Conservative management for postprostatectomy urinary incontinence

Continence mechanisms

Urinary continence depends on a complex interaction of smooth and striated muscle fibres blended together to form the continence mechanism. Considerable debate has existed in the literature as to whether incontinence after prostatectomy is due to an effect on the detrusor (bladder) muscle or on the sphincter, as commonly these abnormalities coexist (Peyromaure 2002). New detrusor overactivity and intrinsic sphincter deficiency due to sphincteric injury (Ficazzola 1998; Groutz 2000; McGuire 1990) or weakness (Majoros 2006) are cited as the most important causes of persistent incontinence after radical prostatectomy. Debate continues on whether detrusor overactivity is a primary or secondary factor. Whereas some report overactivity as the primary cause of postprostatectomy incontinence (Golubuff 1995; Leach 1995) others argue strongly that even if other factors play a role, intrinsic sphincter deficiency is the primary cause of UI after radical prostatectomy (Aboseif 1996; Chao 1995; Groutz 2000; Gudziak 1996; Kondo 2002; Majoros 2006; Winters 1997).

Risk factors for postprostatectomy UI after radical prostatectomy include pre‐existing abnormalities of detrusor contractility (Leach 1995) and older age (Kondo 2002). This is possibly because in older men there is evidence of rhabdosphincter atrophy and neural degeneration (Burnett 1998; Chao 1995). Other risk factors include previous TURP (Jacobsen 2007); pre‐operative radiotherapy (Kondo 2002; Rainwater 1988); trauma; a spinal cord lesion; new obstruction due to recurrence, bladder neck contracture, or urethral stricture (Litwiller 1997); Parkinson's disease (Kondo 2002); dementia; and medications (Khan 1991). A surgeon's inadequate skill and expertise can determine post‐operative incontinence rates (Eastham 1996). In addition, having surgery in a hospital which performs fewer than 20 radical prostatectomies a year may be a factor (Albertsen 1997).

After TURP, UI is thought most likely to be due to pre‐existing abnormalities of bladder function, such as poor compliance or detrusor overactivity, rather than direct sphincter injury (Abrams 1991), possibly because removal of the prostatic tissue removed some of the protective mechanism for continence.

1. Pelvic floor muscle training (PFMT)

This involves any method of training the pelvic floor muscles to contract. It includes teaching performance of an accurate voluntary pelvic floor muscle contraction using biofeedback and co‐ordinating and timing the contraction against increases in intra‐abdominal pressure, often called functional PFMT.

Traditionally, biofeedback involves the use of equipment to provide visual or auditory feedback about the pelvic floor muscle function to enable one to train, strengthen and increase endurance and co‐ordination of the pelvic floor muscle contractions. Simple auditory biofeedback can also be provided by the therapist informing the patient when a contraction is felt through digital anal examination during the pelvic floor muscle contraction. Additionally, pelvic floor muscle contraction electromyography (EMG) can be used as a surrogate for biofeedback, as well as for measuring the intra‐rectal pressure.

The theoretical basis of PFMT is that repeated, volitional contractions of selected pelvic floor muscles may improve their strength and efficiency during periods of increased intra‐abdominal pressure and can inhibit detrusor activity. In a systematic review of the literature on female UI, Berghmans and colleagues noted that a pelvic floor muscle contraction may raise the urethra and press it towards the symphysis pubis, prevent urethral descent, and improve structural support of the pelvic organs (Berghmans 1998). They further pointed out that PFMT may result in hypertrophy of the peri‐urethral striated muscles thereby increasing the 'external mechanical pressure' on the urethra.

2. Electrical stimulation (non‐invasive) delivered via surface electrodes

Electrical stimulation (ES) works by activating the motor fibres of the pudendal nerve, which can result in contraction of the pelvic floor muscles or the striated peri‐urethral musculature, supporting the intrinsic part of the urethral sphincter closing mechanism (Berghmans 2013). This may be important in the management of men with SUI by stimulating the intrinsic sphincter, strengthening the pelvic muscles and raising the patient's awareness of these muscles in a similar way to biofeedback. ES can also be helpful in men with detrusor overactivity or UUI because it can stimulate afferent fibres of the pudendal nerve, decreasing the sensation of urgency and inhibiting parasympathetic activity which results in a decrease in involuntary detrusor contractions (Berghmans 2013). Two types of non‐invasive ES are detailed below. The parameters of the ES used in studies vary depending on the type of UI and ES. Parameters include pulse width and duration, current intensity, stimulus frequency, current source, pulse shape, duration of treatment and total number of sessions, and rest to work ratio.

