Title: Effect of pelvic floor muscle training using mobile health applications for stress urinary
incontinence in women: a systematic review.
Version: 0 Date: 25 Jun 2022
Reviewer's report:
I used the CASP instrument for systematic reviews as my template for appraisal. As the paper
authors did, I also looked at the PRISMA checklist to see if the items were adequately reported.
I also read the registered protocol for the review on PROSPERO.
First, I note the following inconsistencies between the paper and the registered protocol, and
none of the changes are mentioned in the methods of the paper:
• The protocol includes women with stress urinary incontinence and stress predominant mixed
urinary incontinence. The paper mentions only SUI.
• The protocol states adherence as the main outcome measure with incontinence severity as an
additional measure. This is reversed in the paper.
• The protocol is for a systematic review with meta-analysis. The paper presents as if the
objective was always a systematic review with narrative synthesis (see page 6 “Therefore
this review extends the current literature providing a narrative synthesis of the most recent
RCTs….etc”.)
• The protocol states only papers in English are considered for inclusion. The paper says there
is no language restriction.
Did the review address a clearly focused question? Yes. However, there is the issues (see above)
about whether the population had SUI only (or could have stress predominant UI) and what
the primary outcome of importance was. In the background to the paper this statement is made
“unfortunately adherence remains a weakness in today’s PFMT programs”. Do you mean that
the design or delivery of PFMT does not try to enhance adherence, or do you mean women
continue to find it difficult to do enough exercise, or something else?
Did the authors look for the appropriate sort of papers? Yes.
Were the important, relevant studies included? Probably. The confusion about English language
limitation (or not) needs clarifying. No search dates are given. It is not clear what this statement
means “studies containing titles that met the study objectives but did not have abstracts and
full text available were removed.” It is also not clear whether authors considered conference
abstracts, theses and other grey literature eligible or not, and if not why not? With regard to the
search, why (if the I of the PICOT is smartphone applications) does the search include a term for
“web-based”. Also, there is no clear definition anywhere of what is or is not considered PFMT
for the purposes of the review. Nor is there a clear definition of what is eligible within the scope
of a smartphone application or not – for instance, these can be anything from a simple alarm
app through to a Bluetooth biofeedback device with real-time feedback to a health professional
via the woman’s phone. Please provide more information of how smartphone application was
defined for the purposes of the review. There were clearly a very large number of records found
with searching. How were these managed – referencing software, xls spreadsheets, etc?
Assessment of the quality of the included studies? Yes. Was this assessment done at study or
outcome level? How was this assessment intended to be used in analysis? Risk of bias across
studies is not mentioned and this is somewhat inconsistent with protocol that mentions analysis
of subgroups (if possible).
Have results been combined and was it reasonable to do so? I have a number of concerns here.
First regarding the data. Was the data collection form piloted? Among the data items, what
does “measurement time” mean? Also among the data items whey are only the Broome scale
and self-reported adherence mentioned as possible measures? There are other ways of measure
adherence, include data collected by the smartphone application. Second the number of included
studies. This is not accurate. There are, in fact, only n=6 included studies. Three of the studies
are the same study with more than one publication (i.e. a short term and longer-term follow
up) – Loohuis et al 2021a and 2021b is the same study, Sjostrom et al 2013 and 2015 is the
same study, and Asklund et al and Hoffman et al are also the same study. It is not appropriate to
count the same study twice as this ‘overweights’ their contribution in multiple ways and skews
quality assessments etc. Third, there is no description of the narrative synthesis approach, and
no explanation is given of why a meta-analysis was not conducted when it seems (based on the
protocol) it would be quite possible to do this using SMD (at least for the incontinence quality
of life data) if the data were grouped into post-treatment and longer-term follow up. Fourth, in
Table 3 it is not clear what maximum score is for any of these measures, or if higher scores better
or worse. The n= per group is not presented (important as this often changes with follow up).
What are the overall results, and how precise are the results? It is not clear. The results are very
descriptive and repeat the table and this seems unnecessary. Succinct summaries would be more
useful, including plausible explanations for differences in observed effects. I don’t understand
why between group differences are not calculated for any study at any time point and presented
in text/tables? A great deal of the reporting is within group difference (e.g. baseline to post-
treatment) rather than focusing on between group difference which is the important/primary
comparison in randomised trials.
Minor editorial. I note in Table 1 (Jin et al) that the participant number doesn’t add up.
Please note I have deliberately not commented on abstract or discussion as you may wish to
revise these in line with the comments above before further peer review.