Abstract
Rationale
Maternal sepsis is the third leading cause of maternal mortality globally. However, the risk of maternal sepsis can be reduced by administering antibiotics prophylactically before infection occurs. Previous research has assessed the effects of azithromycin prophylaxis during pregnancy, but evidence is lacking on the effects of other types of antibiotics, and the potential for antimicrobial resistance.
Objectives
To assess the effects of antibiotic prophylaxis in women in labour after 28 weeks’ gestation on the prevention of maternal and neonatal infections and mortality.
Search methods
We used CENTRAL, MEDLINE, Embase, one other database, and two trial registries, together with reference checking, citation searching, and contact with study authors to identify eligible studies. We did not restrict the search by publication type or language. The latest search date was 30 July 2024.
Eligibility criteria
We included randomised controlled trials involving pregnant women in labour after 28 gestational weeks, comparing any antibiotic prophylaxis with placebo or no treatment. We included trials of women anticipating a vaginal delivery, irrespective of baseline risk factors (unselected, lower‐risk, or higher‐risk), and without an indication for antibiotic prophylaxis in any care setting. We excluded trials that enroled only women with a planned caesarean section or a known bacterial infection (such as group B Streptococcus), and trials evaluating antibiotics for treatment rather than prevention.
Outcomes
Our key outcomes of interest, as presented in the summary of findings table, were: incidence of maternal sepsis, maternal mortality, neonatal sepsis, neonatal mortality, wound infection (perineal), adverse effects of antibiotics, and neonatal intensive care unit (NICU) admission.
Risk of bias
We used the revised Cochrane risk of bias tool for randomised trials (RoB 2) to assess the risk of bias.
Synthesis methods
We synthesised results for each outcome using random‐effects meta‐analysis in Review Manager. Meta‐analyses were conducted using the inverse‐variance method for dichotomous and continuous outcomes. We used a narrative synthesis following the SWiM (Synthesis Without Meta‐analysis) reporting guideline for outcomes that could not be pooled statistically due to heterogeneity or limited data. We summarised key findings from individual studies descriptively and structured by outcome domain. We used GRADE to assess the certainty of evidence for each outcome.
Included studies
We included four trials with 42,846 participants (21,501 in the intervention groups versus 21,345 in the control groups). All were individually randomised trials conducted in low‐ and middle‐income countries. Three trials used a single oral dose of azithromycin in the intervention group, while the fourth used a combination of azithromycin and amoxicillin. All four trials used a placebo control.
Synthesis of results
We judged three trials to have an overall low risk of bias, and the remaining trial to be at 'some concerns', due to reporting bias. Below, we report on the key outcomes of interest, as presented in the summary of findings table.
Compared to placebo, any antibiotic use:
• probably reduces maternal sepsis (1.8% in the placebo group versus 1.2% in the antibiotic group; risk ratio (RR) 0.65, 95% confidence interval (CI) 0.56 to 0.77; I2 = 0%; 4 studies, 42,430 participants; moderate‐certainty evidence).
• likely results in little to no difference in maternal mortality (RR 1.21, 95% CI 0.63 to 2.33; I² = 0%; 4 studies, 42,371 participants; moderate‐certainty evidence).
• results in little to no difference in neonatal sepsis (RR 1.03, 95% CI 0.96 to 1.10; I² = 0%; 4 studies, 42,862 participants; high‐certainty evidence).
• results in little to no difference in neonatal mortality (RR 1.03, 95% CI 0.87 to 1.21; I² = 0%; 4 studies, 42,678 participants; high‐certainty evidence).
• results in little to no difference in perineal wound infection (1.5% in the placebo group versus 1.0% in the antibiotic group; RR 0.80, 95% CI 0.64 to 0.99; 1 study, 25,114 participants; high‐certainty evidence).
• results in little to no difference in NICU admission (RR 1.03, 95% CI 0.94 to 1.12; I² not applicable; 1 study, 29,084 participants; high‐certainty evidence).
The evidence is very uncertain about the effects of antibiotic use on antimicrobial resistance (AMR). One trial showed higher short‐term detection of azithromycin‐resistant bacteria in some maternal samples, but no persisting differences at 11 to 13 months, while in neonates, AMR was rare (very low‐certainty evidence).
Authors' conclusions
Offering a single oral dose of prophylactic antibiotics to pregnant women in labour after 28 gestational weeks or more probably reduces maternal sepsis. It likely results in little to no difference in maternal mortality, and results in little to no difference in neonatal sepsis, neonatal mortality, perineal wound infection, and NICU admission. Evidence on antimicrobial resistance is very uncertain: short‐term increases in resistant organisms were observed in some maternal samples, but no persisting between‐group differences were found at 11 to 13 months' follow‐up. Implementation should be cautious and accompanied by antimicrobial stewardship and AMR surveillance, and future research should better quantify AMR effects and identify optimal antibiotic strategies.
Funding
This work was partially funded by UNDP/UNFPA/UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), a co‐sponsored programme executed by the World Health Organization (WHO) and partially supported by JST Grant Number JPMJPF2108.
Registration
Registration: PROSPERO (2024) CRD42024582129
Plain language summary
Do antibiotics given during labour prevent infections in mothers and babies?
Key messages
Giving antibiotics to women in labour (whose pregnancies were at least 28 weeks along) probably reduces their risk of developing sepsis – a life‐threatening condition that happens when the body overreacts to an infection.
Giving antibiotics in this way makes little or no difference to the number of babies who develop sepsis or die, and probably makes little or no difference to the number of women who die.
The evidence about the adverse (i.e. harmful, unwanted) effects of preventative antibiotics is very uncertain, so we do not know if this treatment contributes to the problem of antimicrobial resistance – when antibiotics stop being effective at fighting bacterial infections.
What is antibiotic prophylaxis, and its benefits and risks?
'Antibiotic prophylaxis' means giving antibiotics to prevent infection before any signs appear. This approach has shown some benefit in reducing infections in new mothers and newborn babies. However, routinely giving women preventative antibiotics during labour is controversial due to concerns about unnecessary antibiotic use and antimicrobial resistance.
What did we want to find out?
We wanted to assess the effects of giving preventative (i.e. 'prophylactic') antibiotics to women during labour, whose pregnancies were at least 28 weeks along (i.e. 28 weeks' gestation). We looked at how many women and babies got infections, particularly sepsis, and how many died.
What did we do?
We searched for studies that compared prophylactic antibiotics with a placebo in pregnant women in labour after 28 weeks’ gestation. A placebo is an inactive substance that looks identical to the antibiotic but has no therapeutic effect. This allows researchers to measure the true impact of the intervention.
The studies included women planning a vaginal birth, as long as they did not have a specific medical reason to receive antibiotics (such as a planned caesarean section or a known infection).
We compared and summarised the study results, and rated our confidence in the evidence, based on factors such as study methods and sizes.
What did we find?
We identified four studies involving a total of 42,846 pregnant women. The studies were conducted in 10 countries: Bangladesh, Burkina Faso, Cameroon, the Democratic Republic of Congo, The Gambia, Guatemala, India, Kenya, Zambia, and Pakistan, all low‐ and middle‐income countries.
Roughly half of the women received prophylactic antibiotics (a single dose by mouth), and half received a placebo.
Compared to placebo, prophylactic antibiotics:
probably reduce the number of women who develop sepsis;
probably make little or no difference to the number of women who die;
make little or no difference to the number of newborns who develop sepsis or die;
make little or no difference to the number of women who develop a perineal wound infection (an infection of the tissue between the vagina and anus);
make little or no difference to the number of babies admitted to the neonatal intensive care unit (NICU).
Only one study looked at antimicrobial resistance, and we are not confident in its evidence. The study reported short‐term increases in antibiotic‐resistant bacteria found in some samples (e.g. of breast milk, nasal or vaginal swabs) from women given antibiotics compared to those given placebo, but these differences disappeared by 13 months. In newborns, antimicrobial resistance was rare.
What are the limitations of the evidence?
We had moderate or high confidence in the evidence about the number of women and babies who developed infections (including sepsis) or died. As noted above, we are not confident in the evidence about antimicrobial resistance. Antimicrobial resistance patterns and antibiotic use practices vary widely, and the studies focused primarily on azithromycin, a broad‐spectrum antibiotic, without evaluating other options. The long‐term impact on antibiotic resistance remains very uncertain and requires further research.
How current is this evidence?
The evidence is current to July 2024.
Summary of findings
Summary of findings 1. Summary of findings table ‐ Any antibiotic compared to placebo for maternal and neonatal outcomes.
| Any antibiotic compared to placebo for maternal and neonatal outcomes | ||||||
| Patient or population: women in labor at 28 weeks' gestation or later, in any care setting, regardless of risk category (unselected, low‐risk, or high‐risk), provided no indication for antibiotic prophylaxis exists Setting: Bangladesh, Burkina Faso, Cameroon, Democratic Republic of Congo, The Gambia, Guatemala, India, Kenya, Pakistan, and Zambia Intervention: any antibiotic Comparison: placebo | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect (95% CI) | № of participants (studies) | Certainty of the evidence (GRADE) | Comments | |
| Risk with placebo | Risk with any antibiotic | |||||
| Maternal sepsis (within 28 to 56 days postpartum) | 18 per 1000 | 12 per 1000 (10 to 14) | RR 0.65 (0.56 to 0.77) | 42430 (4 RCTs) | ⊕⊕⊕⊝ Moderatea,b | Any antibiotic probably reduces maternal sepsis. |
| Maternal mortality (within 28 to 56 days postpartum) | 1 per 1000 | 1 per 1000 (0 to 2) | RR 1.21 (0.63 to 2.33) | 42371 (4 RCTs) | ⊕⊕⊕⊝ Moderatec | Any antibiotic likely results in little to no difference in maternal mortality. |
| Neonatal sepsis (within 28 to 56 days after birth) | 71 per 1000 | 73 per 1000 (68 to 78) | RR 1.03 (0.96 to 1.10) | 42862 (4 RCTs) | ⊕⊕⊕⊕ Highd | Any antibiotic results in little to no difference in neonatal sepsis. |
| Neonatal mortality (within 28 to 56 days after birth) | 13 per 1000 | 13 per 1000 (11 to 16) | RR 1.03 (0.87 to 1.21) | 42678 (4 RCTs) | ⊕⊕⊕⊕ Highd | Any antibiotic results in little to no difference in neonatal mortality. |
| Wound infection (perineal) (within 28 to 56 days postpartum) | 15 per 1000 | 12 per 1000 (10 to 15) | RR 0.80 (0.64 to 0.99) | 25114 (1 RCT) | ⊕⊕⊕⊕ High | Any antibiotic results in little to no difference in maternal wound infection. |
| Adverse effects of antibiotics: antimicrobial resistance | One individually randomised, placebo‐controlled trial (primary report: Oluwalana 2017) assessed antimicrobial resistance (AMR) via multiple subgroup analyses reported in secondary publications (Roca 2016; Jagne 2022) and a 12‐month follow‐up (Bojang 2018), using different methods and time points, precluding meta‐analysis. In a post hoc analysis of the trial (Jagne 2022), azithromycin‐resistant Streptococcus pyogenes (GAS) was assessed in a subset of 715 mother–newborn pairs with complete samples (363 placebo, 352 azithromycin). Samples were taken from the nasopharynx (days 3, 6, 14, 28), breast milk (same days), and vaginal swabs (days 8–10). Azithromycin‐resistant GAS was more frequently detected in maternal vaginal samples in the azithromycin group (1.99% vs 0.28%; P = 0.035), largely due to Streptococcus dysgalactiae subsp. equisimilis (SDSE[A]) carrying mefA and msrD resistance genes. In neonates, resistant GAS isolates were very rare and comparable between groups (one in each arm). In a secondary report from the same trial (Roca 2016), bacterial carriage was assessed through day 28 (> 90% follow‐up) among 829 women (414 azithromycin, 415 placebo; 843 births). Azithromycin reduced overall bacterial carriage (e.g. neonatal nasopharyngeal carriage at day 6: 28.3% vs 65.1%), but resistant Staphylococcus aureus was more commonly detected in the azithromycin group across maternal and neonatal samples (e.g. breast milk 8.1% vs 16.4%, prevalence ratio (PR) 0.49; vaginal swab 8.9% vs 14.1%, PR 0.63). At 11–13 months, the follow‐up report found no persisting between‐group differences in infant nasopharyngeal carriage or azithromycin resistance (Bojang 2018). | (1 RCT) | ⊕⊝⊝⊝ Very lowe,f,g | The evidence is very uncertain about the effect of any antibiotic on adverse effects of antibiotics (including emergence of antibiotic‐resistant bacteria). | ||
| Neonatal intensive care unit (NICU) admission (within 28 to 56 days after birth) | 64 per 1000 | 65 per 1000 (60 to 71) | RR 1.03 (0.94 to 1.12) | 29084 (1 RCT) | ⊕⊕⊕⊕ Highd | Any antibiotic results in little to no difference in NICU admission. |
| *The risk in the intervention group (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 certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different. Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect. | ||||||
| See interactive version of this table: https://gdt.gradepro.org/presentations/#/isof/isof_question_revman_web_453125455629832627. | ||||||
a Downgraded one level for indirectness: two trials (accounting for 8.8% of the pooled effect) defined maternal sepsis as clinical signs of infection (e.g. fever, uterine tenderness) without organ dysfunction, differing from the World Health Organization (WHO) sepsis definition. b Not downgraded for imprecision: 95% CI is entirely outside the minimal important difference (MID) of 0.75 to 1.25. c Downgraded one level for imprecision: despite a large sample size (42,371 participants), maternal deaths were rare and the wide 95% CI (0.63 to 2.33) includes both benefit and harm, crossing the MID of 0.75–1.25. d Not downgraded for imprecision: 95% CI is entirely within the MID of 0.75–1.25, indicating little or no clinically important effect. e Downgraded two levels for risk of bias. Risk of bias for this outcome was assessed at the trial level using RoB 2. Antimicrobial resistance evidence derives from multiple publications of the same Gambian RCT (primary report: Oluwalana 2017), including a short‐term microbiological carriage report (Roca 2016), a post hoc resistance analysis (Jagne 2022), and a 12‐month follow‐up (Bojang 2018). We judged it to be at high risk of bias due to subgroup‐only analyses, selective reporting, incomplete sampling frames, and variation in measurement methods and timing; overall risk of bias for this outcome is high. f Downgraded one level for inconsistency: substantial heterogeneity across studies with different definitions, sample types, and measures. g Downgraded one level for imprecision: very small number of resistant isolates leading to highly uncertain effect estimates.
