JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-11-97 (2011)

Reviewer's report
Title:The value of age and medical history for predicting the likelihood of
colorectal cancer and adenomas
Version: 1Date:13 January 2011
Reviewer: William Hamilton
Reviewer's report:
Thank you for asking me to referee this paper. I can confirm I know the subject,
and that I have no conflicts of interest.
Summary
This paper describes a large cohort of patients referred for colonoscopy in an
Australian centre. It seeks to identify a scoring system (derived from a
multivariable model) to predict cancer or polyps. The results are presented as
ROC curves, and the researchers conclude their scoring system can identify
people to be triaged for colonoscopy.
Although the overall paper is of some interest, it has several drawbacks.
First, the cohort is extremely disparate; it was anyone over 18 referred for
colonoscopy. So these may have been screening colonoscopies, suspected
cancer, follow-ups. This means two things: the results only pertain to such a
heterogeneous group of patients, and that they cannot be used as a selection
method for referral for colonoscopy. The authors don’t suggest the latter, but
unless they make explicit in their title that the study is in the referred population a
reader could easily be misled. MAJOR
Second, if the aim of the paper was to create a method of triage, then the logical
outcome variable for study would be ‘condition worth identifying by colonoscopy’
as a binary variable. Their multinomial regressions (which are quite pretty) are
actually too sophisticated! RECOMMENDED
Third, other scoring systems are omitted. The SELVA score aims to do precisely
the same thing. Its creation was published in the Lancet and its validation in
Wales was published this year. I can find the reference if the authors cannot.
MAJOR
Fourth, at least one ROC curve should be shown. The key need is for a steep left
side with very low sensitivity and very high specificity – these are the patients
who may be able to avoid colonoscopy completely. I simply don’t think their table
4 results are workable in clinical practice. Medico-legally a patient referred for
colonoscopy who is not offered the service but who harbours cancer will cost the
service much more than the savings generated by triage. MAJOR
Fifth, The conclusion that FH and symptoms are poor predictors of cancer is only
true in the referred population, and even in them most studies find rectal bleeding
a positive predictor. RECOMMENDED
Finally, have the editors examined the previous publications from this cohort?
How different is this one?
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-11-97 (2011)

Reviewer's report
Title:The value of age and medical history for predicting the likelihood of
colorectal cancer and adenomas
Version: 1Date:7 April 2011
Reviewer: Michael Hoffmeister
Reviewer's report:
In this study from Australia including 8200 participants aged 18 years or older
and undergoing colonoscopy in practices or in hospitals for any reason, an
attempt was made to predict different grades of colorectal neoplasia from
information of a self-administered questionnaire and from medical records. The
aim of the study was to find a combination of risk factors that predicts prevalence
of cancer, advanced adenomas and other adenomas, respectively, in order to
better select people at higher risk and to save resources spent on colonscopy.
Among the study's strengths are the assessment of information before the date
of colonoscopy, the availability of medical records, and the large number of
participants. However, from my point of view, there are some major concerns
with respect to the informative value of the results.
Major compulsory revisions:
(1) What is the practical relevance of this prediction model? What is the target
group? Of course, age is the major risk factor. Is this prediction model eligible for
all age groups? The prevalence of most risk factors and the set of risk factors
vary with age.
(2) The mixture of subjects with a history of colonoscopy or even with neoplastic
findings at previous colonoscopy and subjects with no previous colonoscopy
brings in different underlying risks (let alone the risks of those who have
colonoscopies or advanced neoplasia before the age of 40 or 50). If the aim is to
sort out people in the average-risk population who should be advised to have a
colonoscopy, why not focus e.g. on people with no previous colonoscopy? The
target group should be defined more clearly.
(3) How do people have a positive history of polyps although no previous
colonoscopy was performed so that we know?
Minor Essential Revisions:
(4) Table 4 can be omitted. In my opinion, it doesn't add to the major result of this
study and an appropriate discussion would distract from the major findings, as
this table is not easy to comprehend.
(5) The conclusions are poor and include an introductory part (first 2 sentences)
that can be omitted. Please provide a more focussed discussion and
conclusions. Who will be assisted by your models, and what is the rationale for
recommending colonoscopy on the basis of your models?
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-11-97 (2011)

Reviewer's report
Title:The value of age and medical history for predicting colorectal cancer and
adenomas in people referred for colonoscopy.
Version: 2Date:7 June 2011
Reviewer: William Hamilton
Reviewer's report:
They've done OK in this revision. I've no extra points to make.
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-11-97 (2011)

