JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-12-166 (2012)

Reviewer's report
Title:IgG and IgG4 antibodies in subjects with irritable bowel syndrome: a case
control study in the general population
Version: 1Date:20 August 2012
Reviewer: Thierry PICHE
Reviewer's report:
This paper is a negative study showing no association between IBS symptoms
and IgG (4) against food. The topic is of interest since food intolerance seems to
play a role in the pathophysiology of IBS symptoms. Authors have chosen to
point out the role of late allergic phase using IgG against food.
The paper is well written and presented although there is some limitations that
need to be clarify:
Major points
The major point relates to the presentation of data that should be stratified
between IBS subtypes. In fact, taking IBS as a whole group includes the risk to
mask a putative association since the pathogenic role of allergic factors seems to
be more stringent in IBS patients with diarrhea predominance.
It is also important to better detail how was performed the diagnosis of IBS. Did
patients only answered to questionnaires at a time or IBS diagnosis was done
during a medical visit in the past ?
In this line, did patients had colonoscopy with histologic analysis to exclude
microscopic colitis or colitis associated with mucosal mast cell/eosinophils
increased numbers ?
The frequency of atopy and allergic rhinitis was slightly higher in IBS patients,
confirming the importance to separate between IBS subtypes and to test the
analysis also in patients having allergic symptoms.
Minor points
The possibility of cross reactivity between other major antigens coming from diet
but also inhalants should be briefly added in the discussion section.
The hypothesis of using IgG4 against food as IBS predictors needs to be
softened because of the complexity of various allergic responses/phases except
IgG4 and also cross reactivity between multiple antigens that are both possibly
involved in the pathophysiology of IBS. Therefore data in table 2 are not
surprising and should be limited in the manuscript only.
Details concerning medications (histamine antagonist, mast cell stabilizers), IBS
duration, origin of IBS (post-infective?), exclusion of celiac disease should be
given.
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-12-166 (2012)

Reviewer's report
Title:IgG and IgG4 antibodies in subjects with irritable bowel syndrome: a case
control study in the general population
Version: 2Date:24 October 2012
Reviewer: Thierry PICHE
Reviewer's report:
The paper has been improved according to the comments and may be suitable
for publication. Many thanks for your contribution in the field.
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.
Review for 10.1186/1471-230X-12-166 (2012)