Background
Description of the condition
Maternal sepsis (also referred to as peripartum sepsis) is one of the leading causes of maternal death worldwide [1, 2]. It is a life‐threatening condition that arises when an infection during pregnancy, childbirth, or the postpartum period triggers a systemic inflammatory response [3]. Beyond its severe implications for the pregnant woman, peripartum sepsis significantly increases the risk of neonatal infections, preterm birth, and neonatal mortality [4]. Bacterial transmission from mother to baby can cause neonatal sepsis, pneumonia, and meningitis. This means that preventing maternal infection is critical to both maternal and neonatal survival [5].
Peripartum sepsis can develop from infections of the genital tract, urinary tract, surgical wounds, or other sites associated with labour and birth. Common causative pathogens include Group B Streptococcus, Escherichia coli, Staphylococcus aureus, and Klebsiella pneumonia [6]. Peripartum sepsis often presents with fever, tachycardia, hypotension, uterine tenderness, and signs of systemic inflammation. If left untreated, it can rapidly progress to septic shock and multi‐organ failure. Prior evidence suggests that peripartum sepsis and the maternal inflammatory response can negatively impact foetal immune development and microbiome colonisation, with potential long‐term consequences for the baby’s health [ 7, 8, 9, 10].
The risk of maternal sepsis is heightened in cases of prolonged labour, premature rupture of membranes, caesarean section, poor hygiene during childbirth, and when underlying maternal conditions such as diabetes or anaemia are present. Additionally, healthcare‐associated factors, such as inadequate infection control measures or overuse of invasive procedures, contribute to the spread of bacterial infections [11]. Importantly, these life‐threatening infections in pregnant women can be prevented through various interventions, including essential knowledge of infection prevention and control for healthcare workers, screening and management by trained healthcare workers, and antibiotic prophylaxis [12, 13, 14, 15].
Description of the intervention and how it might work
The intervention under consideration is the prophylactic use of antibiotics for preventing maternal infections during labour and birth. Prophylactic antibiotics are administered before an infection occurs to reduce the risk of bacterial colonisation and subsequent infection. Prophylactic antibiotics may be used in certain subgroups of women who are at higher risk of infection (such as those undergoing caesarean section or forceps delivery), or in women without specific risk factors – the latter group is the focus of this review. Various antibiotics have been evaluated for prophylactic use in labour, with azithromycin being one of the most commonly studied agents.
Azithromycin is a broad‐spectrum macrolide antibiotic with anti‐inflammatory properties that is effective against a range of bacteria commonly associated with maternal infections, such as Streptococcus and Staphylococcus species. When given to pregnant women in labour, azithromycin has been shown to reduce the incidence of maternal sepsis, endometritis, incisional infections, and urinary tract infections [16]. However, its effectiveness in preventing neonatal infections remains unclear. Systematic reviews focused on azithromycin for prophylaxis reported that when used as prophylaxis during labour, it effectively prevents maternal sepsis, but does not reduce the incidence of neonatal sepsis [12, 13]. Other antibiotics, such as an amoxicillin/clavulanic acid combination, have also demonstrated efficacy in preventing maternal infections in certain settings [17, 18]. However, the impact of prophylactic antibiotics on neonatal infections, including neonatal sepsis, remains uncertain.
One of the major concerns with widespread prophylactic antibiotic use is the potential for antimicrobial resistance (AMR). The overuse (excessive or unnecessary use) or misuse (incorrect selection, dosing, or duration) of antibiotics can lead to the development of antimicrobial‐resistant strains, which may undermine their effectiveness over the longer term. Despite these concerns, there is limited research on antibiotic overuse amongst pregnant women. Studies in India, Tanzania, and Korea suggest high rates of antibiotic prescribing in obstetric care [19, 20, 21, 22, 23], highlighting the need for more judicious use of antibiotic prophylaxis in pregnancy and childbirth.
The World Health Organization (WHO) currently recommends that prophylactic antibiotics should be offered to women undergoing caesarean section and, as of 2021, to those undergoing operative vaginal birth (i.e. vacuum‐assisted or forceps delivery) [15, 24]. However, there is no explicit WHO recommendation regarding routine prophylactic antibiotic use during labour for women without specific risk factors. The WHO guidelines state that routine antibiotic use after uncomplicated vaginal birth is not recommended [14]. Recent trials of azithromycin use in women in labour without specific risk factors have provided new evidence regarding its potential benefits and risks [12]. While prophylactic antibiotics are widely used in specific obstetric scenarios, their routine use in women with uncomplicated vaginal births who do not have clear clinical indications remains a subject of ongoing debate. It is crucial to carefully assess the available evidence to balance the benefits of infection prevention against the risks of antimicrobial resistance and unnecessary antibiotic exposure.
Why it is important to do this review
A recent systematic review of randomised controlled trials suggests that azithromycin prophylaxis in women in labour without specific indications in low‐ and middle‐income countries can prevent maternal sepsis and associated harms [13]. However, this review focused exclusively on azithromycin and did not assess the effects of other antibiotics such as amoxicillin and clavulanic acid. Furthermore, there are somewhat conflicting findings regarding its role in preventing neonatal infections, and its overall impact on maternal and neonatal morbidity and mortality. For example, while intrapartum administration of azithromycin has been shown to reduce maternal sepsis or postpartum infections, it does not reduce neonatal sepsis or mortality rates [13].
Our review builds on this evidence by expanding the scope to include any prophylactic antibiotic used during labour and assessing whether studies involving different antibiotics demonstrate comparable benefits. A large trial investigating the use of amoxicillin and clavulanic acid prophylaxis after operative vaginal birth showed significant benefits in preventing maternal infections [17, 18]. Although this trial suggests a potential role for antibiotic prophylaxis beyond women at clear clinical risk, its population consisted of women undergoing operative vaginal birth, which does not reflect the focus of our review, which aims to assess prophylactic antibiotic use amongst women without specific clinical indications or interventions. Therefore, a more comprehensive systematic evaluation is warranted to determine the optimal use of prophylactic antibiotics in women without specific indications.
Given the increasing global concern over AMR, it is crucial to assess whether the routine use of prophylactic antibiotics during labour in women without specific indications is justified. While azithromycin is inexpensive, easy to store, and widely available, the implications of widening its use need careful consideration, particularly as azithromycin resistance will likely result from wider use. Prior systematic reviews and trials have assessed the effects of azithromycin prophylaxis during pregnancy [3, 25, 26], but evidence is lacking for prophylaxis using other types of antibiotics. Therefore, this review aims to systematically evaluate the available evidence on the use of any type of prophylactic antibiotic during labour in women without specific indications. The findings will help inform clinical practice and guidelines, supporting healthcare professionals in making evidence‐based decisions regarding antibiotic prophylaxis during the intrapartum and early postpartum periods.
Objectives
To assess the effects of antibiotic prophylaxis in women in labour after 28 weeks’ gestation on the prevention of maternal and neonatal infections and mortality.
Methods
We followed the Methodological Expectations for Cochrane Intervention Reviews (MECIR) standards when conducting the review [27], and the PRISMA 2020 checklist for reporting the findings [28]. As this Cochrane review was specifically developed to inform WHO guidelines, and due to the urgency of supporting timely decision‐making, the protocol was not published but was registered in PROSPERO (CRD42024582129; [29]), to ensure transparency and adherence to systematic review standards.
To enhance the comprehensiveness and clinical relevance of the findings, we modified the original PROSPERO‐registered protocol in several ways. Although maternal satisfaction and intrapartum stillbirth were not amongst the outcomes originally specified in the PROSPERO registration, we added these at the request of the World Health Organization, along with additional measures recommended in WHO’s perinatal antibiotic administration guidelines. A further methodological adjustment involved the adoption of random‐effects models for all analyses, diverging from the protocol’s original specification of fixed‐effect models for most analyses. We made this change in response to editorial and peer‐reviewer feedback and to account for potential clinical and methodological heterogeneity across studies, regardless of statistical heterogeneity levels. Furthermore, we introduced two additional subgroup analyses beyond those prespecified in the protocol: comparisons between low‐risk and high‐risk cohorts, as well as between preterm and full‐term deliveries. The rationale for these additions was to more precisely elucidate the potential heterogeneity of intervention effects across clinically meaningful populations, thereby strengthening the applicability of the review’s conclusions. In the protocol, pyloric stenosis was not explicitly named but was included under the category of 'other neonatal adverse events' within the additional outcomes. In the review, we specified pyloric stenosis as a sub‐outcome to improve clarity, as it was reported as a distinct neonatal adverse event in some included trials. This specification did not alter the original outcome classification or analysis plan.
Criteria for considering studies for this review
Types of studies
We included all published, unpublished, and ongoing individual and cluster‐randomised control trials (RCTs). We excluded quasi‐RCTs (e.g. randomisation of treatment by date of admission, etc.) and cross‐over trials.
Types of participants
Eligible participants were women or girls (of any age) in labour at 28 weeks' gestation or later, anticipating vaginal delivery, and without a clear clinical indication for antibiotic prophylaxis (e.g. planned caesarean section, confirmed bacterial infection). We included participants irrespective of baseline risk factors for infection (e.g. age, comorbidities, socioeconomic status), to ensure broad applicability. We excluded trials enroling only women with planned caesarean section or those evaluating antibiotics for treatment (rather than prevention). Our primary focus was on women without established indications for antibiotic prophylaxis (i.e. not already recommended for antibiotics), to clarify effects in those for whom the benefit remains uncertain.
Types of interventions
The intervention in this review comprised any type or class of antibiotic administered prophylactically during labour after 28 gestational weeks only; any regimens continuing treatment postpartum were excluded, with no restrictions on the route of administration or dosage. The comparator was either a placebo or no treatment. To clarify, this review included only trials investigating single‐dose prophylactic antibiotic administration initiated after the onset of labour. While reducing therapeutic antibiotic regimens (typically involving multiple doses over several days) is indeed an established approach to minimise antimicrobial resistance, we excluded studies that assessed such prolonged therapeutic regimens or postnatal continuation protocols, as these were outside the scope of this review.
Outcome measures
We included studies that met the eligibility criteria above, even if they did not report any of the outcomes listed below. Outcome time points were defined by trial authors.
Critical outcomes
Maternal outcomes
Incidence of maternal sepsis
Incidence of maternal mortality
Neonatal outcomes
Incidence of neonatal sepsis
Incidence of neonatal mortality
Important outcomes
Incidence of any wound infection or perineal wound infection
Adverse effects of antibiotics (including the emergence of antibiotic‐resistant bacteria, and other adverse events such as vomiting, diarrhoea, or pyloric stenosis)
Neonatal ICU admission
Other maternal infections (chorioamnionitis, endometritis, mastitis or breast abscess, pyelonephritis, Clostridioides difficile colitis)
Other neonatal infections (excluding sepsis, meningitis, pneumonia, congenital infections)
Cost of care
Maternal satisfaction
Intrapartum stillbirth
Search methods for identification of studies
The searches were conducted without restrictions by publication year, publication type, or language.
Additionally, we contacted corresponding authors when relevant data were not included in published studies, and considered the eligibility of both unpublished studies and studies available only as abstracts based on the selection criteria.
Electronic searches
The search was conducted on 30 July 2024. The information specialist initially developed the search strategies for Ovid MEDLINE, which were subsequently adapted for use in other databases to ensure consistency. Searches of Embase and CINAHL (Cumulative Index to Nursing and Allied Health Literature) were conducted using the randomised‐controlled‐trial filter provided by the Cochrane Highly Sensitive Search Strategy for identifying randomised controlled trials and controlled clinical trials [30]. The PRISMA flow diagram illustrates the search results. Detailed search strategies for each database are provided in Supplementary material 1.
The electronic searches were conducted in the following databases:
Cochrane Central Register of Controlled Trials (CENTRAL; 2024, Issue 7) via the Cochrane Register of Studies (CRS);
MEDLINE Ovid (1946 to 30 July 2024);
Embase Ovid (1980 to 30 July 2024); and
CINAHL EBSCO (1982 to 30 July 2024).
We also searched to identify the registrations using the following sites:
ClinicalTrials.gov (https://clinicaltrials.gov/; searched 30 July 2024); and
WHO International Clinical Trials Registry Platform (ICTRP; https://www.who.int/clinical-trials-registry-platform; searched 30 July 2024).
Searching other resources
We searched the reference lists of all included studies and relevant systematic reviews for additional studies. We also searched trial registries (e.g. ClinicalTrials.gov, WHO ICTRP) to identify ongoing or unpublished studies. As part of our efforts to identify any potentially problematic studies, we checked for post‐publication amendments (including expressions of concern, errata, corrigenda, and retractions) related to all included and potentially eligible studies.
