Abstract
Background
One to eight per cent of women suffer third‐degree perineal tear (anal sphincter injury) and fourth‐degree perineal tear (rectal mucosa injury) during vaginal birth, and these tears are more common after forceps delivery (28%) and midline episiotomies. Third‐ and fourth‐degree tears can become contaminated with bacteria from the rectum and this significantly increases in the chance of perineal wound infection. Prophylactic antibiotics might have a role in preventing this infection.
Objectives
To assess the effectiveness of antibiotic prophylaxis for reducing maternal morbidity and side effects in third‐ and fourth‐degree perineal tear during vaginal birth.
Search methods
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register (31 August 2014) and the reference lists of retrieved articles.
Selection criteria
Randomised controlled trials comparing outcomes of prophylactic antibiotics versus placebo or no antibiotics in third‐ and fourth‐degree perineal tear during vaginal birth.
Data collection and analysis
Two review authors independently assessed the trial reports for inclusion and risk of bias, extracted data and checked them for accuracy.
Main results
We identified and included one trial (147 women from a pre‐planned sample size of 310 women) that compared the effect of prophylactic antibiotic (single‐dose, second‐generation cephalosporin ‐ cefotetan or cefoxitin, 1 g intravenously) on postpartum perineal wound complications in third‐ or fourth‐degree perineal tears compared with placebo. Perineal wound complications (wound disruption and purulent discharge) at the two‐week postpartum check up were 8.20% and 24.10% in the treatment and the control groups respectively (risk ratio (RR) 0.34, 95% confidence interval (CI) 0.12 to 0.96). However, the high failed‐appointment rate may limit the generalisability of the results. The overall risk of bias was low except for incomplete outcome data. The quality of the evidence using GRADE was moderate for infection rate at two weeks' postpartum, and low for infection rate at six weeks' postpartum.
Authors' conclusions
Although the data suggest that prophylactic antibiotics help to prevent perineal wound complications following third‐ or fourth‐degree perineal tear, loss to follow‐up was very high. The results should be interpreted with caution as they are based on one small trial.
Plain language summary
Antibiotic prophylaxis for third‐ and fourth‐degree perineal tear during vaginal birth
Background
Most women are able to give birth without serious damage to their perineum. However, severe perineal trauma, which affects the muscle or tissue in the back passage, occurs in 1% to 8% of women giving birth and is common when forceps are used. There is an increased chance of infection when this happens. Pain in this area can impact not only on a woman's daily activity but also on her relationship with her baby and her partner.
When a woman has a severe perineal tear during vaginal birth, there is thought to be an increased risk of infection. Antibiotics are often prescribed to prevent infection.
Review question To assess how effective antibiotic prophylaxis is to prevent perineal wound infection compared with placebo or no treatment to prevent perineal wound infection and to compare different antibiotic regimens.
Main findings
The review identified one trial, involving 147 women. This trial was conducted to explore the benefit of routine prophylactic antibiotics (intervention group) versus placebo (control group) for women with severe perineal tears. The result showed fewer perineal wound complications in the intervention group at two weeks postpartum. There was no statistically significant difference in perineal wound complications before discharge and at six weeks' postpartum.
The one included study was terminated before it reached the pre‐planned sample size and had a high rate of loss to follow‐up
Quality of the evidence
The included study was of high methodological quality except for incomplete follow‐up. We assessed reduction of perineal wound infection in third‐ or fourth‐degree tear by antibiotic prophylaxis as low to moderate quality of the evidence. However, the results are based on one small trial and there was a high loss to follow‐up. More research is needed.
