JerMa88/BMC_Womens_Health_Peer_Reviews huggingface dataset:
Reviewer's report
Title:Hormonal contraception and HIV infection among women in Cameroon
Version: 1Date:2 June 2008
Reviewer: Charles Morrison
Reviewer's report:
This manuscript deals with an important issue – a possible association between
the use of hormonal contraception and the risk of HIV acquisition. This issue is
especially important in areas of sub-Saharan Africa where HIV prevalence and
incidence rates are high and where hormonal contraception is the most highly
utilized form of birth control. The authors use data from the 2004 Cameroon DHS
to conduct this cross-sectional analysis.
Unfortunately, I believe that the study/analysis design and measurement of some
of the key variables is too weak to make a meaningful contribution to the
literature on any etiologic relationship between hormonal contraception and HIV
infection. [There are now 10-20 prospective studies of this issue, mostly
conducted in Africa, that provide better information about this possible
relationship.] The most important issue is the cross-sectional nature of the study
with the consequent lack of clarity concerning the timing of contraceptive use vs.
the timing of HIV infection. In addition the measurement of hormonal
contraceptive use is crude (ever vs. never, current vs. no current use), there are
relatively low number of hormonal contraceptive users (especially current users),
contraceptive use is not validated against clinic records, and different types of
hormonal contraceptives that could have differential effects on HIV infection are
all lumped together into one category. I also believe that measurement of and
control for important sexual behavior variables (e.g. condom use, number of
coital acts, primary vs. casual partners, partner risk behaviors) and other sexually
transmitted infections is weak.
I would suggest that the authors rewrite the paper as a descriptive paper on
contraceptive practices, sexual behaviors and HIV prevalence among women in
Cameroon and submit the paper to either a reproductive health or behavioral
specialty journal. In such a manuscript the fact that the data is drawn from a
nationally representative sample of sexually active Cameroonian women would
be a distinct strength.
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.
Reviewer's report
Title:Hormonal contraception and HIV infection among women in Cameroon
Version: 1Date:24 June 2008
Reviewer: Isabelle Heard
Reviewer's report:
This study was aimed at understanding whether the use of hormonal
contraceptives differed by HIV-status among women of reproductive age. The
rational for the study was that theoretically, the use of hormonal contraceptives
could predispose women to HIV infection. A national representative sample of
4538 sexually active women were interviewed using a structured questionnaire.
In multivariate analysis, no significant association was found between current
users of HC and HIV status, whereas the ever use of HC was positively
associated with HIV-status.
In this study, the question was well defined, the method appropriate and well
described. Result section is clear with sound data. Table 1 and 2 are easy to
read. Discussion is well organised and limitations of the study are clearly stated.
Finally, this article should be accepted without revision, as presented data are
important at least in term of Public health at the country level.
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.
Reviewer's report
Title:Hormonal contraception, sexual behaviour and HIV infection among
women in Cameroon
Version: 2Date:9 October 2008
Reviewer: Charles Morrison
Reviewer's report:
This version of the manuscript is much improved as it is descriptive and does not
try to infer association between hormonal contraception and HIV acquisition. This
is appropriate since it is a cross-sectional study with rather weak measures of
hormonal contraception.
Minor Essential Revisions
Still needs careful editing and spell checking
* Introduction: Update the 40.3 million with the newer figure of 33 million cited in
the most recent UNAIDS report.
* Methods: Say Calverton, Maryland, USA. Under 'Data Collection' should say
'Blood sample for HIV testing' rather than 'test'.
* Results: Under Socio-demographics the higher confidence interval for women
who lived in Urban area '7.84%' is incorrect. Please correct.
Should correct 'windowed and divorced'.
Under 'Sexual behavior' the sentence starting with 'Women with higher lifetime
number' is redundent with the previous sentence. Please delete.
* Discussion: In first sentence would say 'population-based nationally
representative survey'. In the para starting 'In the current HIV prevalence" it
should say 'In the current study HIV prevalence'. In the following paragraph in the
last sentence, I would change 'to increase infectiousness of HIV' to 'to increase
HIV acquisition'.
Discretionary Revisions
Abstract: In the Methods I would say that this comes from a nationally
representative sample. In the Conclusions I would say that "We conclude that the
prevalence of HIV amony sexually active women in Cameroon varies
according..."
