Complementary and alternative therapies for post-caesarean pain

  • Protocol
  • Intervention

Authors


Abstract

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

To assess the effectiveness and safety of complimentary alternative therapies for post-caesarean pain.

Background

Description of the condition

A caesarean section (CS) is the most frequent major surgery currently performed in the world, with an estimated 18.5 million procedures being performed each year (WHO 2005a; WHO 2013). According to estimates of the World Health Organization (WHO), 15% of all deliveries are by CS, with large differences between and within countries. While CSs account for over 50% of all deliveries in several Latin American countries and in China, the CS rate is less than 5% in several regions of Africa (Althabe 2006; Betrán 2007; Ronsmans 2006). Over the last four decades the rates of CS have been steadily increasing in most high- as well as in many low- and middle-income countries, for reasons that are not yet completely understood (Cavallaro 2013; WHO 2013).

It is estimated that 50% to 71% of all patients who undergo any type of surgery will experience moderate to intense pain (Apfelbaum 2003). As after any major surgery, postoperative pain is inevitable after a CS. The intensity of this pain is variable and influenced by several factors including individual sensitivity, age, psychological, social and environmental factors (Pan 2006).

There are compelling reasons for adequate pain relief after CS, including women's satisfaction and comfort, as well as the reduction of long-term adverse effects for mothers and infants. Higher pain scores after CS are associated with the development of chronic pain three months after the surgery ( Cançado 2012). Compared to women with mild pain, women with severe pain in the first day after a CS are 2.5 to 3 times more likely to develop postpartum depression and persistent pain eight weeks after delivery (Eisenach 2008). Moreover, persistent pain associated with depression can lead to negative maternal behaviour and affect the cognitive development of the infants (Grace 2003). Compared to other postoperative patients, women in the postpartum period following CS are at higher risk of thromboembolism and this risk can be further exacerbated by immobility related to pain or excessive sedation induced by opioids (Pan 2006).

Woment who have a caesarean delivery present unique challenges in the treatment of postoperative pain. While the women need medication to reduce the pain associated with having to sit, rise and walk relatively soon after their surgery to care for their infants, they also need to remain alert and energetic enough to interact with and breast feed their newborns (Sousa 2009). To achieve these goals, the ideal analgesic for a woman who delivers by CS should produce minimal maternal side effects, minimal or no interference with caring for her newborn or discharge from hospital and also have minimal transfer in breast milk and consequently little or no effect on neonates (Pan 2006).

Description of the intervention and how the intervention might work

The term complementary and alternative medicine (CAM) refers to a group of medical and healthcare systems, practices and products that are not generally considered to be part of conventional medicine (Committee CAM 2005; WHO 2001; WHO 2002; WHO 2005b; Wieland 2011). Complementary medicine used for postoperative analgesia include aromatherapy, acupuncture, massage, music therapy and transcutaneous electrical nerve stimulation (TENS), all included in list of the CAM operational definition (Wieland 2011). These practices can be used alone or to complement other forms of pain relief, including analgesic drugs (Dowswell 2009; Good 2001; Good 2002; Kim 2006; Smith 2011b; Smith 2012).

Aromatherapy

Aromatherapy is the therapeutic use of essential oils extracted from plants (Stevensen 1994). Aromatherapy oils can be inhaled or rubbed on the patient's skin to alleviate stress and pain. Each oil is believed to have different therapeutic properties according to its chemical composition and lavender is one of the most used for pain relief (Bagetta 2010). The soothing effects of lavender oil are due to its lipophilic monoterpenes which react with cell membranes and cause changes in the activity of ion channels, carriers and nervous receptors (Kim 2006).

Acupuncture

Acupuncture is a therapeutic modality involving the insertion of fine needles through the skin (White 2009). It has been extensively studied in the management of acute and chronic pain (Garcia 2009; Vickers 2012; Wang 2008). There are different hypotheses to explain how acupuncture leads to pain reduction. Some studies indicate that its analgesic effects are due to the release of beta-endorphins in the lumbar spine and increased 5-hydroxy tryptophan levels in the cerebrum. Other explanations include the overriding of the pain stimulus by the biochemical lines of acupuncture in the transmitting process of the central nervous system and the more traditional explanation is that acupuncture frees a blockage of "Qi" or energy flow (Green 2002; Zhang 2014).

