JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-10-28 (2010)

Reviewer's report
Title:Differential detection of nuclear envelope autoantibodies in primary biliary
cirrhosis using routine and alternative methods
Version: 1Date:9 January 2010
Reviewer: Marlyn Mayo
Reviewer's report:
Major Compulsory Revisions: none
Minor Essential Revisions: none
Minor Discretionary Revisions:
1. Figure legend 4 does not seem to match labeling of figure (? figure meant to
show purity of nuclear enveloped isolated from rat liver and ? IIF on Hep2
slides?)
2. Please clarify how many of the 103 sera were AMA positive. Just the ones in
Figure 4?
Comment:
1. The question posed by the authors is well defined: How do the different
methods of detecting nuclear envelope Abs in PBC compare with respect to
sensitivity and specificity and what are the reasons for discrepancies between
the different methods?
2. The methodology is sound and thorough. It is described well enough that
others could duplicate their methods.
3. The data confirm several previously reported findings, including an imperfect
correlation between IIF, ELISA and IB for detecting ANEA, the ability of other
autoAbs to interfere with IIF detection of ANEA, that anti-gp210 accounts for
most ANEA. However they also report several distinct findings, including
excellent results with purified rat nuclei IIF and lack of p62 reacitvity. They did
seem to have poorer results with the commerically available ELISA than others
have reported. The article is of interest mainly to pathologists, immunologists, or
hepatologists who utilize these assays. The authors have shown beautiful results
using IIF with isolated nuclei, although this may be too cumbersome a technique
to employ in clinical laboratories. Likewise, the finding that all the AMA positive
sera obscured the ability to see ANEA on IIF, even with their techniques, limits
clinical utility of that assay in PBC patients. Adding a second antigen to the
ELISA and/or using both IgG and IgM secondary antibodies in the IIF assay,
however, are easily done and are excellent recommendations that come from
this work.
4. Data is presented in an unbiased fashion. The number of percentages and
degree of overlap and separation of test results becomes overwhelming at times,
but the data are necessary and the figures help to clarify.
5. The data support the conclusion that current lab techniques can be improved
by adding other substrates.
6. Limitations are not discussed in detail, but there are not many.
7. The introduction refers to the other studies evaluating these assays fairly.
8. The title and abstract clearly convey what has been found.
9. The manuscript is meticulously drafted, albeit lengthy.
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 declar that I have no competing interests.
Review for 10.1186/1471-230X-10-31 (2010)

Reviewer's report
Title:How does comorbidity affect cost of health care in patients with irritable
bowel syndrome? A cohort study in general practice
Version: 1Date:30 November 2009
Reviewer: Pierre Pare
Reviewer's report:
This is a well conducted study with adequate analysis of the data recorded by
appropriate measures.
1. No major or minor comments.
2. Discretionary revisions:
a. Material and methods: Criteria for inclusion into the study deserve clarity. 208
Rome II defined patients confirmed by clinical diagnosis were invited to
participate. It should be clear that the remaining of 733 assessed patients were
or not IBS patients based on Rome II criteria. If so do the demographics of these
patients differ from the study group and why were they not invited to participate?
b. Discussion: Since a contral group with non IBS related chronic health
conditions was not assessed, the discussion should expand more, based on
available literature, on comparison with such groups. Although it is clear that this
cohort of general practice IBS patients drives more cost from comorbidity than
from IBS itself, this may not be unique to this chronic condition since illness
behaviour is also a feature of several health conditions.
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. In the past five years, I have
received support and funding by Novartis Pharmaceuticals Corporation for
conducting IBS studies.
Review for 10.1186/1471-230X-10-31 (2010)