Also, at the end of the Conclusions I would say "the incidence of HIV infection
among women using and not using hormonal contraceptive methods."
Discussion Section: At the end of the paragraph beginning " The low level of
hormonal contraceptive use", I would add a sentence talking about the need for
more education of women about family planning and more easily accessible
family planning services in Cameroon. There is clearly alot of unmet
contraceptive needs in Cameroon.
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.
Reviewer's report
Title:Correlates of intimate partner violence among pregnant women in Rwanda
Version: 2Date:16 June 2008
Reviewer: Ann L Coker
Reviewer's report:
BMC IPV in Rwanda
Second Review
This manuscript has improved somewhat but the same review points remain. My
comments are essentially the same as the first review.
1. The issue regarding the study design is not resolved in this revision. If you
sampled such that half the population was HIV+ then you must have been
interested in HIV status as research question. I would state that you have a case
control study and your primary research question is “Are women who are HIV+
more likely to have a history of partner violence?” Currently the manuscript lacks
focus. Directly stating an hypothesis would better shape the manuscript.
2. Add response rates. What proportion of women refused participation?
3. Include the measures of partner violence used and reference these.
4. Decide on terms. Either use intimate partner violence or domestic violence; do
not both interchangeably. I still found examples of partner and domestic violence
in this version.
5. Results should be presented to address the primary research question. If it is
HIV and partner violence then rates of IPV should be presented by HIV status.
6. There is no discussion in the methods of what variables are included in models
to result in adjusted ORs. How did you decide that factors were or were not
confounders? Those variables included in multivariate models need to be listed
in Table 2.
7. I still think a conceptual model would help the author and reader focus on the
analysis and important of this work.
Finally, the discussion must include specific ways in which these study findings
may affect prenatal care in Rwanda. What are the implications of the high
prevalence of IPV during pregnancy? We know that both IPV and HIV have
significant implications for maternal and infant health. This needs to be
discussed. While calling for universal screening may address IPV in the long
term, are there services to address IPV in Rwanda. Further, are there efforts to
prevent IPV? What might these be? How might prenatal care providers use the
data in this report?
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.
Reviewer's report
Title:Correlates of intimate partner violence among pregnant women in Rwanda
Version: 2Date:18 June 2008
Reviewer: Fariyal F Fikree
Reviewer's report:
I congratulate the authors on the study - as remarked earlier, research on
intimate partner violence is uncommon in the developing world. I have a couple
of additional remarks:
1. The paper will benefit greatly from an extensive revision with respect to
scientific writing style.
2. Please mention (page 4, end of second para) that this paper is based on a
sub-set analysis of a larger study.
3. The description of the sample size calculation is still not clear. From my
reading of the manuscript, I am not sure what variable the "P" that was used in
the sample size formula reflects. Is it the proportion of women using antenatal
services, HIV testing (86%)or adherence to the PMTCT program (8.7%). The
decison by the study investigators to increase the total sample size to 600 with
equal proportion of HIV+ and HIV- pregnant women will have increased the
power of the study. However, the authors did not mention what the power of the
study sample is?
4. In the response letter, the authors describe the recruiting process but have not
included this in the revised text.
5. For the readers who are not familiar with Rwanda it will be helpful if you
mention on page 4 (lines 4-5) the location of the antenatal clinics (all urban, or
some urban and some rural). How many of the 600 women were from the three
sampling sites.
Level of interest: An article of importance in its field
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.
Declaration of competing interests:
I declare that I have no competing interests
Reviewer's report
Title:Correlates of intimate partner violence among pregnant women in Rwanda
Version: 3Date:18 August 2008
Reviewer: Ann L Coker
Reviewer's report:
Revision #2
Major Revisions
How is it possible that 100% of women agreed to participate in this study? What
written consent obtained?
If the authors used the Conflict Tactic Scale then reference this scale. Don't
reference other studies that used this tool.
Include the variables you adjusted for when calculating adjusted ORs in the
legend for the relevant table. The tables should stand on their own thus the
legend would indicate those confounders included in the modeling.
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.
Reviewer's report
Title:Correlates of intimate partner violence among pregnant women in Rwanda
Version: 3Date:20 August 2008
Reviewer: Fariyal F Fikree
Reviewer's report:
The authors have revised the manuscript based on my earlier comments. In this
revised manuscript the following item needs clarification/editing:
Page 4, para 3, line 19: the authors state "Consecutive antenatal clinic attendees
were the sample was from urban area while the other half was from rural areas".
