Planned hospital birth compared with planned home birth for pregnant women at low risk of complications

Abstract

Background

Observational studies of increasingly better quality and in different settings suggest that planned hospital birth in many places does not reduce mortality and morbidity but increases the frequency of interventions and complications. Euro‐Peristat (part of the European Union's Health Monitoring Programme) has raised concerns about iatrogenic effects of obstetric interventions, and the World Health Organization (WHO) has raised concern that the increasing medicalisation of childbirth tends to undermine women’s own capability to give birth and negatively impacts their childbirth experience. This is an update of a Cochrane Review first published in 1998, and previously updated in 2012.

Objectives

To compare the effects of planned hospital birth with planned home birth attended by a midwife or others with midwifery skills and backed up by a modern hospital system in case a transfer to hospital should turn out to be necessary. The primary focus is on women with an uncomplicated pregnancy and low risk of medical intervention during birth. 

Search methods

For this update, we searched Cochrane Pregnancy and Childbirth’s Trials Register (which includes trials from CENTRAL, MEDLINE, Embase, CINAHL, WHO ICTRP, and conference proceedings), ClinicalTrials.gov (16 July 2021), and reference lists of retrieved studies.

Selection criteria

Randomised controlled trials (RCTs) comparing planned hospital birth with planned home birth in low‐risk women as described in the objectives. Cluster‐randomised trials, quasi‐randomised trials, and trials published only as an abstract were also eligible.

Data collection and analysis

Two review authors independently assessed trials for inclusion and risk of bias, extracted data, and checked the data for accuracy. We contacted study authors for additional information. We assessed the certainty of the evidence using the GRADE approach. 

Main results

We included one trial involving 11 participants. This was a small feasibility study to show that well‐informed women ‐ contrary to common beliefs ‐ were prepared to be randomised. This update did not identify any additional studies for inclusion, but excluded one study that had been awaiting assessment. The included study was at high risk of bias for three out of seven risk of bias domains. The trial did not report on five of the seven primary outcomes, and reported zero events for one primary outcome (caesarean section), and non‐zero events for the remaining primary outcome (baby not breastfed). Maternal mortality, perinatal mortality (non‐malformed), Apgar < 7 at 5 minutes, transfer to neonatal intensive care unit, and maternal satisfaction were not reported. The overall certainty of the evidence for the two reported primary outcomes was very low according to our GRADE assessment (downgraded two levels for high overall risk of bias (due to high risk of bias arising from lack of blinding, high risk of selective reporting and lack of ability to check for publication bias) and two levels for very serious imprecision (single study with few events)).  

Authors' conclusions

This review shows that for selected, low‐risk pregnant women, the evidence from randomised trials to support that planned hospital birth reduces maternal or perinatal mortality, morbidity, or any other critical outcome is uncertain. As the quality of evidence in favour of home birth from observational studies seems to be steadily increasing, it might be just as important to prepare a regularly updated systematic review including observational studies as described in the Cochrane Handbook for Systematic Reviews of Interventions as to attempt to set up new RCTs. As women and healthcare practitioners may be aware of evidence from observational studies, and as the International Federation of Gynecology and Obstetrics and the International Confederation of Midwives collaboratively conclude that there is strong evidence that out‐of‐hospital birth supported by a registered midwife is safe, equipoise may no longer exist, and randomised trials may now thus be considered unethical or hardly feasible. 

Plain language summary

Planned hospital birth versus planned home birth

What is the issue?

Most pregnancies among healthy women are normal, and most births could take place without unnecessary medical intervention. However, it is not possible to predict with certainty that no complications will occur in the course of a birth. Thus, in many countries, it is believed that the safest option is for all women to give birth at hospital. In a few countries, however, it is believed that as long as a woman is cared for during pregnancy and assisted during birth by a midwife, with transfer between home and hospital available (if needed), then home birth is, and can be, an integrated part of maternity care. It seems increasingly clear that anxiety and easy access to many medical procedures at hospital may lead to increased levels of intervention, which in turn may lead to further interventions and finally to unnecessary complications. In a planned home birth assisted by an experienced midwife with collaborative medical backup in case transfer should be necessary, these drawbacks are avoided, while the benefit of access to medical intervention when needed is maintained.

Why is this important?

Increasingly, better observational studies suggest that planned hospital birth for women at low risk of complications is not any safer than planned home birth assisted by an experienced midwife with collaborative medical backup, but it may lead to more interventions and more complications. Presentation of potential benefits and harms of a planned hospital birth compared to a planned home birth is likely to be highly relevant to pregnant women.

What evidence did we find?