Summary of findings
Summary of findings for the main comparison. Antibiotic prophylaxis versus no treatment for perineal tear for third‐ and fourth‐degree perineal tear during vaginal birth.
| Antibiotic prophylaxis versus no treatment for perineal tear for third‐ and fourth‐degree perineal tear during vaginal birth | ||||||
| Patient or population: Women with third‐ and fourth‐degree perineal tear during vaginal birth Settings: A hospital in USA Intervention: Antibiotic prophylaxis versus no treatment for perineal tear | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect (95% CI) | No of Participants (studies) | Quality of the evidence (GRADE) | Comments | |
| Assumed risk | Corresponding risk | |||||
| Control | Antibiotic prophylaxis versus no treatment for perineal tear | |||||
| Infection rate at 2 weeks postpartum ‐ perineal wound infection in third‐ or fourth‐degree tear | Study population | RR 0.34 (0.12 to 0.96) | 107 (1 study) | ⊕⊕⊕⊝ moderate1,2 | ||
| 241 per 1000 | 82 per 1000 (29 to 232) | |||||
| Moderate | ||||||
| 241 per 1000 | 82 per 1000 (29 to 231) | |||||
| Infection rate at 6 weeks postpartum ‐ perineal wound infection in third‐ or fourth‐degree tear | Study population | RR 0.38 (0.13 to 1.09) | 128 (1 study) | ⊕⊕⊝⊝ low1,2,3 | ||
| 192 per 1000 | 73 per 1000 (25 to 209) | |||||
| Moderate | ||||||
| 192 per 1000 | 73 per 1000 (25 to 209) | |||||
| Fever or puerperal febrile morbidity | Not estimable | 0 study | See comment | This outcome was not reported in the one included study. | ||
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: Confidence interval; RR: Risk ratio; | ||||||
| GRADE Working Group grades of evidence High quality: Further research is very unlikely to change our confidence in the estimate of effect. Moderate quality: Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate. Low quality: Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate. Very low quality: We are very uncertain about the estimate. | ||||||
1 Small sample size and not met optimal information size (OIS) criteria. 2 We could not judge inconsistency due to the inclusion of only one study. 3 Confidence interval overlaps no effect.
Background
Description of the condition
Episiotomy is the incision in the perineal area to enlarge the vaginal orifice for easier vaginal birth. It consists of two types: midline or median and mediolateral style. Many studies have shown that routine episiotomy can cause such problems as persistent perineal pain, unsatisfied postpartum sexual function, and increasing anal sphincter injury leading to faecal or flatus incontinence (Christianson 2003; Jones 2000; Labrecque 1997; Nager 2001; Signorello 2001). Pain in this area can impact not only on a woman's daily activity but also on her relationship with her baby and her partner. A restrictive episiotomy policy (strict criteria to perform episiotomy only in proper cases such as short stature mother with short perineum, large size baby, or imminent severe laceration of perineum) has been in place for many years and is strongly supported by a Cochrane systematic review (Carroli 1999). In addition, prenatal perineal massage has also been introduced into practice to prevent perineal tears (Davidson 2000; Eason 2000; Johanson 2000; Labrecque 1999). One randomised controlled trial failed to show the effectiveness of perineal massage but concluded that it did no harm (Stamp 2001). A Cochrane review concluded that antenatal digital perineal massage reduces the incidence of perineal trauma (mainly episiotomies) (Beckmann 2013).
Most women are able to give birth without serious damage to the perineum, but 1% to 8% of women suffer severe perineal tears (anal sphincter injury, with or without rectal mucosa injury) during vaginal birth (De Leeuw 2001; Riskin‐Mashiah 2002; Samuelsson 2000; Samuelsson 2002; Sultan 1994). These tears are more common after operative vaginal birth, especially when forceps are used. The incidence of severe perineal lacerations after the use of forceps has been reported as 21% for third‐degree and 7% for fourth‐degree tears (Bofill 1996). Other risk factors include race (Asian women have the highest risk, perhaps due to small size mother and short perineum), midline episiotomy (short distance to anal sphincter), nulliparity (lesser elasticity than a multiparous mother), and high birthweight baby (De Leeuw 2001; Goldberg 2003; Homsi 1994; Jones 2000; Labrecque 1997; Nager 2001; Sultan 1994).