3. Lifestyle adjustment

This includes fluid adjustment, healthy diet, avoiding excessive caffeine, physical exercise, weight loss and cessation of smoking.

4. Extra‐corporeal magnetic innervation

This involves the use of a magnetic chair to stimulate contraction of the pelvic floor muscles and sacral nerve roots, without the discomfort of inserting an anal probe (Galloway 2000).

5. External penile compression devices (penile clamps)

These devices use an external clamp to achieve non‐surgical compression of the urethra.

Timing of the intervention

Conservative treatment can be started before or after surgery. In general, when it is delivered to all men (whether before or after) the aim is to prevent the development or persistence of UI. We have therefore distinguished between treatment of all men who do have UI (treatment) as opposed to a mixed population of men some of whom do not have UI (prevention).

Types of studies

Randomised controlled trials and quasi‐randomised trials of conservative management to prevent or treat UI after TURP or radical prostatectomy were included. Trials were included if they used any single conservative therapy or any combination of conservative therapies. Other forms of clinical trials were excluded. Analysis of trials in men having radical prostatectomy was done separately from those in men having a TURP.

Types of participants

Adult men with UI following prostatectomy.

Types of interventions

PFMT; biofeedback (verbal or machine‐mediated); electrical stimulation (ES) via a surface electrode (e.g. anal probe ES, sticky patch electrode, transcutaneous electrical nerve stimulation (TENS)); extra‐corporeal magnetic innervation (ExMI); lifestyle adjustment; and external penile compression devices. These interventions could be compared with no treatment or with each other, alone or in combination.

The following comparisons were made for treatment or prevention of UI after prostatectomy.

Types of outcome measures

Electronic searches

This review has drawn on the search strategy developed for the Incontinence Review Group. Relevant trials were identified from the Incontinence Review Group Specialised Register of controlled trials which is described, along with the Group's search strategy, in the Incontinence Group's module in The Cochrane Library. The register contains trials identified from the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, MEDLINE In‐Process, and handsearching of journals and conference proceedings. The Incontinence Group Specialised Register was searched using the Group's own keyword system; the search terms used were:
 ({design.cct*} OR {design.rct*})
 AND
 ({topic.urine.incon.postprost*})
 (All searches were of the keyword field of Reference Manager 2012).
 The date of the most recent search of the Specialised Register for this review was 5 February 2014. Most of the trials in the Incontinence Group Specialised Register are also contained in CENTRAL.

Specific searches were also performed for this update of the review.

• CENTRAL (OvidSP) (2014, Issue 1) was searched on 26 February 2014.

• EMBASE (OvidSP) (January 2010 to Week 3 2014) was searched on 20 January 2014.

• CINAHL (EBSCOhost) (January 1982 to 18 January 2014) was searched on 22 January 2014.

• ClinicalTrials.gov (via the Cochrane Register of Studies (CRS) interface) and World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (both searched on 29 January 2014).

The strategies used to search these databases can be found in Appendix 3.

Searching other resources

Selection of studies

The list of abstracts for each update was reviewed independently by two review authors and results compared. The full text articles of references or abstracts identified as potentially relevant by either review author were retrieved and reviewed by both. Reference lists of relevant review articles were reviewed to identify any further trials. References were assessed based on the population, interventions, control management, outcomes and overall study design. Using the full texts of the potentially relevant published studies and abstracts, the same two review authors independently reviewed the studies for relevance and inclusion. Authors were contacted for further data or clarification of methods. Disagreements were resolved through discussion; third party arbitration was not required.

Attempts were made to contact authors of trial reports if clarification was necessary. Studies were excluded from the review if they made comparisons other than those pre‐specified or if data were unavailable. Excluded studies were listed with reasons for their exclusion.

Data extraction and management

Data for the trials were extracted independently by two review authors using a standard form developed for this purpose. The following information was included:

• study method and characteristics (design, method of randomisation, inclusion and exclusion criteria, withdrawals and dropouts);

• participants (type of surgery, age, timing of randomisation, baseline incontinence or not);

• type of intervention, timing (before or after surgery, or both) and duration of therapy, co‐interventions;

• control (no treatment or sham therapy or other active treatment);

• outcomes (types of outcome measures, reported outcomes, adverse events).