Data collection and analysis
Selection of studies
The search results were managed using EndNote [31], where all identified records were imported. Duplicate records were identified and removed using the built‐in duplicate detection tool to streamline the study selection process. For screening, pairs of authors (from DS, NY, EN, HS, OR, and EO) independently evaluated titles and abstracts against predefined eligibility criteria using Rayyan (https://www.rayyan.ai) [32]. Subsequently, full‐text articles of potentially relevant studies were reviewed independently by the same authors.
The two screening authors discussed any disagreements during the selection process. If consensus could not be reached, we consulted a third review author (EO) to make a final decision. We created a PRISMA flow diagram to map the number of records identified, screened, excluded, and included in the review.
To ensure the trustworthiness of included studies, we checked each against criteria adapted from the Cochrane Pregnancy and Childbirth Checklist [33]. This included checks for research governance (e.g. presence of retraction notices, prospective registration, availability of protocols or ethics approval letters), baseline characteristics (e.g. plausible distributions of participant data), feasibility (e.g. realistic recruitment timelines and follow‐up data), and results (e.g. absence of implausible findings or inconsistencies in randomisation methods).
Where studies raised concerns about trustworthiness, we attempted to contact the study authors to resolve issues or gather additional information. If we could not obtain adequate information, we placed these studies in the 'awaiting classification' category, documenting our reasons for this decision and details of communication attempts.
Data extraction and management
Working independently, two or more authors (of DS, HS, EN, NY, and OR) conducted data extraction using Microsoft Excel [34]. We piloted the data extraction form in at least one study in the review. Data extraction was collaborative, with discussions between two authors and consultation with a third (EO) when disagreements arose. This ensured that all perspectives were considered and decisions made collectively.
The extraction table included the following information:
author names;
publication year;
study location;
study design;
types and numbers of participants;
intervention and comparison details;
study outcomes;
outcome measurement tools/scales/points;
results;
funding sources and conflicts of interest.
We contacted corresponding authors to request additional information for analysis in the case of missing data. However, if we obtained no further data, we used a modified intention‐to‐treat (ITT) analysis for the missing data.
Risk of bias assessment in included studies
We used the revised Cochrane risk of bias tool for randomised trials (RoB 2) to assess the risk of bias for the outcomes included in the summary of findings table, rather than for all reported outcomes in the trials [35]. This tool ensures a standardised approach to evaluating methodological quality and identifying potential biases that could influence the results. We conducted the evaluation using a Microsoft Excel assessment form [34].
The assessment covered the following domains, as outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions [35].
Bias arising from the randomisation process. We examined whether the randomisation process was adequately described and whether it generated truly random sequences. We classified methods such as computer‐generated random numbers or random number tables as low risk of bias; non‐random methods, such as allocation based on hospital records or birthdates, as high risk of bias; and unclear descriptions as having an unclear risk of bias.
Bias due to deviations from intended interventions. This domain evaluated whether participants remained in their assigned intervention groups throughout the study and whether deviations were balanced across groups. We also considered blinding to determine if knowledge of group allocation could have influenced deviations from the intended interventions.
Bias due to missing outcome data. We assessed the completeness of outcome data, including the rates of attrition and exclusions. We judged studies with minimal or balanced missing data across intervention groups to have a low risk of bias. If missing data were substantial or unevenly distributed, or if reasons for missing data were inadequately reported, we classified these as high risk of bias.
Bias in measurement of the outcome. This domain focused on whether outcome assessors were blinded and whether the measurement methods were appropriate and consistently applied across groups. If lack of blinding or poor measurement techniques could plausibly influence the results, we judged these as having a high risk of bias.
Bias in selection of the reported result. We investigated whether all prespecified outcomes were reported and whether the reported outcomes matched those listed in study protocols or registries. We classified selective reporting, such as omitting non‐significant outcomes, as high risk of bias.
We evaluated each domain using signalling questions, with responses categorised as:
yes;
probably yes;
probably no;
no;
no information.
These responses were used to guide an overall judgment for each domain as:
low risk of bias;
some concerns;
high risk of bias.
Following this, we assigned an overall risk of bias judgment for each study, incorporating all domains. For outcomes with narratively reported results, we assessed the risk of bias at the study level using RoB 2, considering selection, measurement, and reporting biases.
Working independently, two review authors (of DS, NY, HS, and EN) assessed the risk of bias for each included study. In cases where discrepancies arose, we discussed the issue to reach consensus. If disagreements could not be resolved, we consulted a third author (EO) to make the final decision. This multistage process ensured that the assessments were rigorous, unbiased, and transparent.
For studies employing a cluster‐randomised design, we planned to use the RoB 2 tool for cluster‐RCTs, which includes two additional domains to address the specific challenges associated with this study design [36]. However, we included no cluster‐RCTs in this review, so this step was unnecessary.
Intention‐to‐treat effect and sensitivity analysis
We used the intention‐to‐treat effect to assess the impact of assignment to intervention groups. We performed sensitivity analyses where necessary to explore the robustness of the findings and the influence of assumptions made during data synthesis. For cluster‐RCTs, we would have accounted for the potential effects of clustering on the results, using the intracluster correlation coefficient (ICC) when available.
This detailed approach ensured that the risk‐of‐bias assessments were robust, methodologically sound, and provided a transparent evaluation of the reliability of the included studies. We summarised the results of the assessments and used these to guide the interpretation of the findings.
Measures of treatment effect
For dichotomous data, we presented results using risk ratios (RR) with 95% confidence intervals (CIs).
For continuous data, we used the mean difference (MD) when reported outcomes were measured in the same way. We used the standardised mean difference (SMD) to combine data when the same outcomes were reported but measured in different ways. Where trials reported continuous data as median and interquartile range (IQR) and data passed the test of skewness, we converted the median to mean and estimated the standard deviation (SD) as IQR/1.35.
When an outcome was reported in a format unsuitable for meta‐analysis, we converted it to the required format, as shown in Chapter 6 of the Cochrane Handbook for Systematic Reviews of Interventions [37].
Unit of analysis issues
Multi‐arm trials
We followed the guidance in the Cochrane Handbook for Systematic Reviews of Interventions to address possible unit of analysis issues that can arise due to the inclusion of multi‐arm trials [38] (of which there was one in this version of the review (Subramaniam 2021 [17, 18, 39])). Specifically, for dichotomous outcomes, we combined the two intervention groups in Subramaniam 2021 into a single group for comparison with the control group, summing the sample sizes and the number of events across the two intervention groups. For continuous outcomes, we combined the means and standard deviations of the two intervention groups, using the methods described in the Cochrane Handbook. This approach ensured accurate data synthesis for meta‐analysis.
Cluster‐randomised trials
Although we included no cluster‐randomised trials in this version of the review, we outline here how we will manage them in future updates if included. Cluster‐randomised trials present unique challenges due to the potential for intracluster correlation, which can lead to overestimated sample sizes if not properly adjusted. To address this, we will adjust for clustering by adjusting sample sizes and standard errors using an estimate of the intracluster correlation coefficient (ICC). We would derive the ICC from the trial itself, if available, or from a similar trial or study population. If we obtain ICC estimates from external sources, we will report this and conduct sensitivity analysis to assess the impact of varying ICC values. We will synthesise cluster‐RCTs with individually‐randomised trials only if there is minimal heterogeneity between study designs and if the interaction between the intervention effect and the randomisation unit is unlikely. We will report any heterogeneity arising from the inclusion of cluster‐randomised trials, and conduct subgroup analyses to investigate the effects of the randomisation unit on the overall findings.
Cross‐over trials
We did not include cross‐over trials in this review, as the design is not appropriate for the intervention under investigation.
Other complex designs
If we include studies with non‐standard designs (e.g. repeated measures, events that may recur, or randomisation of multiple body parts) in future updates of this review, we will follow the methodological guidance provided in Chapters 6 and 11 of the Cochrane Handbook for Systematic Reviews of Interventions[40, 41].
Dealing with missing data
We carefully documented the levels of attrition in the included studies. We evaluated the potential impact of missing data on the overall treatment effect by conducting sensitivity analyses to explore the influence of studies with substantial missing data on the results.
For all outcomes, we performed analyses based on the ITT principle wherever possible. This approach ensured that all participants randomised to each group were included in the analysis, regardless of whether they received or adhered to the assigned intervention. Specifically, this meant that the denominator for each outcome was the total number of participants randomised to each group, ensuring a consistent and unbiased analysis framework.
When outcome data were missing due to reasons unrelated to the outcome, and missing data were evenly distributed between intervention and control groups, we used a modified ITT (mITT) approach. In these cases, we adjusted the denominator for each outcome to reflect the number of participants randomised, minus those known to have missing outcomes.
In situations where missing data were not adequately explained, unevenly distributed between groups, or suspected to be related to the outcome, we made efforts to contact the study authors for clarification. If no satisfactory explanation was provided or the missing data could not be resolved, we conducted sensitivity analyses to assess the robustness of the findings and to evaluate the potential impact of the missing data on the review’s conclusions.
Reporting bias assessment
We planned to evaluate reporting bias if we included 10 or more studies in any meta‐analysis. However, in this review, none of the meta‐analyses included 10 or more studies.
For future updates, if the number of included studies in a meta‐analysis reaches 10 or more, we will assess potential reporting biases, such as publication bias, using funnel plots. We will visually inspect for funnel plot asymmetry to detect any indications of bias. In cases where funnel plot asymmetry is observed, we will explore potential causes, such as small‐study effects or other sources of bias, and document these findings. We may also employ additional methods, including statistical tests for funnel plot asymmetry, if appropriate. For all assessments, two review authors (e.g. DS and HS) will independently evaluate reporting biases. We will resolve any disagreements through discussion or by consulting a third author (e.g. EO). If necessary, we will contact study authors to obtain or confirm relevant information about missing or unreported outcomes.
Synthesis methods
We conducted statistical analyses using Review Manager (RevMan) [42]. We applied a random‐effects meta‐analysis model to combine data, as we anticipated clinical heterogeneity amongst the included trials, which could lead to variations in treatment effects. This model considers the summary effect as the average of a distribution of possible treatment effects, allowing for differences between studies. If we deemed the average treatment effect to be not clinically meaningful due to substantial heterogeneity, we did not combine trials in a meta‐analysis. We reported the results from random‐effects analyses as the average treatment effect with 95% CIs, along with estimates of heterogeneity (Tau² and I²).
We conducted all analyses according to the intention‐to‐treat (ITT) principle. This included participants who underwent intrapartum caesarean section after randomisation. Randomisation was maintained in the analysis, ensuring that all participants were analysed in the groups to which they were originally assigned.
Amongst the included studies, two trials used generalised linear models (GLM) to adjust neonatal outcomes. Roca 2023 [43, 44], conducted in The Gambia and Burkina Faso, adjusted for covariates such as country, birth weight, and 1‐minute Apgar score to improve statistical power in their logistic regression models analysing neonatal sepsis and mortality. Tita 2023 [45, 46, 47, 48, 49, 50, 51, 52, 53, 54, 55] included adjustments using GLM for trial site, multiple births correlation, and high‐risk infection status to estimate relative risks and 95% confidence intervals for neonatal outcomes, including sepsis and mortality. To synthesise these results appropriately, we employed the general inverse‐variance (GIV) method. This approach ensured that the effect estimates and standard errors derived from the adjusted analyses were integrated accurately into the meta‐analysis. Such a method enables a robust synthesis that accounts for the adjustments made in the primary studies, reflecting their statistical rigour and ensuring comparability in the combined analysis.
Although we included no cluster‐randomised trials in this review, future updates may incorporate such studies. In these cases, we would also use the GIV method to combine effect estimates and SEs, with adjustments made for ICCs if necessary. We would perform sensitivity analyses to evaluate the impact of varying ICC values.
When meta‐analysis was not feasible, we synthesised results narratively, following the SWiM (Synthesis Without Meta‐analysis) reporting guideline for outcomes that could not be pooled statistically due to heterogeneity or limited data [56]. We summarised key findings from individual studies descriptively and structured these summaries by outcome domain. We documented the rationale for not performing a meta‐analysis to ensure transparency.
Investigation of heterogeneity and subgroup analysis
We initially planned to perform subgroup analyses to explore potential effect modifiers and better understand the impact of the intervention across different populations and settings. However, all included studies were conducted in low‐ and middle‐income countries, precluding a subgroup analysis by income level (e.g. low‐ and middle‐income versus high‐income countries).
Additionally, the limited variability in participant characteristics across studies prevented meaningful subgroup analyses based on factors such as age group (e.g. adolescents versus non‐adolescents) or socioeconomic status.
We conducted subgroup analyses according to the type of antibiotic regimen, comparing trials that used a single antibiotic agent with those that used a combination regimen. These analyses were applied to all predefined core outcomes (maternal sepsis, maternal mortality, neonatal sepsis, and neonatal mortality).
To compare subgroup effects, we used interaction tests available in RevMan. These tests examined whether differences in effect estimates between subgroups showed evidence of a difference. We reported results with the Chi² statistic, P value, and interaction test I² value, which quantified the extent of heterogeneity between subgroups.
We assessed heterogeneity amongst trials using the I² statistic and the Chi² test. Substantial heterogeneity was identified when there was evidence of variability in effect estimates that could not be explained by chance alone. The I² statistic quantified the proportion of variability due to heterogeneity, while the Chi² test assessed whether observed differences between studies exceeded what would be expected by chance. When substantial heterogeneity was observed, we carefully considered its clinical implications and its impact on the interpretation of the meta‐analysis results.
A significant P value from the interaction test indicated that the subgroup effect might differ significantly across categories.
Methods for conducting subgroup analyses
Subgroup analyses were designed to address the following factors, when applicable.
