Version: 1Date:24 July 2013
Reviewer: Frank Friedenberg
Reviewer's report:
Reviewer Comments
The article is an interesting idea which looks at the possibility of using the
SmartPill to measure gastric emptying after exposure to placebo, a drug which
should decrease gastric motor activity (morphine), and a drug which should
accelerate gastric emptying (erythromycin).
Specific Comments- I believe these are all major compulsory issues.
1. The age span of the subjects are of some concern in that there may be
intrinsic differences in the response to medication in an individual who is 19 vs. a
subject who is 65 years. Also there is no mention that subjects or researchers
were blinded.
2. Statistical Analysis – the comment about the capsule not exiting the stomach
within 6 hours in 6 tests belongs in the results section. Moreover there is concern
at arbitrarily picking 6 hours as the emptying time for those individuals in which
the capsule did not exit by 6 hours. Therefore in someone whose capsule exited
at 5.5 hours it would seem by analysis that a capsule that would have taken 8
hours was only 30 minutes slower using a high end cutoff of 6 hours. I think the
analysis should have been done with elimination of these studies and this
represents a shortcoming of the technology.
3. I don’t agree that the inferential analysis should assume a normal distribution.
4. I don’t understand what a heteroscedastic linear model is – would refer to a
statistician. In my opinion the analysis should have consisted of pairwise
comparisons of motility parameters between placebo (essentially your pre-
values or baseline) and after drug.
5. p 7. Under gastric emptying time – how were the differences between placebo
and erythromycin calculated? What is the P value for the difference which should
be used rather than saying “statistically significant”
6. I think Tables 1 and 2 need to be redone eliminating the 6 cases where the
capsule did not pass until the meal was given. Probable should be presented as
medians with IQR and range.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I have no competing interests.
Review for 10.1186/1471-230X-14-2 (2014)

Reviewer's report
Title:Detection of Drug Effects on Gastric Emptying and Contractility Using a
Wireless Motility Capsule
Version: 1Date:28 July 2013
Reviewer: Stefan Rauch
Reviewer's report:
Minor Essential Revisions
The authors have conducted an interesting study using a novel wireless motility
capsule in order to assess the pharmacological effect on gastric emptying. They
have used two different drugs (morphine, erythromycin) compared with placebo
(saline) to study GET in healthy volunteers. I have only a few comments that
should be addressed:
The authors should elaborate a little bit on the inter- and intraindividual
differences in gastric emptying time in healthy persons found in previous studies.
Although there was a statistical significant difference in GET - in general - it
seems that gastric emptying of the capsules in this study remains physiologically.
Furthermore, it would be helpful to show if there is any variability in GET by
giving the IQR.
All the volunteers have received a standardized meal. Food per se can alter
gastric motility. I would add a few remarks about the influence of food and
nondigestible solids on gastric emptying despite the similar formula meals.
What was the rational for using these drug doses? 150 mg erythromycin seems
to be a subtherapeutic dose compared with the data in the literature.
Typing error:
Page 7, line 11 subjects instead of subjected
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-2 (2014)

Reviewer's report
Title:Detection of Drug Effects on Gastric Emptying and Contractility Using a
Wireless Motility Capsule
Version:2Date:30 October 2013
Reviewer: Frank Friedenberg
Reviewer's report:
I think the author's have made the necessary changes for publication.
Minor
Table 1 can be eliminated and just incorporated into the text
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Review for 10.1186/1471-230X-14-2 (2014)

Reviewer's report
Title:Detection of Drug Effects on Gastric Emptying and Contractility Using a
Wireless Motility Capsule
Version:2Date:9 November 2013
Reviewer: Stefan Rauch
Reviewer's report:
Dear editor,
All of my concerns have been addressed in the revised manuscript. I recommend
to publish the mansucript.
Thank you very much for giving me the opportunity to review this manuscript.
Best regards,
Stefan Rauch
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-14-1 (2014)

Reviewer's report
Title:Over-expression of COX-2 mRNA in colorectal cancer
Version: 1Date:25 August 2013
Reviewer: Wenjuan He
Reviewer's report:
Hennie MJ Roelofs et al. conducted mRNA analysis of COX2 expression in 60
patients comparing colorectal cancer tissues with nearby normal tissues using
three different normalization methods, tissue weight or house-keeping genes
B2M or GAPDH. Their data demonstrated statistically significant over-expression
of COX2 mRNA in tumor tissues by all of the three normalization methods.
Normalization by tissue weight has shown the best correlation, with increased
COX2 in around 80% of all patient tumor samples. The authors hence concluded
that examination of COX2 mRNA and normalization by tissue weight is the best
method for determining COX2 levels in colorectal cancer and their data is
consistent with COX2 as a risk biomarker for this type of cancer.
In summary, the present study is carefully designed, well described and it is a
relatively large scale analysis compared to similar published studies examining
COX2 expression in colorectal cancer. My concerns or comments are listed
below which should be addressed to improve the present manuscript.
Major Compulsory Revisions
1. The authors found COX2 mRNA expression normalized by tissue weight
showed the best correlation with tumor when compared to normalization by other
house-keeping genes. Was this due to the fact that some house-keeping gene
expression also changed in tumor tissues?
2. Can absolute quantification method be used to measure COX2 mRNA level
instead of relying on normalization?
3. Did COX1 mRNA expression change in tumor tissues? COX1 is a very good
control to compare to COX2.
4. Western blot or immunostaining to confirm up-regulation of COX2 protein
expression is important supporting data to show.
5. The authors found COX2 expression level was independent of tumor grade or
lymph node metastases. Could the authors further comment on the role of COX2
during colorectal cancer development? And whether patients with up-regulated
COX2 expression or not respond differently to COX2 inhibitor treatment?
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-1 (2014)