We searched for evidence from randomised controlled trials (RCTs) (studies where participants are randomly assigned to one of two or more treatment groups) in July 2021. No new RCTs were identified in addition to the two previously identified very small RCTs. Only one RCT (involving 11 women and their babies) contributed data to the review, so it is not possible to draw any conclusions from such a small number of women and babies. To the extent that the study reported data, the certainty of the evidence was very low. We found no strong evidence from RCTs to favour either planned hospital birth or planned home birth for pregnant women at low risk of complications. Several things have been added to the review in this update. Most importantly, the evidence has been placed in the context of today. As advised in the updated version of the Cochrane Handbook, we have also a) added a conceptual framework to illustrate the proposed mechanism of action of the complex intervention ‘planned hospital birth’, and b) reassessed the evidence using a whole range of new tools, methodologies, and terminology. These exercises did not lead to a substantially different interpretation of the available evidence, but the implications have changed.

What does this mean?

There is not enough evidence from RCTs (considered the best form of evidence of effectiveness) to allow firm conclusions to be drawn. Also, further RCTs are not considered feasible, and they are no longer considered appropriate by many midwives, obstetricians, and parents. As the quality of evidence from observational studies is steadily increasing, it might be useful to include evidence from properly performed systematic reviews of observational studies in future updates of this review.

Summary of findings

Summary of findings 1. Summary of findings table ‐ Planned hospital birth vs. Planned home birth for Pregnant women at low risk of complications.

Patient or population: Pregnant women at low risk of complications Setting: Well‐organised health care systems Intervention: Planned hospital birth Comparison: Planned home birth
Outcomes	Anticipated absolute effects* (95% CI)		Relative effect (95% CI)	№ of participants (studies)	Certainty of the evidence (GRADE)	Comments
	Risk with Planned home birth	Risk with Planned hospital birth
Maternal mortality ‐ not reported	‐	‐	‐	‐	‐	Outcome was not reported
Perinatal mortality ‐ not reported	‐	‐	‐	‐	‐	Outcome was not reported
Apgar < 7 at 5 min ‐ not reported	‐	‐	‐	‐	‐	Outcome was not reported
Transfer to neonatal intensive care unit ‐ not reported	‐	‐	‐	‐	‐	Outcome was not reported
Caesarean section	Not pooled	Not pooled	Not pooled	11 (1 RCT)	⊕⊝⊝⊝ Very lowa,b	Evidence is uncertain
Baby not breastfed	200 per 1000	315 per 1000 (36 to 854)	OR 1.84 (0.15 to 23.38)	11 (1 RCT)	⊕⊝⊝⊝ Very lowa,b	Evidence is uncertain
Maternal satisfaction ‐ not reported	‐	‐	‐	‐	‐	Outcome was not reported
*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; OR: odds 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_430762719464558163.

^a We downgraded two levels for high overall risk of bias (due to high risk of bias arising from lack of blinding, high risk of selective reporting and lack of ability to check for publication bias)
^b We downgraded two levels for very serious imprecision: single study with few events

Background

Medicalisation of childbirth is a central feature in Western societies (Johanson 2002). The majority of women living in high‐ and middle‐income countries have given birth in hospitals since the middle of the 20th century. However, there are regions where home birth is considered part of normal practice (Comeau 2018; Sundhedsloven 2019). It is of historical interest to note that the transfer of low‐risk births from home to hospital in the 1960s, despite lack of high‐quality evidence, was one of the pivotal issues when Archie Cochrane laid out the ideological ground for The Cochrane Collaboration. Cochrane awarded ‘the wooden spoon’ to obstetrics (Cochrane 1989), because "The speciality missed its first opportunity in the sixties, when it failed to randomise the confinement of low‐risk pregnant women at home or hospital. [...] Then, having filled the emptying beds by getting nearly all pregnant women into hospital, the obstetricians started to introduce a whole series of expensive innovations into the routines of pre‐ and postnatal care and delivery, without any rigorous evaluation. The list is long, but the most important were induction, ultrasound, foetal monitoring, and placental function tests" (Cochrane 1979). The relationship between hospitalisation, childbirth, and intervention is still an important issue as "Concern about the iatrogenic effects of obstetric intervention in women who do not have a clinical need for it has put 'normal' birth firmly on the agenda for the 21st century” (EURO‐PERISTAT 2008). The World Health Organization (WHO) now explicitly expresses concern that there “has been a substantial increase over the last two decades in the application of a range of labour practices to initiate, accelerate, terminate, regulate or monitor the physiological process of labour”, and that this “increasing medicalization of childbirth processes tends to undermine the woman’s own capability to give birth and negatively impacts her childbirth experience” (WHO 2018). 

The question which motivated this view was (Olsen 1997b): to what extent is it possible to select a group of low‐risk women who might benefit from planning a home birth that is backed up by a collaborative, medical support system in case a transfer should turn out to be necessary, rather than plan a hospital birth initially? As the title of the review was reversed in the last update to 'Planned hospital birth versus planned home birth' (Olsen 2012), and as the concerns regarding harms from unnecessary medicalisation have increased since then (WHO 2018), it is now more meaningful to ask: what are the benefits and harms of routinely offering healthy women with an expected uncomplicated birth to give birth at hospital compared to a planned home birth in a well‐organised home birth service backed up by a collaborative, medical support system in case a transfer should turn out to be necessary?