It is not clear from this statement whether the recruitment process (consecutive
antenatal clinic attendees) were similar in the urban and rural sites. If not, what
was the recruitment process in the rural site. Why was the recruitment process
different. Will the variation in the recruitment process affect the study? If no, why
not, If yes why.
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.
Declaration of competing interests:
I declare that I have no competing interests
Reviewer's report
Title:Intimate partner violence among pregnant women in Rwanda
Version: 4Date:29 September 2008
Reviewer: Fariyal F Fikree
Reviewer's report:
The author's have satisfactorily responded to all the 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'
Reviewer's report
Title:Reference population for international comparisons and time trend
surveillance of preterm delivery proportions in three countries
Version: 1Date:18 March 2008
Reviewer: Anjel Vahratian
Reviewer's report:
Thank you for the opportunity to review this manuscript. I found it interesting to
read and well-written.
Major Compulsory Revisions: None
Minor Essential Revisions: None
Discretionary Revisions: None
What next?: Accept without revision
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.
Reviewer's report
Title:Reference population for international comparisons and time trend
surveillance of preterm delivery proportions in three countries
Version: 2Date:14 May 2008
Reviewer: emile papiernik
Reviewer's report:
thank you for your answers and remarks
Your answer about homogeneity pointA of primiparity does not change my
opinion, the fact that the first pregnacy is the best predictor of the risk of
prematurity for the other pregancies as established by Bakketag remains true,
but the opposit that you propose that the risk of prematurity is easy to measure
for a first pregnancy is not verified by all the series I know, if you do not know
more about a previous pregancy terminated by an abortion or the risk of the
effect of a malformed uterus that is impossible to recognize during a first
pregancy.
About point B I did not find haw your definition of your referance population would
better explain the rise of preterm births in Denmark if you do not test new
hypothesis
point C I did not find the paper on pubmed, please send to me
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 intersts out of quality of science
Reviewer's report
Title:Reference population for international comparisons and time trend
surveillance of preterm delivery proportions in three countries
Version: 3Date:31 May 2008
Reviewer: emile papiernik
Reviewer's report:
the reviewer did receive your previous publication$your paper is of interess for
the work of comparision of medical results in different medical countries and
should interess the editor for that
But the paper fails for its central technical proposition which is to use a reference
population
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 have no competing interests'
Reviewer's report
Title:Reference population for international comparisons and time trend
surveillance of preterm delivery proportions in three countries
Version: 3Date:21 August 2008
Reviewer: Mika Gissler
Reviewer's report:
Several countries have reported increased preterm birth rates, for example
Denmark and United Kingdom, while no decrease has been reported in some
other countries, including for example Finland. Since prematurity is one of the
main causes of poor infant outcomes, it is important to explore the causes behind
the negative time trends.
In the paper by Morken et al., this is done internationally by comparing data from
three Scandinavian countries. The main aim is not to explore risk factors for
preterm birth, but to analyse if the general preterm birth trends are similar for a
pre-defined "low-risk" group called reference population. The inclusion criteria -
based on the availability of variables in the three national Medical Birth Registers
- were 1) age 20-35 years, 2) being primiparous 3) having spontaneously
conceived pregnancy, 4) singleton pregnancy and 5) mother's birth in the country
of delivery. The analysis showed that there a significant differences in preterm
birth trends in the three study countries. First, different trends by country are not
explained by variation in maternal background factors. Second, it is an important
finding that the increase in preterm birth rate in Denmark is even more evident in
the reference population excluding several groups with high risk for preterm birth
(e.g. multiple births, ART births and births among old parturients). This implicates
that the causes for this increase in Denmark have to be investigated in more
detailed.
The study idea is scientific sound and the study is carefully planned and
performed. The results are clearly presented and the discussion is good. The
only remark I have for Table 1c, for which the 1996 rate is 33.2% instead of
332.1%.
Reviewer's report
Title:Change over time in factors associated with domestic violence by intimate
partner in Egypt: analysis of two surveys
Version: 1Date:11 February 2008
Reviewer: Lars Åke Persson
Reviewer's report:
In this paper the authors depart from the module on partner violence against
women in two Demographic Health Surveys, 10 years apart, and analyses
changes in the prevalence of violence and changes in the pattern of associated
background factors. It provides new knowledge especially regarding the
dynamics of the associated background factors, e.g. the consequences of
changing educational background of women and men in society.
