Relief of pain due to uterine cramping/involution after birth

Andrea R Deussen; Pat Ashwood; Ruth Martis; Fiona Stewart; Luke E Grzeskowiak

doi:10.1002/14651858.CD004908.pub3

. 2020 Oct 20;2020(10):CD004908. doi: 10.1002/14651858.CD004908.pub3

Relief of pain due to uterine cramping/involution after birth

Andrea R Deussen ^1,^✉, Pat Ashwood ¹, Ruth Martis ², Fiona Stewart ³, Luke E Grzeskowiak ⁴

Editor: Cochrane Pregnancy and Childbirth Group

PMCID: PMC8094397 PMID: 33078388

Abstract

Background

Women may experience differing types of pain and discomfort following birth, including cramping pain (often called after‐birth pain) associated with uterine involution, where the uterus contracts to reduce blood loss and return the uterus to its non‐pregnant size. This is an update of a review first published in 2011.

Objectives

To assess the effectiveness and safety of pharmacological and non‐pharmacological pain relief/analgesia for the relief of after‐birth pains following vaginal birth.

Search methods

For this update, we searched Cochrane Pregnancy and Childbirth’s Trials Register, ClinicalTrials.gov, the WHO International Clinical Trials Registry Platform (ICTRP) (31 October 2019), and reference lists of retrieved studies.

Selection criteria

Randomised controlled trials comparing two different types of analgesia or analgesia versus placebo or analgesia versus no treatment, for the relief of after‐birth pains following vaginal birth. Types of analgesia included pharmacological and non‐pharmacological. Quasi‐randomised trials were not eligible for inclusion.

Data collection and analysis

Two review authors independently assessed trials for inclusion, conducted 'Risk of bias' assessment, extracted data and assessed the certainty of the evidence using the GRADE approach.

Main results

In this update, we include 28 studies (involving 2749 women). The evidence identified in this review comes from middle‐ to high‐income countries. Generally the trials were at low risk of selection bias, performance bias and attrition bias, but some trials were at high risk of bias due to selective reporting and lack of blinding. Our GRADE certainty of evidence assessments ranged from moderate to very low certainty, with downgrading decisions based on study limitations, imprecision, and (for one comparison) indirectness.

Most studies reported our primary outcome of adequate pain relief as reported by the women. No studies reported data relating to neonatal adverse events, duration of hospital stay, or breastfeeding rates. Almost half of the included studies (11/28) excluded breastfeeding women from participating, making the evidence less generalisable to a broader group of women.

Non‐steroidal anti‐inflammatory drugs (NSAIDs) compared to placebo

NSAIDs are probably better than placebo for adequate pain relief as reported by the women (risk ratio (RR) 1.66, 95% confidence interval (CI) 1.45 to 1.91; 11 studies, 946 women; moderate‐certainty evidence). NSAIDs may reduce the need for additional pain relief compared to placebo (RR 0.15, 95% CI 0.07 to 0.33; 4 studies, 375 women; low‐certainty evidence). There may be a similar risk of maternal adverse events (RR 1.05, 95% CI 0.78 to 1.41; 9 studies, 598 women; low‐certainty evidence).

NSAIDs compared to opioids

NSAIDs are probably better than opioids for adequate pain relief as reported by the women (RR 1.33, 95% CI 1.13 to 1.57; 5 studies, 560 women; moderate‐certainty evidence) and may reduce the risk of maternal adverse events (RR 0.62, 95% CI 0.43 to 0.89; 3 studies, 255 women; low‐certainty evidence). NSAIDs may be better than opioids for the need for additional pain relief, but the wide CIs include the possibility that the two classes of drugs are similarly effective or that opioids are better (RR 0.37, 95% CI 0.12 to 1.12; 2 studies, 232 women; low‐certainty evidence).

Opioids compared to placebo

Opioids may be better than placebo for adequate pain relief as reported by the women (RR 1.26, 95% CI 0.99 to 1.61; 5 studies, 299 women; low‐certainty evidence). Opioids may reduce the need for additional pain relief compared to placebo (RR 0.48, 95% CI 0.28 to 0.82; 3 studies, 273 women; low‐certainty evidence). Opioids may increase the risk of maternal adverse events compared with placebo, although the certainty of evidence is low (RR 1.59, 95% CI 0.99 to 2.55; 3 studies, 188 women; low‐certainty evidence).

Paracetamol compared to placebo

Very low‐certainty evidence means we are uncertain if paracetamol is better than placebo for adequate pain relief as reported by the women, the need for additional pain relief, or risk of maternal adverse events (2 studies, 123 women).

Paracetamol compared to NSAIDs

Very low‐certainty evidence means we are uncertain if there are any differences between paracetamol and NSAIDs for adequate pain relief as reported by the women, or the risk of maternal adverse events. No data were reported about the need for additional pain relief comparing paracetamol and NSAIDs (2 studies, 112 women).