Reviewer's report
Title:IgG and IgG4 antibodies in subjects with irritable bowel syndrome: a case
control study in the general population
Version: 2Date:2 November 2012
Reviewer: Lena Öhman
Reviewer's report:
No additional comments.
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 1Date:18 May 2012
Reviewer: Guy Eslick
Reviewer's report:
This is an interesting topic for a meta-analysis. However, there are some
important issues which need to be addressed.
THERE ARE TYPOGRAPHICAL AND GRAMMATICAL ERRORS
THROUGHOUT THE MANUSCRIPT WHICH NEED TO BE CORRECTED.
1. METHODS: Could the authors please update their literature search from Dec
2011.
2. METHODS: Could the authors also please include MEDLINE as a database to
conduct their searches in addition to the other databases already selected.
3. DATA EXTRACTION: Please define what "RR" is for the reader.
4. RESULTS: All results (RR; 95% CI) can be to 2 decimal places.
5. PUBLICATION BIAS: The authors could use the Classic fail-safe method. See
Orwin R. A fail-safe N for effect size in meta-analysis. Journal of educational
statistics 1983;8:157-159.
6. DISCUSSION: Did females drink more Green tea than males?
7. TABLE 2: All the estimates with several studies with a large sample size have
no heterogeneity, while estimates with a couple of studies and small sample size
are very heterogeneous, please mention in DISCUSSION.
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 1Date:23 May 2012
Reviewer: Alessandra Tavani
Reviewer's report:
The subject is interesting, but the meta-analysis has not been conducted
properly. First the authors should follows the usually used MOOSE guidelines
and the bibliographic research is not correctly done as a few papers on the
relationship between green tea consumption and esophageal cancer are missing.
The authors do not indicate if they have done also manual search based on
references of the included papers, which is essential. The number of total cases
and exposed cases in the categories considered in the analyses should be
reported. Also the number of studies and subjects included in the subgroup
analyses should be reported.
Minor points:
The abstract is not enough informative (eg the authors do not indicate how many
prospective and case-control studies are included)
OR and RR are used as synonymous and they are not
A meta-analysis can’t be based on one only nested-case-control study
The language must be improved
Level of interest: An article of importance in its field
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 1Date:2 June 2012
Reviewer: Ellen E Kampman
Reviewer's report:
This paper bij Zheng et al describes a meta-analysis of the epidemiological
literature on green tea consumption and esophageal cancer. This is an important
topic given the incidence of esophageal cancer worldwide and the potential of
green tea to reduce the risk. The meta-analysis appears to be conducted
according to the rules, the paper is well written, however the english needs
considerable editing.
Major Compulsory Revisions
. Abstract should contain methods used as well as heterogeneity of study results
. Q statistic is described in the method while the I2 is given.
. Sensitivity analyses could possibly be added.
. Would a dose-response analysis be possible?
. Could a case-control study from Iran by Islami et al, 2009 be missed? If yes,
how could this have happened?
. Page 5 Highest versus lowest... heterogeneity should be discussed.
. method used for the assessment of tea consumption in the different studies
could be included and possibly used for stratification.
. Could the studies be stratified on the number and type of confounding variables
adjusted for?
. Could the exact similar finding between prospective versus case-control and
Japan versus China not simple be due to including the same studies in the
analyses? See also table 2.
. In the discussion, the authors try to provide a potential mechanism explaining
the protective effect in women and not in men. However, although estrogens may
influence esophageal cancer risk, it is not clear how green tea could be
associated with hormonal effects. Do women drink more green tea, is there more
variation in green tea drinking among women? Do women drink and smoke less,
etc etc?
. The discussion should include some discussion on reverse causation which
may explain the differences observed between case-control and cohort studies.
More detail needs to be provided about the fact that all studies among women
are case-control studies.
. Brief remark about population versus hospital based case-control studies in the
discussion is not clear and should be more focused on how this could have
influenced the results of this meta-analysis.
. Specific estimates on smoking and alcohol should be excluded from the
discussion.
Minor Essential Revisions
. Two decimals should be used instead of three
. References need editing, e.g. 10-12
. In the Discussion references 18 and 19 are focused on esophageal and not on
colorectal cancer.
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 2Date:4 September 2012
Reviewer: Alessandra Tavani
Reviewer's report:
After revision the paper has greatly improved. However there is still an important
limitation. The keywords the authors used are imprecise. The term “tea” is not
enough when in a bibliographic research you need to obtain all papers.
Databases usually search keywords only in the text and not in Tables and tea
could be included in a Table together with other foods without comment in the
text, especially if it is not related to the studied disease. Thus the authors should
use “tea OR food OR diet OR beverage OR drinking…….”. Maybe they will not
find other papers, but this must be checked. Otherwise authors risk to exclude
mainly null papers, which is a big bias for a quantitative overall risk estimate of
the risk.
There are other smaller limitations which do not preclude paper publication, but
render the paper less informative than it could be:
1) As for the dose-response analyses asked by one referee, the authors say that
they could not perform the analysis because papers have used inconsistent
measures of the amount of tea consumption. This is an intrinsic limitation of all
meta-analyses. However, what it is usually done is that the authors select all
papers reporting at least 3 categories of consumption and pool their results for a
low/medium/high intake.
2) The authors should also report drinkers vs non drinkers; to obtain the category
“drinkers” they should pool within each study all categories of drinkers.
3) The sensitivity analysis has not been shown.
4) It is not indicated to which category of consumption the RR/OR refer to:
highest vs lowest in each paper? If this is the case the authors should also do
report a RR/OR estimate excluding the paper considering only drinkers vs non
drinkers.
Possibly all these suggested analyses will not change the message of the paper,
but they add much information and render the paper more methodologically
correct.
Level of interest: An article of importance in its field
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 2Date:7 September 2012
Reviewer: Guy Eslick
Reviewer's report:
None
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-12-165 (2012)

Reviewer's report
Title:Green tea consumption and risk of esophageal cancer: a meta-analysis of
epidemiologic studies
Version: 2Date:9 September 2012
Reviewer: Ellen E Kampman
Reviewer's report:
The authors have responded to my comments. Because of the language barrier,
it is difficult to judge, however, whether all changes suggested were indeed
included in the text.
The fact that women have a decreased risk could not only be due to hormonal
factor, but, and I do find this more important, to the fact that female studies were
case-control studies, were conducted in China, and that the number of studies
were limited. I would suggest the hormonal mechanism only after mentioning all
the other possibilities.
Level of interest: An article whose findings are important to those with closely
related research interests
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.
Review for 10.1186/1471-230X-12-164 (2012)