Low‐ and middle‐income countries versus high‐income countries
Adolescents versus non‐adolescents
Population (low‐risk cohort versus high‐risk cohort)
Term of delivery (preterm versus full‐term)
For each subgroup, we stratified studies based on these predefined characteristics, and compared effect estimates between subgroups. We carefully interpreted the clinical and methodological relevance of the subgroup findings.
Equity‐related assessment
This review considered equity‐related factors relevant to the research question, particularly those likely to influence access to antibiotic prophylaxis and maternal health outcomes in low‐ and middle‐income countries (LMICs). We extracted and summarised available information on place of residence (country and region), socioeconomic context, and access to healthcare services as reported in the included studies. We selected these characteristics because they are known to affect health service availability, affordability, and use.
While participant‐level equity data such as education, ethnicity, or detailed socioeconomic status were not consistently available in the included trials, our analysis interpreted the findings in light of these structural inequities. This approach was intended to identify and describe contextual factors that may contribute to differences in intervention effectiveness, support equitable implementation, and inform practice and policy in LMIC settings.
Sensitivity analysis
We did not conduct any sensitivity analyses in this review, as we judged none of the included studies to be at a high risk of attrition or selection bias. Additionally, we included no cluster‐randomised trials, and therefore, no assumptions regarding ICCs were required.
However, we may conduct sensitivity analyses in future updates of this review if we include studies with higher risks of bias or cluster‐randomised trials. These analyses would investigate the robustness of the synthesised results by assessing the impact of methodological quality, the weight of individual studies, and alternative assumptions on the overall findings. Potential sensitivity analyses could include:
excluding studies at an overall high risk of bias to evaluate how their removal affects the results;
exploring the impact of clustered data from cluster‐RCTs, by exploring the range of ICC values and their influence on the effect estimates.
Future sensitivity analyses would help ensure the robustness and reliability of the conclusions, particularly in the presence of additional or diverse study designs. If we had identified any retracted studies, we planned to conduct sensitivity analyses excluding those studies to evaluate their potential impact on the review findings.
Certainty of the evidence assessment
We generated a summary of findings tables for the comparison of 'Any antibiotic versus placebo' using GRADEpro GDT software [57].
We used the GRADE approach to assess the certainty of the evidence for each of the following outcomes presented in the table [58]: maternal sepsis, maternal mortality, neonatal sepsis, neonatal mortality, wound infection (perineal), adverse effects of antibiotics: antimicrobial resistance, and neonatal intensive care unit (NICU) admission. This process involved evaluating the outcomes against five key domains: risk of bias, inconsistency, indirectness, imprecision, and publication bias. We evaluated the risk of bias by integrating the results of the RoB 2 assessments. This included considerations such as randomisation, blinding, and the completeness of outcome reporting. We assessed inconsistency by examining variability in results across studies, using statistical measures such as I² and visual inspection of forest plots. When we observed substantial heterogeneity that could not be explained, we downgraded the certainty of the evidence. We assessed indirectness by determining whether the populations, interventions, comparisons, and outcomes studied were directly relevant to the review question. We considered evidence based on indirect comparisons or surrogate outcomes as less certain. We evaluated imprecision by examining the width of confidence intervals and whether they included the null effect, particularly if they led to conflicting clinical interpretations; we prespecified an RR minimal important difference (MID) of 0.75 to 1.25 and downgraded the certainty of evidence for outcomes whose 95% CI crossed this range for imprecision. We assessed publication bias by considering potential selective outcome reporting within trials (based on the RoB 2 assessments) and by evaluating whether there was evidence of small‐study effects or missing studies. As fewer than 10 studies were included in each meta‐analysis, formal statistical tests such as funnel plots were not appropriate.
Based on the evaluation of these domains, we rated the certainty of the evidence for each outcome as high, moderate, low, or very low. High certainty indicated that further research was unlikely to change confidence in the estimate of effect, while very low certainty implied that any estimate of effect was highly uncertain. By systematically applying the GRADE framework, this review provides a transparent and robust evaluation of the certainty of the evidence, supporting evidence‐based decision‐making and identifying areas where further research is needed.
Two review authors (EO and DS), working independently, performed the assessment, resolving any disagreements through discussion. We explain all downgrading decisions in the footnotes of the summary of findings table.
Consumer involvement
This review did not involve consumers, patients, or members of the public directly in the review process. The decision not to involve consumers was due to limited resources and its specific focus on synthesising evidence from existing studies.
While no direct consumer input was incorporated, the review prioritises outcomes that are widely recognised as critical to maternal and neonatal health based on existing literature and clinical importance. In future updates, we will consider including consumers or other stakeholders to provide additional perspectives, particularly in refining outcomes, interpreting findings, or enhancing the dissemination of results to non‐academic audiences.
Results
Description of studies
Results of the search
The literature search, conducted up to 30 July 2024, yielded a total of 6678 reports. After removing duplicates, we screened 5235 titles and abstracts and excluded 5171 irrelevant reports. We screened 64 full‐text reports and trial registry reports and excluded 35 reports as they did not meet the review eligibility criteria. No records were identified through searching other sources, but we did identify and include one additional study through handsearching, following peer‐reviewer feedback. The primary reasons for exclusion are provided in Figure. We included four trials (22 reports) in this review (Oluwalana 2017 [59, 60, 61, 62, 63, 64]; Roca 2023; Subramaniam 2021; Tita 2023). Table provides a summary of the included trials (see also Supplementary material 2). The list of excluded studies is provided in Supplementary material 3. We listed two trials (three reports) as 'awaiting classification' (De Meeus 1991 [65, 66]; Swidan 2021 [67]). We identified three ongoing trials (four reports) (ISRCTN16415327 [68]; Hume‐Nixon 2022 [69, 70]; NCT06488781 [71]). The characteristics of studies awaiting classification and ongoing are shown in Supplementary material 4 and Supplementary material 5, respectively.
1.
PRISMA study flow diagram
1. Overview of included studies and synthesis table illustrating key study characteristics.
| Study name (year) country | Study design | Location/setting | Intervention details | Population (sample size: intervention/control) | Outcomes with available data (synthesis method/metric) | Definition of outcomes | Outcome time point of assessment | Method of synthesis |
Funding source, Conflicts of interest |
| Intervention type: any antibiotic prophylaxis | |||||||||
| Oluwalana 2017 | RCT | The Gambia | A single oral dose 2 g of azithromycin | Pregnant women in labour (n = 414/415) | Maternal sepsis | Prevalence of maternal sepsis, based on clinician judgement, considering low abdominal pain, dysuria, bacteriuria, offensive vaginal discharge, and specific blood and urine test results during blinded assessment, without requiring organ dysfunction criteria |
Within 56 days postpartum | MA | Joint funding from the Medical Research Council (MRC) UK and the Department for International Development (DFID) under the MRC/DFID Concordat agreement as part of the EDCTP2 program supported by the European Union (reference MR/J010391/1) The authors have indicated they have no financial relationships relevant to this article to disclose. |
| Maternal mortality | Prevalence of maternal mortality rate (death from any cause) | Within 56 days postpartum | MA | ||||||
| Neonatal sepsis | Prevalence of neonatal sepsis, defined as “predominantly due to the transmission of pathogenic bacteria during birth and early life from the mother to the offspring,” with diagnosis based on clinician judgement during blinded assessment | Within 56 days postnatal | MA | ||||||
| Neonatal mortality | Prevalence of neonatal mortality rate (death from any cause) | Within 28 days postnatal | MA | ||||||
| AMR | Proportion of bacterial isolates from maternal and neonatal nasopharyngeal, oropharyngeal, and rectal swabs showing resistance or intermediate susceptibility to azithromycin, as determined by antimicrobial susceptibility testing. Follow‐up assessments conducted at 11 to 13 months to evaluate persistence of resistance | Postpartum at 1, 4, and 8 weeks; and at 11–13 months. | Narrative | ||||||
| Mastitis or breast abscess | Clinically diagnosed mastitis, including breast abscess | Within 56 days postpartum | MA | ||||||
| Intrapartum stillbirth | Birth of a baby with no signs of life after the onset of labour, excluding cases with intrauterine foetal death confirmed before randomisation | At birth | MA | ||||||
| Roca 2023 | RCT | The Gambia and Burkina Faso | A single oral dose 2 g of azithromycin | Pregnant women in labour (n = 5991/5992) |
Maternal sepsis | Prevalence of maternal sepsis, defined as maternal hospitalisation with a sepsis diagnosis and at least one of the following within 28 days postpartum: uterine tenderness, foul‐smelling lochia, abnormal vaginal discharge, or fever; or, if no sepsis diagnosis was made at admission, the presence of at least two of these criteria. Bacterial‐confirmed postpartum sepsis was considered bacterially confirmed if bacteria were isolated from blood, cerebrospinal fluid, or a wound | Within 28 days postpartum | MA | UK Research and Innovation under the Joint Global Health Trial Scheme (JGHT; reference No. MC_EX_MR/P006949/1), Medical Research Council Unit The Gambia at the London School of Hygiene and Tropical Medicine, and the Bill & Melinda Gates Foundation (OPP1196513) Dr Nakakana reported being an employee of GlaxoSmithKline and owning shares of the company. Dr Tinto reported receiving grants from Medical Research Council that supported the achievement of the study activities in Burkina Faso during the conduct of the study. Drs Roca and D'Alessandro reported receiving grants from Joint Global Health Trial (JGHT) Scheme (Wellcome), UK Department for International Development, and the Bill & Melinda Gates Foundation during the conduct of the study. No other disclosures were reported. |
| Maternal mortality | Prevalence of maternal mortality rate (death from any cause) | Within 28 days postpartum | MA | ||||||
| Neonatal sepsis | Prevalence of neonatal sepsis rate. Roca 2023 classified neonatal sepsis into early‐onset (≤ 3 days) and late‐onset (4 to 28 days), using composite criteria: laboratory findings (e.g. positive cultures, elevated CRP, WBC count, ANC, platelet count, CSF WBC) plus clinical signs such as respiratory distress, temperature instability, feeding problems, bleeding diathesis, lethargy or irritability, and CNS symptoms | Within 28 days postnatal | MA | ||||||
| Neonatal mortality | Prevalence of neonatal mortality rate (death from any cause) | Within 28 days postnatal | MA | ||||||
| Adverse effects of antibiotics：Vomiting | Maternal adverse event, defined as vomiting reported by the mother or observed by clinical staff | Postpartum at 1, 4, and 8 weeks. | MA | ||||||
| Adverse effects of antibiotics：Pyloric stenosis | Neonatal adverse event, defined as pyloric stenosis diagnosed by a clinician | Within 8 weeks postnatal | MA | ||||||
| Mastitis or breast abscess | Breast pain, redness, tenderness and localised mass with or without fluctuance (confirmed if it is associated with a culture‐positive breast swab) | Within 28 days postpartum | MA | ||||||
| Other neonatal infection | Clinically diagnosed neonatal infections, excluding sepsis, meningitis, pneumonia, and congenital infections | Within 8 weeks postnatal | MA | ||||||
| Intrapartum stillbirth | Birth of a baby with no signs of life after the onset of labour, excluding cases with intrauterine foetal death confirmed before randomisation | At birth | MA | ||||||
| Subramaniam 2021 | RCT | Cameroon | Group 1: a single oral dose 1 g of azithromycin Group 2: a single oral dose 1 g of azithromycin + 2 g of amoxicillin |
Pregnant women at term ≧ 37 weeks of GA (n = group 1: 253, group 2: 253/250) | Maternal sepsis | Prevalence of maternal sepsis, defined according to World Health Organization criteria suspected or confirmed infection plus signs of mild‐to‐moderate organ dysfunction (tachycardia, low blood pressure, tachypnoea, altered mental status, and reduced urinary output) | Within 42 days postpartum | MA | Merck for Mothers Investigator Studies Program Grant (MISP#54628; PI: Tita) Waldemar A. Carlo reports they have been a director for Mednax. Jeff M. Szychowski reports that his institution received funding from the NIH. Alan T. Tita reports that money was paid to his institution from Pfizer Inc. The other authors did not report any potential conflicts of interest. |
| Maternal mortality | Prevalence of maternal (death from any cause) | Within 42 days postpartum | MA | ||||||
| Neonatal sepsis | Prevalence of neonatal sepsis, defined as need for sepsis work‐up, based on presence of sepsis clinical signs or symptoms (including hypothermia, fever of 38°C or higher, irritability, poor feeding, hypotonia) | Within 42 days postnatal | MA | ||||||
| Neonatal mortality | Prevalence of neonatal mortality (death due to any cause) | Within 42 days postpartum | MA | ||||||
| Wound infection | Presence of either superficial (skin or subcutaneous tissue) or deep (fascia or muscle) incisional surgical‐site infection or infection of a perineal laceration characterised by clinical diagnosis or fever, pain, erythema, and in duration around the incision or purulent discharge, including necrotising fasciitis; an outcome of abscess required radiologic or surgical confirmation | Within 42 days postpartum | MA | ||||||