Reviewer's report
Title:The value of age and medical history for predicting colorectal cancer and
adenomas in people referred for colonoscopy.
Version: 2Date:20 June 2011
Reviewer: Michael Hoffmeister
Reviewer's report:
Thank you very much for your reply (however, changes in the manuscript should
be highlighted).
Major:
(1) In table 2, please provide the absolute numbers of participants and their
percentage with respect to all participants (N (%)) next to the variable subgroups,
such as age groups, gender, colonoscopy yes/no etc.
(2) Page 15, para 2, last sentence: the sentence about cancer prevalence should
be re-evaluated, as your low prevalence of cancer is presumably attributable to
the high proportion of subjects under 50 years (27%), whereas the study (not
"studies") on screening colonoscopy cited included subjects aged 40-80 years
only.
(3) Conclusions, page 16: In your reply, and in the abstract you speak of
'prioritisation' as one major use of the model. This is not reflected in the
conclusions of the discussion.
(4) Methods, page 5, para 2: Please provide a sound description of the study
design. This is likely not a 'trial' (which is commonly used as abbreviation of
'clinical trial'). Rather, it seems to be a cross-sectional study among patients
undergoing colonscopy.
Minor:
(5) Conclusions, page 16, first sentence: I guess 'developed' rather than
'developing' countries were referred to.
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-11-96 (2011)

Reviewer's report
Title:The Frequency Of Microscopic And Focal Active Colitis In Patients With
Irritable Bowel Syndrome
Version: 2Date:25 May 2011
Reviewer: Joel H Rubenstein
Reviewer's report:
The authors have conducted a cross-sectional case-control study estimating the
association of symptoms of IBS with microscopic colitis, finding that it is found in
3% of IBS patients, and 4.3% of non-constipated IBS patients. They also report a
substantial minority of IBS patients with focal active colitis.
Major concerns:
1) The average age of the IBS patients was 46, which seems higher than in most
studies, and might explain the relatively high proportion found to have MC. What
were the ages of the IBS patients found to have MC? Table I suggests that
patients greater than age 50 with IBS symptoms were excluded – is this not the
case?
2) Was the terminal ileum intubated routinely to exclude crohn’s ileitis?
3) 2nd to last paragraph of results: “biopsy samples were taken … to ascertain
that there was no pathology present in the controls.” - were controls excluded if
they have abnormal pathology? If so, this would be an error, as the comparison
of prevalence of MC or focal colitis would be biased by selection.
4) Were no patients found to have collagenous colitis?
Minor suggestions:
1) The classification of Groups I, II, and III are not well known and cumbersome
for the reader. The authors might change this to IBS-C, IBS-D, and IBS-M
(constipation, diarrhea, mixed).
2) Results first paragraph states that the average age of both groups was
identical, which contradicts Table 2 and later in the paragraph.
3) Discussion first paragraph omits reference numbers for the articles by Kao and
Chey.
4) 2nd to last paragraph of Discussion: “the incidence was almost 20%.” Should
read “prevalence.”
5) Same paragraph: “College of Gastroenterology” should read “American
College of Gastroenterology”
6) Tables II and III mis-spell lymphocytic
7) Figures 1 and 2 are redundant to the tables, and could be omitted.
Level of interest: An article of importance in its field
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 declare that I have no competing interests.
Review for 10.1186/1471-230X-11-96 (2011)

Reviewer's report
Title:The Frequency Of Microscopic And Focal Active Colitis In Patients With
Irritable Bowel Syndrome
Version: 3Date:2 August 2011
Reviewer: Darren Brenner
Reviewer's report:
Thank you for the time and effort you have put into revising this manuscript. I
believe this is a much clearer version worthy of publication. I have only a few
additional comments
Minor Essential Revisions:
1. Study limitations: This needs to be broadened. I appreciate that you comment
on the differences in age gender but I would appreciate if you would state why
these differences are important and why the % of women w/IBS enrolled was so
low. Is this commen from trials in Turkey as it is uncommon in trials in the USA.
2. Introduction: In the sentence on the prevalenc of IBS being 7.4-19.1% I would
comment that this is the prevalence in Turkey
3. Materials and Methods: I appreciate the catergorization of IBS patients as per
Rome III subclassifications; however, the criteria you use to define IBS-D/M/C
are not per Rome III. I would change the "according to Rome III" to modified
Rome III
4. Materials and Methods: Are per my prior question re: alarm symptoms you
reference the Olden paper. While this was an excellent paper for its time there
have been subsequent studies. I would recommed that you modify the table such
that it is more consistent with the data from the ACG EBM statement which is
your citation #33.
5. Results: At the end "there was no significant differnce among the incidence of
FAC..." this is placed prior to the actual data. I would move this sentence below
the next sentence starting with "FAC was found in 6.6%..."
6. Discussion: You refernce the Chey study on colonoscopy and note that
aternative diagnoses were identified in 1.9% of IBS patients. Please clarify this
as non-constipated IBS patients.
7. Discussion: 3rd paragraph 1st word: Microscopic misspelled. Please correct.
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-11-94 (2011)