Reviewer's report
Title:Comparison between the recovery time of alfentanil and fentanyl in
balanced propofol sedation for gastrointestinal and colonoscopy: a prospective,
randomized study
Version: 1Date:19 August 2012
Reviewer: Barbara Braden
Reviewer's report:
General comments
This randomized, double-blind study by Ho et coworkers is clearly designed and
well presented. It compares alfentanil and fentanyl for additional sedo-analgesia
in patients undergoing combined gastroscopy and colonoscopy under deep
sedation with midazolam and propofol.
The total doses of 0.05 mg of fentanyl and 0.5 mg of alfentanil are relatively small
in a young patient cohort (more than 90% <75 years of age) and probably
contributed only marginally to the deep sedation which was mainly achieved by
intravenous propofol. This might explain why no differences between both groups
apart from the costs have been detected. Previous studies showing differences
between alfentanyl and fentanyl used higher doses and no propofol.
Minor essential revisions:
Abstract:
(1) Not all readers will be familiar with New Taiwan Dollars. The percentage of
excess costs between fentanyl and alfentanil or the cost difference in US Dollars
would be more informative for most readers.
Introduction:
(2) What does “minimal residual effect for endoscopy” mean in terms of
midazolam, fentanyl and alfentanil?
Discussion
(3) It should be discussed whether deep sedation is really desirable or should
better be avoided for standard colonoscopies (10% minor cardiopulmonary
complications in mainly healthy subjects in this study). Pain sensation is a valued
alarm signal for the endoscopist who might risk perforation if he ignores it and
pain during colonoscopy often indicates suboptimal endoscopic techniques.
(4) Mean total procedure times of 15 minutes for gastroscopy, changing scopes
and colonoscopy appear rather short in the light of the recommended 6 min
withdrawl time. Please comment.
(5) What are the regulations for propofol sedation (deep sedation) in Taiwan?
Is the administration of propofol restricted to anasthetists? Is ECG monitoring or
capnography mandatory for endoscopic procedures under deep sedation?
The paper will need careful revision of spelling/grammar.
Discretionary Revisions:
Anaesthetic costs:
(7) In many countries, propofol is administered safely by non-anaesthetists (Rex
et al., Gastroenterology 2009, 137:1229), even in general practices. In other
countries such as the UK, propofol sedation requires administration by an
anaesthetist. Is there any evidence that the very costly presence of an
anaesthetist improves the safety outcome?
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 declare that I have no competing interests.
Review for 10.1186/1471-230X-12-163 (2012)

Reviewer's report
Title:Rumination syndrome in children and adolescents: a school survey
assessing prevalence and symptomatology
Version: 2Date:6 June 2012
Reviewer: Guillaume Gourcerol
Reviewer's report:
The question raised in the paper from Rajindrajith and colleagues, eg the
prevalence of rumination among children, remains to date unsolved as
underlined by the authors. To this perspective, the study brings some novelty.
However, the data presented in this paper, eg the prevalence is up to 5%, are to
some extent unexpected. In fact, rumination syndrome is believed (wrong or
right) to be extremely uncommon, at least in western countries where it has been
studied more extensively. To me, there is one major pitfall in this study that
needs to be clarified. I am not sure whether the authors have picked up from their
survey the symptoms of rumination or symptoms of GERD. In fact, the authors
used an auto-questionnaire, while the rome III criteria have not been designed to
be used as self-administered questionnaires. Indeed, it might be difficult for an
adult (and even more for a child) to make the difference between GERD
symptoms (for instance regurgitation of food) and rumination symptoms
(regurgitation of food that has to be reshewed). Confusion can be also increased
by using translated questionnaires that have not been validated vs the original
English one. The confusion appears even more obvious to me when addressing
the nocturnal occurrence of symptoms, that is present in the exclusion criteria
“-b. do not occur during sleep”, while “13.6% had difficulty in sleeping due to
symptoms of rumination”. Therefore, to clarify this issue, and to ascertain that the
unexpected prevalence of rumination syndrome in Sri Lanka holds true, the
authors should provide also the prevalence of GERD symptoms, including
heartburn and regurgitation.
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-12-163 (2012)