Description of the intervention
When a woman has a severe perineal tear during vaginal birth, there is thought to be an increased risk of infection. Laceration of the vagina and perineum during vaginal birth are classified as first‐, second‐, third‐ and fourth‐degree tears. First‐degree tears involve the vaginal mucosa and connective tissue. Second‐degree tears involve the vaginal mucosa, connective tissue and underlying muscles. Third‐degree tears involve a complete transection of anal sphincter and fourth‐degree tears involve the rectal mucosa (Cunningham 2001; WHO 2003). When the rectal mucosa is ruptured, the wound is classified as contaminated (Waddell 1994) or clean‐contaminated (Mangram 1999). Antibiotic prophylaxis is generally used where wounds have become, or are likely to become, contaminated, such as in colorectal surgery (Oates 1986; Song 1998). A Cochrane review has also shown antibiotic prophylaxis to be effective in reducing puerperal morbidity after cesarean section (Smaill 2002). On the other hand, a Cochrane review on antibiotic prophylaxis after operative vaginal birth could not conclude its effectiveness (Liabsuetrakul 2004).
How the intervention might work
A woman contracting infection after a severe perineal tear may also be at risk of other morbidities as a result of the tear, such as haematoma, dyspareunia (painful sexual intercourse), incontinence and recto‐vaginal fistula (Crawford 1993; Homsi 1994; Labrecque 1997; Nager 2001; Signorello 2001; Sorensen 1988; Sultan 2002; WHO 2003). While some authorities recommend that prophylactic antibiotics be used for severe perineal tears (WHO 2003), others have recommended against this course of action (Whitfield 1995). As widespread use of antibiotics may contribute to antibiotic‐resistant bacteria (Towers 1998; Weinstein 1996), the over‐use of antibiotics is being discouraged by many groups.
Why it is important to do this review
Antibiotic prophylaxis is a low‐cost, accessible intervention that may prevent considerable maternal morbidity. It is therefore important to establish the benefits of prophylactic antibiotics for infection after severe perineal tears, and also to assess whether there are any adverse effects on mother or infant, by systematically reviewing the evidence.
Objectives
To assess the effectiveness of antibiotic prophylaxis for reducing maternal morbidity and side effects in third‐ and fourth‐degree perineal tears during vaginal birth.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials and cluster‐randomised controlled trials. We did not plan to include quasi‐randomised controlled, cross‐over trials or include studies that were presented only as abstracts.
Types of participants
Mothers with third‐ and fourth‐degree perineal tears as a result of vaginal birth.
Types of interventions
Antibiotic regimens used to prevent perineal wound infection compared either with placebo, or no treatment; antibiotic treatment in women who get infection only; and comparisons between different antibiotic regimens.
Types of outcome measures
Primary outcomes
Fever or puerperal febrile morbidity (body temperature of 38ºC or higher occurring on any two occasions in the first 10 days postpartum, exclusion of the first 24 hours).
Perineal wound complications, including infection (oedematous, erythematous, wound edge with pain, serosanguinous or frankly purulent material), or wound dehiscence (wound separation).
Secondary outcomes
Serious infectious complications (such as bacteraemia, septic shock, septic thrombophlebitis, necrotising fasciitis, or death attributed to infection).
Pain (wound pain score or variously measured by authors).
Woman's comfort (unable to sit down or breast feed) while in hospital and six weeks postpartum.
Length of hospital stay for mother.
Adverse reaction (such as allergic reaction, anaphylaxis, diarrhoea).
Maternal‐infant interactions including breastfeeding.
Sexual function including dyspareunia (pain on sexual intercourse), sexual satisfaction, sexual sensation, time to resuming sexual intercourse.
Woman's satisfaction.
Recto‐vaginal fistula (hole between the vagina and rectum).
Search methods for identification of studies
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Electronic searches
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (31 August 2014).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:
monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
weekly searches of MEDLINE;
weekly searches of Embase;
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.
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.
[For details of additional searching carried out by authors for the initial version of the review (Buppasiri 2005), see:Appendix 1.]
Searching other resources
We checked the references of retrieved articles to locate other relevant trials.
We did not apply any language restrictions.
Data collection and analysis
For methods used in the previous update, please see Buppasiri 2010. For this update no new studies were identified from the updated search. However, full risk of bias was performed for the included study and the quality of the evidence was assessed using the GRADE approach.
In future updates, the full methods outlined in Appendix 2 will be used.