Reviewer's report
Title:Psychopathological features of irritable bowel syndrome patients with and
without functional dyspepsia: a cross sectional study
Version: 1Date:20 July 2010
Reviewer: Laurie Keefer
Reviewer's report:
Thank you for the opportunity to review this paper. The manuscript is well-written
and the methodology and statistics are adequate. That said, the major concern I
have with this manuscript is that it does not really add significantly to what we
already know about the relations between FD, IBS and psychopathology.
Perhaps a larger sample size or the inclusion of several other psychological
questionnaires/interviews would make this previously reported observation more
definitive.
Major Compulsory Revisions
1. An estimate of power and a justification that the relatively small sample size is
adequate should be included
2. While differences were found between groups, they are not really clinically
significant-- scores on the SCL90R fell within the normal range for several
variables. I wonder whether a nonparametric statistic might be more useful, ie.
comparing functional v. dysfunctional SCL90 X group.
3. The authors conclude that the IBS+FD group have a greater severity of
psychopathology than IBS alone--however, they failed to control for other known
variables affecting this link including symptom severity and quality of life
impairment. While I realize that not all of the common questionnaires have been
validated in Italian, it still would have been appropriate to get a patient or
physician rating of symptom severity or functional impairment, etc.
4. It may have been more compelling to have included a group of FD patients
alone to tease out the "contribution" FD has to the association between IBS and
psychopathology.
Minor Essential Revisions
1. The authors should include in their discussion the potential limitation of having
>10% of their sample being referred from other gastroenterologists-- this implies
that the patients in this group were more distressed or refractory and may have
biased the results. This is particularly important because of the small sample
size.
2. Antidepressant therapies are commonly used in refractory functional gi
disorders-- what proportion of your patients were already using psychological
medications and how might this have affected the findings.
3. The authors should justify the breakdown of FD patients by subtype-- are there
theoretical reasons why these groups might be expected to differ? Also, why not
breakdown the IBS patients by subtype too then (IBS-D, IBS-C, etc.)? Again, a
larger sample may have been more useful in this regard.
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-11-94 (2011)

Reviewer's report
Title:Psychopathological features of irritable bowel syndrome patients with and
without functional dyspepsia: a cross sectional study
Version: 2Date:24 November 2010
Reviewer: Michael Crowell
Reviewer's report:
Manuscript ID: BMC MS 2070463711382080
Title: Psychopathological features of irritable bowel syndrome patients with and
without functional dyspepsia: a cross sectional study
Dear Editor,
The paper has been revised and improved from the original version. The authors
have adequately addressed my concerns related to design and statistical issues
except for one point. Point 5 of my previous review raised the concern that the
type I error was inflated due to multiple testing of the SCL90 subscales without
correction or specifically stating that the alpha level was not corrected for multiple
testing. The study evaluated differences between IBS and IBS+FD for 10 scales
resulting in a dramatic inflation of type I error rate. With 10 separate statistical
tests the potential to find a p-value less than 0.05 is greater than 40% provided
that the endpoints are not highly correlated. The authors should be more specific
about their primary hypothesis and use the GSI at 0.05 and adjust the subscales
or at least point out that no adjustments were made and that type I error rate was
inflated. Given the size of most of the p-values these adjustments are unlikely to
change the outcome of the study, but should be reported appropriately.
My concern can be readily addressed, at which time I would recommend that the
paper be accepted at the discretion of the managing Editors.
Thank You,
Michael D. Crowell, Ph.D., FACG, AGAF
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 declare that I have no competing interests.
Review for 10.1186/1471-230X-11-94 (2011)

Reviewer's report
Title:Psychopathological features of irritable bowel syndrome patients with and
without functional dyspepsia: a cross sectional study
Version: 2Date:6 December 2010
Reviewer: Laurie Keefer
Reviewer's report:
Thank you for your thoughtful responses.
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-11-95 (2011)