Reviewer's report
Title:Rumination syndrome in children and adolescents: a school survey
assessing prevalence and symptomatology
Version: 2Date:5 July 2012
Reviewer: Kathleen Blondeau
Reviewer's report:
The authors studied the prevalence of rumination syndrome in a group of
otherwise healthy children and adolescents in Sri Lanka. They conclude that the
overall prevalence of RS is 5.1%, with an impact on sleep and school in less than
15% of children.
Major Compulsory Revisions
The authors state that they investigated the prevalence of RS in otherwise
healthy children. Which other disease were excluded? Can this be better
specified.
As statistics are an important part of the data analysis, the authors may need to
better describe in the methods section the statistical test they used for
comparison of the different parameters as this is unclear.
The specific questionnaires used in the study should be better clarified in the
methods section, including if the Rome III questionnaire is appropriate for
children and which questionnaires where used to assess stress factors etc….
Minor essential Revisions
On p3 the authors state that there is no statistical significance (p<0.05). I assume
this is an error
Did the authors assess the frequency of rumination episodes and was there any
association with other factors such as sex, stress, weight loss,…..
Discretionary Revisions
Are there any population data in a dults and how does this compare to the
pediatric population?
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, but I do not feel adequately qualified to assess the
statistics.
Review for 10.1186/1471-230X-12-163 (2012)

Reviewer's report
Title:Rumination syndrome in children and adolescents: a school survey
assessing prevalence and symptomatology
Version: 3Date:21 September 2012
Reviewer: Kathleen Blondeau
Reviewer's report:
The authors have corrected the manuscript according to the reviewer's
suggestions.
The questions raised in the first revision were appropriatly answered by the
authors.
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-12-163 (2012)

Reviewer's report
Title:Rumination syndrome in children and adolescents: a school survey
assessing prevalence and symptomatology
Version: 4Date:19 October 2012
Reviewer: Guillaume Gourcerol
Reviewer's report:
no additional concerns
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-12-162 (2012)

Reviewer's report
Title:HCV genotype 1a shows a better virological response to antiviral therapy
than HCV genotype 1b
Version: 2Date:15 September 2012
Reviewer: Antonio Gasbarrini
Reviewer's report:
Major compulsory revisions
1) Inno Lipa Versant HCV 2.0 has good sensitivity and accuracy in differentiating
gen 1a from gen 1b HCV. However, in a producer supported comparison, gen 1
subtype could not be determined in 2% of 129 patients (Verbeeck J et al. J Clin
Microbiol 2008;46:1901).
The Authors should indicate in the "results" section the number of patients with
an undetermined subtype, if they had some.
2) In this large observational study on gen 1 patients, the SVR rate was similar
for subjects treated with alpha 2a and alpha 2b pegylated interferon. Although it
was not obtained in a randomized trial, this result is different from the one
obtained by Ascione and coworkers with the same pegylated interferons and
ribavirin doses (Gastroenterology 2010;138:116). This "real life" difference
should be discussed.
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-12-160 (2012)

Reviewer's report
Title:Gene and functional up-regulation of the BCRP/ABCG2 transporter in
hepatocellular carcinoma
Version: 1Date:10 September 2012
Reviewer: Suresh Ambudkar
Reviewer's report:
The revised manuscript is significantly improved. Authors have addressed most
of our concerns adequately. However, authors need to make a minor correction
in the last sentence in the abstract—it should be changed to—“The rapid
up-regulation of ABCG2 due to exposure to doxorubicin emphasizes the
importance of this transporter in accounting for drug resistance in liver tumors.”
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-12-161 (2012)

Reviewer's report
Title:Prevalence and risk factors of gastroesophageal reflux symptoms in a
Chinese retiree cohort
Version: 1Date:15 June 2012
Reviewer: P. Marco Fisichella
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
4. Does the manuscript adhere to the relevant standards for reporting and data
deposition? n/a
5. Are the discussion and conclusions well balanced and adequately supported
by the data? Yes
6. Are limitations of the work clearly stated? Yes
7. Do the authors clearly acknowledge any work upon which they are building,
both published and unpublished? n/a
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.
Review for 10.1186/1471-230X-12-161 (2012)