NSAIDs compared to herbal analgesia

We are uncertain if there are any differences between NSAIDs and herbal analgesia for adequate pain relief as reported by the women, the need for additional pain relief, or risk of maternal adverse events, because the certainty of evidence is very low (4 studies, 394 women).

Transcutaneous nerve stimulation (TENS) compared to no TENS

Very low‐certainty evidence means we are uncertain if TENS is better than no TENS for adequate pain relief as reported by the women. No other data were reported comparing TENS with no TENS (1 study, 32 women).

Authors' conclusions

NSAIDs may be better than placebo and are probably better than opioids at relieving pain from uterine cramping/involution following vaginal birth. NSAIDs and paracetamol may be as effective as each other, whereas opioids may be more effective than placebo. Due to low‐certainty evidence, we are uncertain about the effectiveness of other forms of pain relief. Future trials should recruit adequate numbers of women and ensure greater generalisability by including breastfeeding women. In addition, further research is required, including a survey of postpartum women to describe appropriately their experience of uterine cramping and involution. We identified nine ongoing studies, which may help to increase the level of certainty of the evidence around pain relief due to uterine cramping in future updates of this review.

Plain language summary

Relief of pain caused by uterine cramping or involution after giving birth

This updated review investigates the effectiveness and safety of drug and non‐drug pain relief in women experiencing after‐birth pains following vaginal birth. Giving an agent for pain relief was compared to an inactive placebo, to no treatment, or to a different type of agent in randomised controlled trials.

What is the issue?

Women may experience cramping pain and discomfort following the birth of their baby, as the uterus contracts and returns to its normal pre‐pregnancy size. These pains usually last for two to three days after the birth. Women who have previously had a baby are more likely to experience after‐birth pains. Breastfeeding stimulates the uterus to contract and increases the severity of the pains.

Types of pain relief used to treat the pain include paracetamol, non‐steroidal anti‐inflammatory drugs (NSAIDs) ibuprofen and naproxen, opioids including codeine, and non‐medicine methods such as herbal preparations and transcutaneous electrical nerve stimulation (TENS).

Why is this important?

Management of pain after birth is important, as the pain can affect a mother carrying out her normal activities as well as bonding with and caring for her baby. After‐pains can interfere with establishing breastfeeding.

What evidence did we find?

We searched for evidence from randomised controlled trials (October 2019) and identified 28 studies (2749 mothers) who were in hospital after uncomplicated single births. Most of the evidence is low‐certainty because the studies did not include sufficient numbers of women. Many of the studies excluded breastfeeding women.This makes the evidence less relevant to a broader group of women. No studies reported evidence on adverse events in the newborn infants.

NSAIDs are probably better than placebo (a dummy treatment) in giving adequate pain relief as reported by the women (11 studies, 946 women; moderate‐certainty evidence), and they may reduce the need for additional pain relief (4 studies, 375 women; low‐certainty evidence). There may be little difference between NSAIDs and placebo in the risk of adverse events in the mother (9 studies, 598 women; low‐certainty evidence).

NSAIDs are probably better than opioids in providing adequate pain relief as reported by the women (5 studies, 560 women; moderate‐certainty evidence) and may reduce the risk of adverse events in the mother (3 studies, 255 women; low‐certainty evidence). NSAIDs may slightly reduce the need for additional pain relief compared with opioids (2 studies, 232 women; low‐certainty evidence).

Opioids may be better than placebo for adequate pain relief as reported by the women (5 studies, 299 women; low‐certainty evidence) and for the need for additional pain relief (3 studies, 273 women; low‐certainty evidence). Opioids may increase the risk of adverse events in the mother compared with placebo (3 studies, 188 women; low‐certainty evidence).

Very low‐certainty evidence means we are uncertain if paracetamol is better than placebo for adequate pain relief as reported by the women, the need for additional analgesia, or risk of maternal adverse events (2 studies, 123 women).

Very low‐certainty evidence means we are uncertain if NSAIDs are better than herbal pain relief for adequate pain relief as reported by the women (4 studies, 394 women), the need for additional pain relief (1 study, 90 women) or risk of maternal adverse events (1 study, 108 women).

Very low‐certainty evidence means we are uncertain if there is any difference between TENS and no TENS for adequate pain relief as reported by the women (1 study, 32 women).

What does this mean?

NSAIDs may be better than placebo and are probably better than opioids at relieving after‐birth pains following vaginal birth. The quality of the evidence was poor and we are uncertain about the effectiveness of other forms of pain relief. Future trials should recruit adequate numbers of women and ensure greater relevance by including breastfeeding women. Further research could also include a survey of women after delivery to capture their experience of after‐birth pains following vaginal birth.

Summary of findings

Background

Description of the condition

Women may experience differing types of pain and discomfort following the birth of their baby. This may include incisional pain after a caesarean section, perineal pain following perineal trauma or episiotomy during vaginal birth, nipple pain from breastfeeding and cramping pain (often called after‐birth pain) associated with involution of the uterus. Following birth, the uterus returns to its normal size through involution, a process of intermittent uterine contractions. These involutionary contractions may be painful and are commonly felt for two or three days after birth (Paliulyte 2017).