Reviewer's report
Title:The occurrence of Urinary Tract Infection before development of Primary
Biliary Cirrhosis: a case control study.
Version: 1Date:10 March 2011
Reviewer: Ikuko Haruta
Reviewer's report:
The authors studied OR of UTI and smoking as risk factors of PBC. There are
already several reports about these (plus additional factors). So the findings in
this report seemed to be not novel.
1) Was ethnicity considered for characteristic of cases?
2) In Table 1, smokers were classified never, ever and missing. How about
current and former?
3) Does ‘CI’ mean ‘95% CI’?
4) Although authors commented about diabetes as a known risk factor for the
development of UTI in page 7 and listed in the Table 1, there was no analysis
and argument about diabetes in Discussion.
5) Page 13, line 267-268 is over speculation. Did authors studied about the
cause of UTI? Was there any information that E. coli was dominant in these PBC
patients’ urine culture, when they had been diagnosed as pyelonephritis? Any
supportive data?
6) Page 14, line 289, what do you mean ‘some laboratory’?
7) The first time when authors wrote bacterial name, it should be written full
spelling.
(page 4, line 75; N. aromaticivorans, page 8, line 160 E. coli.) And E. coli should
be expressed Italic (page p14, line 291 and 293).
8) Page 13, line 274-276, ‘ Secondary … urothelial membrane’ is over
speculation as well. Any evidence or referenced paper?
9) Is reference number 23, (Suppl A-837) published paper ?
Review for 10.1186/1471-230X-11-95 (2011)

Reviewer's report
Title:The occurrence of Urinary Tract Infection before development of Primary
Biliary Cirrhosis: a case control study.
Version: 1Date:10 March 2011
Reviewer: Dimitrios Bogdanos
Reviewer's report:
The report by Varyani et al determined whether urinary tract infections are more
common in patients with primary biliary cirrhosis (PBC) prior to the diagnosis of
the disease compared to controls with chronic liver disease. Their case control
study is based on the UK General Practice Research Database (GPRD). These
findings will help the ongoing debate as to whether urinary tract infection has a
causal or casual relationship with this disease.
Their findings indicate that PBC is associated with UTI prior to diagnosis and that
this association is stronger in younger PBC patients. Thus, it appears that in PBC
patients before the age of 55, 31% had a prior diagnosis of UTI compared to 20%
of age and sex matched controls.
The study is of interest. My view is that such methodological studies are needed
to better understand the association of risk factors such as urinary tract infections
or smoking with the development of PBC or other autoimmune liver diseases.
Major point
The Authors need to make clear that one of the limitation of their studies was that
the control population of patients with chronic liver diseases was predominantly a
population of male patients (60%) when that of PBC is strikingly a female
population. Also, the control population with patients with chronic liver diseases
was younger than that of PBC. These differences clearly affect the results given
in cohorts not adjusted for age and sex as urinary tract infection is likely to be
more frequent in older women.
Minor Points
The Authors need to give more details/brief description of the GPRD and a link to
its website. The must also make clear in the abstract and methodology that
GPRD is a UK database.
Several original and review articles discussing the role of E.coli infection in PBC
and molecular mimicry studies involving E. coli and PBC-specific autoantigens
are missing and should be included Dis Markers. 2010;29(6):301-11; Clin Rev
Allergy Immunol. 2011 Feb 22; Clin Rev Allergy Immunol. 2009 Feb;36(1):30-9;
Dig Liver Dis. 2003 Nov;35(11):801-5; J Hepatol. 2004 Jan;40(1):31-9.
Page 13, Discussion 268 & 269, it is molecular mimicry ...instead of .... molecular
mimickery
Level of interest: An article of importance in its field
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-11-95 (2011)

Reviewer's report
Title:The occurrence of Urinary Tract Infection before development of Primary
Biliary Cirrhosis: a case control study.
Version: 2Date:8 April 2011
Reviewer: Dimitrios Bogdanos
Reviewer's report:
The revised manuscript addresses satisfactorily the comments of the reviewers
Level of interest: An article of importance in its field
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-11-95 (2011)

Reviewer's report
Title:The occurrence of Urinary Tract Infection before development of Primary
Biliary Cirrhosis: a case control study.
Version: 2Date:12 April 2011
Reviewer: Ikuko Haruta
Reviewer's report:
The paper demonstrated that PBC associated with UTI prior to diagnosis,
especially in associateion with younger PBC patients, based on the UK GPRD.
The paper is corrected side by side following reviewers’ comments and much
clearly emphasized their results of case control study. The paper is now
acceptable for publication.
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 decleare that I have no competing interest.
Review for 10.1186/1471-230X-11-95 (2011)

