Evidence-Based: Physical Therapy Pelvic Floor



Randomized trials
Randomized trials (also called randomized controlled
trials or randomized clinical trials [RCTs]) provide a
mechanism for estimating the effects of interventions.
They involve samples of people (trial ‘subjects’ or ‘participants’)
drawn from clinical populations who either
have a health disorder (in studies of treatment) or are at
risk of a health disorder (in studies of prevention).
Each participant in the trial is randomly allocated to
receive the intervention of interest or not. The group of
participants that does not receive the intervention of
interest is often called the ‘control group’. Subsequently
the experimenter compares the outcomes of participants
in the intervention and control groups.

There are a number of variations on this broad
approach (Herbert et al 2005). In the simplest version,
participants are allocated to groups that receive intervention
or a group that receives no intervention. Alternatively,
participants in both groups could receive
standard care but participants in one group could
receive, in addition, the intervention of interest. Or one
group could receive an intervention and the other group
could receive a different intervention. If participants are
randomized to groups all of these variations can be
called randomized trials.

Two features differentiate randomized trials from
other studies of the effects of intervention: there is comparison
between outcomes of groups that do and do not
receive a particular intervention, and participants are
allocated to conditions using a random procedure.
These features make it possible to separate out the
effects of intervention from other factors that infl uence
clinical outcomes, such as the natural history of a condition,
or statistical phenomena such as statistical regression.
The logic is as follows: randomization generates
groups that are likely to be very similar, especially in
large trials. So when we give the intervention of interest
to one group and not the other, differences in the outcomes
of the two groups are attributable to the intervention.

A complication is that, because randomization
produces similar but not identical groups, differences in
outcomes could be due to small differences between
groups at baseline. Statistical methods can be used to
assess whether this is plausible or not. This means that
the difference between the outcomes of the two groups
in a randomized trial provides an estimate of the effect
of intervention.

Importantly, randomization is the only way to
generate two groups that we can know are comparable.
No other method can assure a ‘fair comparison’ between
intervention and control groups. (Some empirical evidence
suggests well-conducted non-randomized trials
often produce similar results to randomized trials
[Benson & Hartz 2000, Concato et al 2000; but see Kunz
& Oxman 1998], but there is no reason why we should
expect that to be so.) For this reason randomized trials
can claim to be the only method that can be expected
to generate unbiased estimates of the effects of

Systematic reviews

Many physical therapy practices, including several
interventions for the pelvic fl oor, have been subjected to
multiple randomized trials. Where more than one trial
has examined the effects of the same intervention we
can potentially learn more from a careful examination
of the totality of evidence provided by all relevant
randomized trials than from any individual trial. Potentially
we can get more information about the effects of
an intervention from literature reviews rather than from
individual studies.

Until a couple of decades ago, reviews of the literature
were conducted in an unsystematic way. Authors
of reviews would fi nd what they considered to be relevant
trials, read them carefully, and write about the
fi ndings of those trials. The authors of the best reviews
were able to differentiate between high- and low-quality
trials to bring together a balanced synthesis that fairly
refl ected what existing trials said about the effects of the

Nonetheless, traditional (narrative) reviews have
always had one important shortcoming: their methods
are inscrutable. It is hard for readers of narrative reviews
to know if the review was carried out optimally. Readers
cannot determine, without specifi c knowledge of the
literature under review, whether the reviewer identifi ed
all of the relevant trials or properly weighted the fi ndings
of high-quality and low-quality studies. Also,
readers usually cannot know how the reviewer went
about drawing together the fi ndings of the relevant
trials to synthesize the review’s conclusions. There
must always be some concern that the evidence
provided in narrative reviews is biased by selective
reporting of studies, unbalanced assessment of trial
quality, or partial interpretations of what the best trials

The method of systematic reviews was developed
in the late 1970s to overcome some of the shortcomings
of narrative reviews (Egger et al 2001, Glass et al 1981).
The most important characteristic of systematic reviews
is that they explicitly describe the methods used to
conduct the review; typically systematic reviews have a
methods section that describes how the search was
conducted, how trials were selected, how data were
extracted, and how the data were used to synthesize
the fi ndings of the review. Thus, in systematic reviews,
the methods are transparent. This means the reader can
make judgments about how well the review was

A principle that underlies the design of most systematic
reviews is that the methods should minimize bias
by attempting to fi nd all relevant trials, or at least a
representative subset of the relevant trials. Also, predetermined
criteria are used to assess the quality of
trials, and to draw together the fi ndings of individual
trials to generate an overall conclusion.