Extracted data were compared by two review authors for completeness and accuracy, and cross‐checked by another review author if necessary. Disagreements were resolved through discussion and review of the trial report. New data were entered using RevMan5 software.

Assessment of risk of bias in included studies

The risk of bias of the trials was assessed using the Cochrane 'risk of bias' tool.

The following methodological parameters were recorded:
 1) identification of study as randomised or quasi‐randomised;
 2) description of inclusion and exclusion criteria;
 3) potential for selection bias (method of sequence generation, adequacy of random allocation concealment) rating;
 4) potential for bias around the time of treatment or during outcome assessment (blinding of participants, personnel, outcome assessors);
 5) potential for selection bias in the analysis (description of withdrawals, dropouts, participants lost to follow up, analysis based on intention to treat).

Measures of treatment effect

Analyses were based on available data from all included trials that were relevant to the comparisons and outcomes of interest. Meta‐analysis was undertaken where data were available from more than one study assessing the same outcome. A fixed‐effect model was used for calculations of pooled estimates and their 95% confidence intervals (CIs), or a random‐effects model if there was heterogeneity. For categorical outcomes we related the numbers reporting an outcome to the numbers at risk in each group to calculate a risk ratio (RR) with 95% CI. For continuous variables we used means and standard deviations to calculate a mean difference (MD) with 95% CI. If similar outcomes were reported on different scales, we calculated the standardised mean difference (SMD). We reversed the direction of effect if needed to ensure consistency across trials. If data to calculate RRs or MDs were not given, we utilised the most detailed numerical data available to calculate the actual numbers or means and standard deviations (for example test statistics, P values).

Unit of analysis issues

The primary analysis was per man randomised.

Dealing with missing data

Analysis of the data was on an intention‐to‐treat basis to the furthest possible extent. This meant all participants were analysed in the groups to which they were randomised. If this was not the case, we considered whether to exclude the trial. Attempts were made to obtain missing data from the original trialists. However, if this was not possible data were reported as given in the studies, except if there was evidence of differential loss to follow up from the randomised groups. In that case, the use of imputation of missing data was considered. If trials reported sufficient detail to calculate MDs but gave no information on the associated standard deviation (SD), the outcome was assumed to have a SD equal to the highest SD from other trials within the same analysis.

Assessment of heterogeneity

Trials were only combined if they were thought to be clinically similar. We assessed heterogeneity between studies by visual inspection of plots of the data, the Chi² test for heterogeneity and I²statistic (Higgins 2011). We used the thresholds for interpretation of the I² statistic in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2003).

Assessment of reporting biases

Due to the difficulty of detecting and correcting for publication bias and other reporting biases, the authors aimed to minimise their potential impact by ensuring a comprehensive search for eligible studies and by being careful to watch for duplication of data. Funnel plots could not be utilised because there were fewer than 10 trials in each meta‐analysis.

Data synthesis

Included trial data were processed as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

For dichotomous outcomes, data were summarised (for example number of people for whom an outcome is present or not) and risk ratios (RR) calculated with their 95% CIs. For continuous outcomes, each trial was summarised using the mean value for each group and SD, and combined as mean difference (MD) if the same scale (for example pad test in grams of urine) was used for the outcome measurement in more than one trial. A fixed‐effect model was used to calculate the summary statistic and the 95% CI. Heterogeneity was assessed visually and using the Chi² test for heterogeneity and the I² statistic (Higgins 2003). Forest plots were examined and potential sources influencing heterogeneity identified. Possible sources of heterogeneity were explored statistically through subgroup analysis. Where synthesis was deemed not appropriate, a narrative overview was planned.

Trials were combined if interventions were based on similar clinical criteria. To combine trial data, a meta‐analysis was conducted and a fixed‐effect model approach to the analysis was utilised unless there was evidence of heterogeneity across studies, in which case a random‐effects model was used.

Subgroup analysis and investigation of heterogeneity

We planned to perform subgroup analysis based on cancer stage but there were not enough data.

Sensitivity analysis

We planned to perform sensitivity analysis to investigate the effect of including or excluding trials at high risk of bias, however not enough trials were in the meta‐analysis.