Massage

Massage produces body relaxation, deeper respiration, improved quality of sleep and pain reduction (Bauer 2010; Hattan 2002). Local massage may have systemic pain-modulating effects due to stimulation of the “nonpainful” nerve fibres that interfere with pain transmission in the spinal cord. The feet and hands are good massage areas because they have abundant mechanoreceptors that stimulate nonpainful nerve fibres, resulting in pain inhibition (Kimber 2008; Wang 2004).

Music therapy

Music therapy has been shown to reduce postoperative pain, anxiety and stress (Good 2001; Good 2002). The commonly accepted theory is that music acts as a distracter, focusing the patient’s attention away from negative stimuli to something pleasant and encouraging. By occupying the mind with something familiar and soothing, music would allow the patient to escape and relax into his or her “own world” (Nilsson 2008).

Transcutaneous electrical nerve stimulation (TENS)

TENS has been extensively investigated for several types of pain relief, including postoperative and CS pain (Bjordal 2003; Paula 2006; Sluka 2001).

Trials on the use of CAM for post-CS pain date back to the 1980s and involved TENS. More recently, there have been several controlled studies evaluating the benefits of massage, aromatherapy, acupuncture and music therapy to reduce post-CS pain, anxiety, nausea and vomiting.

Studies typically refer to the gate control theory of pain to explain the effects of high-frequency TENS. The stimulation of large diameter afferent fibres inhibits the input from small diameter afferent fibres in the substantia gelatinosa of the spinal cord. This is thought to be a segmental inhibition that does not involve descending inhibitory pathways. On the other hand, low-frequency TENS would relieve pain by activating endogenous opioid pathways (Desantana 2008; Kocyigit 2012; Sluka 2001).

Why it is important to do this review

Pain after CS can affect the well being of the mother and her ability to care for, breast feed and interact with her newborn infant and can have significant long-term adverse effects (Eisenach 2008). Postoperative CS pain is often inadequately managed because conventional pain relieving strategies are underused often because of concerns about the adverse maternal and neonatal effects of the most commonly used drugs (Gadsden 2005; Pan 2006).

There are systematic reviews which have assessed the use of CAM as alternative or complimentary forms of treatment for pain in childbirth (Barragán 2011; Jones 2012; Smith 2006; Smith 2011a; Smith 2011b; Smith 2012) and there are several trials on CAM for postoperative pain after CS. However, there are no systematic reviews of the literature which assess the effectiveness and safety of CAM compared with other forms of treatment for postoperative pain relief in CS. The findings of this review will be useful to help inform women and doctors about the potential benefits and disadvantages of CAM for pain relief after CS.

Objectives

To assess the effectiveness and safety of complimentary alternative therapies for post-caesarean pain.

Methods

Criteria for considering studies for this review

Types of studies

Randomised controlled trials (including those using a cluster-randomised design) comparing CAM, alone or associated with other forms of pain relief, versus other treatments or placebo or no treatment, in the treatment of post-CS pain. Quasi–randomised studies will be eligible for inclusion. Studies using a cross-over design will not be eligible for inclusion. Studies available only in abstract form will not be included in the review.

Types of participants

Women in the postpartum period after a CS.

Types of interventions

All types of CAM according to the WHO criteria (Committee CAM 2005; WHO 2001; WHO 2002; WHO 2005b), including acupuncture, aromatherapy, massage, music therapy and TENS for the treatment of postoperative pain in women submitted to CS. We will compare the following.

  1. CAM versus placebo.

  2. CAM versus no treatment.

  3. CAM plus analgesia versus placebo plus analgesia.

  4. CAM plus analgesia versus analgesia.

Types of outcome measures

Primary outcomes
  • Pain measured by validated instrument or scoring system (such as the visual analogue scale) up to discharge

  • Adverse effects (worsening of pain, anxiety, backache, pruritus, sedation)

Secondary outcomes
  • Vital signs

  • Rescue analgesic requirement

  • Length of hospitalisation

  • Women's satisfaction

  • Breasfeeding at discharge

  • Interaction with the baby

  • Walking at discharge

  • Pain at six weeks after discharge

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.