Reviewer's report
Title:How does comorbidity affect cost of health care in patients with irritable
bowel syndrome? A cohort study in general practice
Version: 1Date:1 January 2010
Reviewer: George Longstreth
Reviewer's report:
The authors thoroughly studied the health care costs in 164 general practice
(GP) patients with IBS. The study is potentially important, as IBS is very
common, and the report has novelty because of its focus on GP patients. The
findings supplement other reports of the prominence of non-gastrointestinal
symptoms and associated costs in patients with IBS.
Major Compulsory Revisions
1) I am concerned about the possibility of enrichment of the study group with
patients whose costs were high. Authors report that there were 830 consecutive
GP patients with IBS defined by Rome II criteria, yet the GPs entered only 208
into the study after agreeing with the diagnosis. Authors should report exactly
what the GPs were told about the study; in particular, were they told that the
study would focus on health care costs, especially non-IBS costs? It seems
unlikely that ¾ of the patients with Rome II-positive IBS did not actually have IBS,
and authors should discuss the possibility that many of them had lower costs
than the included patients. Authors should also report what the study nurses
knew about the planned analysis, as they could have been biased in their data
collection. Specifically, did they know that non-IBS costs would be compared with
IBS costs?
2) The failure to find an association between costs and severity of IBS conflicts
with previous findings; for example the uncited publication: Longstreth GF, et al.
Am J Gastroenterol 2003;98:600-607. That article reported an association
between severity of abdominal pain/discomfort and costs in 558 subjects with
IBS. Authors should comment on the possibility that their method of measuring
severity underlies this finding. They should also comment on whether the number
of cases was too small to detect an association of severity with cost.
3) Finally, authors should provide further information on their regression analysis.
Specifically, were their more than 10 events per variable, as is recommended?
Level of interest: An article of limited interest
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-10-31 (2010)

Reviewer's report
Title:How does comorbidity affect cost of health care in patients with irritable
bowel syndrome? A cohort study in general practice
Version: 2Date:11 February 2010
Reviewer: George Longstreth
Reviewer's report:
I thinki they have responded satisfactorily.
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-10-27 (2010)

Reviewer's report
Title:Small intestinal mucosa expression of putative chaperone fls485
Version: 1Date:15 April 2009
Reviewer: Michael George
Reviewer's report:
The authors present a study of fls485 mRNA and protein localization in human
small intestinal tissue with the goal of increasing understanding of its potential to
function in differentiation of epithelial cells along the crypt-vilus axis. While such
information would be of interest in the field, there are concerns with this set of
data that will need to be addressed. No functional information was presented and
the localization analysis with regard to the CVA did not supply any relevant new
information. Improvements in the experiments and data presentation will help to
more clearly address the questions of fls485 localization and function.
Major Compulsory Revisions:
1. No molecular weight markers were run with the Western blots gels, thus
detection of fls485 cannot be confirmed. The Western blot analysis in Figure
2C-D showing significantly different staining patterns in tissues and a loss of the
double band at 50-55 KDa detected by Ab #7 in the cell lines in Figure 1 adds
further concerns to the protein analyses. Improvements may require a better
antibody. It would be very interesting to see fluorescent images of GFP tagged
fls485 in healthy and diseased tissues, and may add considerable insight into
both localization and function.
2. The data in Figure 3A-B are confusing. Because the control data is plotted, it is
unclear what the “fold change” is in comparison to. Figure 3C-D does not supply
any information that supports the graphs shown in A-B. The authors should show
expression of fls485 in celiac diseased tissue versus healthy control tissue and
demonstrate a reduction.
Minor Essential Revisions:
1. The authors should provide references for numerous descriptions of “standard
procedures”, “standard protocols”, “conventional clinical and histological criteria”,
etc. described in the Methods section.
2. Lines should be numbered for review
3. The Discussion should focus less on restating previous findings and discuss
the implications of the results obtained by the authors. This section is expected to
improve substantially once the suggested experimental improvements have been
made
Discretionary Revisions:
1. Writing is difficult to read in several places
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-10-27 (2010)

Reviewer's report
Title:Small intestinal mucosa expression of putative chaperone fls485
Version: 1Date:13 July 2009
Reviewer: Dan Hershko
Reviewer's report:
In the present manuscript, the authors describe the expression of fls485 in the
small mucosa of normal subjects and patients wuth celiac disease. this study
was followed previous findings by the group that the fls485 gene was 1 among
415 genes expressed in enterocytes. The expression and function of here they
show that fls485 protein in human tissues is unknown.
The authors have found, as previously reported, that fls485 is found with
increasing gradient from crypt to villi of normal mucosa and that the expression of
the protein is impared in celiac disease Marsh IIIa-c.
Major concerns:
1. the antibodies generated expressed two distinct bands, one of the expected
size and another unexpected band. This may lead to false interpretation of the
results observed by immunohistochemistry.
2. although the authors claim that an agreement between mRNA exists, they do
not provide the results of all experiments and the distribution of the results in
normal mucosa. attempts should also be made to reproduce the results of in-situ
hybridization.
3. Since the function and meaning of these results are still unclear the
importance of the findings are of limited interest.
Level of interest: An article of limited interest
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-10-27 (2010)

