Title: Intimate partner violence among reproductive-age women in Central Gondar Zone,
Northwest, Ethiopia: a population-based study
Version: 3 Date: 03 Feb 2022
Reviewer's report:
The purpose of this cross-sectional, population-based household survey was to describe the
prevalence of intimate partner violence and associated factors among a community-based sample
of reproductive age women (age 15-49) in the Central Gondor zone of Ethiopia.
The fact that this is a population-based household survey is a great strength of the investigators'
approach. While this is not clearly stated, it also seems that this study may represent the first such
survey of reproductive age women in Ethiopia? (If this is indeed the case, I strongly encourage
the investigators to state this clearly and underscore the contribution of this study to the overall
literature.)
However, despite these notable strengths, I can't recommend this manuscript for publication as
written. I’m so sorry to say this – I admire what the investigators are trying to do and I think it
is important – I just think there are too many serious issues with this paper. I will try to provide
comments that may help for revision plans.
The abstract states that the investigators were interested in past-year intimate partner violence
prevalence (the abstract, by the way, seems to be the only place I could find that clearly
indicated they were interested in “past year” vs lifetime or any other time frame) and associated
factors. The inclusion criteria for this study appear to be a) women age 15-49 who reside in
a chosen household and are b) willing to talk to an interviewer. In other words – inclusion
criteria did not specify whether women were partnered or not. I think this is fine for the purpose
of including and interviewing women; where it causes problems is when unpartnered women
are not differentiated or excluded in analyses of risk/associative factors, and that is the most
significant issue I have with this paper.
CORE ISSUE: I spent a lot of time figuring out who was included in the study and the analyses,
because it wasn’t entirely clear. It appears that the entire sample (804 women) is used in each
analysis – descriptive and inferential. This makes sense in Table 1; it makes considerably less
sense in Table 2 and 3 (if the interest here is understanding the impact of IPV) and makes none
in Table 4.
The problem with including the entire sample – where having a partner in NOT an apparent
inclusion criterion -- is that women who are at risk for partner violence in the past year are women
who have had a partner in the past year (whether married or not).  No partner, no exposure to
the risk variable. That means including women with no partner in inferential analyses doesn’t
make sense here.  So by way of example, take this statement in the text:
“Those reproductive age women who are married were 3.85(AOR=3.85,95%CI:2.38,6.22) times
more likely to have partner violence among currently non married individuals.”
Please consider this: Including women who were not partnered in the analysis actually makes
the odds ratios impossible to interpret. A more useful analysis in terms of marital status (or any
other factor) as an factor associated with partner violence would be restricted to **only women
actually at risk of exposure to partner violence *** – that is, the ones who have partners – but
adding up the n’s in Table 4 makes it clear that all the women, partnered or not, at risk of IPV or
not, were included in this analysis. Similarly, the investigators analyze the associations between
IPV and other variables such as the number of children (>3, 1-3, no children), having household
food insecurity, exposure to life-threatening events, depression symptoms – but in each case,
Table 4 suggests that unpartnered women are again included in these analyses. I’d strongly
encourage the investigators to rethink their analysis strategy for their data – and when they are
interested in the prevalence of symptoms related to IPV (like depression) or factors related to
IPV (like how many kids a woman has, whether she is married to her partner, how much alcohol
she drinks) to think carefully about which women to include in the analyses (and then describe
their analysis strategy and label their tables clearly to reflect this). It is primarily for this reason
I do not think this article should be accepted for publication – it is a serious limitation.
Other major issues:
• No safety procedures related to IPV whatsoever are described in this study. How and where
were women actually interviewed? Were other household members present, could they hear?
Were any resources provided, any follow up for distress? Was there a protocol for this?
• The description of how the needed sample size was estimated is confusing; it is similarly
confusing why the investigators estimated they would have 10% refusal rate and needed 845
participants but stopped at recruiting 845 women, ending up with 804 actual participants. Why
not overrecruit by 10% if they needed 845? Some explanation or justification would be useful.
• It needs to be stated clearly and consistently throughout the manuscript how IPV was
operationalized and measured. Did the authors use the long form of the WAST, or a short form?
Does IPV positive in this study mean past year? I’m unclear why the cut score is >1 – in the
literature, the WAST cut score has generally been something like 13 in high income countries
and 10-13 used in low and middle income countries (e.g., Malaysia, China, South Africa). The
reference the investigators provide for the WAST (Coker et al) is a very old article where Coker
et al didn’t use the WAST, as far as I can tell. This then gives me pause about who/how women
are classified as IPV positive in this study.
Minor issues:
• In general, please describe measures more thoroughly – the number and type of questions,
their question domains (including sample questions, e.g., I don’t know really what the “lifetime
events” measure covers), their scoring, any psychometric data? Used before in this population?
And importantly – time reference? IPV, depression, anxiety, stress, drinking over what prior
time period? I quite like that the investigators used the HFIAS, but the scoring of this measure
is complicated, and I can’t tell how they actually scored the measure.
• Please use caution with claims of causation in a cross-sectional design – e.g., the header in
the findings describing “determinants of intimate partner violence”, in the discussion statements
like “The study also demonstrated that the odds of developing partner violence among women
that have moderate social support were 40% lower among women with strong social support”
– one could also just as reasonably conclude that an abusive partner substantially and often
intentionally disrupts a woman’s social support network – and in any case you can’t support
either determination with this study design. Both studies cited in the discussion to support this
claim also used cross-sectional data.
• Could use English editing. I am always hesitant to make this critique, because I admire LMIC
investigators who are doing such important work (usually with substantially fewer resources)
AND writing in a second language -- it is so impressive to me!!! --  but at times the English here
does interfere with the ability to understand.
Good luck to the investigators – I am so sorry I had to critique these issues – I hope you persevere
in your important work.