Interventions for women in subsequent pregnancies following obstetric anal sphincter injury for improving health

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

The objective of this review is to assess the effects of antenatal and intrapartum interventions for women in subsequent pregnancies following a previous obstetric anal sphincter injury to improve health.


Perineal trauma (damage to the area between the vaginal orifice and anus) occurs in over three-quarters of vaginal births (Albers 1999; McCandlish 1998). Obstetric anal sphincter injury (OASI) occurs during childbirth and as the name suggests, involves the anal sphincter (the ring of muscle controlling the entrance to the rectum) and is classed as severe trauma. OASI has been reported in up to 18% (range 1.7% to 18%) of vaginal births (Harkin 2003; Hirayama 2012; Lowder 2007). There is wide variation in reported rates of OASI between countries which may be due to under or over reporting, differences in training in the recognition of OASI and the variety of tools used to identify injury. Tools used include: clinical examination, endoanal ultrasonography (use of an ultrasound probe to identify sphincter damage), anal manometry (use of a pressure sensitive probe to measure muscle tone) and patient questionnaires (to assess symptoms and quality of life). The occurrence of OASI also depends on several predisposing risk factors; therefore, the inclusion or exclusion or changes in the incidence of risk factors (for example, use of forceps and episiotomy) will alter the denominator population and influence the incidence rate (Abbott 2010).

Incidence rate

The difficulties associated with estimating the rate of primary OASI are also associated with estimating the rate of recurrent OASI. Harkin 2003 reported a five-fold increase in the risk of recurrent OASI compared to the risk of injury for multiparous births, although these data included only 45 women having a spontaneous birth following primary OASI, of which only two sustained a second, third-degree tear. Conversely, Dandolu 2005 reported a lower combined rate of recurrent third- or fourth-degree tears compared to primary third- or fourth-degree tears, (5.76% versus 7.31%) but an increase in the rate of recurrent fourth-degree tears in women with previous primary fourth-degree tears compared to women with previous third-degree tears (7.73% versus 4.69%). The authors did not adjust for confounders, including parity and acknowledged that the reduction in the rates of modifiable risk factors such as forceps and episiotomy may have influenced the incidence rates. Peleg 1999 reported a doubling in the rate and Payne 1999 a three-fold increase in the rate of recurrent severe tears compared to those women with no tear or minor tear at the previous birth, with the highest recurrence rate in women who had undergone a repeat midline episiotomy. Although data regarding risk of recurrence of severe trauma are limited and conflicting, in the UK, the National Institute for Health and Clinical Excellence (NICE) intrapartum care guidance suggests the risk of recurrent severe trauma is similar to the risk of severe trauma at a first vaginal birth (NICE 2007).

Predisposing risk factors

Predisposing risk factors identified for primary OASI include: ethnicity (Wheeler 2012), episiotomy, forceps delivery, increasing maternal age, primiparity, induction and length of labour, vacuum extraction, neonatal head circumference and birthweight greater than 4 kg (Fizgerald 2007; Hirayama 2012; Kudish 2008; Williams 2005). Predisposing risk factors identified for recurrent OASI include: episiotomy, forceps and vacuum extraction (Dandolu 2005; Payne 1999; Peleg 1999). Use of episiotomy with forceps or vacuum seems to produce the greatest risk of recurrent anal sphincter injury (Dandolu 2005).

Adverse effects

OASI is associated with an increased risk of short- and long-term morbidity which could seriously effect quality of life. Sequalae include: perineal pain (Macarthur 2004), dyspareunia (painful intercourse) (Rathfisch 2010), defaecatory dysfunction, and urinary and faecal incontinence (Fenner 2003; MacArthur 1997; Richter 2006). Perineal pain is an immediate consequence that may affect maternal and infant bonding, ability to breastfeed and to increase the risk of urinary retention and dyspareunia (Barrett 2000; Buhling 2006), and could influence well-being and the risk of depression (Brown 2000).

Possibly the most distressing adverse effect of OASI is anal incontinence related to anal sphincter injury and pudendal nerve damage (Fynes 1998). Four per cent of women report faecal incontinence following vaginal birth (MacArthur 1997). For women who have sustained OASI, the incidence of anal incontinence is related to the severity of the sphincter defect observed at follow up. For example, following clinically identified severe perineal trauma at the time of birth, 13% of women without identifiable sphincter defects on postnatal endo-anal ultrasound (EAUS) reported anal incontinence, whereas 64% with internal and external defects on EAUS reported anal incontinence (Laine 2011). Incontinence rates may worsen with time and following subsequent births irrespective of degree of perineal trauma sustained in these deliveries (Baghestan 2012; Bek 1992). Various factors have been identified that may help in determining the risk of anal incontinence following a subsequent birth; these include age, parity, presence and severity of symptoms, EAUS-identified injury and impaired sphincter function assessed by manometry.

Anal incontinence in the absence of identified OASI at the time of birth, may be in part due to pudendal nerve damage or unidentified anal sphincter damage. Sultan 1993 identified over 30% more anal sphincter injuries using EAUS compared with clinical examination alone. This difference may, however, be related to the experience of and/or technique used by the person undertaking the initial clinical examination rather than the superior sensitivity of EAUS (Andrews 2006).