Reviewer's report
Title:Small intestinal mucosa expression of putative chaperone fls485
Version: 2Date:2 December 2009
Reviewer: Mark Musch
Reviewer's report:
The addition of additional functional data on fls485 is very important and it
establishes a probable role for this chaperone potentially in a number of
physiological and pathophysiological states. Future work will likely establish a
role for this chaperone not only in normal protein processing, but also in states of
unfolded protein responses, but this awaits further work. The clarity of the
manuscript was good and the revisions have made the potential roles of the
chaperone even clearer and provided greater insight into its actions.
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-10-27 (2010)

Reviewer's report
Title:Small intestinal mucosa expression of putative chaperone fls485
Version: 2Date:5 December 2009
Reviewer: Michael George
Reviewer's report:
Major Compulsory Revisions:
1. The authors have attempted to address the lack of functional analysis in their
characterization of fls485 in the original manuscript by utilizing a Caco2 in vitro
intestinal epithelial model system. Unfortunately, simply showing a slight increase
in fls485 transcript levels between high and low density Caco2 cultures did not
provide any functional insights. This set of experiments could have been
designed better. The authors should assay expression of known biomarkers to
demonstrate differentiation since Caco2 is a well-established model system, and
attempted to determine if alterations in fls485 expression are associated with
changes in Caco2 maturation/differentiation characteristics.
2. In situ mRNA analyses (Figure 2A/B) suggests the fls485 transcript is
widespread but more concentrated in the crypt regions and, intracellularly,
accumulating towards the luminal region of the plasma membrane. On the other
hand, immunohistochemistry suggests fls485 protein is concentrated toward the
upper regions of the villus and not in the crypts. Furthermore, the protein signal is
not accumulated at the plasma membrane as the mRNA is. Because multiple
products are recognized in Western blots by the antibodies used and differential
staining patterns are observed, depending on the Ab clone and/or cell line used,
the localization studies of tissue sections are difficult to interpret and
inconclusive. The authors devote part of the Discussion to address this issue, yet
in the Discussion, they also state that “immunostainings of sectioned
paraffin-embedded normal human small intestinal mucosa with #7, #10 or
subclones revealed an essential overlap with fls485 mRNA in situ hybridization
pattern. The authors also state in the Discussion that “… colocalization of EGFP
and fls485 immunosignaling was found in EGFP-fls485158 3T3 transfectants”.
However, there was no “co-localization” data presented, only Western blots
confirming an EGFP-fls485158 chimeric protein was expressed. The inaccurate
statements should be revised in the Discussion and the discrepancy between
tissue localization of fls485 mRNA and protein really does need to be resolved.
The authors’ suggestion of laser capture microdissection could be very effective
in this regard.
Minor Essential Revisions:
1. The writing is difficult to read in several places and should be edited more
carefully.
Discretionary revisions:
1. It would be informative perhaps to see internal localization of the
EGFP-fls485158 chimeric protein and whether this may change as Caco2 cells
grow to confluence and differentiate.
Level of interest: An article of limited interest
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-10-27 (2010)

Reviewer's report
Title:Small intestinal mucosa expression of putative chaperone fls485
Version: 2Date:26 January 2010
Reviewer: Dan Hershko
Reviewer's report:
I have carefully read the revised manuscript and the comments of the other
reviewers. It seems that much effort has been put into correcting the manuscript.
Nevertheless, the study still lacks in providing functional results and the biological
importance of the examined protein.
Review for 10.1186/1471-230X-10-26 (2010)