Reviewer's report
Title:Prevalence and risk factors of gastroesophageal reflux symptoms in a
Chinese retiree cohort
Version: 1Date:2 September 2012
Reviewer: Greger Lindberg
Reviewer's report:
This study aimed at investigating the prevalence of GERD in a population of
Chinese retirees. There are several problems with the approach that the authors
have taken to address this question.
Major compulsory revisions:
1. This study is based on questionnaire data. It is unclear if data were obtained
by staff interviewing subjects, as described in "Questionnaire about reflux" or if
the questionnaire was filled out by the subjects themselves as could be deduced
from the preceding section "The study cohort".
2. Has the questionnaire been validated? Does it pick up patients with GERD?
There is no information about this in Methods. If the questionnaire has not been
validated, it is difficult to judge the value and validity of results.
3. The key question for the symptom heartburn is perhaps flawed. The feeling of
heartburn is usually not described as a "burning pain" but perhaps as a "burning
sensation". I am uncertain how the two words pain and sensation translates to
Chinese langauages but in English they are separate. Again I wonder if this
particular question has been validated for eliciting the symptom heartburn or for
finding people with GERD.
4. I am intrigued by the association of reflux symptoms with a past (or present)
history of "chronic gastritis". What was the definition of chronic gastritis? Was it
symptom based or based on histology? Please consider two possibilities: chronic
gastritis due to H. pylori infection might be expected to lead to decreased acid
production at higher age and therefore protect against GERD; or chronic gastritis
as a symptom-based diagnosis which might equate to GERD.
Minor essential revisions:
5. Obesity is normally defined as BMI>=30, whereas overweight is defined as
BMI 25.0-29.9. Why did the authors choose a different definition? It is also
unclear if people with 28.0 were considered as overweight or obese since 25-28
includes 28.0 but so does >=28. Please revise this definition.
6. Language is fairly good but needs an update by a native English speaking
person.
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 declare that I have no competing interests
Review for 10.1186/1471-230X-12-161 (2012)

Reviewer's report
Title:Prevalence and risk factors of gastroesophageal reflux symptoms in a
Chinese retiree cohort
Version: 3Date:3 October 2012
Reviewer: P. Marco Fisichella
Reviewer's report:
Accept without revision
The did a good job in aswring the comments, in my opinion
Review for 10.1186/1471-230X-12-161 (2012)

Reviewer's report
Title:Prevalence and risk factors of gastroesophageal reflux symptoms in a
Chinese retiree cohort
Version: 3Date:3 November 2012
Reviewer: Greger Lindberg
Reviewer's report:
The authors have answered all my questions.
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-12-123 (2012)

Reviewer's report
Title:Prevalence and factors associated with nonalcoholic fatty liver disease in
shanghai work-units
Version: 1Date:7 May 2012
Reviewer: Jian-gao G Fan
Reviewer's report:
This is a large survey on prevalence of nonalcoholic fatty liver disease among
workers in Shanghai with good results, and the manuscript is well writen,
although there are some similar papers published in other journals.
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-12-158 (2012)

Reviewer's report
Title:Effect of Laparoscopic Splenectomy in Patients with Hepatitis C and
Cirrhosis Carrying IL28B Minor Genotype
Version: 1Date:8 May 2012
Reviewer: Masashi Mizokami
Reviewer's report:
Motomura T. et al. described the efficacy of splenectomy before the induction of
PEG-IFN/RBV(IFN) therapy to liver cirrhosis with IL28B minor allele(s). Because
low success rate of IFN therapy to cirrhosis or those who have IL28B SNPs
minor type is a serious problem, it is of interest that the removing spleen would
improve the viral response rate in genetically disadvantaged patients. This draft
seems to be very interesting, although there are still some problems.
Minor Essential Revisions
1. Page 6, line 14. ” Eighty-one of 125 patients achieved a VR (70.4%). “
It is described “127 patients were enrolled in the current study” in the paragraph
“Methods”. How is the difference between 125 and 127 ?
Discretionary Revisions
1. Page 5, paragraph ”Patient’ Characteristics”.
It is well-known that viral response rate to IFN therapy is correlated with HCV
genotype. Please make the analysis with HCV genotype.
2. Figure 2C
In Figure 2C, the authors mentioned that comparing Hb levels of 4 and 8 weeks
after the IFN therapy, there is no significant difference between Spx group and
non-Spx group. However, Figure 2C strongly suggested that #Hb between 0 and
4 weeks of IFN therapy might be significantly different. So, I would like to
recommend to analize all data with#Hb again.
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-12-158 (2012)