The incidence and severity of after‐birth pains is not widely reported. However, multiparous women usually experience more pain as the lost tone of the uterus of the multiparous woman contracts and relaxes alternately (Blackburn 2013). This is also true of a uterus that is greatly distended by a multiple pregnancy or polyhydramnios (Pessel 2019). It has been further hypothesised that childbirth can induce central neural changes that increase predisposition for pain during the postpartum period, suggesting multiparous women's perception of uterine cramp pain is increased through a process of central sensitisation of nociceptive neurons (Marieb 2019). Endogenous oxytocin released during breastfeeding stimulates the uterus to contract and increases the severity of after‐birth pains felt by the mother (Wambach 2021). Thus after‐birth pains may hinder successful breastfeeding, reducing the mother's ability to care for her new baby and may impair the establishment of good‐quality mother‐baby interactions. In contrast, the uterus of the primiparous woman remains contracted after birth (Rankin 2017), hence these women do not commonly experience after‐birth pains. It has been documented that some women consider their after‐birth pains to be a major burden requiring powerful analgesia (Baddock 2019).

A number of randomised trials comparing the safety and effectiveness of various pharmacological and non‐pharmacological forms of pain relief have been published. After‐birth pains and perineal tissue injury after vaginal birth are established clinical pain conditions that call for the investigation of the efficacy of new pain relief treatments including non‐pharmacological and pharmacological analgesia (Bloomfield 1998; Mall 2019).

Description of the intervention

Analgesia is any agent used to relieve pain. The Oxford Advanced Learner's Dictionary defines the term analgesia as "the loss of the ability to feel pain while still conscious" (Oxford 2020). Analgesia includes pharmacological and non‐pharmacological interventions aiming to relieve pain. Pharmacological analgesia can be further classified: simple analgesics (including paracetamol and non‐steroidal anti‐inflammatory drugs (NSAIDs) like aspirin and naproxen), opioid analgesics (including codeine and morphine) (MIMS 2020), and herbal analgesics. Herbal remedies are usually not required to be registered and are derived from a plant or plant part or an extract or mixture of these (Merriam‐Webster 2020). There are many different herbal preparations thought to have anti‐inflammatory properties which have been used for centuries for this purpose (Maroon 2010). There is interest in alternative anti‐inflammatory options, given the side‐effect profile of many NSAIDs (Oguntibeju 2018).

Non‐pharmacological analgesia may include massage, heat packs, cold packs, hypnotherapy, hydrotherapy, acupuncture and transcutaneous electrical nerve stimulation (TENS) (Coutaux 2017; Gallo 2018).

How the intervention might work

Analgesia can stop or decrease pain or the perception of pain in several ways. Systemic analgesic drugs can be categorised into different classes:

Simple analgesics like paracetamol inhibit central nervous system prostaglandin synthesis (Ritter 2019);
NSAIDs, including aspirin and naproxen, have an anti‐inflammatory action (Ritter 2019);
Narcotic analgesics including codeine and morphine reduce perception of pain by inhibiting pain‐transmission neurons and reducing the psychological response to pain (Ritter 2019);
Herbal preparations used as analgesics are believed to inhibit inflammatory pathways, similarly to NSAIDs (Maroon 2010);
TENS is thought to inhibit nociception through somatosensory electrical input (Peng 2019).

Why it is important to do this review

Women may experience pain after birth from several sources, including uterine involution and perineal trauma. Management of pain after birth is important and can impact on a woman's return to normal activities and caring for her baby.

There is little in the literature to guide women and clinicians in the management of pain from uterine cramping/involution. The aim of this review is to systematically assess what is known about the effectiveness and safety of analgesia for relief of pain from uterine cramping/involution.

This review is an update of a review first published in 2011 and will contribute to what is known about the management of postpartum pain.

Objectives

To assess the effectiveness and safety of pharmacological and non‐pharmacological pain relief/analgesia for the relief of after‐birth pains following vaginal birth.

Methods

Criteria for considering studies for this review

Types of studies

We assessed all identified published and unpublished randomised controlled trials (RCTs), comparing two different types of analgesia or analgesia versus placebo or analgesia versus no treatment, for the relief of after‐birth pains following vaginal birth. We have included studies that met the inclusion criteria, including those which were reported in abstract form only. We excluded abstracts reporting interventions for postpartum pain that did not separately report on pain from uterine involution. We also excluded studies reporting interventions specifically for the prevention of pain due to uterine cramping/involution. We further excluded studies where pain due to uterine cramps was not reported separately from other pain. We have not included quasi‐randomised studies in this review. Cluster‐randomised trials were eligible for inclusion.

Types of participants

Women who have given birth vaginally, requiring analgesia for after‐birth pains.

Types of interventions

Randomised controlled trials comparing any type of analgesia (excluding pharmacological analgesics that are no longer available or that are not approved for use in this population) for after‐birth pains following vaginal birth versus:

any other type of analgesia;
placebo;
no treatment.

Analgesic intervention may be administered once as a single dose or with the dosage repeated at therapeutic intervals.