Reviewer's report
Title:The effects of thiopurine therapy on health-related quality of life in
Inflammatory Bowel Disease patients
Version: 1Date:1 May 2009
Reviewer: Lloyd Sutherland
Reviewer's report:
Minor typos Page 2 para 1 Line 1 The inflammatory bowel disease s(IBD)
Crohn’s disease
The author reports the results of their study of 82 IBD patients who were on
azahtioprine for 12 months. Patients took azathioprine for a variety of indications
(mainly maintenance of IBD) and their response was measured by changes in a
variety of measures both disease specific *(IBDQ) and general (SF-36). They
found that most patients had an improvement in their indices which they consider
to be the effect of the azathioprine.
Minor comments
A typo Line I para 1 (Background
The inflammatory bowel disease s(IBD) Crohn’s disease
Should be consistent with spelling of cyclosporine or cyclosporin
Only a few patients with UC were taking oral mesalamine; was that because the
topical group were mainly mesalamine as well.
Important points
Excuse my ignorance but is your unit the only unit interested in IBD in Valencia?
Is there any evidence of a referral bias,
Why were pts who started thioprurine excluded from entering the study.
What percentage of the clinic population (92) entered the study, how many
declined to participate
Why did patients withdraw from the study?
Does the 10 patients who withdrew from the study by 12 months include the 5
who withdrew by month \
Could the authors provide additional data regarding the impact on the conclusion
that the patients with UC had lower indices than the CD patients. Since some of
the CD patientswho were receiving azathoprine had few symptoms and the UC
patients had greater disease and more symptoms. This might bias the findings.
The discussion could be reduced by 25%
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
NO
Review for 10.1186/1471-230X-10-26 (2010)

Reviewer's report
Title:The effects of thiopurine therapy on health-related quality of life in
Inflammatory Bowel Disease patients
Version: 2Date:5 August 2009
Reviewer: Lloyd Sutherland
Reviewer's report:
I sm not conveinced that we need a biostatistician's comments pm this paper.
The major concern mighr have the number of multiple comparsons but the
authors have noted this in their comments and revisions
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-10-26 (2010)

Reviewer's report
Title:The effects of thiopurine therapy on health-related quality of life in
Inflammatory Bowel Disease patients
Version: 2Date:11 August 2009
Reviewer: Tomm Bernklev
Reviewer's report:
I have read through the comments from the Authors and it is my clear impression
that they have taken my comments into consideration and altered the manuscript
in accordance with this.
The problem with the IBDQ 36 version instead of 32q still remains, but the
Authors have given a good explanation as to why this is the case.
I would recommend the manuscript to be published in its present form.
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 interest
Review for 10.1186/1471-230X-10-25 (2010)

Reviewer's report
Title:Budd-Chiari Syndrome: Long term success via hepatic decompression
using transjugular intrahepatic porto-systemic shunt
Version: 1Date:2 October 2009
Reviewer: Juan Gonzalez-Abraldes
Reviewer's report:
This study reports a single center experience over 20 years with patients with
Budd-Chiari Syndrome. The center has a special experience in TIPS (since TIPS
was developed there). They gathered 20 patients. Among them 13 underwent
TIPS and 4 liver transplantation.
Major Compulsory Revisions
1. The recent study by Darwish Murad S (Ann Intern Med. 2009 Aug
4;151(3):167-75), which is the only prospective study on Budd-Chiari, should be
quoted and commented. A relevant finding of that study is that almost 50% of the
patients can be managed conservatively.
2. The authors should discuss the fact that they have not used covered stents.
This is not unexpected, since the availability of these stents is relatively recent.
The use of covered stents have been associated with a lower rate of dysfunction,
both in patients with cirrhosis (Bureau et al, Gastroenterology 2004) and
Budd-Chiari syndrome (Hernández-Guerra et al, Hepatology 2004)
3. Table 1: 3 patients (those that did not had TIPS or liver transplantation) are not
reported. They should be added to the table
Minor Essential Revisions
4. The authors should discuss that some patients previously considered of
unknown etiology can be currently diagnosed of myeloproliferative syndromes by
the analysis of JAK2 mutation.
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-10-24 (2010)

