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Interventions for treating postpartum constipation

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To evaluate the effectiveness of interventions for the treatment of postpartum constipation.

Background

Description of the condition

Postpartum constipation is a common condition affecting postpartum mothers (Cheng 2008). The postpartum period starts from childbirth and includes the following six weeks during which the mother's body returns to the pre‐pregnant state (Liu 2009). Constipation can be defined as difficult bowel evacuation characterised by straining, lumpy or hard and dry stools, sensation of incomplete evacuation, anorectal obstruction, or manual manoeuvres (Higgins 2004). According to the Rome III criteria, chronic functional constipation in adults is defined as having two or more of the following symptoms for at least three months: straining in at least 25% of defecations, lumpy or hard stools in at least 25% of defecations, sensation of incomplete evacuation in at least 25% of defecations, sensation of anorectal obstruction or blockade in at least 25% of defecations, manual manoeuvres (e.g., digital evacuation, support of the pelvic floor) to facilitate at least 25% defecations, fewer than three defecations per week; loose stools are rarely present without the use of laxative (Lee‐Robichaud 2011). Since the pelvic floor muscles play an important role in defecation, injury to the levator ani muscle during childbirth may lead to constipation in the postpartum period (Shafik 2002). Other studies found that forceps delivery, prolonged second stage of labour and higher child birth weight could result in anal sphincter injury resulting in postpartum constipation (Sultan 1993). When the range of bowel habit parameters were compared between postpartum lactating mothers and postpartum non‐lactating mothers, urgency symptoms were considerably higher in postpartum mothers who were not breastfeeding (Derbyshire 2007). Haemorrhoids are also a common anorectal medical condition in pregnancy and the postpartum period causing painful defecation and swelling at the anus resulting in constipation. Some other specific postpartum factors such as breastfeeding and obstetric events seem to affect bowel function during the postpartum period (Bradley 2007).

The prevalence of postpartum constipation was estimated to be 24% at three months postpartum by Bradley 2007. The same study found that constipation, as classified by the Rome II criteria, affects up to 25% of women throughout pregnancy and at three months postpartum. Another study reports a prevalence of constipation in the puerperium as 41.8% by self report and 24.7% as classified by the Rome criteria (Ponce 2008), while defecation symptoms in early pregnancy (12 weeks gestation) in women with lower body mass index (BMI) were associated with constipation at 12 months after child birth (van Brummen 2006).

Constipation is a functional bowel disorder and can significantly reduce the perceived quality of life in adults (Daisy 2002). Postpartum constipation is identified mostly by symptoms such as pain or discomfort and bowel habit and stool characteristics which makes the diagnosis both subjective and objective. Therefore the use of time transit (Bristol Stool Form Scale) and Rome criteria is necessary for clinical diagnosis, evidence‐based management and research (Longstreth 2006). The causes of constipation can be classified as lifestyle‐related, disease‐related, or drug‐induced (Candy 2011).

Description of the intervention

Appropriate interventions for the treatment of constipation depend on the cause (Candy 2011). Although interventions specifically tailored for postpartum constipation are few, some of the interventions targeting constipation in general can also be used to treat postpartum constipation. Lifestyle modifications that include adequate fibre (such as fruits, cucumber, soup and vegetables) (Liu 2009) and water and fluids (Candy 2011) in the diet can help to relieve the symptoms and prevent recurrences of constipation. Soluble fibre helps soften the stools and insoluble fibre adds bulk to the stools and thereby stimulates bowel movements (Balch 2010). Laxatives can be used to treat constipation and are grouped in the following categories according to their function: bulk forming laxatives, osmotic laxatives, stimulant laxatives, faecal softeners and lubricants (Candy 2011). Bulk forming laxatives (such as bran, psyllium, and methylcellulose) work by increasing the weight and water content of the stools and thereby facilitate the peristaltic movement of stools (Balch 2010). Osmotic laxatives (such as lactulose and polyethylene glycol (PEG)) add water into the colon which then improves bowel movement (NIH 2007). A recent Cochrane review reported the treatment effect of two osmotic laxatives (lactulose versus PEG) for chronic constipation and concluded that PEG is superior to lactulose in improving the form and frequency of the stool, relieving abdominal pain, and in decreasing the need for additional products (Lee‐Robichaud 2011). Stimulant laxatives (such as bisacodyl, castor oil, and senna) ease the bowel movement by irritating the intestinal wall (Balch 2010). Stool softeners work by lubricating stools, thereby improving the passage of stools through the intestines (NIH 2007). Surgical interventions can also be used to treat constipation, for example, surgical repair of anorectal problems such as rectal prolapse (NIH 2007). Studies have also reported on the efficacy of acupuncture and Chinese herbal medicine as an intervention in treating postpartum constipation. A randomised controlled trial (Eogan 2007), found that administration of a stool‐bulking agent in addition to a laxative is not suitable during the postpartum period for women who have sustained anal sphincter injury at vaginal delivery. Also, some types of laxatives are not recommended for use by postpartum mothers because they may be distributed into breast milk resulting in undesired effects in breast fed babies.

Why it is important to do this review

The postpartum period is an important stage in a mother's life, and for her newborn baby. Considering the morbidity effects of constipation, cost and negative impact on quality of life (Peppas 2008), an evaluation of the effectiveness of available interventions for the treatment of postpartum constipation is necessary. Although a number of systematic reviews on constipation have been published (for example Gordon 2011; Higgins 2004; Jewell 2009; Lee‐Robichaud 2011; Mugie 2011; Peppas 2008), currently there is no systematic review published on interventions for the treatment of postpartum constipation specifically. Although there are some interventions for the treatment of general constipation, not all of them are suitable for use in the postpartum period particularly for nursing mothers because some of these laxatives are excreted in breast milk. Furthermore, cultural beliefs about the postpartum period may result in some lifestyles with certain prescribed diets and lack of exercise, both of which may promote postpartum constipation (Liu 2009). A systematic review is therefore necessary to summarise and evaluate the effectiveness and safety of various interventions for the treatment of postpartum constipation.