Types of outcome measures

Primary outcomes

Adequate pain relief as reported by the woman, or by determination of > 50% relief of pain (either as stated by the woman or calculated using a formula)*

Secondary outcomes

Need for additional pain relief
Pain relief, however measured by the authors
Number of women with adverse events, including nausea, vomiting, sedation, constipation, diarrhoea, drowsiness, sleepiness, psychological impact
Number of infants with adverse events, including vomiting, sedation, constipation, diarrhoea, drowsiness, sleepiness
Duration of hospital stay
Any breastfeeding at hospital discharge
Any breastfeeding at six weeks postpartum
Maternal views (using a validated questionnaire)
Maternal postpartum depression

*Assessment of 50% pain relief via summed pain intensity difference (SPID) scores (1.23 x SPID%max ‐ 2.3 = proportion with 50%) (Cooper 1997; Moore 1997a; Moore 1997b).

Search methods for identification of studies

The following Methods section is based on a standard template used by Cochrane Pregnancy and Childbirth.

Electronic searches

For this update, we searched Cochrane Pregnancy and Childbirth’s Trials Register by contacting their Information Specialist (31 October 2019).

The Register is a database containing over 25,000 reports of controlled trials in the field of pregnancy and childbirth. It represents over 30 years of searching. For full current search methods used to populate Pregnancy and Childbirth’s Trials Register, including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL; the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link.

Briefly, Cochrane Pregnancy and Childbirth’s Trials Register is maintained by their Information Specialist and contains trials identified from:

monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
weekly searches of MEDLINE (Ovid);
weekly searches of Embase (Ovid);
monthly searches of CINAHL (EBSCO);
handsearches of 30 journals and the proceedings of major conferences;
weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.

Search results are screened by two people and the full text of all relevant trial reports identified through the searching activities described above is reviewed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth review topic (or topics), and is then added to the Register. The Information Specialist searches the Register for each review using this topic number rather than keywords. This results in a more specific search set that has been fully accounted for in the relevant review sections (Included studies; Excluded studies; Ongoing studies).

In addition, we searched ClinicalTrials.gov and the WHO International Clinical Trials Registry Platform (ICTRP) for unpublished, planned and ongoing trial reports (31 October 2019), using the search methods detailed in Appendix 1.

Searching other resources

We tried to contact the original trial authors for clarification or additional data (this is identified in the tables under included or excluded studies), and searched the reference lists of trials and review articles.

We did not apply any language restrictions.

Data collection and analysis

For methods used in the previous version of this review, seeDeussen 2011.

The following Methods section is based on a standard template used by Cochrane Pregnancy and Childbirth.

For this update, we used the following methods for assessing the 56 reports that we identified as a result of the updated search.

We defined the number of participants achieving adequate pain relief as one of the following:

The number of women reporting 'good' or 'excellent' pain relief when asked about their level of pain relief four to six hours after receiving their allocated treatment (we extracted the information as dichotomous data);
The number of women who reported 50% pain relief, or greater;
The number of women who achieved 50% pain relief, or greater, as calculated by using derived pain relief scores (TOTPAR (total pain relief) or SPID) over four to six hours.

It is common to use categorical or visual analogue scales for pain intensity and to calculate the results for each participant over periods of four or six hours, as SPID or TOTPAR (Moore 1996). From these categorical scales, it was possible to convert results into dichotomous data (the proportion of participants achieving at least 50%, or greater, max TOTPAR) using standard formulae (Moore 1996; Moore 1997b). Converting data in this way allowed us to use these data in a meta‐analysis (Moore 1997a; Moore 1997b). We used the following equations to estimate the proportions of participants achieving at least 50% of maximum TOTPAR.

Proportion with more than 50% maxTOTPAR = (1.33 x mean %maxTOTPAR – 11.5)

With %maxTOTPAR = mean TOTPAR x 100/(maximum score x number of hours) Cooper 1997; Moore 1997b).

Proportion with more than 50% maxTOTPAR = (1.36 x mean %maxSPID – 2.3)

With %maxSPID = mean SPID x 100/(maximum score x number of hours) (Cooper 1997; Moore 1997a).

The number of participants achieving at least 50% maxTOTPAR was then calculated by multiplying the proportions of participants with at least 50% maxTOTPAR by the total number of participants in the treatment groups. The number of participants with at least 50% maxTOTPAR was then used to calculate the relative benefit and number needed to treat for an additional beneficial outcome.

Where studies used more than one method of calculating adequate pain relief, our preference for analyses and reporting purposes, in order of decreasing preference, was: i) the proportion with at least 50% maxTOTPAR calculated using SPID; ii) the proportion with at least 50% maxTOTPAR calculated using TOTPAR; and iii) the number of participants reporting 'good' or 'excellent' pain relief/number of participants reporting at least 50% pain relief. We also assessed the number of participants who re‐medicated in the period of four to eight hours, as well as the median time to re‐medication, if data were available.

Selection of studies

Two review authors independently assessed for inclusion all the potential studies identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted a third review author.