Reviewer's report
Title:Effect of Laparoscopic Splenectomy in Patients with Hepatitis C and
Cirrhosis Carrying IL28B Minor Genotype
Version: 1Date:14 September 2012
Reviewer: José M. Ladero
Reviewer's report:
Minor essential revisions
1. Virological response (VR) must be defined in the abstract as "response during
therapy". The use of this criteria as a reflect of result of therapy is confusing
because the gold standard for therapeutic response is sustained viral response
(SVR: undetectable HCV-RNA in serum 6 months after the end of therapy). This
result must be probably known in all patients and I strongly suggest to the
authors to reevaluate their analysis under the scope of SVR, as the clinical
interest of this study consists on the repercusion of splenectomy (with or without
its effect on the functional role of the analysed polymorphisms) on the definitive
results of therapy.
2. The conclusion on the relation between IL28B polymorphism and splenectomy
in terms of VR rely on a small number of splenectomized patients (11 cases) and
the difference is near the limit of significance. Thus, it seems adequate to
consider other baseline prognostic factors for response, mainly viral genotype but
also viral load and age.
Discretinary revisions:
1. What was the rate of therapeutic failure due to cytopenias (mainly
thrombopenia) in ecach group? It seems probable that more patients in the
non-splenectomy group suffered from extreme thrombopenia during therapy
leading to its interruption or at least to a reduction in IFN dosage.
2. The expression "Type C cirrhotic patients" in the abstract may be confusing as
it may be interpreted as "Child-Pugh class C". Instead, it should be better
"patients with HCV-induced cirrhosis"
3. Page 8, 3rd. paragraph, line 3: < 10(4) or 10(5)?
4. Table 2: should it be better to provide date on odss ratio with confidence
interval for categorical variables instead the huge p value.
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 competing interest to declare
Review for 10.1186/1471-230X-12-157 (2012)

Reviewer's report
Title:A comparative study of 22-channel water-perfusion system and solid-state
system with 36-sensors in esophageal manometery
Version: 1Date:26 July 2012
Reviewer: Albert Bredenoord
Reviewer's report:
In this study a 36-channel solid state high-resolution manometry system (SSM) is
compared to 22-channel water-perfused manometry (WPM). Significant but
differences were found in LES location, LES relaxation ratio and UES pressure.
WPM was better tolerated and easier to introduce. The authors should be
complimented with their efforts, it is important to compare new diagnostic
techniques (SSM) with older, established systems (WPM). I have listed some
comments below.
1. The authors state that SSM provided higher resolution images and more
information that WPM. How was this scored? What parameters were used for
this comparison?
2. The differences in LES position and LES relaxation ratio are significant but
very small and probably clinically irrelevant (on average less than 0.5 cm).
Please discuss this. How often was the difference in LES location more than 1
cm and how often more than 2 cm? What do the authors regard as clinically
relevant?
3. Please discuss that besides the differences in techniques there is also a
considerable normal variation that can explain part of the variation when
performing a second test in the same subject as shown by Bogte et al
Neurogastroenterol Motil. 2011 Jul;23(7):e271-6.
4. The point of performing the polynomial equations is not clear to me.
5. The analyses have been done using parametric pairwise comparisons. I think
that when comparing two diagnostic techniques it is better to use Blant-Altman
plots and Kappa statistics. Also, I would be very surprised if these data were
normally distributed and I think that presentation as medians and IQR would
therefore be more appropriate. Also, the statistic tests used should be
non-parametric tests.
6. A 36-sensor circumferential HRM catheter from MMS is described but to my
knowledge this catheter does not exist. Did the authors use the catheter with
unidirectional sensors instead?
7. It is described that the SSM catheter can be equipped with impedance but
WPM systems can also be used with impedance.
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 research funding from MMS
Review for 10.1186/1471-230X-12-157 (2012)