To summarize, systematic reviews generally provide
a better source of information about the effects of an
intervention than narrative reviews because they employ
transparent methods designed to minimize bias

What can’t randomized trials and
systematic reviews tell us?

Theoretically, randomized trials could provide us with
estimates of the effects of every physical therapy intervention
and every component of every physical therapy
intervention. In practice, we are a long way from that
position, and it is likely we will never get there.
Randomized trials are cumbersome instruments.

They are able to provide unbiased estimates of the effects
of interventions, but do so at a cost. Many trials enroll
hundreds or even thousands of participants and follow
them for months or years. The magnitude of this undertaking
means that it is not possible to conduct trials to
examine the effects of every permutation of every component
of every intervention for every patient group.
In practice the best that randomized trials can provide
us with is indicative estimates of effects of typical interventions
administered in a small subset of reasonable
ways to typical populations, even though we know that
when the intervention is applied in clinical settings its
effects will vary depending on precisely how the intervention
is administered and precisely who the intervention
is administered to.
Randomized trials can suggest treatment approaches,
but the fi ne detail of how interventions are implemented
will always have to be supplemented by clinical experience,
by our understandings of how the intervention
works, and by common sense.
Randomized trials and systematic reviews of randomized
trials are suited to answering questions about
the effects of interventions, but are not able to answer
other sorts of questions. Different sorts of designs are
required to answer questions about the prognosis of a
particular condition or about the interpretation of a
diagnostic test (Herbert et al 2005).
A major limitation of randomized trials is that the
methods developed for analysing randomized trials can
only be applied to quantitative measures of outcomes.
But it is not possible to quantify the full complexity of
people’s thoughts and feelings with quantitative measures
(Herbert & Higgs 2004). If we want to understand
how people experience an intervention we need to
consult studies that employ qualitative methods, such
as focus groups or in-depth interviews, rather than randomized
trials. In general, qualitative methods cannot
tell us about the effects of intervention but, because they
can tell us about people’s experiences of intervention,
they can inform decisions about whether or not to intervene
in a particular way.

How can the evidence be located,
and how much evidence is there?

Several databases can be used to locate ran domized
trials and systematic reviews of the effects of
PubMed indexes the general health literature and can
be accessed free of charge at http://www.pubmed.
CENTRAL, part of the Cochrane Library (http://
www.mrw.interscience.wiley.com/cochrane/), specifi -
cally indexes randomized trials and is free in many
countries. (To see a list of countries from which
CENTRAL can be accessed free of charge, follow the
link to ‘Do you already have access?’).
The only database that specifi cally indexes randomized
trials and systematic reviews of physical therapy
interventions is PEDro. It is freely available at www.
pedro.fhs.usyd.edu.au. In May 2005, a quick search of
the PEDro database for records indexed as relevant to
the ‘pelvic fl oor or genitourinary system’ yielded 183
randomized trials and 40 systematic reviews. The quality
of these trials will be discussed in the next section.

Dimensions of quality of randomized trials
and systematic reviews

Randomized trials and systematic reviews vary greatly
in quality. There are high-quality studies that have been
carefully designed, meticulously conducted and rigorously
analysed, and there are low-quality studies that
have not!
Physical therapists must be able to differentiate
between high- and low-quality studies if they are to be
able to discern the real effects of intervention.
A key characteristic of high-quality randomized
trials and systematic reviews is that they are relatively
unbiased. That is, they do not systematically underestimate
or overestimate effects of intervention.
And of course high-quality trials and reviews must
also be relevant to clinical practice. That is, they must
tell us about the effects of interventions when administered
well to appropriate patients, and about the effects
of the intervention on outcomes that are important.
Finally, high-quality trials and reviews provide us with
precise estimates of the size of treatment effects. The
precision of the estimates is primarily a function of the
sample size (the number of subjects in a trial or the
number of subjects in all studies in the review). Thus
the highest quality trials and reviews, those that best
support clinical decision making, are large, unbiased
and relevant.
The following sections consider how readers of trials
and reviews can assess these aspects of quality.