Reviewer's report
Title:The occurrence of Urinary Tract Infection before development of Primary
Biliary Cirrhosis: a case control study.
Version: 2Date:25 July 2011
Reviewer: Pietro Invernizzi
Reviewer's report:
This paper by Varyani et al reports data on the casual relationship between
urinary tract infection (UTI) and primary biliary cirrhosis (PBC). It has been
consistently reported an association between UTI and PBC, but all previous data
were based on retrospective studies. The question of the role of UTI in PBC is of
relevance. Unfortunately the current study is not real prospective study. These
authors analysed a validated UK population-based database. As discussed by
the authors, this study have a number of bias, but it is far the strongest study
design among those on this issue. This study is not conclusive on this topic.
From a statistical point of view, since gender and age can well affect results, it is
better to have a similar proportion of female subjects also in the chronic liver
disease group (about 85% instead of the current 40% of female subjects) and of
similar age with the PBC patients (about 62 years instead of the current 54
years). By matching PBC and CLD patients, it is well possible that the specificity
of UTI and PBC will be lost. Indeed, the current findings do not clearly support
such specificity.
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.
Review for 10.1186/1471-230X-11-92 (2011)

Reviewer's report
Title:Association of RUNX 3 Promoter Methylation with Gastric Cancer: a
Pooled Study
Version: 3Date:25 April 2011
Reviewer: Kohji Miyazaki
Reviewer's report:
Basically, the authors made lots of mistakes in Figures and Tables of this
manuscript. At first, they selected 17 eligible papers finally. However, first two
papers were reported by the same author as shown in Figure 2. Furthermore,
different patient number was written in M+/M- of normal tissue, in which 7/93 in
1st Waki(a) 2003, 4/19 in 2nd Waki(a) 2003. Moreover, in Event column of Figure
2, M+/M- actually represents M+/total number. For instance, in report by Hiraki
(2010), M+/M- in cancer is 28/21, not 28/49, M+/M- in normal is 14/21, not 14/49.
Concerning these mistakes, 1082 patients (475/M+, 453/M-) should be
accounted in total number of cancer patients, however 1403 (475/M+, 928/M-)
was written in Table 1. As same in Figure 2, wrong numbers of patient were
plotted in Figure 3 and 4.
Level of interest: An article of insufficient interest to warrant publication in a
scientific/medical journal
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.
Review for 10.1186/1471-230X-11-92 (2011)

Reviewer's report
Title:Association of RUNX 3 Promoter Methylation with Gastric Cancer: a
Pooled Study
Version: 3Date:4 May 2011
Reviewer: Stefania Boccia
Reviewer's report:
Major Compulsory Revisions
• English is really poor and needs to be improved by an English-mother tongue
• In the abstract authors state that the ‘trend of OR was…’ but they did not
formally test for a trend in any part of the ms.
• Authors performed many statistical tests to address the publication bias, but
certainly the funnel plot and the meta-trim method are enough. Please remove
the Harbord graph which is superfluous.
• Figure 1 represents the flow-chart of the selection process of articles, but given
the large number of figures/tables, it is suggested to drop.
• All the additional tables are really unnecessary, except the figure 1 that I would
preserve and use as Table 1 (not additionally).
• Subgroup analysis: 9th line from the bottom: ‘The heterogeneity was existed in
the studies’…it is not clear if authors refers to the heterogeneity among the
overall studies selected. Please clarify and refer to a Figure.
• Subgroup analysis: 13th line from the bottom: ‘…which made the OR from
significant (fixed) to no significant..’. Please authors choose a statistical model
based on the heterogeneity then be consistent across the ms, avoiding to use
both methods.
Minor Essential Revisions:
Typing mistakes across the ms
Level of interest: An article of importance in its field
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-11-92 (2011)

Reviewer's report
Title:Association of RUNX 3 Promoter Methylation with Gastric Cancer: a
Pooled Study
Version: 3Date:5 May 2011
Reviewer: Young-Sik Kim
Reviewer's report:
The authors conducted a meta-analysis of the association between RUNX3
promoter methylation and gastric cancer. They concluded that RUNX3 promoter
methylation is strongly associated with gastric cancer with a pooled OR of 5.63.
The manuscript gives valuable information but contains some errors.
1)In Abstract, total number of patients was described as 2374, but the number in
Fig. 2 was 1740 (928+812).
2)In Abstract, the OR of the undifferentiated gastric cancer against the
well-differentiated was described as 0.59. In Results (p11, lines 1-3) The
undifferentiated gastric cancer also had higher methylation OR...
These sentences are confusing and contradictory. The authors should present
the OR of undifferentiated gastric cancer against the well-differentiated cancer.
3)In Introduction(p4, line24), "gastric, cancers..." comma should be removed.
4)In Method (p6, lines 12-13), Did the authors really searched using "the Social
Science Citation Index"?
5)The inclusion criteria should be described in detail in the method section.
6)In Results, asymmetry tests of the funnel plot should be described.
7)In Figures 2-4, the X-axis labels (gastric cancer and normal tissue) are
reversed.
8)In Figure 6 (Funnel plot), what's the meaning of the orange line?
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-11-92 (2011)