The paper is well written and analyses seem overall to have been performed in a
careful and critical manner.
I would like the authors to elaborate a bit more carefully on the possible
consequences of the very brief question in the first survey and the much more
careful questionnaire (with similar design as in the WHO multi-country study
questionnaire) in the second survey. Previous experience tells that a brief
question renders a great underestimate of the true frequency of domestic
violence, while a block of questions as in the second survey results in a more
valid result. The consequences of this may impact not only estimated level of
frequency of violence but also associations with background factors.
It should be mentioned also in â##Methodsâ## in Abstract that data collection
methods were different in survey 1 and 2.
Sometimes the authors use the word â##effectâ## when dealing with the
associations between background factors and violence â## I prefer association.
Reviewer's report
Title:Change over time in factors associated with domestic violence by intimate
partner in Egypt: analysis of two surveys
Version: 3Date:13 May 2008
Reviewer: Farah Ahmad
Reviewer's report:
Manuscript Title: Change over time in factors associated with domestic
violence by intimate partner in Egypt: analysis of two surveys
The authors have revised the manuscript by incorporating some changes
that were suggested including the exclusion of ‘help seeking’
variables as different aspects were measured in 1995 and 2005.
The revised paper still needs to take a different approach in reporting
of the Results and the Discussion due to different questions used to
measure wife beating in 1995 and 2005 DHS. The revised version still
compares the rates of wife beating measured in 1995 and 2005 with an aim
to examine “change overtime”. For example, the first paragraph in
the discussion section states "Information from the two DHS conducted 10
years apart in Egypt was evaluated to investigate changes over time in
the incidence and factors associated with wife beating. There are
several important findings in this study. First, there was little change
over time in the reported incidence of wife beating..."Unfortunately,
the authors can’t make any conclusions about such “change
overtime” though they dearly wish to do so.
In my view, the authors should take a critical approach. Starting from
the introduction section, they should include a criticism of the use of
inconsistent measures in the national survey to assess wife beating in
1995 and 2005 . Then, they should accordingly describe their research
objectives, such as: What are the rates of wife beating in 1995 and 2005
using single-item and multiple-item measures? What are the significant
risk makers for wife beating in 1995 and 2005? To make the inconsistent
measurement more clear for the audience, please include a table with
rates of “each” of the items - with full wording - used in 2005 and
1995.
For the discussion section, the authors should briefly present the
rates of 1995 and 2005 and then focus more on different possible (even
counter intuitive) interpretations of these rates in order to highlight
the limitations posed by inclusion of different measures in the two
national surveys. At the same time, they should discuss the historical
significance of this change from single-item to multiple-item
measurement as a reflection of increasing acknowledgment of wife beating
at the national level. Perhaps, a discussion on international efforts to
use similar measures could be added here (e.g. WHO multi-site study
etc.) or how public health research and interventions have moved
overtime from “physical” violence to inclusion of “emotional and
psychological” abuse. The part of discussion on risk markers could
then discuss the “similarities” and “differences” in the risk
markers for 2005 and 1995. The discussion should also include
implications for public health initiatives.
I hope that authors will find these comments useful!
Reviewer's report
Title:Change over time in factors associated with domestic violence by intimate
partner in Egypt: analysis of two surveys
Version: 3Date:14 May 2008
Reviewer: Lars Åke Persson
Reviewer's report:
I am satisfied with the way the authors have responded, and the revisions they
have made in the manuscript.
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.
Reviewer's report
Title:Change over time in factors associated with domestic violence by intimate
partner in Egypt: analysis of two surveys
Version: 3Date:12 June 2008
Reviewer: Muhammad M. M Haj-Yahia
Reviewer's report:
It's clear that the authors inserted major revisions into their paper, following the
reviews of all three reviewers. Undoubtedly, the current version of the paper is
improved to a great extent, compared with the previous version. Nevertheless, I
am not satisfied of their revision of the Method section, based my comments on
that section.
Although this dissatisfaction is not a sufficient reason to reject the revised version
of the paper I leave it up to your discretion how to deal with the matter.