Data extraction and management

We designed a form to extract data. For eligible studies, two review authors extracted the data using the agreed form. We resolved discrepancies through discussion or, if required, we consulted a third review author. We entered the data into Review Manager 5 software (RevMan 2014) and checked them for accuracy.

When information about any of the above was unclear, we planned to contact authors of the original reports to provide further details.

We contacted a number of authors of the original reports to provide us with further details. However, the response rate was low, and is identified in the tables of included and excluded studies (seeCharacteristics of included studies and Characteristics of excluded studies).

Assessment of risk of bias in included studies

Two review authors independently assessed risks of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020a). Any disagreement was resolved by discussion or by involving a third assessor.

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

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

We assessed 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 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 considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.

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

We assessed 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 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 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 was reported, or could be supplied by the trial authors, we planned to re‐include missing data in the analyses which we undertook.

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

We assessed the methods as:

low risk of bias (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported);
high risk of bias (where not all the study’s prespecified outcomes have been reported; one or more reported primary outcomes were not prespecified; 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 describe for each included study any important concerns we had about other possible sources of bias.

Measures of treatment effect

Dichotomous data

For dichotomous data, we present results as the summary risk ratio (RR) with its 95% confidence interval (CI).

Continuous data

We used the mean difference (MD) if outcomes were measured in the same way between trials. We used the standardised mean difference (SMD) to combine trials that measured the same outcome, but used different methods.

Unit of analysis issues

Cluster‐randomised trials

We intended to include cluster‐randomised trials in the analyses along with individually‐randomised trials, although none were identified. If identified in future updates, we will adjust their sample sizes or standard errors using the methods described in the Cochrane Handbook, Section 23.1.4 (Higgins 2020b), 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 we consider the interaction between the effect of intervention and the choice of randomisation unit to be unlikely. We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity or subgroup analysis to investigate the effects of the randomisation unit.

Cross‐over trials

We identified cross‐over trials as not being appropriate for this intervention.

Dealing with missing data

For included studies, we noted levels of attrition. In future updates, if more eligible studies are included, 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 conducted analyses, as far as possible, on an intention‐to‐treat basis, i.e. we attempted to include all participants randomised to each group in the analyses. The denominator for each outcome in each trial was the number randomised minus any participants whose outcomes were known to be missing.

Assessment of heterogeneity

We assessed statistical heterogeneity in each meta‐analysis by visual inspection of the forest plot and by using I² and Chi² statistics. We interpreted I² as follows:

0% to 40%: heterogeneity might not be important;
30% to 60%: may represent moderate heterogeneity;
50% to 90%: may represent substantial heterogeneity;
75% to 100%: considerable heterogeneity

We were unable to explore substantial heterogeneity by subgroup analysis as the range of analgesia was so wide that subgroup comparison was not possible. We had intended to explore the data with a subgroup analysis for caesarean section, but it was too difficult to differentiate between incisional pain and uterine cramping; hence we excluded these data from the review.

Assessment of reporting biases

Where there were 10 or more studies in the meta‐analysis we investigated reporting biases (such as publication bias) using funnel plots. We assessed funnel plot asymmetry visually, and if asymmetry was suggested by a visual assessment we performed exploratory analyses to investigate it.

Data synthesis

We carried out statistical analysis using the Review Manager 5 software (RevMan 2014). We used a fixed‐effect meta‐analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect, i.e. where trials were examining the same intervention, and we judged the trials’ populations and methods to be sufficiently similar.

If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or if we detected substantial statistical heterogeneity, we used a random‐effects meta‐analysis to produce an overall summary if we considered an average treatment effect across trials to be clinically meaningful. The random‐effects summary was treated as the average range of possible treatment effects and discussed the clinical implications of treatment effects differing between trials. If the average treatment effect was not clinically meaningful, we did will not combine trials. Where we used random‐effects analyses, we present the results as the average treatment effect with a 95% confidence interval.

Subgroup analysis and investigation of heterogeneity

We intended to explore possible sources of heterogeneity using subgroup analyses. However, this was not possible with the included trials. The range of analgesia, the timing of observations and the types of observations were too varied.

In future updates of this review, as more data become available, we plan to carry out the following subgroup analyses:

nulliparous versus primiparous;
up to six hours after birth versus more than six hours; up to 12 hours after birth versus more than 12 hours; up to 18 hours after birth versus more than 18 hours; up to 24 hours after birth versus more than 24 hours; up to 48 hours after birth versus more than 48 hours; up to 72 hours after birth versus more than 72 hours;
type of anaesthesia during birth (for example, epidural anaesthesia versus no anaesthesia).

We will restrict subgroup analyses to the primary outcomes.

We will assess subgroup differences by interaction tests available within RevMan 5 (RevMan 2014). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.

Sensitivity analysis

We intended to conduct sensitivity analyses by comparing the outcomes before and after exclusion of the trials at high risk of bias or unclear risk of bias for sequence generation or allocation concealment; however, the included trials and their outcomes were too varied.