Reviewer's report
Title:A comparative study of 22-channel water-perfusion system and solid-state
system with 36-sensors in esophageal manometery
Version: 1Date:16 August 2012
Reviewer: Marcelo F. Vela
Reviewer's report:
1. Interesting small study comparing water-perfused versus solid-state high
resolution manomtery.
2. For a full paper publication the authors would have to repeat the experiment in
a larger number of patients (not volunteers) to see if diangosis is affected by type
of catheter and also look at correlation of Chicago Classification variables using
the two different systems.
3. The data they present which is mainly on healthy controls, may be better
suited for a "brief communication" or "short report".
4. The authors state that SSM provided "more information". What is not clear is
whether this increase in amount of information is clinically relevant (in other
words, will the diagnosis change? is there a risk of false positives or false
negatives with the reduced data from the WPM approach?).
5. Table 1 should show the units of measurement for each variable (mmHg, cm,
etc).
6. In addition to LES relaxation ratio, they should calculate and compare
integrated relaxation pressure.
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.
Declaration of competing interests:
Advisory Panel - GIven Imaging.
Review for 10.1186/1471-230X-12-156 (2012)

Reviewer's report
Title:Lubiprostone stimulates intestinal mucin release
Version: 2Date:6 August 2012
Reviewer: Ning Yang
Reviewer's report:
The work communicated by the author represents an extension to his previous
study about lubiprostone. In addition to chloride secretion, the present study
shows that lubiprostone also has prostaglandin-like actions on mucus release in
the mouse small intestine, which may be greater potential for the therapeutic
applications of lubiprostone.
Minor Essential Revisions
1. Background, first paragraph, please delete the “(CF)” in “cystic fibrosis (CF)
transmembrane conductance regulator (CFTR)”.
2. Mucus is a slippery discharge that comprised mucins, inorganic salts, water,
cells and so on, while mucins, a family of high molecular weight, heavily
glycosylated proteins, are the major components of mucus. In the present study,
the author were more likely measuring the relatively quantity of mucus instead of
mucins since the contents in either the standards or the perfusates are not pure
mucins.
3. In Materials and Methods, Measurement of intestinal mucin release using an
ex vivo system., please clarify how many segments were taken from each mouse
and how many mice were used in each group.
4. In Materials and Methods, Quantification of released mucins., were the sample
unknowns determined using the standard curve data from the same
nitrocellulose membrane every time? According my personal experience, the
color of the dried blots changes with even a tiny condition difference, such as
temperature, time. The dots of sample unknowns should be compared with the
dots of the standards under the same condition.
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-12-156 (2012)

Reviewer's report
Title:Lubiprostone stimulates small intestinal mucin release
Version: 3Date:20 September 2012
Reviewer: Yasutada Akiba
Reviewer's report:
no more comment
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-12-156 (2012)

Reviewer's report
Title:Lubiprostone stimulates small intestinal mucin release
Version: 3Date:28 September 2012
Reviewer: Ning Yang
Reviewer's report:
I appreciate the author for his further efforts to revise the manuscript. The
manuscript has been satisfactorily revised in-line with my comments. No further
comments are offered.
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-12-155 (2012)

Reviewer's report
Title:Candidiasis and other oral mucosal lesions during and after interferon
therapy for HCV-related chronic liver diseases
Version: 3Date:23 July 2012
Reviewer: Alessio Aghemo
Reviewer's report:
Major Compulsory Revisions
The Authors keep referring to anti-HCV therapy as IFN therapy, but de facto
patients were treated with PegIFN plus ribavirin. There are small papers showng
Ribavirin to cause salivary gland ipairment (Aghemo et al Hepatitis Monthly
2011), hence the authors should comment prvious findings and change all the
manuscript referring also to Ribavirin as a potential cause of orla lesions.
I would like to have more data on salivary flow during treatment and follow-up.
Did they return to normal in the follow-up? I would add this data in the results
section
Were salivary flow rates associated with oral lesions at baseline or on tx?
Minor essential revisions
How was Sjogren excluded? Were all patients tested for auto-antibodies at
baseline? This needs to be specified
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-12-155 (2012)

Reviewer's report
Title:Candidiasis and other oral mucosal lesions during and after interferon
therapy for HCV-related chronic liver diseases
Version: 3Date:10 September 2012
Reviewer: Takafumi Saito
Reviewer's report:
Nagao et al. reported that oral candidiasis is associated with body weight loss
and hypoalbuminemia during IFN-based antiviral therapy in patients of chronic
hepatitis C.
Major points
1. They have drawn a conclusion from the results of the 14 patients who had
checkups for oral mucosal diseases throughout the regimen of IFN treatment.
The presence of oral candidiasis before IFN therapy seems to predict body
weight loss which is a serious adverse event of IFN, because 5 of 7 patients with
oral candidiasis had already it before IFN therapy. The reviewer recommends to
emphasize this important information in the text.
2. The statistical analysis of table 3 needs to be improved. Group A consists of
only 2 patients. There is no distribution of the variables, and the use mean +- SE
is not appropriate.
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-12-155 (2012)