Results of the search

For the current update (2014) of the review 764 possibly relevant articles and abstracts were identified. Sources and numbers of potentially eligible titles were:

• Incontinence Review Group Specialised Register (193);

• CENTRAL (37);

• updated search of EMBASE (354);

• CINAHL (23);

• ClinicalTrials.gov (125);

• WHO ICTRP (32).

Overall 96 reports of 50 studies were included in the qualitative synthesis. Fifty‐nine reports of 27 studies were included in the quantitative synthesis. Four trials are awaiting further information from the authors (Crivellaro 2011;Delmastro 2010; Lilli 2006 NEW; Zhang 2007) and eight trials are ongoing (Burnett 2012; Burnett 2013;Fode 2012 NEW;Goode 2014;Mina 2013; Ng 2011;Terrone 2007; Zopf 2012).

Forty‐one reports of 36 studies were excluded and reasons are given in the 'Characteristics of excluded studies' table. The flow of the literature through the assessment process is shown in the PRISMA study flow chart (Figure 1).

Included studies

Excluded studies

In total 36 studies were excluded. The majority of the studies that did not meet the inclusion criteria were excluded because the study design was not appropriate or the intervention was not relevant for the population of interest. See the Excluded studies table for a more detailed description.

Allocation

Blinding

Blinding was not described in most trials. In complex interventions such as physical therapy it is not possible to blind either the clinicians or the participants from the intervention, however, if blinding did not take place in trials they were judged to be at high risk of bias. This may have an impact on the outcome of interest and was considered while assessing the quality of evidence. Yamanishi 2006 used a sham device for the control group and this was the only trial that was deemed to be at low risk of bias in terms of blinding of participants.

In terms of blinding of personnel:

• 9 trials (Burgio 2006; Centemero 2009; Dijkstra‐Eshuis 2013; Geraerts 2013; Moore 1999; Moore 2008; Porru 2001; Tienforti 2012; Yamanishi 2006) were deemed to be at low risk of bias;

• 17 trials (Bales 2000; Filocamo 2005; Floratos 2002; Glazener RP 2011; Glazener TURP 2011; Hou 2013; Joseph 2000; Liu 2008; Manassero 2007; Marchiori 2010; Moore 2004; Overgard 2008; Parekh 2003; Park 2012; Ribeiro 2008; Robinson 2008; Seleme 2008) were deemed to be at high risk of bias; and

• 23 trials (Ahmed 2012; Dubbelman 2004; Fader 2013; Fode 2014; Franke 1998; Ghanem 2013; Goode 2009; Hoffman 2005; Koo 2009; Laurienzo 2013; Mariotti 2009; Martini 2011; Mathewson‐Chapman 97; Morihiro 2011; Nowak 2007; Opsomer 1994; Perissinotto 2008; Robinson 2009; Tobia 2008; van Kampen 1998; Wille 2003; Yokoyama 2004; Zhang 2007) were at unclear risk.

Burgio 2006; Moore 1999 and Moore 2008 indicated that a single therapist, blinded to control group outcomes, provided all treatment. Dijkstra‐Eshuis 2013 and Geraerts 2013 reported that the post‐operative physiotherapist was blinded to allocation and physical therapy provided by the pre‐operative therapist.

In terms of blinding of outcome assessment:

• 7 trials (Burgio 2006; Dijkstra‐Eshuis 2013; Geraerts 2013; Moore 2008; Park 2012; Tienforti 2012; Yamanishi 2006) were deemed to be at low risk of bias because they had outcome assessors who were not involved in the provision of the intervention or were not aware of allocation when entering data;

• 1 trial (Fode 2014) was found to be at high risk of bias; and

• 42 trials (Ahmed 2012; Bales 2000; Centemero 2009; Dubbelman 2004; Fader 2013; Filocamo 2005; Floratos 2002; Franke 1998; Ghanem 2013; Glazener RP 2011; Glazener TURP 2011; Goode 2009; Hoffman 2005; Hou 2013; Joseph 2000; Koo 2009; Laurienzo 2013; Liu 2008; Manassero 2007; Marchiori 2010; Mariotti 2009; Martini 2011; Mathewson‐Chapman 97; Moore 1999; Moore 2004; Morihiro 2011; Nowak 2007; Opsomer 1994; Overgard 2008; Parekh 2003; Perissinotto 2008; Porru 2001; Ribeiro 2008; Robinson 2008; Robinson 2009; Seleme 2008; Tibaek 2007; Tobia 2008; van Kampen 1998; Wille 2003; Yokoyama 2004; Zhang 2007) were at unclear risk because this information was not provided.