Detecting bias in randomized trials
When we read reports of randomized trials we would
like to know if the trials are biased or not. Another way
of saying this is that we need to assess the validity (or
‘internal validity’) of the trials.
One way to assess internal validity is to see how well
the trial has been designed. Over the past 50 years methodologists
have refi ned the methods used to conduct
randomized trials to the extent that there is now consensus,
at least with regards to the main features of trial
design, about what constitutes best practice in the design
of clinical trials (Moher et al 2001, Pocock 1984). This
suggests we could assess internal validity of individual
trials by examining how well their methods correspond
to what is thought to be best practice in trial design.
Alternatively, we could base judgments about the
validity of trials on empirical evidence of bias. Several
studies have shown that, all else being equal, certain
design features are associated with smaller estimates of
the effects of intervention (e.g. Chalmers et al 1983,
Colditz et al 1989, Moher et al 1998, Schulz et al 1995).
This has been interpreted as indicating that these design
features are markers of bias.
Potentially we could use either of these approaches:
we could base decisions about the validity of trials
either on expert opinion or empirical evidence. There is
much debate about which is the best way to assess
validity. But fortunately both approaches suggest that
trial validity should be assessed by looking for the presence
of similar features of trial design.

Random allocation
Most methodologists believe that true random allocation
reduces the possibilities for bias, and some empirical
evidence supports this position (Kunz & Oxman
1998). To ensure that allocation is truly randomized it is
important to ensure that the person who recruits patients
into the trial is unaware, at the time he or she makes
decisions about whether or not to admit a patient into
the trial which group the patient would subsequently
be allocated to. Similarly, it is important that patients do
not know which group they would be allocated to. This
is referred to concealment of the allocation schedule.
Failure to conceal allocation potentially distorts randomization
because experimenters might be reluctant to
let patients with the most serious symptoms into the
trial if they know the patient is to be allocated to the
control group, and patients may be less likely to choose
to participate in the trial if they know they will subsequently
be allocated to the control group. This would
generate groups that are not comparable at baseline
with regard to disease severity, so it introduces potential
for serious bias. For this reason concealment is
thought to protect against bias in randomized trials.
Indeed, empirical evidence suggests failure to conceal
allocation may be one of the most important indicators
of bias (Chalmers et al 1983, Schulz et al 1995).
Of the trials of physical therapy for the pelvic fl oor
listed on the PEDro database, only 27% explicitly conceal
the allocation schedule.

A second key design feature is blinding. Blinding
implies that a person (such as a trial participant or a
person assessing trial outcomes) is unaware of whether
the trial participant is in the intervention group or the
control group.