Reviewer's report
Title:Over-expression of COX-2 mRNA in colorectal cancer
Version: 1Date:26 August 2013
Reviewer: li liang
Reviewer's report:
Major compulsory revisions:
1. The authors performed qPCR to detect the mRNA level of COX-2 relative to
tissue weight or the mRNA levels of two housekeeping genes in 60 paired CRC
tissues. They did not mention the quality of mRNAs extracted from tissues.
Moreover, it is too simple for experimental design. The changes of COX-2 protein
levels should be shown by Western blotting in the same CRC tissues.
2. The clinicopathological analyses of COX-2 in 60 paired CRC tissues should be
shown in a table.
3. The figure of COX-2 expression in CRC tissues is not intuitive. Figures with
bar may be better.
Minor essential revisions
1. There are many grammar and careless mistakes. Some sentences are hard to
read. Authors should have the manuscript edited by a native English speaker
with scientific experience.
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests' below.
Review for 10.1186/1471-230X-14-1 (2014)

Reviewer's report
Title:Over-expression of COX-2 mRNA in colorectal cancer
Version:2Date:31 October 2013
Reviewer: li liang
Reviewer's report:
The authors made some improvements of the original version. However, they did
not give reasonable answers for Q1,3 in major compulsory reversions. Thus, I
suggest that this paper is unable to be accepted.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
No
Review for 10.1186/1471-230X-14-1 (2014)

Reviewer's report
Title:Over-expression of COX-2 mRNA in colorectal cancer
Version:2Date:6 November 2013
Reviewer: Wenjuan He
Reviewer's report:
The authors have adequately addressed most of my concerns.
- Major Compulsory Revisions
N/A
- Minor Essential Revisions
N/A
- Discretionary Revisions
The authors agree that COX-1 mRNA level will be a good control in their study
(#3). Given that cDNAs from patients have already been generated, it is an easy
experiment to do. COX-1 level will be an important control to show in comparison
to the disease relevant COX-2 level.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-14-1 (2014)

Reviewer's report
Title:Over-expression of COX-2 mRNA in colorectal cancer
Version:2Date:7 November 2013
Reviewer: Karen W. Makar
Reviewer's report:
The authors present a study in which they examined the expression of PTGS2
(the gene encoding the Cox-2 enzyme) in 60 tumor and normal tissue pairs via
real-time RT-PCR. Expression data was compared using three different
normalization strategies- tissue weight and two individual housekeeping genes
(B2M and GAPDH). While using tissue weight could be an attractive alternative
normalization strategy, the data presented are still inadequate to reach the
conclusion that this method is superior.
Major Compulsory Revisions:
1. The conclusion that the tissue normalization strategy is “more accurate” is still
unfounded. This paper does not present experimental data on inter- and intra-
assay variance, or biological or technical replicates. This data and a statistical
comparison of the accuracy and/or precision of the tissue normalization vs.
housekeeping gene methods would be necessary to support such a conclusion.
Either the statements about superior accuracy need to be curtailed in recognition
of the absence of rigorous methodological data, or proper assay development
experimental data need to be included in tables/figures to support these
statements. The tissue normalization procedure has promise, but the authors
should not overstate what their data supports.
2. Please provide details (e.g. formula) explaining the tissue normalization
strategy in the Methods. The authors state that for each sample 1ug of RNA was
converted into cDNA. Given that larger tissues would likely yield more RNA (and
the RNA yields and tissue weights are not provided), it is unclear from the text
how the ug RNA yield/mg tissue per sample is incorporated in the normalization
procedure.
Minor revisions-
Tissue weight normalization alone would not capture variability in RNA quality,
which is an essential component of the MIQE guidelines (ref 24) as discussed
recently in Bustin et al, Nature Methods Oct 2013. This is not discussed.
Background paragraph 3, 3rd sentence: there is a large space between
“subjected to” and “was suppressed” and this sentence makes no sense.
Discussion paragraph 7, missing a period after “tumor tissue.”
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: No, the manuscript does not need to be seen by a statistician.
Declaration of competing interests:
I have no competing interests