Summary of findings and assessment of the certainty of the evidence

For this update we assessed the certainty of the evidence using the GRADE approach, as outlined in the GRADE handbook, to consider the certainty of the body of evidence relating to the following comparisons.

NSAID versus placebo
NSAID versus opioid
Opioid versus placebo
Paracetamol versus placebo
Paracetamol verses NSAID
NSAID versus herbal analgesia
TENS versus no TENS

We included the following outcomes in the assessment of the certainty of evidence:

Adequate pain relief as reported by the woman;
Need for additional pain relief;
Number of women with adverse events, including nausea, vomiting, sedation, constipation, diarrhoea, drowsiness, sleepiness, psychological impact;
Number of infants with adverse events, including vomiting, sedation, constipation, diarrhoea, drowsiness, sleepiness;
Duration of hospital stay;
Any breastfeeding at hospital discharge;
Any breastfeeding at six weeks postpartum.

We used GRADEpro Guideline Development Tool to create ’Summary of findings’ tables. We produced a summary of the intervention effect and a measure of certainty for each of the above outcomes using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of the body of evidence for each outcome. The evidence can be downgraded from 'high certainty' by one level for serious (or by two levels for very serious) limitations.

Results

Description of studies

Results of the search

See Figure 1.

For this update we identified 56 trial reports to assess.

We included nine new trials (17 reports) (Asti 2011; Chananeh 2018; Dastjerdi 2019; De Sousa 2014; Kantor 1984a; Kheiriyat 2016; Ozgoli 2017; Pourmaleky 2013; Simbar 2015). We excluded 24 new studies (29 reports) (Afravi 2019; Bachar 2018; Bahri 2019; Barhan 2019; Bilgin 2016; Blue 2018; Can 2015; Cunha 2011; Katz 2019; Kayman‐Kose 2014; Kenton 2011; Kim 2019; Kumbar 2017; Li 2014; Li 2015; Mirror 2019; Narimatsu 2001; Nazari 2018; Ozgoli 2018; Parsa 2019; Soltani 2017; Tafazoli 2013; Vaziri 2017; Yogev 2015) and added one trial report to a previously excluded study (Sunshine 1983). We considered two trials, previously excluded because they were conference proceedings that did not include enough detail for inclusion, now eligible for inclusion in this update (Bloomfield 1983; Bloomfield 1986c), although still providing no data.

There are nine ongoing studies (IRCT2015050322053N1; IRCT20190217042739N1; NCT04037202; IRCT2016070428240N2; IRCT2016100930238N1; IRCT20171208037792N1; IRCT201707283860N33; IRCT20180428039454N1; NCT03617900), all of which are trial registrations. We have been in contact with one author (IRCT201707283860N33), whose study has been submitted for publication with the findings embargoed until publication.

Included studies

There are 28 studies included with 2749 women (Asti 2011; Bettigole 1981; Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1981; Bloomfield 1983; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1986c; Bloomfield 1987; Chananeh 2018; Dastjerdi 2019; De Sousa 2014; Jain 1978; Kantor 1984a; Kheiriyat 2016; Laska 1981 Study 1; Laska 1981 Study 2; Mehlhorn 2005; Okun 1982; Olsen 2007; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Skovlund 1991a; Skovlund 1991b; Tehrani 2015).

Design

All of the included studies are randomised controlled trials. Two of these randomised trials used a sequential trial design (Skovlund 1991a; Skovlund 1991b).

Twelve studies were randomised studies with two arms (Asti 2011; Chananeh 2018; Dastjerdi 2019; De Sousa 2014; Kheiriyat 2016; Olsen 2007; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Skovlund 1991a; Skovlund 1991b; Tehrani 2015). Five studies had three arms (Bettigole 1981; Bloomfield 1977 Study 2; Bloomfield 1986c; Jain 1978; Kantor 1984a). Three studies had four arms (Bloomfield 1977 Study 1; Bloomfield 1986b; Mehlhorn 2005). One study had five arms (Bloomfield 1986a). One report included two studies, one with six arms (Laska 1981 Study 1) and a second with seven arms (Laska 1981 Study 2).

Four studies with five arms (Bloomfield 1978; Bloomfield 1981; Bloomfield 1983; Okun 1982) and one study with four arms (Bloomfield 1987) included medications that are no longer in use; therefore only arms with current medications or placebo were included. Three studies reported two arms that could be included (Bloomfield 1978; Bloomfield 1987; Okun 1982) and one study reported three arms that could be included (Bloomfield 1981).

Sample sizes

The samples sizes range from 21 women (Olsen 2007) to 203 women (Bloomfield 1986c).

Setting

All of the studies included in this review enrolled women who were hospital inpatients following the birth of their baby. Thirteen studies enrolled women in the USA (Bettigole 1981; Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1981; Bloomfield 1983; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1986c; Bloomfield 1987; Jain 1978; Kantor 1984a; Okun 1982); eight studies enrolled women in Iran (Asti 2011; Chananeh 2018; Dastjerdi 2019; Kheiriyat 2016; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Tehrani 2015); two studies enrolled women in Venzuela (Laska 1981 Study 1; Laska 1981 Study 2); two enrolled women in Norway (Skovlund 1991a; Skovlund 1991b); one study enrolled women in Sweden (Olsen 2007); one in Germany (Mehlhorn 2005), and one in Brazil (De Sousa 2014).