This 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.

In addition, we will contact the Cochrane Complementary Medicine Field for a search of their Trials Register.

Searching other resources

We will check reference lists of the included studies manually to identify any additional studies. We will contact specialists in the field and authors of the included trials for unpublished data.

We will not apply any language restrictions.

Data collection and analysis

The data collection and analysis methods in this section are based on the Cochrane Pregnancy and Childbirth Group's standard methods text.

Selection of studies

After merging the search results and removing duplicate records, two review authors (Sandra Zimpel (SAZ) and Gustavo Porfírio (GP)) will independently screen the references identified by the literature search. Titles and abstracts will be assessed to select potentially relevant reports which will be retrieved for full text reading. We will retrieve and examine the full text of selected studies for compliance with eligibility criteria. The reason for exclusion of individual trials will be documented. A third author (Maria Torloni (MRT)) will be consulted in case any disagreements arise during this process. We will present the process of study identification and selection using the PRISMA flow chart diagram.

Data extraction and management

We will create a specific data abstraction form to extract relevant information from each of the included studies. Two review authors (SAZ, GP) will independently extract the data using this form. We will resolve discrepancies through discussion or, if required, we will consult a third author (MRT). We will enter data into Review Manager software (RevMan 2014) and check it 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 (SAZ, GP) 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 author (MRT).

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

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

We will categorise 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 will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We will categorise 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 categorise 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 categorise 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 categorise methods as:

  • low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);

  • high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done 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 categorise 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 categorise 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 Handbook (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 variables, we will calculate the risk ratio (RR) and 95% confidence intervals (CIs) .

Continuous data

For continuous data, mean differences (MD) and 95% CIs between treatment groups will be calculated if studies report exactly the same outcomes. If similar outcomes are reported on different scales, the standardised mean difference (SMD) and 95% CI will be calculated.

Time-to-event data

For time-to-event data, since the most appropriate way of summarising them is to use methods of survival analysis and express the intervention effect as a hazard ratio, these data will be taken directly from the results of the studies. If estimates of log hazard ratios and standard errors can be obtained from results of the studies, these data will be combined using the generic inverse-variance method (Higgins 2011).

Unit of analysis issues

The unit of analysis is based on the individual participant (unit to be randomised for interventions to be compared), i.e. the number of observations in the analysis should match the number of individuals randomised. In the case of studies with multiple intervention groups, we will combine groups to create a single pair-wise comparison, combining all relevant intervention or control groups into a single group (Higgins 2011).

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 Handbook 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.

Cross-over trials

Cross-over trials will not be eligible for inclusion.

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 an I² is greater than 30% and either a 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 2014). 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 of the 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% CIs, 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:

  • multiparous versus primiparous women;

  • first caesarean versus repeat caesarean;

  • elective caesarean versus emergency caesarean.

Subgroup analysis will be restricted the review's primary outcomes.

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.

Sensitivity analysis

If there are an adequate number of studies, sensitivity analyses will be performed based on separation of studies according to risk of bias analysing the effect of trial quality in the primary outcomes. This will be done by excluding the trials most susceptible to bias based on our 'Risk of bias' assessment, i.e., those with inadequate randomisation sequence generation, allocation concealment, high levels of post-randomisation losses or exclusions and uncertain or unblinded outcome assessment (Deeks 2001). We will also carry out sensitivity analysis for primary outcomes by removing quasi-randomised trials to examine the effect of excluding such trials.

Acknowledgements

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) and the Group's Statistical Adviser.

Contributions of authors

Sandra A Zimpel (SAZ) is guarantor for the review. She coordinated the contributions from the co-authors and wrote the final draft of the protocol. Edina MK da Silva (EMKS) and Gustavo Porfirio (GP) contributed to writing the methods and statistical analysis sections of the protocol. SAZ and Maria R Torloni (MRT) drafted the clinical sections of the background and responded to the clinical comments of the referees. All authors contributed to the writing the protocol.

Declarations of interest

There are no interest conflicts.

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