| Chorioamnionitis | A fever higher than 38°C on two occasions, 30 minutes apart or 39°C or higher on one occasion, in addition to one or more of the following: foetal tachycardia above 160 beats per minute (bpm), maternal tachycardia above 100 bpm, uterine tenderness or purulent lochia before delivery, or diagnosis by a clinician | Within 42 days postpartum | MA | ||||||
| Adverse effects of antibiotics：Vomiting | Maternal adverse event, defined as vomiting reported by the mother or observed by clinical staff | Within 42 days postpartum | |||||||
| Adverse effects of antibiotics：diarrhoea | Maternal adverse event, defined as diarrhoea reported by the mother or observed by clinical staff | Within 42 days postpartum | MA | ||||||
| Endometritis | A fever higher than 38°C on two occasions 30 minutes apart or 39°C or higher on one occasion, in addition to one or more of the following: uterine tenderness or purulent lochia or diagnosis by a clinical health care professional | Within 42 days postpartum | MA | ||||||
| Mastitis or breast abscess | Maternal breast infection diagnosed clinically by a health professional, including cases with localised pain, swelling, erythema, and/or purulent discharge. | Within 42 days postpartum | MA | ||||||
| Pyelonephritis | Maternal kidney infection, diagnosed clinically by a health professional, typically based on fever, flank pain, and urinary symptoms, with or without laboratory confirmation | Within 42 days postpartum | MA | ||||||
| Intrapartum stillbirth | Birth of a baby with no signs of life after delivery | At birth | MA | ||||||
| Tita 2023 | RCT | Bangladesh Democratic Republic of the Congo Guatemala India Kenya Pakistan Zambia |
A single oral dose 2 g of azithromycin | Pregnant women at term ≥ 28 weeks of GA (n = 14590/14688) | Maternal sepsis | Prevalence of maternal sepsis, defined according to World Health Organization (WHO) criteria as suspected or confirmed infection, including fever (> 100.4°F or 38°C) or hypothermia (< 96.8°F or 36°C), plus one or more signs of organ dysfunction such as tachycardia (≥ 120 beats per minute), low systolic blood pressure (< 90 mm Hg), tachypnoea (> 24 breaths per minute), altered mental status or confusion, reduced urinary output (< 500 mL over 24 hours), jaundice, or renal failure (creatinine level > 1.2 mg/dL) | Within 42 days postpartum | MA | Eunice Kennedy Shriver National Institute of Child Health and Human Development and others; A‐PLUS ClinicalTrials.gov number, NCT03871491 All authors do not have any interests to disclose. |
| Maternal mortality | Prevalence of maternal death (death from any cause) | Within 42 days postpartum | MA | ||||||
| Neonatal sepsis | Prevalence of neonatal sepsis, defined as a proven or possible serious bacterial infection on the basis of the following WHO criteria: severe chest in‐drawing, fever (≥ 100.4°F or 38.0°C), hypothermia (< 95.9°F or 35.5°C), no movement or movement only on stimulation, poor or no feeding, convulsions, pneumonia, or meningitis | Within 28 days postnatal | MA | ||||||
| Neonatal mortality | Prevalence of neonatal mortality (death from any cause) | Within 28 days postnatal | MA | ||||||
| Wound infection | Purulent infection of a perineal wound with or without fever | Within 42 days postpartum | MA | ||||||
| Neonatal admission to special care unit | Neonatal admission to special care units | Within 42 days postnatal | Narrative | ||||||
| Adverse effects of antibiotics: vomiting | Maternal adverse event, defined as vomiting reported by the participant or observed by clinical staff | Within 42 days postpartum | MA | ||||||
| Adverse effects of antibiotics: diarrhoea | Maternal adverse event, defined as diarrhoea reported by the participant or observed by clinical staff | Within 42 days postpartum | MA | ||||||
| Adverse effects of antibiotics: pyloric stenosis | Neonatal adverse event, defined as a clinical diagnosis of hypertrophic pyloric stenosis, typically confirmed by physical examination and/or imaging (e.g., ultrasound) | Within 42 days postnatal | MA | ||||||
| Chorioamnionitis | Fever (> 100.4°F/38°C) in addition to one or more of the following: foetal tachycardia ≥ 160 bpm, maternal tachycardia > 100 bpm, tender uterus between contractions, or purulent/foul smelling discharge from uterus prior to delivery | From randomisation to date/time of delivery | MA | ||||||
| Endometritis | Fever (> 100.4°F/38°C) in addition to one or more of maternal tachycardia > 100 bpm, tender uterine fundus, or purulent/foul smelling discharge from uterus after delivery | Within 42 days postpartum | MA | ||||||
| Mastitis or breast abscess | Fever > 100.4°F/38°C and one or more of the following: breast pain, swelling, warmth, redness, or purulent drainage | Within 42 days postpartum | MA | ||||||
| Pyelonephritis | Fever > 100.4°F/38°C and one or more of the following: urinalysis/dip suggestive of infection, costovertebral angle tenderness, or confirmatory urine culture | Within 42 days postpartum | MA | ||||||
| Other neonatal infection | Neonatal infection other than sepsis, meningitis, pneumonia, or congenital infection, diagnosed clinically by a health professional | Within 42 days postnatal | MA | ||||||
| Stillbirth | Birth of a baby with no signs of life after 24 weeks’ gestation, including both antepartum and intrapartum deaths | At birth | MA | ||||||
AMR: antimicrobial resistance; ANC: absolute neutrophil count; CNS: central nervous system; CRP: C‐reactive protein; CSF: cerebrospinal fluid; GA: gestational age; MA: meta‐analysis of standardised effect sizes, n: number; RCT: randomised controlled trial; WBC: white blood cell; WHO: World Health Organization
Included studies
We included four trials in the review (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023).
Study design
Three trials were two‐arm trials, which were assessed as individually‐randomised, placebo‐controlled trials using parallel groups (Oluwalana 2017; Roca 2023; Tita 2023). Subramaniam 2021 was a three‐arm, individually‐randomised, placebo‐controlled trial using parallel groups.
Sample size
The total sample size was 42,846 participants (intervention group: 21,501, control group: 21,345).
Location/setting
The trials were conducted in 10 countries, all low‐ and middle‐income countries (LMICs): Bangladesh, Burkina Faso, Cameroon, the Democratic Republic of Congo, The Gambia, Guatemala, India, Kenya, Zambia, and Pakistan.
Oluwalana 2017 was undertaken at the Jammeh Foundation for Peace (JFP), a government‐run health centre. Roca 2023 was conducted at two government health facilities located in periurban areas close to the capital and eight peripheral health facilities in rural districts. Subramaniam 2021 was undertaken in six centres within the Cameroon Baptist Convention Health Services. Tita 2023 was conducted at eight sites in seven low‐ or middle‐income countries of the Global Network for Women’s and Children’s Health Research of the Eunice Kennedy Shriver National Institute of Child Health and Human Development (NICHD).
Funding and declarations of interest
All trials addressed funding sources and provided information about the research grant or company funding the trials (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). Oluwalana 2017 stated: "All phases of this study were supported by joint funding from the Medical Research Council (MRC) UK and the Department for International Development (DFID) under the MRC/DFID Concordat agreement as part of the EDCTP2 program supported by the European Union (reference MR/J010391/1)." Roca 2023 stated: "The trial was funded by a grant from UK Research and Innovation under the Joint Global Health Trial Scheme (JGHT; reference No. MC_EX_MR/P006949/1), Medical Research Council Unit The Gambia at the London School of Hygiene and Tropical Medicine, and the Bill & Melinda Gates Foundation (OPP1196513)." Subramaniam 2021 stated that: "Waldemar A. Carlo reports they have been a director for Mednax. Jeff M. Szychowski reports that his institution received funding from the NIH. Alan T. Tita reports that money was paid to his institution from Pfizer Inc. The other authors did not report any potential conflicts of interest." Tita 2023 stated that all authors did not have any interests to disclose at that time in the disclosure forms.
Population
All trials targeted pregnant women; we did not find studies in which only a subset of the intended participants were enroled. Although three studies targeted the general population (Oluwalana 2017; Roca 2023; Tita 2023), Tita 2023 included both women with prolonged labour and those with prolonged rupture of membranes (azithromycin group: 1247 pregnant women, placebo group: 1283 pregnant women). Subramaniam 2021 included women with singleton or twin pregnancies at term (≥ 37 weeks' gestation) who were admitted to the hospital for vaginal birth and experienced either prolonged labour (≥ 18 hours) or prolonged rupture of membranes (≥ 8 hours).
Oluwalana 2017 reported that the median age and interquartile range (IQR) were 26.0 (22.0 to 30.0) years in the azithromycin group and 25.0 (22.0 to 30.0) years in the placebo group. Roca 2023 reported that the median age and IQR were 27.0 (22.0 to 31.0) years in the azithromycin group and 26.0 (22.0 to 31.0) years in the placebo group. While Subramaniam 2021 did not specify age‐related inclusion criteria, the mean ages and SD in the 1 g azithromycin, 1 g azithromycin plus 2 g amoxicillin, and placebo groups were 27.2 ± 5.3, 26.4 ± 5.6, and 26.0 ± 5.3 years, respectively. Tita 2023 reported that the median age and IQR were 24.0 (21.0 to 28.0) years in the azithromycin group and 24.0 (21.0 to 28.0) years in the placebo group.
Oluwalana 2017 and Roca 2023 did not specify gestational age; however, both trials described trial participants as pregnant women in labour. Oluwalana 2017 stated that the median gestational age at enrolment was 36 weeks for both the intervention group and the placebo group. Roca 2023 did not report gestational age. However, over 99% of babies in both arms had a birth weight of 1.5 kg or above, which we judged as over 28 weeks of gestation. Subramaniam 2021 included pregnant women at or above 37 weeks' gestation in labour, and Tita 2023 included pregnant women in labour at or above 28 weeks' gestation.
Trials reported on some other characteristics that could potentially affect the interpretation and generalisability of the review findings. While these trials recruited women in whom a vaginal birth was planned (and excluded those with a planned caesarean section), some participants nonetheless underwent an intrapartum caesarean section. However, this was a small proportion overall (10.3% of participants in the intervention arm and 10.4% in the placebo arm). Randomisation was maintained in both groups, and all participants—including those who underwent intrapartum caesarean sections in all included studies—were analysed according to their originally assigned groups. The analysis was therefore conducted based on the intention‐to‐treat principle. Tita 2023 reported the proportion of intrapartum caesarean sections: 2.4% of participants in the intervention group and 1.2% in the control group underwent intrapartum caesarean delivery after randomisation, and all were analysed in their originally assigned groups. Similarly, women with multiple pregnancies were eligible in four trials, and accounted for 1.1% of participants in the intervention arm and 0.9% in the placebo arm. Additionally, two trials reported that approximately one‐third of participants gave birth during seasons with a high infection risk (34.3% overall in Oluwalana 2017 and 34.8% overall in Roca 2023). The other two trials reported the proportion of women who experienced more than one episode of infection during the study period (10.6% overall in Subramaniam 2021 and 5.5% overall in Tita 2023).
Intervention and comparator
Details of the intervention, background treatments, and treatment durations for each of the included trials are summarised in Table.
All trials used a single dose of oral antibiotics in labour (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). Three trials compared a 2‐g azithromycin group with a placebo group (Oluwalana 2017; Roca 2023; Tita 2023), and one trial had three arms: 1 g azithromycin, 1 g azithromycin plus 2 g amoxicillin, and placebo (Subramaniam 2021). For analysis, we combined the two active arms of Subramaniam 2021 into a single group (azithromycin only, or azithromycin plus amoxicillin) compared to placebo.
All trials compared systemic antibiotics to placebo.
Outcomes
All four studies measured all our critical outcomes and at least one of our important outcomes, with variations in definitions and assessment time points across studies. Details of outcome definitions and assessment time points by study are summarised in Table (Overview of included studies and synthesis table illustrating key study characteristics). Below, we summarise the definitions used by the included studies for our key outcomes of interest (i.e. those reported in the summary of findings table).
Maternal sepsis was defined variably. Tita 2023 and Subramaniam 2021 used WHO criteria, requiring suspected or confirmed infection including fever (> 100.4°F or 38 °C) or hypothermia (< 96.8°F or 36 °C) plus at least one sign of organ dysfunction (e.g. tachycardia ≥ 120 beats per minute, low systolic blood pressure < 90 mm Hg, tachypnoea > 24/minute, altered mental status or confusion, reduced urinary output < 500 mL/24 hours, jaundice, renal failure with creatinine > 1.2 mg/dL). Assessment was up to 42 days postpartum. In contrast, Oluwalana 2017 defined puerperal sepsis based on clinician judgement, considering low abdominal pain, dysuria, bacteriuria, offensive vaginal discharge, and specific blood and urine test results during blinded assessment, without requiring organ dysfunction criteria, assessed within 56 days postpartum. Roca 2023 defined postpartum sepsis as maternal hospitalisation with a sepsis diagnosis and at least one of the following within 28 days postpartum: uterine tenderness, foul‐smelling lochia, abnormal vaginal discharge, or fever; or, if no sepsis diagnosis was made at admission, the presence of at least two of these criteria. Bacterial‐confirmed postpartum sepsis was considered bacterially confirmed if bacteria were isolated from blood, cerebrospinal fluid, or a wound.
Maternal mortality was defined consistently as death from any cause, with minor differences in time frames. Tita 2023 and Subramaniam 2021 assessed deaths within 42 days postpartum, aligning with WHO recommendations. Oluwalana 2017 used a longer window, recording deaths within 56 days postpartum. Roca 2023 assessed deaths within 28 days postpartum.