Participants

All of the studies included women with postpartum pain from uterine cramping, which was assessed and reported separately from other sources of pain. Six studies specifically excluded women with perineal pain or trauma (Asti 2011; Dastjerdi 2019; Olsen 2007; Ozgoli 2017; Simbar 2015; Tehrani 2015) or 3rd and 4th degree trauma (Chananeh 2018); five specified that uterine cramp pain should be greater than perineal pain (Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1986a; Bloomfield 1986b). Two studies reported that when pain was assessed uterine pain and perineal pain (if applicable) were assessed and reported separately (Skovlund 1991a; Skovlund 1991b).

Age as an inclusion/exclusion is specified in seven studies (Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1986a; Bloomfield 1986b; Chananeh 2018; Ozgoli 2017), with five specifying 18 years or older and one study specifying 20 to 30 years. Age was reported in the results of 12 studies (Bettigole 1981; Dastjerdi 2019; De Sousa 2014; Jain 1978; Laska 1981 Study 1; Laska 1981 Study 2; Okun 1982; Olsen 2007; Simbar 2015; Skovlund 1991a; Skovlund 1991b; Tehrani 2015), but ranges were not consistently reported.

Only two studies specified singleton pregnancy (Asti 2011; Chananeh 2018). No studies specified inclusion of twin or higher‐order pregnancies.

Twenty‐three of the studies (Asti 2011; Bettigole 1981; Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1981; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1987; Chananeh 2018; Dastjerdi 2019; De Sousa 2014; Jain 1978; Kheiriyat 2016; Laska 1981 Study 1; Laska 1981 Study 2; Okun 1982; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Skovlund 1991a; Skovlund 1991b; Tehrani 2015) included women who had normal vaginal or uncomplicated births (assumed to be vaginal). Mode of birth was not specified in five studies (Bloomfield 1983; Bloomfield 1986c; Kantor 1984a; Mehlhorn 2005; Okun 1982) and assumed to be inclusive of women with normal births only.

The intention or ability to breastfeed was specified as an inclusion criterion in two studies (Chananeh 2018; Dastjerdi 2019), pain whilst breastfeeding was specified as an inclusion criterion in one study (De Sousa 2014). Breastfeeding was specified as an exclusion criterion in 11 studies (Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1981; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1987; Kantor 1984a; Laska 1981 Study 1; Laska 1981 Study 2; Okun 1982).

Interventions and comparisons

This review includes studies comparing an intervention for pain relief of uterine cramps with a placebo or another form of pain relief.

Pharmacological interventions included: aspirin 650 mg compared with placebo in two studies (Bloomfield 1978; Okun 1982); compared with aspirin 800 mg plus caffeine 64 mg in one study (Jain 1978); compared with placebo, flurbiprofen 50 mg, codeine 60 mg and codeine 120 mg in one study (Bloomfield 1986a); compared with placebo and naproxen 275 mg in one study (Bloomfield 1977 Study 2); compared with placebo and paracetamol 650 mg in one study (Bloomfield 1981); and compared with placebo, ketorolac 5 mg and ketorolac 10 mg in one study (Bloomfield 1986b).

One study (Bloomfield 1986c) with five arms compares aspirin 650 mg, aspirin 1000 mg, paracetamol 650 mg, paracetamol 1000 mg and placebo.

Fenoprofen at different doses is compared with codeine 60 mg and placebo in one three‐arm study (Bettigole 1981), where the fenoprofen dose was 200 mg; one six‐arm study (Laska 1981 Study 1) where the doses of fenoprofen were 50 mg, 100 mg, 200 mg and 300 mg; and in one seven‐arm study (Laska 1981 Study 2) where the doses of fenoprofen were 12.5 mg, 25 mg, 50 mg, 100 mg and 200 mg.

Naproxen 300 mg and 600 mg is compared with codeine 60 mg and placebo in one study (Bloomfield 1977 Study 1). Naproxen 550 mg is compared with placebo in one study (Bloomfield 1987). Naproxen 500 mg is compared with paracetamol 1000 mg in one study (Skovlund 1991a).

Paracetamol 1000 mg is compared with placebo in one study (Skovlund 1991b).

Nalbuphine 15 mg is compared with codeine 60 mg and placebo in one study (Kantor 1984a).

Different doses, 100 mg, 200 mg and 400 mg ibuprofen are compared with aspirin 650mg and placebo in one study with five arms (Bloomfield 1983).

Ibuprofen 400 mg is compared with fennel essence in one study (Asti 2011).