Yamanishi 2006 used a sham device for the control group but there was no statement of whether assessors were aware of this or not.

Incomplete outcome data

Several trials gave no description or did not report dropouts (Centemero 2009; Ghanem 2013; Koo 2009; Marchiori 2010; Morihiro 2011; Perissinotto 2008; Ribeiro 2008; Robinson 2009; Seleme 2008; Yamanishi 2006; Yokoyama 2004), or did not have withdrawals or dropouts (Bales 2000; Liu 2008; Moore 2004; Tobia 2008).

All others reported the number of withdrawals or dropouts, although the reasons were not consistently reported and few, except Moore 2008 and Robinson 2008, discussed how this was dealt with in the analysis. In one trial, outcomes beyond eight weeks were not available for the control group because all the men were treated, and data were not available for over a third of the men in the other two intervention groups (Goode 2009). Two trials were thought to be at risk of bias because of differential dropout from the randomised groups (Dubbelman 2004; Manassero 2007). One trial (Marchiori 2010) that was judged to be at high risk of bias reported that the survey questionnaire used for one of their outcomes was completed correctly but returned by fewer than 10% of the men.

Six trials (Fader 2013; Martini 2011; Nowak 2007; Perissinotto 2008; Robinson 2008; Robinson 2009) did not provide any usable data. Three of these trials (Nowak 2007; Perissinotto 2008; Robinson 2009) did not report how many men were randomised to each group.

Selective reporting

There was significant difficulty in assessing selective outcome reporting because the protocols for most of the included trials were not available for assessment or could not be found. For a few of the trials, data were not available for some of the outcomes stated in the methods section.

Other potential sources of bias

Information about funding was available for 27 of the included studies (Burgio 2006; Centemero 2009; Dijkstra‐Eshuis 2013; Fader 2013; Fode 2014; Franke 1998; Geraerts 2013; Ghanem 2013; Glazener RP 2011; Glazener TURP 2011; Goode 2009; Laurienzo 2013; Moore 1999; Moore 2004; Moore 2008; Morihiro 2011; Overgard 2008; Park 2012; Perissinotto 2008; Ribeiro 2008; Robinson 2008; Robinson 2009; Seleme 2008; Tibaek 2007; van Kampen 1998; Yamanishi 2006; Zhang 2007) and the studies were judged to be at low risk of bias. The rest of the trials were judged to be at unclear risk of bias because there was a lack of information even after contacting the authors.

Thirty‐two trials reported obtaining approval from a medical ethics committee (Ahmed 2012; Burgio 2006; Centemero 2009; Dijkstra‐Eshuis 2013; Dubbelman 2004; Fader 2013; Filocamo 2005; Fode 2014; Geraerts 2013; Ghanem 2013; Glazener RP 2011; Glazener TURP 2011; Goode 2009; Laurienzo 2013; Liu 2008; Manassero 2007; Mathewson‐Chapman 97; Moore 1999; Moore 2004; Moore 2008; Morihiro 2011; Overgard 2008; Park 2012; Perissinotto 2008; Ribeiro 2008; Robinson 2008; Robinson 2009; Seleme 2008; Tibaek 2007; Tienforti 2012; Yamanishi 2006; Yokoyama 2004) and were judged to be at low risk of bias. The remaining 18 trials did not report their source of medical ethical approval and were judged to be at unclear risk of bias after no further information was provided by the authors.

Fourteen trials were deemed to be at unclear risk of bias in terms of obtaining informed consent (Bales 2000; Burgio 2006; Hoffman 2005; Hou 2013; Joseph 2000; Koo 2009; Liu 2008; Marchiori 2010; Martini 2011; Nowak 2007; Opsomer 1994; Parekh 2003; Tobia 2008; Zhang 2007). These authors were contacted but no further information on this matter was provided. The other trials did report obtaining informed consent from patients and therefore were deemed to be at low risk of bias for this domain.