Objectives

To evaluate the effectiveness of interventions for the treatment of postpartum constipation.

Methods

Criteria for considering studies for this review

Types of studies

All randomised controlled trials comparing any intervention for the treatment of postpartum constipation versus another intervention or placebo or no treatment will be included. Studies presented only as abstracts will be included if they meet the inclusion criteria. Cluster‐randomised trials will be included.

Cross‐over trials will be excluded because the physiological condition of women during the first month postpartum might not be the same as sixth months after childbirth.

Types of participants

Postpartum women (up to six months post delivery) diagnosed with postpartum constipation using pre‐specified criteria (Rome and Bristol Stool Form Scale) and self report.

Types of interventions

Intervention

Any intervention for the treatment of postpartum constipation including laxatives, surgery, and educational and behavioural interventions.

Control

Any other intervention for the treatment of postpartum constipation or placebo or no treatment.

Types of outcome measures

Primary outcomes

  1. Pain or straining on defecation

  2. Participant‐reported relief of constipation symptoms

  3. Stool frequency

Secondary outcomes

  1. Stool consistency (e.g. Bristol Stool Scale)

  2. Use of additional products (e.g. alternative laxative agents, enemas)

  3. Relief of abdominal pain

  4. Change in quality of life

  5. Adverse effects caused by the intervention, including:

    • nausea or vomiting

    • pain

    • flatus

    • diarrhoea

    • faecal incontinence

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

Both review authors, Eunice Turawa (ET) and Alfred Musekiwa (AM), will independently screen the results of the search to select potentially relevant studies and apply eligibility criteria using a pre‐designed eligibility form based on the inclusion criteria. Corresponding full‐text articles will be retrieved and used in applying the eligibility criteria. Each of the articles will be scrutinised to ensure that multiple publications of the same trial will be included only once. If eligibility is unclear, we will seek clarification from the trial authors and re‐assess the corresponding articles. We will resolve any disagreement through discussion. We will exclude studies that do not meet the inclusion criteria and state the reasons in the 'Characteristics of excluded studies' table.

Data extraction and management

Using a specially designed pre‐piloted data extraction form, both review authors (ET and AM) will independently extract information on methods, participants, interventions and outcomes from each included study. The following information will be extracted:

  • author, year of publication, country of origin, journal citation, and language;

  • study methods (trial design, duration, risk of bias, setting, study inclusion criteria);

  • participants (number, age, source, inclusion and exclusion criteria, duration of symptoms, previous treatments, underlying conditions, drop‐outs/withdrawals);

  • interventions (type, dose, duration, route of delivery, control used, run‐in phase, treatment phase, follow‐up);

  • outcome data for each of the primary and secondary outcomes above.

For each dichotomous outcome, we will extract the number of participants experiencing the event and the number of participants in each treatment group. For each continuous outcome, we will extract the arithmetic means, standard deviations (or information to estimate the standard deviations), and the number of participants, in each treatment group. For continuous data, if geometric means and their standard deviations on the log scale have been reported, we will extract them. Medians and ranges will also be extracted if these are reported in place of means and standard deviations. 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 the authors of the original reports to provide further details. We will resolve discrepancies through discussion.

Assessment of risk of bias in included studies

Individually randomised trials

Both review authors (ET and AM) will independently assess risk of bias for each included study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The criteria is given in Appendix 1. The domains that will be assessed are adequate sequence generation, allocation concealment, blinding, incomplete outcome data, selective reporting and other potential sources of bias. Each included study will be judged as 'yes' (low risk of bias), 'no' (high risk of bias), or 'unclear' (uncertain risk of bias) according to each of the six domains. The results will be summarised using the 'Risk of bias' summary and the 'Risk of bias' graph in addition to the 'Risk of bias' tables. Where clarity is required or in case of missing data, we will contact the trial authors for clarification. We will resolve any disagreement by discussion.

Cluster‐randomised trials

For cluster‐randomised trials we will assess recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and incomparability with individually‐randomised trials. (Higgins 2011).

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. In either case, corresponding 95% confidence intervals will also be presented. 

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 Section 16.3.4 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 subgroup analysis to investigate the effects of the randomisation unit.

Individually‐randomised trials

Attention to the unit of analysis at the level of randomisation (individual) will be noted using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Multi‐arm trials

When a multi‐arm study contributes multiple comparisons to a particular meta‐analysis, we will either combine treatment groups or split the ‘shared’ group as appropriate and precautions will be taken to avoid the inclusion of data from the same patient more than once in the same analysis.

Dealing with missing data

No imputation measures for missing data will be applied. Where data from the trial reports are insufficient, unclear or missing, we will contact the trial authors by email for additional information or clarification. 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 (< 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, and use formal tests for funnel plot asymmetry. For continuous outcomes we will use the test proposed by Egger 1997, and for dichotomous outcomes we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or 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 meta‐analysis to produce it.

We plan to carry out subgroup analyses (only on primary outcomes) with respect to:

  • type of laxatives (bulk‐forming laxatives versus other types of laxatives);

  • study design (individually‐ versus cluster‐randomised trials).

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

Sensitivity analysis will be performed (only on primary outcomes) provided there are sufficient trials. We plan to conduct sensitivity analysis with respect to:

  • robustness of the methods used regarding allocation concealment;

  • losses to follow‐up;

  • randomisation (randomised versus quasi‐randomised);

  • imputed values of intra‐cluster correlations (ICC).

We will report where the analysis alters the overall treatment effect.