Blinding of the participants in a trial is achieved by
giving a sham intervention to subjects in the control
group. Sham interventions are interventions that resemble
the intervention of interest, but are thought to have
no specifi c therapeutic effect. (An example of an attempt
to use a sham condition in a trial of an intervention for
the pelvic floor is the trial by Sand et al (1995) which
compared the effects of active transvaginal electrical
stimulation with sham stimulation.)
By providing a sham intervention all trial participants
can appear to receive intervention, but only the
intervention group receives active intervention. Consequently
trial participants can be ‘kept in the dark’ about
whether they are receiving the intervention or control
The usual justification for blinding trial participants
is that this makes it possible to determine if an intervention
has more of an effect than just a placebo effect.
In so far as placebo effects occur, they are expected to
occur to an equal degree in intervention and sham intervention
groups, so in sham-controlled trials the
estimated effect of intervention – the difference between
group outcomes – is not influenced by placebo effects.
An additional and perhaps more important justification
is that, in trials with self-reported outcomes, blinding
of participants removes the possibility of bias created
by patients misreporting their outcomes. In unblinded
trials, patients in the intervention group could exaggerate
improvements in their outcomes and patients in the
control group could understate improvements in their
outcomes, perhaps because they think this is what assessors
want to hear. When participants are blinded (when
they do not know if they received the intervention or
control conditions) there should be no difference in
reporting tendencies of the two groups, so estimates of
the effect of intervention (the difference between groups)
cannot be biased by differential reporting.
In most trials of physical therapy interventions for
the pelvic floor it is difficult to administer a sham intervention
that is both credible and inactive. For example,
it is difficult to conceive of a sham intervention for training
pelvic floor muscles. In that case the best alternative
may be to deliver an inactive intervention to the control
group, even if the inactive intervention does not exactly
resemble the active intervention. An example is the trial
by Dumoulin et al (2004) that compared pelvic floor
rehabilitation (electrical stimulation of pelvic floor
muscles plus pelvic floor muscle exercises) with biofeedback.
These authors gave the control group relaxation
massage to the back and extremities in the belief
that this would control, to some degree, the effects of
placebo and misreporting of outcomes. Such trials
provide some control, but perhaps not complete control,
of the confounding effects of placebo and misreporting
of outcomes.
The difficulties of providing an adequate sham intervention
preclude participant blinding in most trials of
physical therapy interventions for the pelvic floor. Only
6% of these trials truly blind participants.
It is also desirable that the person assessing trial
outcomes is blinded. Blinding of assessors ensures that
assessments are not biased by the assessor’s expectations
of the effects of intervention. When objective
outcome measures are used, blinding of assessors is
easily achieved by using assessors who are not otherwise
involved in the study and are not told about which
patients are in the intervention and control groups.
However, blinding of assessors is more difficult when
trial outcomes are self-reported (as, for example, in
studies which ask women whether they ‘leak’). In that
case the assessor is really the participant, and the assessor
is only blind if the participant is blind.
A third feature of trial design that is likely to determine
a trial’s validity is the level of follow-up.
In most trials participants are randomized to groups,
but for various reasons outcome measures are not subsequently
obtained from all participants. Such ‘loss to
follow-up’ occurs, for example, when subjects become
too ill to be measured, or they die, go on holiday, or
have major surgery, or because the researchers lose
contact with the participant. Loss to follow-up potentially
‘unran domizes’ allocation, and can produce systematic
differences in the characteristics of the two
groups, so it potentially biases estimates of the effects
of intervention.
How much loss to follow-up is acceptable in a randomized
trial? When is loss to follow-up so extreme that
it potentially causes serious bias? There is no simple
and universally applicable answer to these questions.
However methodologists have applied threshold losses
to follow-up of between about 10 and 20%. Losses to
follow-up of less than 10% of randomized subjects are
usually considered unlikely to produce serious bias, and
losses to follow-up of greater than 20% are thought be
a potential source of serious bias.
Fortunately most trials of physical therapy interventions
for the pelvic fl oor have adequate follow-up: 67%
of the relevant trials have loss to follow-up of less than
A related but more technical issue concerns problems
with deviations from the trial protocol. Protocol deviations
occur when, for example, people do not receive the
intervention as allocated (e.g. if participants in an exercise
group do not do their exercise), or if outcome
measures are not measured at the allocated times. This
presents a dilemma for the person analysing the data:
should data from these subjects be excluded? Should
data from subjects who did not receive the intervention
be analysed as if those subjects had been allocated to the
control group? The answer to both questions is no!
Most methodologists believe that the best way to
deal with protocol violations is to analyse the data as if
the protocol violation did not occur. In this approach,
called ‘analysis by intention to treat’ (Hollis & Campbell
1999), all subjects’ data are analysed, regardless of
whether they received the intervention as allocated or
not, and their data are analysed in the group to which
they were allocated.

Analysis by intention to treat is thought to be the
least biased way to analyse trial data in the presence of
protocol violations. Of the relevant trials on PEDro 24%
explicitly analyse by intention to treat.

