Reviewer's report 
 Predisposing factors for bacterial vaginosis, treatment efficacy and pregnancy outcome among term Title: 
deliveries; results from a preterm delivery study. 
 1  28 March 2007 Version: Date: 
 Ida Vogel Reviewer: 
Reviewer's report: 
Review of: Predisposing factors for bacterial vaginosis, treatment efficacy and pregnancy outcome among 
term deliveries; results from a preterm delivery study.' P-g Larsson, Lars Fahraeus, Bodil Carlsson, Tell Jacobsson and Urban Forsum BMC 
This is a cohort study of 9000 pregnancies combined with a randomised controlled trial examining the effect 
of clindamycin treatment of BV on the rate of preterm birth. This is a secondary but important outcome of this cohort. Cohorts of 9000 women examined for BV are rarely collected and of high importance 
1. Is the question posed by the authors new and well defined? 
The main aim is to identify risk factors for BV in early pregnancy. They also have secondary (is clindamycin effective in removing BV?) and tertiary aims (Is BV associated with other pregnancy outcomes?) 
One of the main problems in this article is to handle these 3 aims in one article. From the article one must 
believe that all preterm deliveries are excluded from the cohort studied. However, the secondary outcome – 
the efficacy of Clindamycin – should be evaluated in the entire cohort and not only among the term 
deliveries. One could very well imagine that the efficacy was less among the preterm and this was indeed 
why they delivered preterm. Thus this approach would lead to an overestimation of efficacy. In the third 
objective it is also problematic to study in term deliveries only. Eg preeclampsia is very often leading to 
preterm delivery, and thereby many of the preeclampsia cases may be excluded and results may be biased 
against null. 
2. Are the methods appropriate and well described, and are sufficient details provided to replicate the work? 
Methods are appropriately described except the formation of variable. I would like to read how all variables 
were defined. Like: there were 3 smoking variables for each point of exposure status: smoking (yes/no), 
smoking (0/1-10/>10 per day), smoking ceasetation since last (yes/no) 
3. Are the data sound and well controlled? 
It seems to be. To further evaluate this I would appreciate a flow sheet describing the cohort with exclusions 
etc in detail. Further 2x2 tables with numbers would allow further appreciation of the study size: this is a 
large cohort study and there are not too many of those. In spite of that numbers for women with BV and 
prior preterm delivery etc must be low, but cannot be evaluated in the manuscript as it stands. 
4. Does the manuscript adhere to the relevant standards for reporting and data deposition? 
Yes – except the above point that one is unsure whether we are looking at the whole cohort or only term 
deliveries. How about post term deliveries – are they included? And the Clindamycin treated arm – is that included in the reported data? Please give numbers to facilitate interpretation. 
5. Are the discussion and conclusions well balanced and adequately supported by the data? Yes – except 
the final statement. It doesn’t seem like a solid argument – if we can’t find risk factors let us screen all. To initiate a screening program the World Health Organization guidelines should be met – or at least debated in detail. Regarding BV and Clindamycin many of the following are not fulfilled. If BV is not a disease 
causing negative outcomes but only a risk factor as other low risk cohorts have indicated, one cannot expect 
a treatment to be efficient. I am not even convinced BV is an important health problem. 
6. Do the title and abstract accurately convey what has been found? Yes. 
7. Is the writing acceptable? Yes. But the paper is messy and full of errors: eg in the reference one of the 
authors own papers is cited wrongly: ref 15. is now available at BJOG. 2006 Jun;113(6):629-37. 
Major compulsory revisions: 
I. Inclusion of a flowsheet and 2x2 tables 
II. Description of the studied population is with of without preterm deliviers in MM. Discussion of how this 
would affect results in the comment sections. 
III. Why is the frequency of BV very low in this population? Compare with other Scandinavian reports 
(10-20%). 
IV. I think the authors should discuss whether BV is causal. At least 2 large cohort studies on a Danish and 
a UK population have not been able to find associations between BV and PTD. This is not mentioned in the 
text. 
V. There are studies showing a dose response curve effect on smoking and the BV rate. This could also be 
interesting to validate in such a large study. OR without CI are given, but no comparisons seems to have 
been undertaken. 
VI. In the logistic regression analysis was the interaction between BV and smoking and smoking and age 
considered? 
VII. Was confounder analysis done? Low socioeconomic status as well as changing sexual partners would 
be obvious ones to consider. 
VIII. Was a trend test done to examine the change in BV with age in figure one? 
IX. Moderate final conclusion 
Minor essential revisions: 
X. Line 6 p 8 is not readable. 
XI. Results sections seem messy, where data on other outcomes pop up several times. Collect these in one 
section. 
XII. Would it be interesting to examine those who acquire and those who eliminate BV, and what the 
predictors of these changes in status are among those who were not treated? 
XIII. Minor errors throughout the paper. 
 Unable to decide on acceptance or rejection until the authors have responded to the major What next?: 
compulsory revisions 
 An article of importance in its field Level of interest: 
 Needs some language corrections before being published Quality of written English: 
 No, the manuscript does not need to be seen by a statistician. Statistical review: 
Declaration of competing interests: 
'I declare that I have no competing interests'