Identification of Injury

All women who have sustained perineal trauma should have a systematic examination of the vagina, perineum and rectum, including rectal examination before and after perineal repair by an experienced practitioner trained in the recognition and management of perineal tears (NICE 2007; RCOG 2007). Methods of repair for OASI has been examined in a separate Cochrane review (Fernando 2006). To our knowledge, there are no reviews examining the type of repair suture for OASI or interventions for women in subsequent pregnancies following OASI for improving health.

Description of the condition

NICE (NICE 2007; RCOG 2007) recommend perineal or genital trauma caused by either tearing or episiotomy at birth should be defined as follows (described by Sultan 1999):

  • first degree – injury to skin only;

  • second degree – injury to the perineal muscles but not the anal sphincter;

  • third degree – injury to the perineum involving the anal sphincter complex:

    • 3a – less than 50% of external anal sphincter thickness torn;

    • 3b – more than 50% of external anal sphincter thickness torn;

    • 3c – internal anal sphincter torn

  • fourth degree – injury to the perineum involving the anal sphincter complex (external and internal anal sphincter) and anal epithelium.

OASI includes third- and fourth-degree perineal tears. A third-degree perineal tear is defined as a partial or complete disruption of the anal sphincter muscles, which may involve either or both the external (EAS) and internal anal sphincter (IAS) muscles. A fourth-degree tear is defined as a disruption of the anal sphincter muscles with a breach of the anal or rectal mucosa (RCOG 2007).

Description of the intervention

Antenatal interventions for women who have sustained a previous obstetric anal sphincter injury may include the following: pelvic floor exercises that aim to strengthen the pelvic floor and have recently been found to reduce the risk of urinary incontinence (Stafne 2012); biofeedback training which uses computer-generated feedback from rectal balloons to a) improve patient awareness of the presence of faecal material in the rectum and b) to co-ordinate contraction of the external anal sphincter with relaxation of the internal sphincter and c) improve the force of the muscle (Miner 1990; Norton 2012); or stimulation of the sacral nerves that control the lower part of the bowel and sphincters by inserting electrodes in the lower back and connecting them to a pulse generator (Mowatt 2007). Other antenatal interventions include: perineal massage or creams that aim to reduce the risk of perineal tearing. Intrapartum interventions include: induction of labour to reduce the risk of macrosomia (infant birth weight greater than 4 kg) and subsequent risk of trauma; elective caesarean section to avoid vaginal and perineal trauma; vacuum as opposed to forceps to reduce the risk of trauma; selective episiotomy to reduce the risk of severe trauma; and different flexion techniques of the presenting fetal part to reduce the diameter and. in doing so, reduce the risk of subsequent trauma.

How the intervention might work

Interventions may aim to improve the integrity of the anal sphincter (pelvic floor muscle exercises, electrical stimulation), avoid trauma (elective caesarean section) or reduce the risk of trauma (medio-lateral episiotomy, vacuum and flexion techniques) to the perineum and anal sphincter and in doing so reduce the risk of adverse symptoms such as incontinence.

Why it is important to do this review

There are currently no systematic reviews or evidence-based guidance on interventions or strategies for women in subsequent pregnancies following obstetric anal sphincter injury to prevent or reduce the risk of further damage/trauma to the anal sphincter complex. Guidance based on robust evidence would allow us to improve the care in subsequent pregnancies for women who have previously sustained a third-degree tear, thus reducing morbidity and improving health.


The objective of this review is to assess the effects of antenatal and intrapartum interventions for women in subsequent pregnancies following a previous obstetric anal sphincter injury to improve health.


Criteria for considering studies for this review

Types of studies

All identified abstracts, published and unpublished randomised controlled trials assessing the effects of any intervention in subsequent pregnancies following obstetric anal sphincter injury to improve health will be included. Cluster-randomised trials and multi-arm trials will be included. Quasi-randomised controlled trials and cross-over trials will be excluded.

Types of participants

All pregnant women who have sustained obstetric anal sphincter injury during a previous birth.

Types of interventions

We will compare any type of intervention (irrespective of when the intervention is delivered i.e. antenatal versus intrapartum) aimed at reducing the risk of harm in a subsequent pregnancy following obstetric anal sphincter injury with any other intervention or with routine care, i.e. antenatal interventions; such as massage or creams and intrapartum interventions such as vacuum versus selective or routine episiotomy and selective or routine episiotomy with routine care. We will compare different types of the same category of intervention (antenatal or intrapartum) i.e. vacuum versus forceps and flexion of the presenting part versus hands poised or different types of creams.