Detecting bias in systematic reviews
The search strategy
Systematic reviewers attempt to provide an un biased
summary of the fi ndings of relevant trials. Ideally systematic
reviews summarize the fi ndings of all relevant
trials that had ever been conducted. That would achieve
two ends: it would ensure that the reviewer had taken
full advantage of all of the information available from
all extant trials, and it would mean that the summary of
the findings of the trials was not biased by selective
reporting of only those trials with atypical estimates of
the effects of the intervention.
Unfortunately it is usually not possible to fi nd complete
reports of all relevant trials: reports of some trials
are published in obscure journals, others are published
in obscure languages, many are published only in
abstract format, and some are not published at all. Consequently
even the most diligent reviewers will fail to
find some trial reports.
Given that it is usually not possible to fi nd reports of
all relevant trials the next best thing is for reviewers to
obtain reports of nearly all trials. We can use reviews
that summarize nearly all relevant trial reports to tell
nearly all of what is known about the effectiveness of
the intervention.
Incomplete retrieval of trial reports raises another
problem. If reviewers do not identify all trial reports
then there is the possibility that they have retrieved a
particular subset of trials with exceptionally optimistic
or pessimistic estimates of the effect of the intervention.
We would like to be reassured when reading a systematic
review that the reviewer has located a representative
subset of all trials. That is, we would like to know
that the reviewer has not selectively reported on trials
that provide overly optimistic or pessimistic estimates
of the effects of intervention. Even if we cannot expect
reviewers to fi nd reports of all trials we can require that
they fi nd an unbiased subset of nearly all trials.
To this end, most reviewers conduct quite thorough
literature searches. For a Cochrane systematic review
of pelvic fl oor muscle training (PFMT), for urinary
incontinence in women, Hay-Smith et al (2000)
searched the Cochrane Incontinence Group trials
register, Medline, Embase, the database of the Dutch
National Institute of Allied Health Professions,
CENTRAL, Physical Therapy Index and the reference
lists of relevant articles. They also searched the proceedings
of the International Continence Society page by
page. Some reviewers include trials published only as
abstract form, whereas others include only full papers
on the grounds that most abstracts have not been peer
reviewed and often contain too little information to be
Occasionally systematic reviewers conduct limited
searches, for example by searching only Medline. This
is potentially problematic: although Medline is the
largest database of the medical literature such searches
are likely to miss much of the relevant literature. It has
been estimated that Medline only indexes between 17
and 82% of all relevant trials (Dickersin et al 1994).
When reading a systematic review it is important to
check that the literature search in the review is reasonably
recent. If a report of a systematic review is more
than a few years old it is likely several trials will have
been conducted since the search was conducted, and
the review may provide an out-of-date summary of the

Assessment of trial quality
Systematic reviewers may fi nd a number of trials that
investigate the effects of a particular intervention, and
often the quality of the trials is varied. Obviously it is
not appropriate to weight the fi ndings of all trials
without regard to trial quality. Particular attention
should be paid to the highest quality trials because these
trials are likely to be least biased; the poorest quality
trials should be ignored. Systematic reviews should
assess the quality of the trials in the review, and quality
assessments should be taken into account when drawing
conclusions from the review.
A range of methods have been used to assess the
quality of trials in systematic reviews. The most common
approach is to use a quality scale to assess quality, and
then to ignore the fi ndings of trials with low-quality
scores. Commonly used scales include the Maastricht
scale (Verhagen et al 1998) and the PEDro scale (Maher
et al 2003); a copy of the PEDro scale is shown in Box
2.3. These scales assess quality based on the presence or
absence of design features thought to infl uence validity,
including true concealed randomization, blinding of
participants and assessors, adequate follow-up and
intention to treat analysis.
This approach sounds sensible, but there are some
reasons to think that it may discriminate inappropriately
between trials. The available evidence suggests
there is only moderate agreement between the ratings
of different quality scales (Colle et al 2002). Nonetheless,
it is not known how better to assess trial quality, so these
rudimentary procedures must suffi ce for now. For the
time being we should expect systematic reviews to take
intervention, as long as the application of the intervention
in the trial was not obviously suboptimal.

Trials of a particular intervention may be carried out
on quite different patient groups. Readers need to be
satisfi ed that the trial was applied to an appropriate
group of patients. It could be reasonable to ignore the
fi ndings of a trial if the intervention was administered
to a group of patients for whom the intervention was
generally considered inappropriate. An example might
be the application of pelvic fl oor exercises to reverse
prolapse in women who already have complete prolapse
of the internal organs. Most therapists would
agree that once prolapse is complete conservative intervention
is no longer appropriate and surgical intervention
is necessary.
The same caveat applies here: it is impossible to
know with certainty, at the time a trial is conducted,
who an intervention will be most effective for. Again we
must be prepared to give trialists some latitude: we
should be prepared to trust the fi ndings of trials that test
interventions on patients other than the patients we
might choose to apply the intervention to, as long as the
patient group was not obviously inappropriate.

The last important dimension of the relevance of a
clinical trial concerns the outcomes that are measured.
Ultimately, if an intervention for the pelvic fl oor is to
be useful, it must improve quality of life. Arguably
there is little value in an intervention that increases the
strength of pelvic fl oor muscles if it does not also
increase quality of life.
Studies of variables such as muscle strength can help
us understand the mechanisms by which interventions
work, but they cannot tell us if the intervention is worth
doing. The trials that best help us to decide whether or
not to apply an intervention are those that determine
the effect of intervention on quality of life.
Many trials do not measure quality of life directly,
but instead they measure variables that are thought to
be closely related to quality of life. For example, Bø
et al (2000) determined the effect of PFMT for women
with stress urinary incontinence (SUI) on the risk of
incontinence-related problems with social life, sex life,
and physical activity. It would appear reasonable to
expect that problems with social life, sex life and physical
activity directly infl uence quality of life, so this trial
provides useful information with which to make decisions
about PFMT for women with SUI.
In general trials can help us make decisions about
intervention in so far as they measure outcomes that are
related to quality of life.