Mefenamic acid 250 mg is compared with a herbal analgesic in seven studies, including melissa officinalis 150 mg (Dastjerdi 2019); ginger 250mg (Pourmaleky 2013); anethum graveolens extract (dill extract) 1.5 mg/kg body weight (Kheiriyat 2016); anise 60 mg (Ozgoli 2017); pimpinella anisum, apium graveolens and crocus sativus (PAC) 500 mg (Simbar 2015); fennelin (fennel extracts) 30 mg (Tehrani 2015). One two‐armed study compared mefenamic acid with mefenamic acid and Nigella Sativa (Chananeh 2018).

One study with four arms (Mehlhorn 2005) compared combinations of TENS (fixed 100‐Hz), metamizole 625 mg, placebo TENS and placebo metamizole.

One study compared high‐intensity TENS (50 mA for one minute) (HI) with low‐intensity TENS (10‐10 5 mA for one minute) (LI) (Olsen 2007).

One study compared TENS (100‐Hz current and 75 msec pulse for 40 mi) with no treatment (De Sousa 2014).

We noted inconsistencies in the doses of oral analgesics administered across studies. For pharmacological preparations, a number of studies administered doses that are above (Bloomfield 1986a) or below (Bloomfield 1981; Dastjerdi 2019; Kheiriyat 2016; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Tehrani 2015) recognised therapeutic doses used currently in clinical practice. For herbal preparations, therapeutic doses are largely unknown and therefore these could not be assessed (Asti 2011; Dastjerdi 2019; Kheiriyat 2016; Ozgoli 2017; Pourmaleky 2013; Simbar 2015; Tehrani 2015). While a number of studies were identified that included comparisons of different doses of the same analgesic (Bloomfield 1977 Study 1; Bloomfield 1986a; Bloomfield 1986b; Laska 1981 Study 1; Laska 1981 Study 2), none of these studies were adequately designed or powered to identify the optimal dose.

Outcomes

Adequate pain relief as reported by the woman

Summed pain intensity differences (SPID) scores were used to calculate the number of women with adequate pain relief for the meta‐analysis in 11 trials (Asti 2011; Bettigole 1981; Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1981; Bloomfield 1986b; Bloomfield 1987; Laska 1981 Study 1; Laska 1981 Study 2; Okun 1982). One of these studies (Bloomfield 1981) reported SPID scores and the number of women with at least 50% pain relief (or similar), but the number did not agree with the number calculated from the SPID. The reason for the discrepancy was not clear, so for consistency we used the number derived from SPID. We used the estimation of one pain intensity difference (PID) to calculate the number of women with adequate pian relief in four studies (Dastjerdi 2019; De Sousa 2014; Simbar 2015; Tehrani 2015).

One study (Bloomfield 1986a) reported a total pain relief (TOTPAR) score, which we used to calculate number of women reporting adequate pain relief. The number of women with at least 50% pain relief was reported, but did not agree with the number calculated from the TOTPAR. The reason for the discrepancy was not clear, so for consistency we used the number derived from TOTPAR.

Trials varied by the length of time following administration of the intervention when participants' pain was assessed; time intervals from treatment to final assessment included 30 minutes (Kheiriyat 2016; Mehlhorn 2005; Pourmaleky 2013); one hour (Chananeh 2018; Simbar 2015; Tehrani 2015); three hours (Dastjerdi 2019); four hours (Asti 2011; Jain 1978; Skovlund 1991a; Skovlund 1991b); five hours (Laska 1981 Study 1; Laska 1981 Study 2); six hours (Bloomfield 1981; Bloomfield 1983; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1986c; Bloomfield 1987; Kantor 1984a; Ozgoli 2017); seven hours (Bloomfield 1977 Study 2; Bloomfield 1978) and eight hours (Bettigole 1981; Bloomfield 1977 Study 1; Okun 1982. One study assessed pain immediately after treatment (Olsen 2007). One study assessed pain during the breastfeed following treatment (De Sousa 2014).

Need for additional analgesia

The need for additional pain relief was reported by 12 studies (Asti 2011; Bloomfield 1977 Study 1; Bloomfield 1977 Study 2; Bloomfield 1978; Bloomfield 1986a; Bloomfield 1986b; Bloomfield 1987; De Sousa 2014; Kantor 1984a; Mehlhorn 2005; Skovlund 1991a; Skovlund 1991b) and 11 of these reported data that could be included in meta‐analysis (Mehlhorn 2005 only reported the statistical significance of the difference between groups).

Pain relief, however measured by the authors

One study reported the number of women rating their pain at 1 to 4 points on a 1 ‐ 10 visual analogue scale (VAS) used for assessing pain (Mehlhorn 2005). One study reported the VAS assessing pain (De Sousa 2014).

Pain relief reported by four studies (Jain 1978; Olsen 2007; Skovlund 1991a; Skovlund 1991b) could not be included in meta‐analysis. Jain 1978 reported pain at four hours following the intervention as a percentage of the baseline pain assessed by a VAS. Olsen 2007 reported the median decrease in VAS seven hours after the intervention. Two studies reported the difference in pain intensity at two hours (Skovlund 1991a) and four hours (Skovlund 1991b) following the intervention.