Types of outcome measures

Primary outcomes
  1. Incidence of recurrent third-/fourth-degree tear (as defined by authors of individual trials)

  2. Anal incontinence (flatus, fluid and solid stool)

Secondary outcomes
  1. Induction of labour

  2. Instrumental vaginal birth (forceps and vacuum)

  3. Caesarean birth

  4. Perineal trauma (as defined by authors of individual trials)

  5. Gestational age at birth

  6. Birthweight

  7. Admission to special care baby unit

  8. Breastfeeding

  9. Maternal well-being and quality of life

Long term
  1. Dyspareunia (as defined by authors of individual trials)

  2. Perineal pain (as defined by authors of individual trials)

  3. Resumption of sexual intercourse

  4. Presence of symptoms of anal sphincter damage (as defined by authors of individual trials and including: flatal (accidental leakage of gas) and faecal incontinence, urgency, urinary incontinence)

  5. Maternal well-being and quality of life (at all time points reported)

Search methods for identification of studies

Electronic searches

We will contact the Trials Search Co-ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.

The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:

  1. monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);

  2. weekly searches of MEDLINE;

  3. weekly searches of EMBASE;

  4. handsearches of 30 journals and the proceedings of major conferences;

  5. weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.

Details of the search strategies for CENTRAL, MEDLINE and EMBASE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.

Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords. 

We will not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult the third review author.

Data extraction and management

We will design a form to extract data. For eligible studies, two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult the third review author. We will enter data into Review Manager software (RevMan 2011 ) and check for accuracy.

When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.

Assessment of risk of bias in included studies

Two review authors will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2011). We will resolve any disagreement by discussion or by involving a third assessor.

In addition to the checks below undertaken for trials comparing one intervention with another, we will assess the risk of bias in multifactorial studies by assessing the risk that data are not presented for each of the groups to which participants were randomised (low, high or unclear risk of bias) and the risk that the study has selectively reported comparisons of intervention arms for some or all outcomes (low, high or unclear risk of bias).

(1) Random sequence generation (checking for possible selection bias)

We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We will assess the method as:

  • low risk of bias (any truly random process, e.g. random number table; computer random number generator);

  • high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);

  • unclear risk of bias.   

(2) Allocation concealment (checking for possible selection bias)

We will describe for each included study the method used to conceal allocation to interventions prior to assignment and we will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We will assess the methods as:

  • low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

  • high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);

  • unclear risk of bias.   

(3.1) Blinding of participants and personnel (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.

We will assess the methods as:

  • low, high or unclear risk of bias for participants;

  • low, high or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.

We will assess methods used to blind outcome assessment as:

  • low, high or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re-include missing data in the analyses which we undertake.

We will assess methods as:

  • low risk of bias (e.g. no missing outcome data or less than 20% missing; missing outcome data balanced across groups);

  • high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis carried out with substantial departure of intervention received from that assigned at randomisation);

  • unclear risk of bias.

(5) Selective reporting (checking for reporting bias)

We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.

We will assess the methods as:

  • low risk of bias (where it is clear that all of the study’s pre-specified outcomes and all expected outcomes of interest to the review have been reported);

  • high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

  • unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

We will describe for each included study any important concerns we have about other possible sources of bias.

We will assess whether each study was free of other problems that could put it at risk of bias:

  • low risk of other bias;

  • high risk of other bias;

  • unclear whether there is risk of other bias.

(7) Overall risk of bias

We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals. 

Continuous data

For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.  

Unit of analysis issues

Cluster-randomised trials

We will include cluster-randomised trials in the analyses along with individually-randomised trials. We will adjust their sample sizes using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster-randomised trials and individually-randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.

We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Dealing with missing data

For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.

For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.

Assessment of heterogeneity

We will assess statistical heterogeneity in each meta-analysis using the T², I² and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either the T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity. 

Assessment of reporting biases

If there are 10 or more studies in the meta-analysis we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually.  If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using the Review Manager software (RevMan 2011). We will use fixed-effect meta-analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random-effects meta-analysis to produce an overall summary if an average treatment effect across trials is considered clinically meaningful. The random-effects summary will be treated as the average range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.

If we use random-effects analyses, the results will be presented as the average treatment effect with 95% confidence intervals, and the estimates of  T² and I².

Subgroup analysis and investigation of heterogeneity

If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random-effects analysis to produce it.

We plan to carry out the following subgroup analyses.

  1. Ethnicity (comparison of women of South Asian, black, middle Eastern or Hispanic ethnicity with each other and with women of white European descent.

  2. Maternal age (less than 35 years of age versus 35 years of age or older).

  3. Number of previous births with anal sphincter injury (once versus twice or more).

  4. Type of previous vaginal birth (instrumental (ventouse and forceps) versus normal).

  5. Macrosomia (less than 4 kg versus 4 kg or more).

We will use primary outcomes in subgroup analyses.

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2011). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.

Sensitivity analysis

We will carry out sensitivity analysis to explore the effects of trial quality assessed by allocation concealment and other risk of bias components, by omitting studies rated as inadequate for these components. If there is statistical heterogeneity, we will explore the effects of random-effects analyses. Sensitivity analysis will be restricted to the primary outcomes.


As part of the pre-publication editorial process, this protocol has been commented on by three peers (an editor and two referees who are external to the editorial team), a member of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.

Contributions of authors

Diane Farrar wrote the first drafts of the protocol, Carmel Ramage and Derek Tuffnell commented and contributed to subsequent drafts.

Declarations of interest

None known.