Radical prostatectomy: treatment of incontinent men after surgery

Radical prostatectomy: prevention of UI in all men having surgery, intervention before or after prostatectomy or both

TURP: treatment of incontinent men, after surgery

TURP: prevention of UI in all men having surgery, intervention before or after prostatectomy, or both

Containment of UI (all men with residual UI)

Treatment trials for urinary incontinence after radical prostatectomy

Twenty‐one trials investigated the effects of PFMT versus no treatment or a variety of other means of stimulating the pelvic floor muscles. There was considerable clinical and statistical heterogeneity in the populations and the timing and frequency of the interventions, hence a random‐effects model was chosen for most of the comparisons where meta‐analysis was possible. Only two trials (Manassero 2007; van Kampen 1998) showed a statistically significant benefit from active treatment versus no treatment control groups (at 12 months and within 6 to 12 months respectively), and the other trials showed conflicting results. There was differential dropout from the control group in the Manassero 2007 trial (these men were assumed to be dry for analysis purposes). Additionally, men in the experimental group in the van Kampen 1998 trial received one session of PFMT in hospital before discharge and were then seen by a physiotherapist for one to two weeks, whereas those in the Manassero 2007 trial were taught PFMT by two urologists using verbal feedback and instructed to perform contractions at home. Because of the heterogeneity a random‐effects model was used, which led to wider confidence intervals (CIs).

Overall, there was not enough evidence to say whether or not PFMT with or without biofeedback was effective as the CIs were wide (for example number of men with incontinence in the intervention groups 193/339 (57%) versus 203/326 (62%) in the control groups, RR for incontinence after 12 months 0.85, 95% CI 0.60 to 1.22, Analysis 1.1.4).

The meta‐analysis was dominated by the Glazener RP 2011 trial, which was a large pragmatic multi‐centre trial conducted in a context where information on PFMT was widely available. This showed no good evidence to support one‐to‐one training by a therapist (for example RR for UI after 12 months 0.98, 95% CI 0.87 to 1.09, Analysis 1.1.4) (Glazener RP 2011). This one large trial had narrow CIswhich did not include a clinically significant difference, pre‐specified to be 15%. The only other large trial (Moore 2008) was in line with the Glazener RP 2011 findings but with wider CIs (RR 1.02, 95% CI 0.70 to 1.48, Analysis 1.1.4) (Moore 2008) despite a more intensive intervention. While men in the Glazener RP 2011 trial had four therapy sessions over three months, in the Moore 2008 trial men were seen weekly for up to six months. The findings in these two trials concurred despite different intensities of intervention, and the quality of evidence for this GRADE‐specific outcome was moderate. Data from quality of life measures and use of pads and pad tests supported the finding of no differences between intervention and control groups.

Three small trials provided data and the meta‐analysis suggested that ES was better than control interventions in terms of less incontinence, regaining continence more quickly and better quality of life, at least in the short term up to six months. The quality of evidence was deemed to be moderate, however less information was available for the longer term.

Individual small trials provided data to suggest that extra‐corporeal magnetic innervation (ExMI) or combinations of treatments might be beneficial but the evidence was limited.

Prevention trials for urinary incontinence after radical prostatectomy

Nineteen trials, some of which enrolled men before surgery and others all men as soon as the catheter was removed, included a mixed population of men with and without incontinence after surgery. Again a random‐effects model was chosen to compensate for the considerable clinical and statistical heterogeneity between the trials. Including the information from the quasi‐randomised trial (Filocamo 2005), the chance of incontinence appeared to be lower in the intervention groups in two trials with data after 12 months. The quality of evidence was judged to be moderate (number of men with UI after one year 10.2% versus 32.1% in the control groups, RR 0.32, 95% 0.20 to 0.51, Analysis 6.1.4).

The meta‐analysis of prevention trials included a number of small trials with wide CIs apart from Filocamo 2005, which was out of line with the others. This was the only large trial to favour the intervention group. The worry is that this trial may have been biased due to a lack of reporting on concealment of allocation.

One small trial (Ribeiro 2008) suggested that men were more likely to be carrying out PFMT, at least soon after the intervention (Analysis 6.9), though this was not reflected in significant differences in higher anal squeeze pressures (Analysis 6.8). Another trial of anal ES was too small to be conclusive (Laurienzo 2013). One small trial (Mariotti 2009) reported that adding anal ES and biofeedback to PFMT was beneficial. One further small trial (Wille 2003) found that PFMT plus anal ES with and without extra biofeedback were both better than PFMT alone at six months, but there was little to choose between the two more intensive interventions (Analysis 10.8). Tienforti 2012 found that pre‐operative PFMT was associated with a reduction in number of incontinence episodes per day, but this was a small trial and larger sample sizes would be needed to draw reliable conclusions.