The most useful piece of information a clinical trial can
give us is an estimate of the size of the effects of the
intervention. We can use estimates of the effect of intervention
to help us decide if an intervention does enough
good to make it worth its expense, risks and inconvenience
(Herbert 2000a, 2000b).
Obtaining estimates of the effects of
intervention from randomized trials and
systematic reviews

Most people experience an improvement in their condition
over the course of any intervention. But the magnitude
of the improvement only partly refl ects the
effects of intervention. People get better, often partly
because of intervention, but usually also because the
natural course of the condition is one of gradual
improvement or because apparently random fl uctuations
in the severity of the condition tend to occur in the
direction of an improvement in the condition. (The latter
is called statistical regression; for an explanation see
Herbert et al 2005.) In addition, part of the recovery may
be due to placebo effects or to patients politely overstating
the magnitude of the improvements in their
As several factors contribute to the improvements
that people experience over time, the improvement in
the condition of treated patients cannot provide a
measure of the effect of intervention.
A far better way to estimate the effects of intervention
is to look at the magnitude of the difference in outcomes
of the intervention and control groups. This is
most straightforward when outcomes are measured on
a continuous scale. Examples of continuous outcome
measurements are pad test weights, measures of global
perceived effect of intervention, or duration of labour.
These variables are continuous because it is possible to
measure the amount of the variable on each subject.
An estimate of the mean effects of intervention on
continuous variables is obtained simply by taking the
difference between the mean outcomes of the intervention
and control groups. For example, a study by Bø
et al (1999) compared pelvic fl oor exercises with a noexercise
control condition for women with SUI. The
primary outcome was urine leakage measured using a
stress pad test. Over the 6-month intervention period
women in the control group experienced a mean reduction
in leakage of 13 g whereas women in the PFMT
group experienced a mean reduction of 30 g. Thus the
mean effect of exercise, compared to controls, was to
reduce leaking by about 17 g (or about 50% of the initial
Other outcomes are dichotomous. Dichotomous outcomes
cannot be quantified on a scale; they are events
that either happen or not. An example comes from the
trial by Chiarelli & Cockburn (2002) of a programme of
interventions designed to prevent post-partum incontinence.
Three months postpartum, women were classified
as being continent or incontinent. This outcome
(incontinent/continent) is dichotomous, because it can
have only one of two values.
When outcomes are measured on a dichotomous
scale we can no longer talk meaningfully about the
mean outcome. Instead we talk about the risk (or probability)
of the outcome; our interest is in how much
intervention changes the risk of the outcome.
Chiarelli and colleagues found that 125 of the 328
women in the control group were still incontinent at 3
months, and 108 of 348 women in the intervention
group were still incontinent at 3 months. Thus the risk
of being incontinent at 3 months was 125/328 (38.1%)
for women in the control group, but this risk was
reduced to 108/348 (31%) in the intervention group. So
the effect of the 3-month intervention was to reduce the
risk of incontinence at 3 months postpartum by 7.1%
(i.e. 38.1 − 31.0%). This figure, the difference in risks, is
sometimes called the absolute risk reduction. An absolute
risk reduction of 7.1% is equivalent to preventing
incontinence in one in every 14 women treated with the
Using estimates of the effects of intervention
Estimates of the effects of intervention can be used to
inform the single most important clinical decision:
whether or not to apply a particular intervention for a
particular patient.
Decisions about whether to apply an intervention
need to weigh the potential benefits of intervention
against all negative consequences of intervention. So,
for example, when deciding whether or not to undertake
a programme of PFMT, a woman with SUI has to
decide if the effects of intervention (including an
expected reduction in leakage of about one-half) warrants
the inconvenience of daily exercise. And when
deciding whether to embark on a programme to prevent
postpartum incontinence a woman needs to decide
whether she is prepared to undertake the programme
for a 1 in 14 chance of being continent when she otherwise
would not be.
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