Reviewer's report
Title:Successful side-viewing endoscopic hemoclipping for Dieulafoy-like lesion
at the brim of a periampullary diverticulum
Version: 1Date:13 January 2010
Reviewer: Kazuki Sumiyama
Reviewer's report:
Thank you very much for reporting this interest case. Although authors reported
hemostasis of bleeding from a juxtapapillary diverculum using a side-viewing
scope as a rare case, it is a standard therapeutic option. I can't see any
convincing reason to publish this case.
Level of interest: An article of insufficient interest to warrant publication in a
scientific/medical journal
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-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 1Date:2 February 2009
Reviewer: Mark Pimentel
Reviewer's report:
In the manuscript by Reddymasu, et al, the authors further delineate the
association between SIBO and IBS. More specifically, the authors find that sex
and age are major determinants of the prevalence of SIBO.
The study has limited data and is small in presentation. However, the data are
vitally important in one way. Recently, a paper speculated that since many IBS
patients are on proton pump inhibitor, that the PPI is affecting the result or even
causing SIBO. While this was speculation, this study answers this question. Thus
even more important than age and sex is this relationship. This needs to be
expounded in the manuscript and included in the discussion.
Perhaps a figure would also be helpful rather than data in a paragraph to make
the paper more interesting.
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-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 1Date:16 February 2009
Reviewer: Stephen Vanner
Reviewer's report:
This study examines IBS patients with a "positive" GBT based on proposed
criteria and correlates this with a number of clinical parameters. More patients
who were female and over the age of 55 had an abnormal test.
Major comments.
1. There is no evidence that the proposed criteria for the GBT detect SIBO.
There is no control group and hence we do not know what proportion of patients
in the normal population would also have an abnormal test using these criteria. It
may be that using criteria an equal number of women over the age of 55 will also
have an "abnormal" test yet lack any symptoms.
Level of interest: An article of limited interest
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 I have no competing interests.
Review for 10.1186/1471-230X-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 1Date:29 July 2009
Reviewer: Philippe Ducrotte
Reviewer's report:
The topic of the Reddymasu's paper is interesting because it is a very important
question to know whether some IBS patients have to be treated with antibiotics.
The authors of this paper report the results of a substantial number of patients
and the paper is well written.
However, the paper cannot be accepted in the current form and the author must
answer to the following questions :
- were the 98 patients consecutive or not ? Did the author refer for a breath test
any patient seeking medical advice for IBS ?
- many patients (more than 35 %) were treated by opiates. This is very unusual in
IBS. The author have to explain why they receive this treatment.
- the authors report that SIBO was more frequent in patients older than 55. Due
to the lack of control group, it is very difficult to interpret this association. The
question is wether the high frequency of SIBO related to IBS or is it rather due to
age ? The authors have to comment this point and outline this major weakness of
their study.
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 no competing interest
Review for 10.1186/1471-230X-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 2Date:17 September 2009
Reviewer: Mark Pimentel
Reviewer's report:
The authors have addressed the concerns i had about PPI use and their lack of
finding an association.
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-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 2Date:28 September 2009
Reviewer: Stephen Vanner
Reviewer's report:
Major Compulsory Revisions
This study lacks a control group and the criteria used for the GBT have not been
validated. Hence, unless the authors can validate these criteria and provide a
proper control group, these observations cannot be interpreted with any
confidence. Refering to previous studies is not adequate because these studies
suffer from the same major flaws.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I have no competing interests.
Review for 10.1186/1471-230X-10-23 (2010)

Reviewer's report
Title:Small intestinal bacterial overgrowth in irritable bowel syndrome: are there
any predictors?
Version: 2Date:30 September 2009
Reviewer: Philippe Ducrotte
Reviewer's report:
The authors have provided satisfactory answers to most of the comments. it
remains unclear why so many patients were treated by opiates and if this factor
affected the results. It would be useful to have at least a comment in the
discussion about this point
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 interest
Review for 10.1186/1471-230X-10-22 (2010)

Reviewer's report
Title:Prevalence of Genetic Polymorphisms in the Promoter Region of the
Alpha-1 Antitrypsin (SERPINA1) Gene in Chronic Liver Disease: a Case Control
Study
Version: 2Date:5 November 2009
Reviewer: Michele Zorzetto
Reviewer's report:
In this paper Karin F. Fok and co-workers typed 297 patients with liver diseases
from various aetiologies and 297 healthy controls for three different SNPs of
alpha1 antitrypsin (c.1973T>C, S and Z), in order to understand the role of alpha
1 alleles in liver disease. They found no associations between the alpha 1 SNPs
and liver disease.
Major
1) The principal limit of this work is represented by the fact that the patients
group is composed by diseases very different one to the other. This could cause
an over or underestimation of the actual contribute of the SNPs. Moreover the
patients group is not in Hardy-Weinberg equilibrium for the c.-1973T>C SNP. If a
population is not in Hardy-Weinberg equilibrium two different events could be
happened:
· The population is stratified for a particular feature
· Some mistakes in genotyping occurred
Therefore is possible that Fok et al. stratified the patients for some features.
2) The only positive associations is between the heterozygous for S allele and
the subgroup of DILI patients. This group is very small (11 patients) then the data
is not so significant
3) Haplotype. The table 2 is not clear. It seems not an haplotype reconstruction
distribution but a multiple genotypes. Probably is better to reconstruct the
haplotype with a software dedicate ( e.g hplus http://cougar.fhcrc.org/hplus/).
4) It would be interesting also calculate the linkage between the different SNPs
(D’ or r2)
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-10-22 (2010)