Neonatal sepsis definitions showed notable variation. Tita 2023 used WHO criteria for proven or possible serious bacterial infection, including severe chest in‐drawing, fever (≥ 100.4°F or 38.0 °C), hypothermia (< 95.9°F or 35.5 °C), no movement or movement only on stimulation, poor or no feeding, convulsions, pneumonia, or meningitis, assessed within 28 days after birth. Subramaniam 2021 defined neonatal sepsis as suspected or confirmed neonatal sepsis requiring sepsis work‐up, based on clinical signs such as hypothermia, fever, irritability, poor feeding, and hypotonia, assessed within 42 days after birth. Roca 2023 classified neonatal sepsis into early‐onset (≤ 3 days) and late‐onset (4 to 28 days), using composite criteria: laboratory findings (e.g. positive cultures, elevated C‐reactive protein, white blood cell count, absolute neutrophil count, platelet count, cerebrospinal fluid white blood cell count) plus clinical signs such as respiratory distress, temperature instability, feeding problems, bleeding diathesis, lethargy or irritability, and central nervous system symptoms. Oluwalana 2017 defined neonatal sepsis as “predominantly due to the transmission of pathogenic bacteria during birth and early life from the mother to the offspring,” with diagnosis based on clinician judgement during blinded assessment, assessed within 56 days after birth.
Neonatal mortality was generally defined as death from any cause within 28 to 56 days of life. Tita 2023, Subramaniam 2021, and Oluwalana 2017 assessed deaths up to 28 to 56 days postpartum, while Roca 2023 defined neonatal mortality as death within 28 days of life but excluded deaths due to severe birth asphyxia, very low birth weight (< 1.5 kg), or major congenital malformations.
Perineal wound infection definitions also differed. Only Tita 2023 explicitly reported perineal wound infection, defined as a purulent infection of a perineal wound with or without fever, assessed within 42 days postpartum. Subramaniam 2021 did not report perineal wound infection; instead, it reported 'any wound infection', a composite outcome including perineal laceration infection, caesarean section wound infection, and episiotomy infection. Perineal laceration infection was defined as a clinical diagnosis of infection in a perineal laceration (including fever, pain, erythema, induration, or purulent discharge, with abscesses confirmed radiologically or surgically), also assessed within 42 days postpartum.
Antimicrobial resistance (AMR) was assessed in Oluwalana 2017 using microbiological cultures from maternal and neonatal nasal swabs, breast milk, and vaginal swabs. Resistance was defined according to local laboratory susceptibility testing, with sampling generally performed within 28 days postpartum or after birth, and follow‐up assessments conducted at 11 to 13 months to evaluate the persistence of resistance.
NICU admission was reported only in Tita 2023, defined as any admission to a neonatal intensive or special care unit within 42 days after birth. Detailed admission criteria were not consistently specified in the trial report.
Excluded studies
During the full‐text screening, we excluded 35 articles. Of these, we listed the following three trials in Supplementary material 3: Discoll 2023 [72]; Kampikaho 1993 [73]; and Nabhan 2014 [74]. We excluded:
Discoll 2023, due to an ineligible intervention: antibiotics were administered during pregnancy, which is a different intervention from the one evaluated in this review;
Kampikaho 1993, due to an ineligible study design; and
Nabhan 2014, due to an ineligible population: participants were pre‐labour.
Risk of bias in included studies
We used Cochrane's risk of bias assessment tool 2.0 to assess the risk of bias for each trial outcome [35].
We assessed the risk of bias for all outcomes in the summary of findings table, including adverse effects of antibiotics (antimicrobial resistance (AMR)), which were reported narratively and assessed at the study level (Supplementary material 6). We considered three trials to be at an overall low risk of bias for all outcomes except adverse effects (Roca 2023; Subramaniam 2021; Tita 2023). We rated Oluwalana 2017as having an overall risk of bias of 'some concerns' due to reporting bias (risk of bias in the selection of reported outcomes). Regarding adverse effects of antibiotics (including AMR), we judged Oluwalana 2017 to have a high risk of bias, based on post hoc subgroup analyses (Domain 1: bias arising from the randomisation process), incomplete sampling frames leading to missing outcome data (Domain 3), variability in measurement methods (Domain 4), and selective reporting (Domain 5).
Synthesis of results
All synthesised results and the summary of findings table are shown in Supplementary material 7 and Table, respectively.
We initially planned to conduct subgroup analyses based on country income level (low‐ and middle‐income countries versus high‐income countries), maternal age (adolescents versus non‐adolescents), population risk (low‐risk versus high‐risk cohorts), and timing of delivery (preterm versus full‐term). However, we did not perform these analyses due to the limited number of included studies. Nonetheless, as the included studies involved two types of prophylactic regimens — azithromycin monotherapy and a combination of azithromycin and amoxicillin (any antibiotic) — we conducted a subgroup analysis to compare the effects of these two regimens.
Any antibiotic versus placebo
Critical maternal outcomes
Incidence of maternal sepsis (within 28 to 56 days postpartum)
Four trials evaluated the effect of antibiotic prophylaxis in labour on maternal sepsis (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled analysis showed moderate‐certainty evidence of a likely reduction in maternal sepsis with antibiotic prophylaxis use in labour (RR 0.65, 95% CI 0.56 to 0.77; I² = 0%; 4 studies, 42430 participants; moderate‐certainty evidence; Figure; Analysis 1.1).
2.
Any antibiotic versus placebo, outcome 1.1: maternal sepsis
Incidence of maternal sepsis: subgroup analysis (polypharmacy versus monopharmacy, within 28 to 56 days postpartum)
We also conducted a subgroup analysis comparing polypharmacy regimens (azithromycin plus amoxicillin) to monotherapy (azithromycin alone). There was no evidence of a difference between subgroups (Chi² = 1.09, degrees of freedom (df) = 1, P = 0.30; I² = 8.3%). The pooled estimate for maternal sepsis in this subgroup comparison was RR 0.66, 95% CI 0.56 to 0.78; I² = 0%; 4 studies, 42430 participants; Analysis 1.2).
Incidence of maternal mortality (within 28 to 56 days postpartum)
Four trials assessed the effects of antibiotic prophylaxis in labour on maternal mortality (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled meta‐analysis showed that antibiotics likely result in little to no difference in maternal mortality compared to placebo (RR 1.21, 95% CI 0.63 to 2.33; I² = 0%; 4 studies, 42371 participants; moderate‐certainty evidence; Figure; Analysis 1.3).
3.
Any antibiotic versus placebo, outcome 1.3: maternal mortality
Incidence of maternal mortality: subgroup analysis (polypharmacy versus monotherapy, within 28 to 56 days postpartum)
A subgroup analysis compared polypharmacy regimens (azithromycin plus amoxicillin) to monotherapy (azithromycin alone). There was no evidence of a difference between subgroups (Chi² = 1.52, df = 1, P = 0.22; I² = 34.0%). The pooled estimate for this subgroup comparison was RR 1.18, 95% CI 0.62 to 2.25; I² = 0%; 4 studies, 42371 participants; Analysis 1.4).
Critical neonatal outcomes
Neonatal sepsis (within 28 to 56 days after birth)
Four trials assessed the effect of azithromycin use in labour on neonatal sepsis (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled meta‐analysis showed that antibiotics result in little to no difference in neonatal sepsis compared to placebo (RR 1.03, 95% CI 0.96 to 1.10; I² = 0%; 4 studies, 42,872 participants; high‐certainty evidence; Figure; Analysis 1.5).
4.
Any antibiotic versus placebo, outcome 1.5: neonatal sepsis
Neonatal sepsis: subgroup analysis (polypharmacy versus monotherapy, within 28 to 56 days after birth)
A subgroup analysis compared polypharmacy regimens (azithromycin plus amoxicillin) to monotherapy (azithromycin alone). There was evidence of little to no difference between subgroups (Chi² = 0.15, df = 1, P = 0.70; I² = 0%). The pooled estimate for this subgroup comparison was RR 1.02, 95% CI 0.96 to 1.10; I² = 0%; 4 studies, 42,872 participants; Analysis 1.6).
Neonatal mortality (within 28 to 56 days after birth)
Four trials assessed the effect of azithromycin use in labour on neonatal mortality (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled meta‐analysis showed that antibiotics result in little to no difference in neonatal mortality compared to placebo (RR 1.03, 95% CI 0.87 to 1.21; I² = 0%; 4 studies, 42,935 participants; high‐certainty evidence; Figure; Analysis 1.7).
5.
Any antibiotic versus placebo, outcome 1.7: neonatal mortality
Neonatal mortality: subgroup analysis (polypharmacy versus monotherapy, within 28 to 56 days after birth)
A subgroup analysis compared polypharmacy regimens (azithromycin plus amoxicillin) to monotherapy (azithromycin alone) for neonatal mortality within 28 to 56 days after birth. There was no evidence of a difference between subgroups (Chi² = 0.68, df = 1, P = 0.41; I² = 0%). The pooled estimate for this subgroup comparison was RR 1.02, 95% CI 0.86 to 1.20; I² = 0%; 4 studies, 42,935 participants; Analysis 1.8.
Important outcomes
Incidence of any wound infection or perineal wound infection (within 28 to 56 days postpartum)
Two studies reported on maternal wound infection (Subramaniam 2021; Tita 2023). However, we could not combine the data in a meta‐analysis because the definitions of wound infection differed between the studies.
Subramaniam 2021 reported any maternal wound infection, defined as the presence of at least one of the following: perineal laceration infection, abdominal wound infection, or episiotomy site infection. There was a reduction in any maternal wound infection with the use of any antibiotic prophylaxis in labour compared to placebo (RR 0.35, 95% 0.13 to 0.90; 1 study, 756 participants; Analysis 1.9).
Tita 2023 was the only trial that reported perineal wound infection (25,114 participants). At 28 to 56 days postpartum, 1.0% of women in the antibiotic group versus 1.5% in the placebo group developed a wound infection (RR 0.80, 95% 0.64 to 0.99; 1 study, 25,114 participants; high‐certainty evidence; Figure; Analysis 1.10). This effect size indicates little to no difference in perineal wound infection between groups.
6.
Any antibiotic versus placebo, outcome 1.10.: other maternal infections: wound infection (perineal)
Adverse effects of antibiotics (including antimicrobial resistance)
Antimicrobial resistance
One individually randomised, placebo‐controlled trial provided very low‐certainty evidence on antimicrobial resistance (AMR) via multiple publications from the same Gambian RCT (Oluwalana 2017): a post hoc resistance analysis [75], a short‐term microbiological carriage report up to day 28 [76], and a 12‐month follow‐up [77]. Methods and sampling frames differed across reports, thus results were not pooled, but are summarised below.
Jagne and colleagues detected azithromycin‐resistant Streptococcus pyogenes (GAS) isolates at comparable rates across nasopharyngeal carriage, breastmilk carriage, and newborns’ nasopharyngeal swabs in both trial arms [75]. However, vaginal samples showed a higher prevalence of resistance in the intervention arm compared to the placebo arm (1.99% versus 0.28%, P = 0.035; very low‐certainty evidence). Amongst newborns, only two resistant isolates were identified, one in each trial arm, suggesting minimal, if any, differences in the presence of antibiotic‐resistant strains in neonatal samples.
In the article by Roca and colleagues [76], bacterial carriage was lower in the intervention arm for newborns and women. For example, amongst newborns in the azithromycin group, there was lower bacterial carriage in nasopharynx samples at day 6, with a prevalence of 28.3% compared to 65.1% in the placebo group (prevalence ratio (PR) = 0.43; P < 0.001; very low‐certainty evidence). Similarly, mothers in the azithromycin group showed reduced bacterial carriage across all sample types. Notably, on day 6, Streptococcus pneumoniae carriage was almost eliminated (PR = 0.08), and by day 28, Staphylococcus aureus carriage was also reduced (PR = 0.57). Post‐intervention analysis of breast milk revealed that bacterial carriage was lower in the azithromycin group (9.6% versus 21.9%; PR = 0.44; P < 0.004; very low‐certainty evidence). Vaginal samples also showed a reduction in bacterial carriage (13.2% versus 24.2%; PR = 0.55; P < 0.001), with S. pneumoniae notably absent from these samples.
However, across all sample types, azithromycin‐resistant bacteria, particularly S. aureus, were more common in the azithromycin group. Bacterial carriage of S. aureus at day 6 of a nasopharyngeal swab from newborns was 63.3% in placebo versus 27.5% in azithromycin (PR = 0.43, 95% CI 0.36 to 0.52; P < 0.001); a nasopharyngeal swab from mothers was 27.2% in placebo versus 7.8% in azithromycin (PR = 0.29, 95% CI 0.20 to 0.42; P < 0.001); breast milk was 16.4% in placebo versus 8.1% in azithromycin (PR = 0.49, 95% CI 0.33 to 0.74; P < 0.001); and vaginal swab was 14.1% in placebo versus 8.9% in azithromycin (PR = 0.63, 95% CI 0.42 to 0.94; P = 0.026). Sensitivity analyses confirmed the consistency of these findings, even in mothers treated less than two hours before birth. For this subpopulation, newborn nasopharyngeal carriage at day 6 was markedly lower in the azithromycin group than the placebo group (35.5% versus 67.5%; PR = 0.53; P < 0.001). These sensitivity analyses were conducted by the original study authors, not by the review authors, and therefore the underlying data are not presented in this review.
Bojang 2018 [77]— a 12‐month follow‐up of the same Gambian RCT — collected nasopharyngeal swabs from 461 infants aged 11 to 13 months and found similar carriage between arms for Streptococcus pneumoniae (85.0% versus 82.1%; odds ratio (OR) 1.23, 95% CI 0.73 to 2.08) and Staphylococcus aureus (21.7% versus 21.3%; OR 1.02, 95% CI 0.64 to 1.64). Prevalence of azithromycin resistance was also similar between arms for S. pneumoniae (1.8% versus 0.9%; OR 2.10, 95% CI 0.30 to 23.38) and S. aureus (3.1% versus 2.6%; OR 1.22, 95% CI 0.35 to 4.47). Taken together with the short‐term findings, these data suggest that any early increase in azithromycin‐resistant organisms did not persist at 12 months.
