Review for 10.1186/1471-230X-11-34 (2011)

Reviewer's report
Title:Presence of intestinal Mycobacterium avium subspecies paratuberculosis
(MAP) DNA is not associated with altered MMP expression in ulcerative colitis
Version: 2Date:11 February 2011
Reviewer: Paul Scully
Reviewer's report:
With regard to the resubmitted article I feel that the subgroup analysis and
treatment analysis adds to the paper itself but I still have issues regarding a
number of the major revisions mentioned previously. I have included the
aforementioned compulsory revisions that I feel still need further clarification
below.
Major Compulsory Revisions
1: A large amount of the introduction and discussion hypothesise that MAP might
represent a
causative agent for CD. However, the sample number of 14 CD patients is a very
small number
to be drawing any conclusions from. Is it possible to increase this number? A
similar number to
the UC cohort would have greater scope to potentially detect MAP DNA and so
may more fully
represent the prevalence of MAP in CD. In addition, it would then allow for a
comparison with
regard to MMP expression. MMP analysis on a greater number of CD patients
may show a
different response with MAP than UC as has been shown with regard to cytokine
production
(Ren et al, (2008) J Gastroenterology and Hepat, 310-314; Clancy et al, (2007)
Digest Liv Dis,
39, 445-451; Sibartie et al, (2010) Inflamm Bowel Dis, 16, 296-304). The paper
would be of a
much greater relevance if it was possible to include a higher number of CD
patients.
Author’s reply:
With this study we followed a dual intent: Our first aim was to determine the
prevalence of MAP DNA in intestinal tissue of patients with IBD and healthy
controls using sensitive and specific PCRs and MAP culture. Furthermore, it has
been shown that PBMCs isolated from cattle infected with John’s disease
upregulate MMP-9 and TIMP upon stimulation with MAP (Coussens PM et al.
Microb Pathog2004, 36:93-108; Coussens PM et al. Vet Immunol Immunopathol
2005, 105:221-234) and murine in vitro and in vivo studies provide evidence that
MMP upregulation plays a pathogenic role in infections caused by pathogenic
mycobacteria (Qiding-Jarbrink et al. Infect Immun 2001, 69:5661-5670). Based
on this evidence, we further aimed to analyze whether IBD patients with
intestinal MAP detection might exhibit a higher mucosal MMP expression than
those without MAP infection. We agree with the reviewer that the inclusion of a
higher number of CD would be beneficial as it would more fully represent the
prevalence of intestinal MAP DNA in CD. However, as it unfortunately currently
not possible to increase the number of CD patients we address to this limitation
in the discussion of our manuscript in the following way: “As our cohort of
patients with CD was relatively small, this result might represent an
underestimation of the frequency of MAP DNA detection in CD patients. Thus, on
the basis of our data, we cannot support nor exclude the hypothesis of an
etiologic involvement of MAP in the pathogenesis of CD”. We also agree with the
reviewer that MMP analysis on a greater number of CD patients might show a
different response to MAP in CD than in UC. Nevertheless, given that we
compared the MMP and TNF-# expression in UC patients with and without MAP
infection, our approach should be sufficient to detect an in vivo regulation of the
respective MMPs by MAP, although the
magnitude of this regulation might differ from that observed in CD. Therefore, we
think that the second intent of our study (to analyze whether MAP positive and
MAP negative IBD patients exhibit a different intestinal MMP expression) can be
addressed appropriately in our study, especially because of the fact that our UC
cohort is quite large (n=49) and the number of UC patients with positive MAP
(n=10) sufficient for statistical calculations.
REPLY:
Based on these numbers if the CD cohort is to be included as part of the paper I
think that details of the power analysis undertaken will have to be included. The
numbers of patients at 14 as far as I can tell is far too few to be making any
comments at all and thus requires further detailing of statistical power analysis or
consideration of not including at all seeing that the numbers cannot be increased.
I agree with the comments on the UC cohort being of a large enough number but
again for completeness further statistics would complement the numbers.
2: With regard to the patients recruited I can see the appropriateness involved in
obtaining
subjects from German and Norwegian populations, however, this raises a
number of issues.
Firstly, although the increase in MAP detection in the German cohort was noted
as nonsignificant,the percentages detected at 29% for Germany and 14% for
Norway does raise the
possibility that with a higher number of subjects this could be of significant
difference. Studies
by Collins et al. (J. Clinical Micro, (2000), 4373-4381) have suggested that
differences between
a Danish and US population may be due to differences in BCG vaccination status
and whether
or not it is a rural population that is sampled. Are the German and Norwegian
populations
similar in this regard? Also, the controls are only taken from the German
population and so it
could be said that this study is not properly controlled with any Norwegian
non-IBD subjects. Is
it possible to include a Norwegian cohort as part of this control group?