Reviewer's report
Title:Prevalence of Genetic Polymorphisms in the Promoter Region of the
Alpha-1 Antitrypsin (SERPINA1) Gene in Chronic Liver Disease: a Case Control
Study
Version: 2Date:20 November 2009
Reviewer: Ahmad Settin
Reviewer's report:
This study concerning the prevalence of c.-1973T>C, Z allele and S allele in a
cohort of patients with liver disease of various aetiologies compared with healthy
controls sounds an interesting study. Generally it is well written, well presented
and well organized with statistically validated data. The main weakness,
however, is the relatively non homogeneous sample of cases with liver disease, if
authors would have focused on one disorder e.g HCV and enriched their sample
of same affected cases, I think will be far more better, In spite of this we still can
speculate that at minimum these genetic polymorphisms did not appear to be a
risk factor for chronicity of liver affection by these disorder.
These include more informative tables about the distribution of all genotypes and
alleles pertaining to A1AT gene significance of difference related to Allele
frequencies in both studied groups and also about
the analysis of frequencies related to the haplotypes analysis of the 3 alleles
together e.g C/S/Z, C/S/M, C/Z/M, T/S/Z, T/S/M, T/Z/M etc. I think figures can be
omitted as well, My final decision is to accept but after minor revision.
Review for 10.1186/1471-230X-10-22 (2010)

Reviewer's report
Title:Prevalence of Genetic Polymorphisms in the Promoter Region of the
Alpha-1 Antitrypsin (SERPINA1) Gene in Chronic Liver Disease: a Case Control
Study
Version: 3Date:18 December 2009
Reviewer: Sally Chappell
Reviewer's report:
The authors have addressed the majority of comments raised during the review
process. The replacement of table 2 is a vast improvement on the previous
version, although I would still like to see a little more detail on how the
diplotypes/haplotypes were constructed. Was a software package (eg HPlus,
Haploview, Unphased) used for this analysis? If so, more detail needs to be
given. Where individuals are either homozygous at all of the polymorphic sites, or
only heterozygous at one site, it is straightforward to determine the haplotypes.
However, this is more difficult with heterozygosity at 2 or more sites, and I would
be interested to know how this was done. Values for linkage disequilibrium (r2)
would also be of interest, and could be added here for the controls and cases
separately.
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-10-22 (2010)

Reviewer's report
Title:Prevalence of Genetic Polymorphisms in the Promoter Region of the
Alpha-1 Antitrypsin (SERPINA1) Gene in Chronic Liver Disease: a Case Control
Study
Version: 3Date:28 December 2009
Reviewer: Michele Zorzetto
Reviewer's report:
In the reviewed paper the authors well answered at all my comments and I have
not other suggestion for this version
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-10-22 (2010)

Reviewer's report
Title:Prevalence of Genetic Polymorphisms in the Promoter Region of the
Alpha-1 Antitrypsin (SERPINA1) Gene in Chronic Liver Disease: a Case Control
Study
Version: 4Date:2 February 2010
Reviewer: Sally Chappell
Reviewer's report:
All comments have been addressed by the authors since the previous version,
and I have no further suggestions.
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-10-21 (2010)

Reviewer's report
Title:Short versus standard treatment with Pegylated interferon alfa-2a plus
ribavirin in patients with hepatitis C virus genotype 2 or 3: the CLEO trial.
Version: 1Date:1 September 2009
Reviewer: Piero Almasio
Reviewer's report:
The paper of Mecenate et al. addresses an important issue of treatment of
HCV-related disease: they assessed if a shorter duration of therapy (12 weeks) is
equivalent to standard schedule (24 weeks) in geno 2 and 3 patients. The final
results demonstrate that in subjects with an RVR (HCV-RNA clearance after one
month of therapy) the rate of SVR is equivalent in the two groups. The paper,
although is partially confirmatory of previous studies, is well designed, with
adequate sample size.
Major comments.
# The main basal features of all included patients should be described in a
separated table.
# Another table should describe the comparison between patients with or without
RVR (including statistical analysis).
# The “per protocol” analysis should be avoided in every part of the paper.
# A table with univariate analysis of SVR should be included (i.e. SVR vs no
SVR). After that another table with multiple logistic regression analysis with OR
(plus 95% C.I.) and beta coefficients should also be included.
# All percentage should be given with one decimal
# The continuous variables with normal distribution should be analyzed with
parametric tests
# The source of infection is a relevant information that should be given
# Figure 2 can be omitted
Minor comments
The English language needs a deep revision
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' below
Review for 10.1186/1471-230X-10-21 (2010)