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Assessment of risk of bias in included studies
Two review authors independently assessed risk of bias for the study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). There were no disagreements. We would have resolved any disagreements through discussion or, if required, we would have involved a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We described for the one 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 described for the 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 described for the 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 described for the 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 described for the included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomisation 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 described for the 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 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 described for the included study any important concerns we had about other possible sources of bias.
(7) Overall risk of bias
We made explicit judgements about whether the included study was at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we planned to assess the likely magnitude and direction of the bias and whether we considered it is likely to impact on the findings. In future updates, we will explore the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis.
For this update (2014) ,the quality of the evidence was assessed using the GRADE approach (Schunemann 2009) in order to assess the quality of the body of evidence relating to the following key outcomes for the main comparison.
Fever or puerperal febrile morbidity.
Perineal wound infection or perineal wound disruption.
The GRADEprofiler (GRADE 2008) was used to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes were produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
Results
Description of studies
Results of the search
The updated search in December 2009 identified two reports of one study (Duggal 2008) ‐ seeCharacteristics of included studies for details. An updated search in June 2014 did not identify any new trials.
Risk of bias in included studies
The one included study was terminated before it reached the pre‐planned sample size and had a high rate of loss to follow‐up (Figure 1).
1.
Methodological quality summary: review authors' judgements about each methodological quality item for each included study.
Allocation
Procedures for adequate allocation concealment were well described in the study. We judged this study to be at low risk of bias for selection bias.
Blinding
The process of blinding was described. The women, investigator and assessor were all blinded. We judged this study to be at low risk of bias for performance and detection bias.
Incomplete outcome data
The planned number of women to be recruited was 310 (155 per arm). The actual number of women recruited was 147 (44.5%, 64 in treatment arm and 83 in control group). The study was terminated before the planned number of women was achieved. The loss to follow‐up rate was high (27%, 40 in 147). The study was therefore considered to be at moderate risk of attrition bias for attrition bias.
Selective reporting
The study was considered to be at low risk of selective reporting because the planned outcome measurement was prospectively registered in clinical trial registration.
Other potential sources of bias
We considered that it was unlikely that there would be other sources of potential bias so this domain was judged to be at low risk of bias.
Effects of interventions
See: Table 1
Single‐dose, second‐generation cephalosporin intravenously (cefotetan or cefoxitin, 1 g, intravenously, or clindamycin, 900 mg intravenously if allergic to penicillin, in 100 mL of saline) was used as the intervention to prevent perineal wound infection or disruption in the third‐ or fourth‐degree perineal tear compared with placebo (100 mL of normal saline intravenously) .
The primary outcome of the included study was gross disruption or purulent discharge at the site of perineal repair by two weeks postpartum.
Perineal wound complications at two weeks postpartum in the treatment and control groups were four of 49 (8.2%) and 14 of 58 (24.1%) respectively (P = 0.037, risk ratio (RR) 0.34, 95% confidence interval (CI) 0.12 to 0.96) (Analysis 1.1).
1.1. Analysis.
Comparison 1 Antibiotic prophylaxis versus no treatment for perineal tear, Outcome 1 Infection rate at 2 weeks postpartum.
Perineal wound infection before discharge and at six weeks postpartum was also reported. There were no perineal wound complications before hospital discharge in both groups. One hundred and twenty‐eight women were checked at six weeks postpartum (19 of 147 (12.9%) did not come for follow‐up at six weeks). There were perineal wound complications in four out of 55 (7.3%) and 14 out of 73 (19.2%) women in the treatment and control groups respectively, (P = 0.07, RR 0.38, 95% CI 0.13 to 1.09) (Analysis 1.2).
1.2. Analysis.
Comparison 1 Antibiotic prophylaxis versus no treatment for perineal tear, Outcome 2 Infection rate at 6 weeks postpartum.
Discussion
Summary of main results
There were marginally significantly fewer perineal wound complications at two weeks' postpartum in the intervention group. There was no statistically significant difference in perineal wound complications before discharge and at six weeks' postpartum. However, loss to follow‐up was 27.2% and 12.9 % at two and six weeks postpartum respectively.