Author’s reply:
We thank the reviewer for addressing this important point. German and
Norwegian patients were recruited from the endoscopic department of the
Universities of Giessen (Germany) and Stavanger (Norway) and its catchment
areas. Stavanger is the third largest city of Norway with approximately 190,000
people living in the Stavanger conurbation. Stavanger municipality has
approximately 120,000 inhabitants. Giessen municipality has approximately
80,000 inhabitants and the administrative county of Giessen enfolds 255,000
people. Therefore, all patients and controls from Germany and Norway recruited
for this study represent an urban population. Concerning the BCG vaccination,
the following can be said: In Norway, the BCG vaccination came into general use
in 1947 for the following populations: ALL 12–14-year-olds, children with
origins in high-incidence countries, children/adolescents with family history or
contact with TB case, children/adolescents before long-term travel to
high-incidence countries, health personnel at high risk of tuberculosis exposure
(Norwegian Institute of Public Health. Forebygging og kontroll av tuberkulose: en
veileder [Guidelines for prevention and control of tuberculosis]. Oslo, Norway:
Norwegian Institute of Public Health, 2002). BCG vaccination was compulsory
during the first decades, but has been voluntary and recommended since 1995.
The general vaccination coverage is calculated to be >90-95% (Infuso A, Falzon
D. European survey of BCG vaccination policies and surveillance in children,
2005. Euro Surveill. 2006;11(3):pii=604; World Health Organization:
Immunization coverage with BCG). The BCG vaccination is no longer generally
recommended since 2009. Therefore, one can assume that the great majority
of Norwegian patients in our study was BCG vaccinated. In Germany, BCG
vaccination was part of the generally recommended newborn vaccination regime
and vaccination coverage was calculated to be >90% (WHO). Since 1998, the
BCG vaccination is no longer generally recommended by the vaccination
committee (“Ständige Impfkommission”, STIKO) of the Robert-Koch-Institute. As
only adult patients were included in our study, it can be likewise assumed that
the great majority of the German IBD and control cohort was BCG vaccinated as
well. Given these considerations, we did not include a second control group from
Norway. Although we fully agree that the factors such as living area and BCG
vaccination status are important to consider when analyzing the prevalence of
MAP, we also believe that such an analysis is
beyond the scope of our study as this would require considerably larger
epidemiologic studies which assess a detailed individual history including, among
others, factors such as housing/living situation, movements, travel history,
number and origin of present and recent household members, present and
previous contact to animals, detailed working history, eating and drinking habits.
REPLY:
With regard to this issue I have to ask the question as to why include a cohort
from Norway at all? I understand the concept of allowing for locoregional
differences but how can this be the case if the controls are all from one country
only? This is a potential source of bias in the paper and does not allow the
exclusion of locoregional differences. The majority of the patients are Norwegian
(n = 42) with German patients (n=21) and German controls only (n=21). A more
full explanation of the reasons for inclusion of these 2 populations should be
included in the paper. This aspect is not discussed at all as far as I can see and I
do not fully understand the basis and merit for the 2 populations. Could this be
further expanded?
4: As part of the methodology only the German patients were cultured for MAP
investigation.
Why was it not possible to conduct a similar design for the Norwegian samples?
Also, with the
high DNA positivity obtained would it be expected that some of the cultured
samples be positive
even with regard to the difficulties of culturing MAP? Was the method validated
for culture and
was any positive control included to ensure that the non-culture of MAP was not
a methodology
issue? Was there consideration to culturing subject stool samples in addition to
aid detection,
due to small size of biopsy used for culture.
Author’s reply:
For the MAP culture, biopsy samples taken during the colonoscopy were added
to a reaction tube with 0.5 ml saline. To guarantee a fast processing and to avoid
potential cross contamination, these biopsies were then immediately transferred
to the Faculty of Veterinary Medicine located on the same medical campus.
Unfortunately such an approach was not possible in Stavanger for the following
reasons: MAP culture is not routinely possible in humans and cultivation of MAP
from tissue, even from animals with Johne’s disease, is usually associated with
many obstacles and therefore requires a certain level of expertise and
experience. This, in part, is because MAP is a fastidious and
mycobactin-dependent bacterium with a generation time over 22 hours. The
spheroplastic form of MAP as reported in tissues of patients with CD presents
even more obstacles to its isolation in a culture medium and in fact requires
special media supplements with additives that support the difference in osmotic
pressure between the intra- and extracellular environment. Further, it may take
up to 18 months for the bacterium to manifest a cell wall so that a long culture
period is required. Due to the lack
of institutions meeting the outlined criteria in Stavanger, we unfortunately had to
restrict the MAP culture to our german cohort. Stool samples for MAP culture
were not used for MAP culture as they would not allow overcoming the difficulties
associated with culturing MAP in vitro.
REPLY:
Again this raises the issues as to why a Norwegian cohort was included so needs
to be more fully addressed in the paper.
Minor Essential Revisions
Page 18: top of page: “(tissue vs. blood) is the relevant size….”
“is” should be included to aid legibility.
Page 20: third line from top. “ and MMP-2 “ is repeated.
Discretionary Revisions
Page 21: “Apart from that” can be left out in the third last line.
Page 18: Middle paragraph “Further” should be “Furthermore” to aid clarity.
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