Reviewer's report
Title:Short versus standard treatment with Pegylated interferon alfa-2a plus
ribavirin in patients with hepatitis C virus genotype 2 or 3: the CLEO trial.
Version: 1Date:24 November 2009
Reviewer: John H Kalbfleisch
Reviewer's report:
Major Compulsory Revisions
(1) The abstract indicates this comparison (86% vs 77%)is statistically significant
(p < 0.05), however, the simple 2x2 Chi-square analysis yields P > 0.10 (not
significant).
Minor Essential revisions
(2) Table 2 needs a footnote. “Values are N(%) unless N = 0.”
(3) Figure 2 is difficult to read. The authors should consider a 2-D figure and
changing the font to something that displays clear readable characters in the
labels of axes and figure body.
(4) Page 9. Logistic regression analysis. The results are clearly stated (but not
supported by table information or figure displays). The statistical model to assess
covariate effects seems to be a “main-effect-only” model. The authors need to
comment (in methods or discussion) as to the appropriateness of the
main-effect-only model choice (which is the basis of the multiple logistic
regression analysis). In particular, were interaction effects among covariates
analyzed or simply ignored? The authors can consider analyzing only the
interaction effects among 4 SVR-covariates listed on page 9. Some readers will
find a table or figure that elaborates on the covariate-odds-ratios a valuable
addition in results.
Additionally, the authors should indicate (in methods) which of the study
participant cases were used (all 210 as one group, or was study group used as a
factor in the logistic regression?).
Discretionary Revisions
(5) Page 7, top line. “alfa” should be “alpha”.
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. John H. Kalbfleisch
Review for 10.1186/1471-230X-10-21 (2010)

Reviewer's report
Title:Short versus standard treatment with Pegylated interferon alfa-2a plus
ribavirin in patients with hepatitis C virus genotype 2 or 3: the CLEO trial.
Version: 2Date:11 December 2009
Reviewer: Piero Almasio
Reviewer's report:
1. In the abstract the dose of Ribavirin is 800-1,200 mg/day, but in the method
section tha Authors indicate that the dose was 1,000-1,200 according to body
weight. Please solve this discrepancy
2. The legend of table 2 is misleading: the correct definition should be
“PATIENTS CHARACTERISTICS ACCORDING TO ACHIEVEMENT OF RAPID
VIROLOGICAL RESPONSE”
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-10-20 (2010)

Reviewer's report
Title:Chromosomal imbalances are uncommon in Chagasic megaesophagus
Version: 2Date:24 August 2009
Reviewer: Ming-Rong Wang
Reviewer's report:
1. None of CM group members developed ESCC, and alterations detected in the
CM group could not represent the exact changes in the early stage of ESCC. In
fact, more copy number changes have been observed in premalignant lesions of
several tumors, including dysplasia of the esophagus. In addition, what the CM
cases did not develop ESCC may be the result of the short follow-up time.
2. The case number of the present study was too limited, especially not enough
for the statistic analyses of the correlations between the copy number changes
and clinicopatholgic parameters. The case number directly affects the reliability
of the conclusions.
3. The quality of Figures 2C and D is not acceptable. It is very difficult to correctly
determine the copy number of the genes tested from such pictures.
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-10-20 (2010)