Overall completeness and applicability of evidence
The one included study, conducted in a developed country, with a relatively high loss of follow‐up, provides insufficient data to address the objectives of this review.
Quality of the evidence
The included study was of high methodological quality; most of the domains were judged to be at low risk of bias except for incomplete outcome data, which we assessed as at high risk of bias. We assessed perineal wound infection in third‐ or fourth‐degree tear reduced significantly by antibiotic prophylaxis at two weeks' postpartum as moderate quality of the evidence and six weeks' postpartum as low quality of the evidence due to the small sample size and because the confidence interval overlaps 'no effect' (Table 1). We could not assess "1. Fever or puerperal febrile morbidity" because the outcome was not reported in the one included study. The inadequate sample size and high loss to follow‐up rate do not allow us to draw a firm conclusion about the benefit of antibiotic prophylaxis in third‐ or fourth‐degree perineal tear after vaginal birth.
Potential biases in the review process
We adhered to the Cochrane Pregnancy and Childbirth Group search strategies and review process. We are not aware of any potential bias in the review process.
Agreements and disagreements with other studies or reviews
There are no other studies or reviews addressing this clinical question.
Authors' conclusions
Implications for practice.
The evidence from the one included study is not strong enough to recommend prophylactic antibiotics for third‐ or fourth‐degree perineal tear after delivery.
Implications for research.
Well‐designed, multicentre, randomised controlled trials are needed before prophylactic antibiotics for third‐ and fourth‐degree perineal tear after vaginal birth can be recommended.
What's new
| Date | Event | Description |
|---|---|---|
| 31 August 2014 | New search has been performed | Review updated. |
| 31 August 2014 | New citation required but conclusions have not changed | Search and methods updated. No new trials identified. 'Summary of findings' table incorporated. |
History
Protocol first published: Issue 1, 2005 Review first published: Issue 4, 2005
| Date | Event | Description |
|---|---|---|
| 31 August 2010 | New search has been performed | Search updated, no new studies identified. One trial identified in the previous updated search has now been included (Duggal 2008). The methods have been updated to reflect the latest Cochrane Handbook. A note about the next update of this review has been added to Published notes. |
| 31 August 2010 | New citation required and conclusions have changed | The scope of the review has changed to include both 3rd and 4th degree perineal tears. |
| 1 December 2009 | Amended | Search updated. Two new reports identified. |
| 13 February 2009 | Amended | Contact details updated. |
| 1 September 2008 | Amended | Converted to new review format. |
Notes
The review authors had contacted the trialists of the one included trial (Duggal 2008) in order to obtain the data separated by degree of perineal tear (3rd or 4th degree) but we have not had a reply from the authors of the trial.
Acknowledgements
The review authors would like to thank Erika Ota for preparing the 'Summary of findings' table for this update. Erika Ota's work was financially supported by the UNDP/UNFPA/UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), Department of Reproductive Health and Research (RHR), World Health Organization. The named authors alone are responsible for the views expressed in this publication.
We would also like to thank Sonja Henderson for her help.
Appendices
Appendix 1. Search strategy
For the initial version of the review, authors searched CENTRAL (The Cochrane Library 2005, Issue 2), MEDLINE (1966 to 15 July 2005) using the strategy below:
#1 PERINEUM single term (MeSH) #2 perine* #3 (tear* or injur* or lacerat* or trauma or damage*) #4 (#2 and #3) #5 (anal near sphincter) or (rectal mucosa) or rectum or (anal epithelium) or anus or (recto‐vaginal fistulae) or (anorectal mucosa) or (anal skin) #6 (tear* or injur* or damage* or lacerat* or rupture* or trauma) #7 (#5 and #6) #8 (obstetric* near tear*) or (obstetric near lacerat*) #9 EPISIOTOMY single term (MeSH) #10 episiotom* or postepisiotom* #11 EXTRACTION OBSTETRICAL explode tree 1 (MeSH) #12 vacuum or ventouse or forcep* #13 deliver* #14 (birth or childbirth or child‐birth or (child next birth)) #15 antibio* #16 ANTIBIOTICS explode all trees (MeSH) #17 (#1 or #4 or #7 or #8) #18 (#9 or #10 or #11 or #12 or #13 or #14) #19 (#15 or #16) #20 (#17 and #18 and #19)
Appendix 2. Methods to be used in future updates
Data collection and analysis
Selection of studies
Two review authors will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third person.