Reviewer's report
Title:Association between RUNX 3 promoter methylation and gastric cancer: a
meta-analysis
Version: 4Date:14 July 2011
Reviewer: Kohji Miyazaki
Reviewer's report:
In this revised manuscript the author extensively corrected mistakes in Figures
and Tables, resulting in adequate data enough to understand. Thus the revised
form could be judged as acceptable in BMC gastroenterology.
Minor comment: ALL author names written in Table 1 should be represented in
reference section.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
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-11-92 (2011)

Reviewer's report
Title:Association between RUNX 3 promoter methylation and gastric cancer: a
meta-analysis
Version: 4Date:15 July 2011
Reviewer: Young-Sik Kim
Reviewer's report:
1. The authors did not clearly explain the meaning of 2374 in the Abstract.
In addition, they did not describe what the autologous and heterologous mean.
2. In 2nd row of Tables 1 and 2, which is correct, M+/M- or M+/N ?
3. In subgroup analysis of the result section, chisqaure is 18.96 (line 2 from the
bottom) but it is different from the value in Table 2.
4. Some grammatical errors are still exist in the discussion(page 11, line 14) and
Fig.5 legend.
5. Many tables need to be concised and removed.
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
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-11-92 (2011)

Reviewer's report
Title:Association between RUNX 3 promoter methylation and gastric cancer: a
meta-analysis
Version: 4Date:21 July 2011
Reviewer: Stefania Boccia
Reviewer's report:
Minor revisions.
Tables and Figures are still redundant. Namely, figure 4, Tables 5 and 6 should
be removed as superfluous. FIgures 1,2 and 3 should be collapsed in only one
Figure, as following: Figure 1 is fine as it is, but you should add at the end the
overall ORs from the 4 strata of ethnic gorups and the 3 strata of the age groups.
Just the overall, without reporting again the OR for each study.
This can be done manually, check some mine previous meta-analyses to
understand what I mean.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
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-11-93 (2011)

Reviewer's report
Title:Cost-Effectiveness of a Mailed Educational Reminder to Increase
Colorectal Cancer Screening
Version: 1Date:16 November 2010
Reviewer: Sujha Subramanian
Reviewer's report:
Major Compulsory Revisions:
1) Sensitivity analysis was based on a 10% variation in point estimates. Better
explanation is needed as to why this approach was selected.
2) Intervention costs in the results sections -- it is not clear exactly what costs are
reported here. It is confusing to have time spent on various activities reported in
this section. There is no mention of how time spent on activities were calculated
in the methods section. Was a time-and-motion analysis used? Better
explanation is required in the methods section to better inform the reader.
3) No details are provided on the timing as to when the FOBT kits were returned
in the intervention and control groups. The reminder mainling was sent out 10
days after the kit and yet the return rate of FOBTs was calculated over a 6-month
period. It would be good to know the when the FOBTs kits were returned (to
understand the pattern of returns) in the intervention and control groups
Minor Essential Revisions
1) The 40% compliance rate with CRC screening recommendations referenced in
the introduction is outdated. Need to update this reference with new data.
2) "In addition, the improvement in screening rats (should be rates)
was about one half of what we observed in our study, and as a result, the ICER
was much higher than what we report."
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-11-93 (2011)

Reviewer's report
Title:Cost-Effectiveness of a Mailed Educational Reminder to Increase
Colorectal Cancer Screening
Version: 1Date:19 November 2010
Reviewer: Guy Launoy
Reviewer's report:
This paper reports results from a cost-effectiveness study from which results
concerning effectiveness have been already published. The new output concerns
thus only cost aspects. The relevance of results concerning cost is limited by
1 the non-reproducibility of costs in other screening organisation and moreover in
other countries. 2- the very limited effective, 3 - the poor part of cost of a
reminder in the global budget of screening experience.
Moreover, authors problematic and references are very limited to north america
experiences.
Concerning study design, econometric and statistical analysis, the study has
been well-conducted. The paper is well-writed, well-structured and pleasant to
read
Level of interest: An article of insufficient interest to warrant publication in a
scientific/medical journal
Quality of written English: Acceptable
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-11-93 (2011)