Nine trials compared one active treatment with another active treatment. Overall there did not seem to be one intervention that proved to be statistically significantly better than another.

Treatment trials for urinary incontinence after TURP

One large trial addressed this comparison (Glazener TURP 2011), comparing four sessions of one‐to‐one therapy with standard management in a context where information about PFMT was widely available. The quality of evidence for the number of incontinent men was moderate but there were no differences between the groups in any of the outcome measures except for performance of PFMT, suggesting that the intervention had changed behaviour but not incontinence or other clinical outcomes.

Prevention trials for urinary incontinence after TURP

Three small trials enrolled men before TURP to receive a minimal PFMT intervention before and after surgery. There were no statistically significant differences in terms of number of incontinent men between the groups but the quality of evidence was deemed to be very low (Analysis 16.1).

Containment of urinary incontinence

One alternative intervention, a clamp fitted to the shaft of the penis, can be used to control unwanted leakage. Men in one trial reported a preference for one type of external compression device compared to two others or no treatment; a Cunningham clamp proved satisfactory to 10 of 12 men with intractable UI (Moore 2004). This may be a viable alternative for some cognitively capable men providing they take into account safety issues such as adequate sensation and the ability to remove the device when it feels too tight or the bladder is full. Another trial which compared pads, sheath catheters, body‐worn urinals and clamps also reported that men found the clamps most effective but painful (Fader 2013).

Men whose incontinence cannot be otherwise controlled can use absorbent pads (Fader 2007; Fader 2008) or a variety of external sheath devices with leg bags. An alternative is an indwelling urinary catheter (Jahn 2007; Moore 2007; Niël‐Weise 2005).

Lifestyle changes

The effect of other conservative interventions such as lifestyle changes remains undetermined as no trials involving these interventions were identified.

Trial quality and methodological assessment

The quality of the estimated treatment effect of any intervention is determined partly by methodological assessment. Methodological flaws within the included trials of this review were assessed using the reports of the trials and therefore were reliant on the quality of reporting. Data were not available in all the trials for many of the pre‐stated outcomes. CIs tended to be wide except for the more recent large trials, and it was difficult to reliably identify or rule out a useful effect.

All trials claimed to be randomised, but only 24 out of 50 trials provided details of adequate sequence generation (Ahmed 2012; Burgio 2006; Centemero 2009; Dijkstra‐Eshuis 2013; Dubbelman 2004; Filocamo 2005; Fode 2014; Glazener RP 2011; Glazener TURP 2011; Goode 2009; Laurienzo 2013; Manassero 2007; Mathewson‐Chapman 97; Moore 1999; Moore 2004; Moore 2008; Overgard 2008; Park 2012; Robinson 2008; Robinson 2009; Tibaek 2007; Tienforti 2012; van Kampen 1998; Yamanishi 2006). Only 20 of the 50 trials provided details of adequate concealment of randomisation (Ahmed 2012; Burgio 2006; Centemero 2009; Dijkstra‐Eshuis 2013; Dubbelman 2004; Fode 2014; Geraerts 2013; Glazener RP 2011; Glazener TURP 2011; Goode 2009; Manassero 2007; Moore 1999; Moore 2004; Moore 2008; Overgard 2008; Park 2012; Robinson 2008; Tibaek 2007; van Kampen 1998; Yamanishi 2006) and were subsequently judged to be at low risk of selection bias. Additionally, blinding to PFMT was not possible, and blinding of outcome assessment appeared to be absent in many trials as it was not discussed. Therefore, many trials were judged to be at high risk of performance and detection bias.

The quality of the evidence was downgraded for the following.

• Study design i.e. there was evidence of methodological flaws in the study design.

• Indirectness i.e. a surrogate outcome was selected when a GRADE‐specific outcome was not reported.

• Inconsistency, when there was evidence of statistical (either clinical or methodological) heterogeneity.

• Imprecision, when the CIwas wide and crossed the line of no effect.

• Publication bias. We planned to use funnel plot for publication bias, however, there were fewer than 10 trials in the meta‐analysis and the funnel plot could not be used.

The quality of the evidence for the critical outcomes ranged from moderate to very low, as evident in the summary of findings tables.