Side effects of antibiotics
Oluwalana 2017 did not report antibiotic‐related adverse effects. Tita 2023 reported on side effects such as nausea, vomiting and diarrhoea, allergic symptoms such as anaphylaxis, liver failure, arrhythmias, and infant pyloric stenosis. Up to 7.1% of participants reported at least one side effect in the prophylaxis group compared to 7.6% in the placebo group (RR 0.93, 95% CI 0.86 to 1.02; 2143 participants). Subramaniam 2021 reported side effects such as vomiting (1.2%, n = 3 in the placebo group; 1.6%, n = 4 in the azithromycin group; 0% in any antibiotic group), diarrhoea (0% in the placebo group; 0.4%, n = 1 in the azithromycin group; 0% in any antibiotic group), intravenous injection site pain (0% in the placebo group; 0% in the azithromycin group; 0.4%, n = 1 in any antibiotic group), allergic reaction (0% in the placebo group; 0% in the azithromycin group; 0.4%, n = 1 in any antibiotic group), and hypertension (0% in the placebo group; 0.8%, n = 2 in the azithromycin group; 0% in any antibiotic group). Roca 2023 reported side effects such as pelvic pain (31.2%, n = 1809 in the azithromycin group; 31.2%, n = 1814 in the placebo group), vomiting (10.1%, n = 587 in the azithromycin group; 6.1%, n = 358 in the placebo group), dizziness (4.4%, n = 255 in the azithromycin group; 5.3%, n = 307 in the placebo group), oedema (4.2%, n = 245 in the azithromycin group; 3.2%, n = 184 in the placebo group), cough (1.5%, n = 86 in the azithromycin group; 1.4%, n = 82 in the placebo group), and reported fever (0.8%, n = 49 in the azithromycin group; 1.3%, n = 73 in the placebo group).
Three trials assessed the effect of any antibiotic prophylaxis on adverse effects of antibiotics (Roca 2023; Subramaniam 2021; Tita 2023). The pooled estimates showed there no clear evidence of a difference between any antibiotic prophylaxis during pregnancy and vomiting (RR 1.31, 95% CI 0.92 to 1.88; I² = 86%; 3 studies, 41657 participants; Analysis 1.11) or diarrhoea (RR 1.16, 95% CI 0.84 to 1.61; I² = 0%; 2 studies, 30032 participants; Analysis 1.12).
Two studies reported on pyloric stenosis as a side effect of antibiotics (Roca 2023; Tita 2023). There was no clear evidence of a difference between any antibiotic prophylaxis in labour and pyloric stenosis (RR 2.43, 95% CI 0.69 to 8.52; I² = 0%; 2 studies; 41,059 participants; Analysis 1.13).
NICU admission (within 28 to 56 days after birth)
Tita 2023 reported this outcome. Compared to placebo, azithromycin prophylaxis makes little to no difference in NICU admission (RR 1.03, 95% CI 0.94 to 1.12; I² not applicable; 1 study, 29,084 infants; high‐certainty evidence; Figure; Analysis 1.14).
7.
Any antibiotic versus placebo, outcome 1.14.: NICU admission
Footnotes NICU: neonatal intensive care unit.
Other maternal infections
Chorioamnionitis
Two trials assessed the effect of antibiotic prophylaxis on chorioamnionitis (Subramaniam 2021; Tita 2023). The pooled estimates showed evidence of a reduction in chorioamnionitis with antibiotic prophylaxis use in labour (RR 0.41, 95% CI 0.18 to 0.92; I² = 21%; 2 studies, 30034 participants; Analysis 1.15).
Endometritis
Two trials evaluated the effect of antibiotic prophylaxis in labour on endometritis (Subramaniam 2021; Tita 2023). The pooled analysis indicated evidence of a reduction in endometritis with any antibiotic (RR 0.66, 95% CI 0.55 to 0.78; I² = 0%; 2 studies, 29973 participants; Analysis 1.16).
Mastitis or breast abscess
Four trials evaluated the effect of any antibiotic prophylaxis on mastitis or breast abscess (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled results showed evidence of a reduction in mastitis or breast abscess with the use of any antibiotic prophylaxis in labour (RR 0.57, 95% CI 0.40 to 0.80; I² = 10%; 4 studies, 42423 participants; Analysis 1.17).
Pyelonephritis
Two trials reported on maternal pyelonephritis (Subramaniam 2021; Tita 2023). The pooled estimates showed evidence of a reduction in pyelonephritis with the use of any antibiotic prophylaxis in labour (RR 0.32, 95% CI 0.15 to 0.70; I² = 22%; 2 studies, 29969 participants; Analysis 1.18).
Clostridioides difficile colitis
No trials reported this outcome.
Other neonatal infections
Two studies reported this outcome (Roca 2023; Tita 2023). Oluwalana 2017 reported data for ‘other neonatal infections’ (RR 0.76, 95% CI 0.58 to 0.99; P = 0.052 for overall infections), but since sepsis was included in these events, it was excluded from the pooled analysis. There was no clear evidence of effects of any antibiotic prophylaxis during labour on other neonatal infections (RR 0.82, 95% CI 0.59 to 1.14; I² = 90%; 2 studies, 41013 participants; Analysis 1.19). Other infections included eye infection with swelling and drainage, skin infection, omphalitis, urinary tract infection, pyelonephritis or kidney infection, pneumonia or lung infection, meningitis, umbilical infection, conjunctivitis, otitis, oral infection, meningitis, and other infections that had been documented in the clinical record [45, 59].
Cost of care
One study conducted a cost‐effective analysis (Tita 2023). In this cost‐effectiveness analysis, intrapartum azithromycin was associated with the prevention of 1592.0 cases (95% CI 1139.7 to 2024.1) of maternal infection, sepsis, or death per 100,000 pregnancies. This translated to averting 248.5 facility readmissions (95% CI 95.3 to 403.7), 866.8 unplanned clinic visits (95% CI 537.8 to 1193.2), and 1816.2 antibiotic regimens (95% CI 1324.5 to 2299.7) per 100,000 pregnancies. Using mean health‐care costs across the A‐PLUS sites, intrapartum azithromycin resulted in net savings of USD (US dollars) 32,661 (95% CI –52,218 to 118,210) per 100,000 pregnancies and averted 13.2 disability‐adjusted life‐years (DALYs) (95% CI 8.3 to 17.9). Sensitivity analyses indicated that the cost of facility readmission, the price of azithromycin, and the probability of infection had the greatest impact on incremental cost. Overall, the intervention was cost‐saving in most model simulations, with 75% of results showing net savings and an additional 17% being cost‐effective (< USD 29,541 per DALY averted, equivalent to 1.0 times gross domestic product (GDP) per capita) across 100,000 simulations. These findings demonstrate that intrapartum azithromycin is generally a cost‐saving intervention for the prevention of maternal infection, sepsis, or death in low‐ and middle‐income countries, supporting its consideration as an economically efficient preventive therapy in these settings. These sensitivity analyses were conducted by the original study authors, not by the review authors, and therefore the underlying data are not presented in this review.
Maternal satisfaction
No trials reported this outcome.
Intrapartum stillbirth
Four trials reported on intrapartum stillbirth (Oluwalana 2017; Roca 2023; Subramaniam 2021; Tita 2023). The pooled analysis showed no clear evidence of a difference in this outcome between groups (RR 1.11, 95% CI 0.85 to 1.44; I² = 0%; 4 studies; Analysis 1.20).
Equity assessment
All included trials were conducted in low‐ and middle‐income countries (LMICs); specifically, Bangladesh, Burkina Faso, Cameroon, the Democratic Republic of Congo, The Gambia, Guatemala, India, Kenya, Pakistan, and Zambia. This provides important evidence from LMIC settings, where infectious disease risk is typically higher. However, the geographic distribution of these studies was limited to certain countries and regions, which may affect the generalisability of the findings to all LMIC contexts.
None of the studies reported results disaggregated by equity‐related characteristics such as socioeconomic status, education level, ethnicity, disability, or migrant status. No subgroup analyses were performed for adolescents or for women with limited access to antenatal care.
Overall, there is a gap in evidence regarding potential differences in effects across social or demographic groups, which limits conclusions about equity impacts. All participants were biological females anticipating vaginal births.
Reporting biases
Due to the small number of included studies, we did not perform funnel plot analysis to assess publication bias.
Discussion
Summary of main results
All four trials (42,846 participants) included in this review were conducted in low‐ and middle‐income countries. Most women in the prophylaxis group (50.2%) received a single oral dose of 1 g or 2 g of azithromycin.
Maternal outcomes
Antibiotic prophylaxis given in labour after 28 weeks’ gestation or longer probably reduces maternal sepsis (moderate‐certainty evidence) and likely results in little to no difference in maternal mortality (moderate‐certainty evidence). Perineal wound infection decreased by only 0.5 percentage points with prophylaxis, suggesting that antibiotic prophylaxis makes little to no difference to the outcome (high‐certainty evidence).
Neonatal outcomes
High‐certainty evidence shows little or no difference between antibiotic prophylaxis and placebo for neonatal sepsis, neonatal mortality, and NICU admission.
Antimicrobial resistance (AMR) and other adverse effects
The evidence was very uncertain: short‐term increases in resistance were observed in some maternal samples, but follow‐up to 11 to 13 months showed no persistent differences. In neonates, AMR was rare (very low‐certainty evidence).
Overall, although single‐dose intrapartum antibiotics may confer a modest reduction in maternal sepsis, their effect on other key outcomes is negligible, and AMR consequences remain unclear. Clean birth practices and quality obstetric care remain the cornerstone of infection prevention.
Limitations of the evidence included in the review
Four studies were included in the review, all reporting results for the critical outcomes.
All studies were individually randomised trials with a placebo arm, and all were assessed as low risk of bias overall except for one study [59]. For Oluwalana 2017, there were some concerns about reporting bias, and we rated the overall risk of bias as 'some concerns'.
Of the four studies, Tita 2023 had over 14,000 participants and Roca 2023 had approximately 5800 participants, meaning their findings dominated pooled analyses. All four trials used prophylactic azithromycin, and Subramaniam 2021 included a combination arm with azithromycin and amoxicillin. All included trials were analysed according to the intention‐to‐treat principle, whereby participants were evaluated in the groups to which they were originally randomised, regardless of subsequent changes in the mode of delivery. In one of the included studies that reported mode of delivery, a small proportion of participants underwent intrapartum caesarean section despite planned vaginal delivery. These cases remained in their originally allocated groups, thereby preserving the benefits of randomisation. Although such deviations from planned delivery could influence clinical outcomes, the low frequency of intrapartum caesarean sections limited the potential for bias in the meta‐analysis. Nonetheless, future studies may consider stratified analyses to evaluate the effects of mode of delivery on intervention outcomes.
The meta‐analysis showed that any antibiotic prophylaxis reduced the risk of chorioamnionitis, whereas azithromycin alone showed little to no difference compared to placebo. Currently, there are insufficient data on the effects of antibiotic prophylaxis on antimicrobial resistance (AMR). Jagne and colleagues have shown that Group A Streptococcus (GAS) resistance was more common in vaginal samples from women in an azithromycin‐treated group [63]. Roca and colleagues detected azithromycin‐resistant Staphylococcus aureus in maternal and newborn nasal swabs and breast milk [64]. Although the evaluation methods were different and could not be combined, azithromycin resistance appeared to be higher in the intervention group within 28 days of the intervention. This likely reflects the selection of pre‐existing resistant strains due to the suppression of susceptible bacteria by azithromycin, rather than the induction of resistance (i.e. the emergence of new resistance traits due to genetic changes induced by azithromycin). More broadly, all four trials were conducted in low‐ and middle‐income countries, primarily in Africa and South Asia; antimicrobial resistance profiles may vary somewhat across these countries, and differ from those in high‐income countries. We also anticipate that azithromycin use (and azithromycin resistance) varies across settings. Therefore, the observed benefits might be context‐specific, potentially influenced by the local prevalence of azithromycin‐susceptible pathogens. Consequently, caution is advised in generalising the available evidence to other settings. Taken together, we could not assess how this intervention might affect AMR over the longer term. Further, the prevalence of maternal and neonatal sepsis remains particularly high in regions such as sub‐Saharan Africa [78, 79]. This high baseline risk underscores the potential impact of effective prophylactic strategies and highlights the applicability of results from reviews like ours to these high‐burden settings.
The certainty of evidence varied across outcomes, reflecting specific limitations identified through the GRADE approach. We used a prespecified range of RR 0.75 to 1.25 as the minimally important difference (MID) threshold when assessing imprecision, downgrading if confidence intervals crossed this range. We rated maternal sepsis as moderate‐certainty evidence. We downgraded one level for indirectness because two trials defined sepsis using broad signs of infection (e.g. fever or clinical diagnosis), rather than the WHO definition, which requires evidence of organ dysfunction resulting from infection, accounting for 8.8% of the pooled effect. We also rated maternal mortality as moderate‐certainty evidence, downgrading by one level for imprecision because the confidence interval was wide and crossed the prespecified MID range. We rated wound infection (perineal) as high‐certainty evidence, with consistent results across studies and no serious limitations identified.
For adverse effects of antibiotics, including antimicrobial resistance (AMR), we rated the certainty of the evidence as very low due to multiple serious concerns. Only two trials reported on AMR, using different methods, sample types, and target organisms, introducing substantial heterogeneity and inconsistency. Data were derived from subgroups rather than full trial populations, with very small numbers of resistant isolates, leading to serious imprecision. There was also a high risk of bias, with post hoc analyses and selective reporting. These limitations prevented meta‐analysis, and because of the heterogeneity and narrative synthesis, the prespecified MID threshold could not be meaningfully applied to assess imprecision in AMR outcomes. We rated neonatal sepsis, neonatal mortality, and NICU admission as high‐certainty evidence, supported by large sample sizes, consistent results, and narrow confidence intervals that remained within the MID range.