Reviewer's report
Title:Chromosomal imbalances are uncommon in Chagasic megaesophagus
Version: 2Date:15 October 2009
Reviewer: Clara Isabel González
Reviewer's report:
This article deals with the identification of potential markers of risk to esophageal
cancer in patients with Chagasic megaesophagus of Brazilian origin. Chagas
megaesophagus increases the risk of esophageal carcinoma, its detection is
difficult and the diagnosis is later resulting in a poor prognosis, therefore the
question is relevant. The authors have some publication related to the subject.
The authors found that the genomic imbalances common in the esophageal
carcinomas were not present in chagasic megaesophagus and therefore will not
be effective markers for risk assessment of ESCC. It is a negative result but the
information may be important for other researchers.
The investigation was performed in paraffin-embedded tissue and analyzed
genomic imbalances common in esophageal carcinomas using the fluorescence
in situ (FISH) technology. The methods are valid and well described, the
interpretation of the results is balanced and the discussion is adequately
supported by the data, the literature data on the topic are clearly acknowledged,
the references are recent and appropriated but excessive, the title and abstract
accurately convey what has been found and the writing is acceptable.
Coments:
Minor essential revision:
a) In the current form, table 1 is very difficult to read and understand, review it.
Some abbreviations are not defined; an example is “T”.
b) Tables 2 and 3 are misconfigured, therefore, it is suggested to correct its
formatting in the revised manuscript.
c) Figure 1 F shows lower resolution compared to the other quadrants.
d) The resolution of figure 2 could be improved especially in quadrants C and D.
Discretionary revisions:
a) The study analyzed tissues obtained from patients with diagnosis of chagasic
megaesophagus. However, the authors did not mention how the diagnosis was
established and confirmed.
b) Highlight the data in the frequency of Chagas disease in Brazil and South
America and its appearance in non-endemic areas.
c) The number of cases in each category as gender, alcoholism and tabaquism is
too small to evaluate the risk factors. Mention the limitation of the low number of
samples.
d) Reduce the number of references to those which are essential.
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-10-20 (2010)

Reviewer's report
Title:Chromosomal imbalances are uncommon in Chagasic megaesophagus
Version: 2Date:3 November 2009
Reviewer: Ulysses Jr Ribeiro
Reviewer's report:
This is an interesting manuscript about the role of chromosomal unbalances in
chagasic megaesophagus patients with high risk of esophageal squamous cell
carcinoma, using FISH technology. The authors have published several papers
in high impact Journals discussing the same subject, studying other genetic
alterations. In this particular study, they could not find sufficient genomic
imbalances that could be used as markers for risk assessment of esophageal
squamous cell carcinoma in patients with chagasic megaesophagus. This is a
reasonable study and the data are well presented.
Minor Essential Revisions
In the title page, please include the Key words.
Specific comments:
Abstract:
Background: Please change: … chronic patients develop megaesophagus or
megacolon. The esophagus dilation is known as chagasic megaesophagus…..
Background: Please change for INTRODUCTION
First paragraph: …in consequence of destruction of the myoenteric and
submucous plexus by the…… The digestive forms, megaesophagus or
megacolon may be observed in advanced …..
Second para: In consequence, food retention or esophageal stasis occurs,
leading to the appearance…..
The diagnosis is frequently late, when the patient is in advanced…..
Third para: ….most frequent cause of death worldwide, but….
The Brazilian National Institute of Resarch in Cancer (INCA) reported that
esophageal cancer was the sixth in the cancer mortality in 2000 with 5,307
deaths. The estimated incidence in 2008 was 10550 new cases with an
incidence per 100 thousand individuals varying among ……
Methods: Please change to MATERIALS AND METHODS,
Subjects and Methods
Second para: Among the 40 CM patients, the mean age was 62.5 years (range:
40-83 years), and 20 were male;
The dilation grade….
2. Fluorescence in situ….
….sections were cut from paraffin-embedded blocks and…….
Results:
Sequences from chromosomes 3, 7 and 9, evaluated…..
Please change all dilatations for dilations.
Discussion
…the risk of ESCC may also be related to megaesophagus due to
Chagas’disease.
The current study detected deletion of CDKN2A…..
Please verify if all the references are correct and mentioned in the text
appropriately.
Discretionary Revisions
Questions:
Do you think that the follow up period (2 to 4 years) is adequate considering the
cancer development in this patient population? Please discuss.
Did you study patients with tumor that have developed in the megaesophagus?
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.
Review for 10.1186/1471-230X-10-20 (2010)

Reviewer's report
Title:Chromosomal imbalances are uncommon in Chagasic megaesophagus
Version: 4Date:1 January 2010
Reviewer: Ming-Rong Wang
Reviewer's report:
All the three reviewers agree that the work of Bellini et al. is of negative results.
Not all negative results should not be published, but the present manuscript
provides no important and reliable information for the relevant readers.
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.