Reviewer's report
Title:Candidiasis and other oral mucosal lesions during and after interferon
therapy for HCV-related chronic liver diseases
Version: 4Date:11 October 2012
Reviewer: Alessio Aghemo
Reviewer's report:
The authors have answered all my queries in detail
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-12-155 (2012)

Reviewer's report
Title:Candidiasis and other oral mucosal lesions during and after interferon
therapy for HCV-related chronic liver diseases
Version: 4Date:14 October 2012
Reviewer: Takafumi Saito
Reviewer's report:
The paper is well revised.
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-12-151 (2012)

Reviewer's report
Title:Variable-stiffness colonoscope makes colonoscope easier?A
meta-analysis of the efficacy compared variable stiffness colonoscope with
standard adult colonoscope
Version: 4Date:13 April 2012
Reviewer: Javier Sola Vera
Reviewer's report:
Minor essential revisions:
Numerous misspelled words. The text includes numerous grammatical and
syntactical errors (including, extensively, the body of the submission). Required a
complete review by an expert in English.
In the "discussion" the authors state: "In the subgroup analysis in our
meta-analysis, the cecal intubation time shortened with the use of adult VSC,
while Othman et al. found no difference between these two instruments." The
problem is that there is probably an error in the article by Othman et al. While the
text says that there is little difference in cecal intubation time in favor of the VSC,
the corresponding figure does not shows any difference. This is probably due to
a typographical error, because the confidence interval in the text is -2.00, -0.06
while the figure is -2.00, 0.06 (despite the "p" in the figure is 0.04). Given this
controversy, I recommend the authors a focus on commenting on the full group
differences with respect to meta-analysis of Othman.
In the "discussion" section, paragraph on complications, add the reference 14. In
the paragraph on limitations add more limitations: no universal method for using
VSC across the studies. Large tertiary centers which limits generalization to other
practice settings.
In "conclusions" section, I can not understand the phrase "probably complicated
the procedure at the mean time." The conclusions should be more easily
understood. Hard to follow. The conclusion "the VSC could be useful for patients
undergoing total unsedated colonoscopy" is not based on any results so I
recommend removing it.
Major compulsory revisions:
In the section "results", subsection "Subgroup and sensitivity analysis" is not
explained what type of anlalisis sensitivity to assess heterogeneity. What type of
analysis performed?.
which studies were exclude and which were the results in changes to the OR and
WMDs.
Discretionary revisions:
Table 2: in "cecal intubation rate", Why include 9 studies, if the meta-analysis
included 8?
Figure 4 is not neccesary.
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
Review for 10.1186/1471-230X-12-151 (2012)

Reviewer's report
Title:Variable-stiffness colonoscope makes colonoscope easier?A
meta-analysis of the efficacy compared variable stiffness colonoscope with
standard adult colonoscope
Version: 4Date:30 April 2012
Reviewer: Praveen Roy
Reviewer's report:
Overall a well done meta-analysis.
Minor
There are few spelling errors that need to be corrected (eg word ' Studie")
Major
In the conclusion the authors report a higher cecal intubation rate ( RR 1.03).
They should explain how this translates clinically in clincal practice. This is
clinically meaningful finding.
Author indicate they did a sentivity analysis to explore heterogenity. They need to
expand on this and explain what they found and how they can explain the
heterogenity.
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-12-151 (2012)

Reviewer's report
Title:Variable-stiffness colonoscope makes colonoscope easier?A
meta-analysis of the efficacy compared variable stiffness colonoscope with
standard adult colonoscope
Version: 5Date:19 June 2012
Reviewer: Javier Sola Vera
Reviewer's report:
Minor essential revisions: still there are misspelled words and grammatical
errors.
Discretionary revisions: In the "conclusions" section. The statement "probably
attenuated the pain of patients at the same time" is not based on results becausa
data on pain were not pooled. I would delete it.
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.
Declaration of competing interests:
I declare that I have no competing interests