We will create a study flow diagram to map out the number of records identified, included and excluded.
Data extraction and management
We will design a form to extract data. For eligible studies, at least two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person. We will enter data into Review Manager software (RevMan 2014) and check for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will assess the method as:
low risk of bias (any truly random process, e.g. random number table; computer random number generator);
high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);
unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal allocation to interventions prior to assignment and will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will assess the methods as:
low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess the methods as:
low, high or unclear risk of bias for participants;
low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess methods used to blind outcome assessment as:
low, high or unclear risk of bias.
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses which we undertake.
We will assess methods as:
low risk of bias (e.g. no missing outcome data; 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 assess the methods as:
low risk of bias (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);
high risk of bias (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We will describe for each included study any important concerns we have about other possible sources of bias.
We will assess whether each study was free of other problems that could put it at risk of bias:
low risk of other bias;
high risk of other bias;
unclear whether there is risk of other bias.
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the 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 data, we will present results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
Cluster‐randomised trials
We will include cluster‐randomised trials in the analyses along with individually randomised‐trials. We will adjust their sample sizes using the methods described in the 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 sensitivity analysis to investigate the effects of the randomisation unit.
Cross‐over trials
Cross‐over trials are not 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 Tau², I² and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either the Tau² 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% confidence intervals, and the estimates of Tau² and I².
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we plan to investigate it using subgroup analyses and sensitivity analyses. We plan to 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.
Immunocompromised versus not immunocompromised pregnant women, such as HIV infection, chronic steroid use.
Women with prolonged prelabour rupture membranes versus women without prolonged prelabour rupture membranes.
Women with preterm prelabour rupture membranes (PPROM) versus women without PPROM.
Third‐degree tears compared with fourth‐degree tears.
We will restrict subgroup analysis to the following outcomes.
Fever or puerperal febrile morbidity.
Perineal wound infection.
Sensitivity analysis
We will perform sensitivity analyses for aspects of the review that might affect primary outcomes (fever or puerperal febrile morbidity and perineal wound infection), such as where there was risk of bias associated with the quality of some of the included trials. We plan to carry out sensitivity analysis to explore the effects of fixed‐effect or random‐effects analyses for primary outcomes with statistical heterogeneity.
Data and analyses
Comparison 1. Antibiotic prophylaxis versus no treatment for perineal tear.
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
|---|---|---|---|---|
| 1 Infection rate at 2 weeks postpartum | 1 | 107 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.34 [0.12, 0.96] |
| 1.1 Perineal wound infection in third‐ or fourth‐degree tear | 1 | 107 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.34 [0.12, 0.96] |
| 1.2 Perineal wound infection in third‐degree tear | 0 | 0 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.0 [0.0, 0.0] |
| 1.3 Perineal wound infection in fourth‐degree tear | 0 | 0 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.0 [0.0, 0.0] |
| 2 Infection rate at 6 weeks postpartum | 1 | 128 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.38 [0.13, 1.09] |
| 2.1 Perineal wound infection in third‐ or fourth‐degree tear | 1 | 128 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.38 [0.13, 1.09] |
| 2.2 Perineal wound infection in third‐degree tear | 0 | 0 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.0 [0.0, 0.0] |
| 2.3 Perineal wound infection in fourth‐degree tear | 0 | 0 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.0 [0.0, 0.0] |
Characteristics of studies
Characteristics of included studies [ordered by study ID]
Duggal 2008.