Limitations of the review processes
Literature searches were undertaken by an information specialist, and all screening steps were performed independently by two or more review authors in accordance with guidance in the Cochrane Handbook for Systematic Reviews of Interventions [37]; we applied no restrictions on year or language. Nevertheless, several limitations remain. First, some outcomes are informed by few trials (in some cases, a single trial), and rare events remain imprecise despite large total sample sizes. Second, we conducted a subgroup analysis comparing azithromycin alone versus azithromycin plus amoxicillin, despite the limited number of studies available for each subgroup. We did this to transparently present all available evidence on different prophylactic regimens, given their clinical relevance. However, the small number of studies limits the reliability of subgroup comparisons, and the results should be interpreted with caution.
Agreements and disagreements with other studies or reviews
Three systematic reviews have addressed similar topics [12, 13, 16]. All of them included RCTs, and the included population, intervention, and outcomes were similar. However, Kuitunen 2024 and Ye 2024 included women who underwent caesarean section; Crosara 2024 and Ye 2024 used azithromycin only for prophylaxis; and Kuitunen 2024 did not assess maternal mortality.
Previous research has demonstrated the benefits of azithromycin, including its use in mass administration programmes in regions with a high prevalence of Chlamydia trachomatis, a pathogen associated with blindness, where it reduced child mortality [80]. Similarly, in sub‐Saharan Africa, mass administration of azithromycin resulted in a notable reduction in child mortality [81]. With its long half‐life, azithromycin is considered a highly effective option for administration during labour. Furthermore, multiple RCTs have evaluated its use as a prophylactic antibiotic during labour, providing a strong basis for this systematic review. Our review evaluated the effects of antibiotic prophylaxis during labour on maternal and neonatal outcomes, and demonstrated the efficacy of azithromycin and other antibiotics in reducing maternal infections, including maternal sepsis, wound infections, chorioamnionitis, endometritis, mastitis or breast abscess, and pyelonephritis. These results support the use of antibiotic prophylaxis during labour in settings with a high risk of infection.
However, the pooled results showed little to no effect on maternal mortality, neonatal outcomes, or stillbirth. Specifically, this review found no impact of antibiotics on neonatal sepsis or neonatal mortality and highlighted the lack of substantial evidence to indicate improvements in neonatal outcomes. These outcomes were not derived from all four clinical studies included in this review but were supported by findings from at least two or three studies. The overall risk of bias for the included studies was generally low or raised some concerns, although the analyses of AMR outcomes were assessed as high risk of bias. While we rated most outcomes as having moderate‐ or high‐certainty evidence in GRADE assessments, we rated the certainty of the evidence for adverse effects, including antimicrobial resistance, as very low.
Previous systematic reviews of beta‐lactam and other antibiotic classes have demonstrated that prophylactic use during the second or third trimester can reduce the risk of puerperal endometritis, premature rupture of membranes, and gonococcal infections. Despite these benefits, no improvements in neonatal outcomes, such as low birth weight or neonatal sepsis, were observed [26]. Similarly, a systematic review comparing azithromycin with placebo in caesarean deliveries found reductions in endometritis, wound infections, and severe maternal adverse events but reported no differences in neonatal mortality or complications between the groups [82]. Additionally, the use of prophylactic antibiotics in operative vaginal delivery was found to effectively reduce the incidence of superficial and deep perineal wound infections, as well as severe postpartum infections, in women undergoing vaginal delivery [83].
This divergence in findings suggests that, while maternal benefits are well‐documented, further research is required to better understand neonatal outcomes. Concerns specifically remain regarding the potential emergence of antibiotic‐resistant bacteria, particularly in relation to the long‐term colonisation of antimicrobial‐resistant strains in mothers and children following a single‐dose administration of azithromycin. While this review included data on antimicrobial resistance from two trials, the heterogeneity of methods precluded meta‐analysis, and long‐term resistance outcomes remain unclear. Other observational studies and RCTs have reported differing outcomes regarding the administration of azithromycin and the emergence of resistant bacteria [84, 85]. Notably, Jagne and colleagues observed a slight increase in resistant Group A Streptococcus in vaginal discharge samples from the azithromycin‐treated group [63], which may suggest a potential association between azithromycin administration and antimicrobial resistance. Further investigations are needed to clarify the clinical significance of this finding. While this review supports the potential benefits of antibiotic prophylaxis during labour, it is important to emphasise that improving hygiene and infection prevention practices during childbirth remains a cornerstone of maternal and neonatal health. Prophylactic antibiotics should complement — not replace — essential measures such as clean birth environments, skilled birth attendance, and adequate postnatal care.
Authors' conclusions
Implications for practice
Offering a single oral dose of prophylactic antibiotics to pregnant women in labour after 28 weeks’ gestation or longer in low‐ and middle‐income countries (LMIC) probably reduces the risk of maternal sepsis. Pooled results show it probably has little to no effect on maternal mortality, and has little to no effect on perineal wound infection, neonatal sepsis, neonatal mortality, and neonatal intensive care unit (NICU) admission. The evidence for antimicrobial resistance (AMR) is of very low certainty: short‐term increases in azithromycin‐resistant bacteria were observed in some maternal samples, but no persisting differences were detected at 11 to 13 months, and in neonates, AMR was rare. Decisions on routine prophylaxis for low‐risk women should balance these modest benefits against the uncertain AMR risks and be guided by local infection risk and stewardship capacity. Clean birth practices and high‐quality obstetric care remain essential pillars of maternal and neonatal health.
Equity‐related implications for practice
Azithromycin is an affordable and widely available antibiotic that is suitable for prophylactic use in both high‐ and low‐resource settings. The concentration of evidence from low‐ and middle‐income countries reflects populations at higher baseline risk of maternal and neonatal infections, where the absolute impact of prophylaxis may be greatest. However, this also limits the generalisability of the findings to higher‐income or lower‐risk settings, where infection risk, AMR patterns, and healthcare access may differ. Moreover, the included trials did not report subgroup analyses by equity‐relevant characteristics, such as socioeconomic status, education level, or ethnicity.
No data were disaggregated for vulnerable groups such as adolescents, migrants, or women with limited antenatal care. Additional equity domains, such as disability or social capital, were also not addressed. These gaps highlight the need for future studies to consider equity‐relevant factors in their design and to report outcomes disaggregated by key social and demographic characteristics.
Implications for research
All included studies were conducted in low‐ or lower‐middle‐income countries. To improve comparability, future research should use standardised definitions for key outcomes, particularly maternal sepsis, which was downgraded due to indirectness where some studies used broad terms, such as “infection”, instead of the World Health Organization definition.
We downgraded the certainty of the evidence for maternal mortality due to imprecision, reflecting the rarity of the outcome. Well‐powered studies with consistent outcome reporting are needed.
Maternal satisfaction was not reported in any trial, despite its relevance to care acceptability. Future studies should include patient‐reported outcomes.
Ongoing or recently completed trials may help address some of these evidence gaps. For example, the AZIN‐V trial includes cost‐effectiveness as a planned outcome and repeated measurement of maternal sepsis using standardised criteria [ISRCTN16415327]. The PreYIAL trial will provide more detailed, standardised assessments of maternal and neonatal infections over extended follow‐up [Hume‐Nixon 2022]. However, none of the ongoing trials explicitly include maternal satisfaction as an outcome, which remains an important evidence gap.
Equity‐related implications for research
While it is essential to focus research on the specific needs of LMIC populations, differences in antibiotic resistance patterns, healthcare infrastructure, and baseline infection risks within and between LMIC settings should be carefully considered, to ensure findings are locally relevant. Future research should incorporate equity‐related stratification in study design and analysis, such as by socioeconomic status, education level, ethnicity, disability, and access to antenatal care. Studies should also prioritise disaggregated reporting for vulnerable groups, including adolescents, migrants, and women with limited healthcare access. Addressing these gaps will improve the relevance, applicability, and fairness of evidence to support context‐appropriate policy and practice in diverse LMIC settings.
Supporting Information
Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016211.
Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.
Supplementary material 1 Search strategies
Supplementary material 2 Characteristics of included studies
Supplementary material 3 Characteristics of excluded studies
Supplementary material 4 Characteristics of studies awaiting classification
Supplementary material 5 Characteristics of ongoing studies
Supplementary material 6 Risk of bias
Supplementary material 7 Analyses
Supplementary material 8 Data package
New
Additional information
Acknowledgements
Mr. Takaaki Suzuki, who is an information specialist at Nara Medical University and Cochrane Japan, supported the literature search.
Editorial and peer‐reviewer contributions
The following people conducted the editorial process for this intervention review.
Sign‐off Editor (final editorial decision): Tracey Woodruff, University of California San Francisco;
Managing Editor (selected peer reviewers, provided editorial guidance to authors, edited the article): Joanne Duffield, Cochrane Central Editorial Service;
Editorial Assistant (conducted editorial policy checks, collated peer‐review comments and supported editorial team): Andrew Savage, Cochrane Central Editorial Service;
Copy Editor (copy editing and production): Faith Armitage, Cochrane Central Production Service;
Peer‐reviewers (provided comments and recommended an editorial decision): Elizabeth M McClure, PhD, RTI International (clinical/content review); Prof. Tippawan Liabsuetrakul, Department of Epidemiology, Faculty of Medicine, Prince of Songkla University, Thailand; (clinical/content review); Alan TN Tita, MD, PhD, University of Alabama at Birmingham (clinical/content review); Zeev Konstantin G. Gurevich, Professor of RAS Academic, Inter‐Parliamentary Union (patient and public review); Nuala Livingstone, Cochrane Evidence Production and Methods Directorate (methods review); and Jo Platt, Central Editorial Information Specialist (search review).
Contributions of authors
DS: Protocol development, study selection, data extraction, data synthesis, risk of bias assessment, GRADE assessment, and manuscript writing.
NY, EN: Protocol development, study selection, data extraction, data synthesis, risk of bias assessment, and manuscript writing.
HS: Protocol development, study selection, data extraction, data synthesis, and risk of bias assessment.
KI: Protocol development and manuscript writing.
OR: Study selection, data extraction, and manuscript writing.
MM, JV: Protocol development and manuscript revision.
EO: Protocol development, study selection, arbitrating disagreements, data synthesis, GRADE assessment, and manuscript writing.
All authors provided comments and approved the final review manuscript.
Declarations of interest
DS declares a grant from the Japan Science and Technology Agency (JST; grant number JPMJPF2108) to support his work on this review. He has no commercial conflicts of interest relevant to this review.
EO was partially supported by grants from the JST (grant number JPMJPF2108) and UNDP/UNFPA/ UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), a co‐sponsored programme executed by the World Health Organization (WHO) for her work on this review; personal payments. She also serves as a senior editor for the Cochrane Central Editorial Service but was not involved in the editorial process for this review.
JV works as a clinician in the West Australian Department of Health and as a maternal health researcher with the World Health Organization and the Burnet Institute. He also holds editorial appointments with Cochrane Pregnancy and Childbirth and Cochrane Effective Practice and Organisation of Care. He was not involved in the editorial process for this review.
NY, EN, HS, KI, OR, and MM: No commercial conflicts of interest relevant to this review.
Sources of support
Internal sources
-
None, Other
None
External sources
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UNDP/UNFPA/ UNICEF/WHO/World Bank Special Programme of Research, Development and Research Training in Human Reproduction (HRP), a co‐sponsored programme executed by the World Health Organization (WHO), Switzerland
EO was partially supported by the WHO for her work on this review.
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Japanese government program: program on open innovation platform for industry‐academia co‐creation (COI‐NEXT), Japan
EO and DS are supported by JST Grant Number JPMJPF2108 for this review. While funding for this review was provided, we have no conflicts of interest to disclose.
Registration and protocol
Registration: PROSPERO (2024) CRD42024582129
Data, code and other materials
As part of this Cochrane Review, the following supplementary materials are available: Supplementary material 1; Supplementary material 2; Supplementary material 3; Supplementary material 4; Supplementary material 5; Supplementary material 6; Supplementary material 7; Supplementary material 8. These supplementary files include full search strategies, characteristics of included, excluded, ongoing, and awaiting classification studies, risk of bias assessments, and the data package used for the analyses in this review. Analyses were conducted using RevMan. Additional materials, including the extracted study‐level data and detailed RoB 2 assessment files, are available from the authors upon reasonable request. Appropriate permissions have been obtained for such use. Analyses and data management were conducted within Cochrane’s authoring tool, RevMan, using the inbuilt computation methods.
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Supplementary material 1 Search strategies
Supplementary material 2 Characteristics of included studies
Supplementary material 3 Characteristics of excluded studies
Supplementary material 4 Characteristics of studies awaiting classification
Supplementary material 5 Characteristics of ongoing studies
Supplementary material 6 Risk of bias
Supplementary material 7 Analyses
Supplementary material 8 Data package
Data Availability Statement
As part of this Cochrane Review, the following supplementary materials are available: Supplementary material 1; Supplementary material 2; Supplementary material 3; Supplementary material 4; Supplementary material 5; Supplementary material 6; Supplementary material 7; Supplementary material 8. These supplementary files include full search strategies, characteristics of included, excluded, ongoing, and awaiting classification studies, risk of bias assessments, and the data package used for the analyses in this review. Analyses were conducted using RevMan. Additional materials, including the extracted study‐level data and detailed RoB 2 assessment files, are available from the authors upon reasonable request. Appropriate permissions have been obtained for such use. Analyses and data management were conducted within Cochrane’s authoring tool, RevMan, using the inbuilt computation methods.