Reviewer's report
Title:Cost-Effectiveness of a Mailed Educational Reminder to Increase
Colorectal Cancer Screening
Version: 3Date:21 February 2011
Reviewer: Kelvin K Tsoi
Reviewer's report:
1. Authors did not give any response on the cost-effectiveness analysis among
different subgroups. As the results are non-reproducibility in other countries, the
subgroup analysis, especially for the race groups, will increase the interest of
readers to cite this study. Subgroup cost-effectiveness analysis can also
demonstrate which patient group will be the most cost saving. e.g. elderly or
tobacco users.
2. Although all the referenced patient-directed intervention studies based on a
10% variation for costs, I don’t think it is a good arbitrary assumption for the
physicians’ salary. The authors can use the salary range in their local hospitals. It
would be a critical challenge for the robustness of a study conclusion if the
sensitivity analysis is not reasonable performed.
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-11-93 (2011)

Reviewer's report
Title:Cost-Effectiveness of a Mailed Educational Reminder to Increase
Colorectal Cancer Screening
Version: 3Date:22 February 2011
Reviewer: Sujha Subramanian
Reviewer's report:
None
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-11-93 (2011)

Reviewer's report
Title:Cost-Effectiveness of a Mailed Educational Reminder to Increase
Colorectal Cancer Screening
Version: 4Date:3 July 2011
Reviewer: Kelvin K Tsoi
Reviewer's report:
The revised version had already addressed the points of my concern. I have no
further comment on the paper.
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-11-91 (2011)

Reviewer's report
Title:Non-Invasive Biomarkers for Hepatic Fibrosis
Version: 1Date:14 April 2011
Reviewer: Laurent Castera
Reviewer's report:
The title of the review is misleading as it deals not only with biomarkers but also
with imaging techniques. Therefore, I would suggest something like:
“Non-invasive markers for hepatic fibrosis”
General comments
Overall the manuscript is too lengthy and needs to be more focused. The
introduction chapters (Biology, type and causes of liver fibrosis) are too long and
need to be shortened. For instance, I’m not sure that the chapter on type and
cause of liver fibrosis is relevant to the topic.
The following are my comments:
1. Endpoints
Basically, it’s important to stress the limitations of liver biopsy which fostered the
development of non invasive methods and the clinically-relevant endpoints
(significant fibrosis and cirrhosis) that may vary according to liver disease
etiologies. Significant fibrosis may not be as relevant in NAFLD (where the
current therapeutic options are limited) as in Hepatitis C.
2. Imaging techniques
The chapter on transient elastography needs to be expanded as in clinical
practice the alternative to biomarkers is the measurement of liver stiffness.
Although it is not approved yet in the US (and the authors may not have personal
experience for this reason), this technique is now widely used worldwide. The
quoted references are inappropriate. Please quote the index studies in Hep C as
well as meta-analyses. Also how transient elastography compare to biomarkers
should be addressed as well as how combination of biomarkers with transient
elastography may increase diagnostic accuracy.
Finally the limitations of this technique should be discussed in more details
particularly in patients with NAFLD as evidenced by a large French series
published last year (Castera et al. Hepatology 2010).
Although MRE is an interesting technique, data are limited and it remains
restricted to research purposes thus far. Another more promising technique
(ARFI) should be mentioned although results are still preliminary.
3. Performance of biomarkers
The chapter on biomarker is too lengthy and needs to be shortened. The review
would be more appealing to readers if performances of biomarkers were
summarized in tables rather than detailed in the text. I would suggest
summarizing the performances according to endpoints and causes of liver
diseases, viral hepatitis, NAFLD, etc… I would also emphasize that the most
used and validated biomarkers are currently APRI (free) and Fibrotest (patented).
Minor comment
I’m not sure that figure1 add much to the topic.
A figure summarizing how the authors suggest to use non invasive methods in
clinical practice would be more useful to the reader.
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-11-91 (2011)

Reviewer's report
Title:Non-Invasive Biomarkers for Hepatic Fibrosis
Version: 2Date:26 May 2011
Reviewer: Tim Cross
Reviewer's report:
The manuscript has been improved considerably since the last submission and
all the points have been addressed. Some issues are touched on briefly but I feel
this is inevitable given the breadth of the review.
I have no further 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 have received travel awards from MSD.
Review for 10.1186/1471-230X-11-91 (2011)