| Methods | Type of study: prospective, randomised, placebo‐controlled trial. Method: randomisation was done by using a random‐numbers table. Women were randomly assigned to a single dose of antibiotic (cefotetan or cefoxitin, 1 g, intravenously, or clindamycin, 900 mg intravenously if allergic to penicillin, in 100 mL of saline) or placebo (100 mL of normal saline intravenously). The nurse was instructed to open the envelope and administer the medication or placebo. The log book was kept in a secure location in medication room. Placebo: yes, normal saline was used. Sample size: to demonstrate a 75% reduction in perineal infection rate with an alpha of 0.05 and a power of 80%, 310 women (155 on each arm) were needed. Only 147 women (83 in placebo group, 64 in treatment group) were enrolled in a 3‐year period. Intention‐to‐treat basis: yes. Loss to follow‐up: 27.2% (40 of 147) women lost at 2‐week postpartum check up. 107 women visited at 2‐week postpartum check up. 23.4% (15 of 64) were missed in treatment group, and 30.1% (25 of 83) in control group. 19 of 147 (12.9%) women were lost to follow‐up at the 6‐week postpartum check up. |
|
| Participants | Location: Santa Clara Valley Medical Center and Stanford University Medical Center's Lucile Parkard Children's Hospital. California, San Francisco, USA. Time frame: September 2003‐June 2006. Eligible criteria: women who sustained third‐ or fourth‐degree perineal laceration after vaginal deliveries. Exclusion: age < 18 years, group B streptococcus positive, human immunodeficiency virus positive, had chorioamnionitis or history of inflammation bowel disease, or were already on antibiotics for any reason. Total recruited: 147 women. Treatment group: 64 women, control group = 83 women. |
|
| Interventions | Treatment group: 64 women. Control group: 83 women. |
|
| Outcomes | Perineal wound infection rate (gross disruption or purulent discharge at site of perineal repair) by 2 weeks postpartum. | |
| Notes | There were 310 preplanned women (155 in each arm). The authors decided to terminated the study after 3 years of enrolment because they could not achieve the preplanned number of women within a reasonable time period. Many women refused to participate and many missed enrolment due to busy labour and delivery wards. Only 147 women were recruited: 64 cases in intervention group and 83 in the control group. | |
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Randomisation was done using a random‐numbers table. |
| Allocation concealment (selection bias) | Low risk | The nurse from another ward was instructed to open the randomisation envelope and administer the medication or placebo. The logbook was kept in a secure location in the medication room. |
| Incomplete outcome data (attrition bias) All outcomes | High risk | 107 of 147 women visited for the 2‐week postpartum check up, then 27.2 % were lost to follow‐up; 15 of 64 (23.4%) in the intervention group and 25 of 83 (30.1%) in the control group. |
| Selective reporting (reporting bias) | Low risk | The authors reported perineal wound complication rates before discharge, and at the 2‐ and 6‐week postpartum check ups. |
| Other bias | Low risk | It is unlikely to have other bias. |
| Blinding of participants and personnel (performance bias) All outcomes | Low risk | The women were randomised to receive a single dose of an antibiotic in 100 mL saline or placebo 100 mL saline by using random‐number tables allocated by a nurse. The clinicians evaluating the women postpartum did not have access to the treatment option. |
| Blinding of outcome assessment (detection bias) All outcomes | Low risk | The clinicians evaluating the women postpartum did not have access to the treatment option. |
Differences between protocol and review
We have broadened the inclusion criteria to include women with third‐degree tears and divided the outcomes into primary and secondary.
Methods updated to the current standard methods of the Cochrane Pregnancy and Childbirth Group.
Contributions of authors
Pranom Buppasiri (PB) updated the review. Pisake Lumbiganon (PL), Jadsada Thinkhamrop (JT) and Bandit Thinkhamrop (BT) approved the updated version for publication.
Sources of support
Internal sources
Faculty of Medicine, Khon Kaen University, Thailand.
Faculty of Public Health, Khon Kaen University, Thailand.
External sources
Thai Cochrane Network, Thailand.
Thailand Research Fund (Distiguished Professor Award), Thailand.
UNDP‐UNFPA‐UNICEF‐WHO‐World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), Department of Reproductive Health and Research (RHR), World Health Organization, Switzerland.
Declarations of interest
None known.
New search for studies and content updated (no change to conclusions)
References
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