Reviewer's report
Title:Non-Invasive Biomarkers for Hepatic Fibrosis
Version: 2Date:26 May 2011
Reviewer: Laurent Castera
Reviewer's report:
The manuscript has been improved.
There are still however some issues that need to be addressed.
Transient elastography
The quoted references are still inappropriate. For instance ref 35 deals with
methotrexate.
Please quote the index studies in Hep C (Ziol Hepatol 2005 and Castera Gastro
2005) as well as meta-analyses (Friedrich-Rust Gastro 2008). Ref 39 is
incomplete: please also quote the first study suggesting that the combination of
fibroscan and biomarkers may increase diagnostic accuracy (Castera Gastro
2005).
Performance of biomarkers
The chapter on biomarker is still too lengthy and needs to be shortened.
The details regarding the different tests available need to be summarized.
Strategies combining biomarkers (APRI and Fibrotest) (Sebastiani J Hepatol
2006 and Hepatology 2009) should be mentioned and discussed.
Table 2: Actitest is not a marker of fibrosis but of inflammation.
The title needs to be changed as previously suggested
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.
Review for 10.1186/1471-230X-11-90 (2011)

Reviewer's report
Title:Role of inducible nitric oxide synthase pathway on methotrexate-induced
intestinal mucositis in rodents
Version: 1Date:24 May 2011
Reviewer: Guntram Grassl
Reviewer's report:
In their manuscript “Role of inducible nitric oxide synthase pathway on
methotrexate-
induced intestinal mucositis in rodents” the authors demonstrate that NOS
inhibitors ameliorate methotrexate-induced intestinal damage. In addition they
show that iNOS-/- mice do not develop strong inflammation upon methotrexate
treatment.
The manuscripts provides novel insights into the role of NO in
methotrexate-triggered mucosal inflammation. However, apparently some parts
were mixed up during the preparation of the manuscript. This needs to be
corrected, so that these parts can be evaluated properly.
Major comments:
1. Mix up in Figure legends/missing figures: Figure legend 4 does not correspond
to any figure in the manuscript.
2. Figure legend 5 corresponds to figure 4.
3. Figure 5 does not have a legend at all.
4. Figures 4 and 5 and their respective Results sections are switched.
Minor comments:
1. The references don’t correspond to the numbers in the text in some cases (eg
introduction, page 4, reference 18 corresponds to reference 21 in the Reference
list) – all references should be checked and corrected.
2. Figure 3: legend reads units/mg of tissue, figure reads /g of tissue. This needs
to be corrected.
3. The addition of labelling within the figure in figure 4 would make it easier to
understand the panels.
4. Table 2: stating the range as (…+/-…) would make it clearer
5. It’s not clear if Figure 3 has data from duodenum, jejunum and ileum combined
or only one of the sections.
6. Why are there only data of the jejunum in Table 3?
7. Table 4: commas should be replaced by points.
8. ‘C57BL’ should probably read ‘C57BL/6’
9. Discussion, page 14: ‘tumor necrosis alpha’ should read ‘tumor necrosis factor
alpha’
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-11-90 (2011)

Reviewer's report
Title:Role of inducible nitric oxide synthase pathway on methotrexate-induced
intestinal mucositis in rodents
Version: 1Date:26 May 2011
Reviewer: jun kobayashi
Reviewer's report:
The authors showed that NOS inhibitors such as aminoguanidine and L-NAME
prevented MTX-induced intestinal damages by inhibiting intestinal iNOS
expressions and subsequent nitrosative stresses and MPO activities. The
experimental designs, the methods, and the results are all easy to understand,
suggesting a possibility to extend an investigation to developing promising
therapeutic solution in this field.
Major Compulsory Revisions:
(1) The descriptions for Fig.4 and Fig.5 in the results and legends does not
match Figs (4 and 5) at all and not enough for all figures. Please check and
rewrite.
(2) The authors showed MTX-induced protein levels of intestinal iNOS. Did you
measure iNOS activities? For example, How about intestinal tissue levels of
nitrite and nitrate.
(3) Where the origin of iNOS? Is it from enterocytes or circulating leukocytes?
(4) Different from duodenum and jejunum, there is no beneficial effect of L-NAME
treatment on villus height recovery in ileum, why?
Minor Essential Revisions:
There are a couple of miss spells in this manuscript.
(1) Introduction, paragraph 4, line 6 from bottom.
nitrotirosine------nitrotyrosine
(2) Discussion, last paragraph, line 9 from bottom.
NOSi---------iNOS
Level of interest: An article of importance in its field
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-11-90 (2011)

Reviewer's report
Title:Role of inducible nitric oxide synthase pathway on methotrexate-induced
intestinal mucositis in rodents
Version: 2Date:11 July 2011
Reviewer: jun kobayashi
Reviewer's report:
The authors have answered all questions I had. The article is acceptable as it is.
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-11-90 (2011)

Reviewer's report
Title:Role of inducible nitric oxide synthase pathway on methotrexate-induced
intestinal mucositis in rodents
Version: 2Date:21 July 2011
Reviewer: Cuong Tran
Reviewer's report:
No further 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