Description of the condition

This review is about healthy pregnant women at term, (Nguyen 2005; Macdonald 2017), for whom no serious complications have been identified prior to the spontaneous initiation of birth and for which the birth is expected to be medically uncomplicated. This is the majority of births that occur globally (WHO 2018); generally, between 70% and 80% of all pregnant women may be considered as low risk at the start of labour (WHO 1996).

Description of the intervention

In line with Archie Cochrane, we consider planned hospital birth as the experimental intervention. 

Hospital practices vary considerably; intervention rates vary with a factor 3 to 5 between countries (e.g. for induction of labour, pre‐labour and overall caesarean section; augmentation of labour), for some interventions even up to a factor 10 to 15 (episiotomy and instrumental births), and in many places the intervention rate is high (Seijmonsbergen‐Schermers 2020). Obstetric departments have plenty of medical equipment that provide doctors, nurses, and midwives with the possibility to intervene in the labour process, and hospitals can offer labouring women a range of interventions that are not available at home. 

Home birth services are offered by midwives and nurse midwives. As part of their professional philosophy, it is emphasised that most births are normal physiological processes (ICM 2014), that this process should be supported, and that routine interventions should be avoided (ICM 2019). Home birth practices are thus closely linked to the midwifery model of care (Davis‐Floyd 2009a; Davis‐Floyd 2009b; Rooks 1999). Variations in the integration of home birth practices into healthcare systems have recently been described in detail (Comeau 2018). In general, only very few medical interventions can be carried out at home, and in case of most complications, women must transfer to hospitals. 

How the intervention might work

Two lines of theoretical reasoning exist that each in their own way explain how planned hospital births for low‐risk women may have impacts on the labouring woman and the fetus/newborn. They have been labelled the medical model and the midwifery model of care (Davis‐Floyd 2009a; Davis‐Floyd 2009b; Rooks 1999). 

The rationale behind the medical model is that a hospital provides a safe environment for a labouring woman, due to the capacity to intervene, without delay, in case of complications (e.g. cord prolapse, abruptio placenta, shoulder dystocia, and fetal heart plummeting for no obvious reason). The quote "Birth can only be defined as normal in retrospect" pinpoints this rationale (WHO 1996). Even though women can labour without the need for medical backup, it is not possible to identify those women or newborns beforehand. It is therefore safest for all women to deliver in a hospital fully equipped with modern technology and professionals who can identify women at risk and intervene in case of emergency. All births, including normal births, are to a high degree attended to as complicated deliveries. Clinicians believe with justification that babies may be rescued by rapid delivery. In their everyday work with average and unselected births, obstetricians fairly often encounter complications, and not too rarely they also face complications that carry a high risk of maternal and fetal death or severe morbidity. In such emergency circumstances, clinicians are often satisfied with interventions even when they have not been tested in randomised trials (e.g. caesarean section or instrumental delivery). And midwives, if in charge of such a seemingly normal birth where complications develop during labour, will transfer responsibility to the obstetricians for surveillance and medical intervention, and subsequently assist the obstetrician under his or her supervision. As emergency complications may also occur among women with low‐risk pregnancies ‐ although at a much lower frequency ‐ the rationale behind planned hospital births for all women irrespective of their risk status is that immediate availability of emergency interventions will decrease the frequency of the, admittedly rarer, seriously bad outcomes without introducing too many adverse effects that might outweigh the theoretical advantage. Examples of emergency complications that concern clinicians the most in relation to low‐risk births, especially if these take place outside the hospital, are abruptio placenta, cord prolapse, shoulder dystocia, and fetal heart plummeting for no obvious reason. These four emergency complications were dealt with at length in the previous version of this review (Olsen 2012).

Conceptual framework for unintended side effects: cascade of interventions 

There is a global concern about an escalating overuse of interventions that were designed to manage complications, and that this overuse may cause iatrogenic harm to the woman and to the newborn child (Renfrew 2014). The phrase ‘cascade of interventions’ was coined by a clinician prior to the era of evidence‐based medicine (Inch 1984; Macdonald 2017), with the intention of describing the experience where, as soon as one intervention into an otherwise naturally developing birth process was carried out, a following cascade of consequential interventions and complications seemed inevitable (Rossignol 2014; Petersen 2013; epidural‐flow‐chart‐cascade‐of 2022; cascade‐of‐intervention‐chart 2022). Planned hospital birth is a complex intervention, so to ensure a framework for the methods and analyses undertaken throughout this review, we have used ‘cascade of interventions’ as an illustration of the possible mechanisms of action of the intervention and its components (Kneale 2015; Thomas 2021), sometimes also called a logic model (Kneale 2015). It usually takes the form of a graphical depiction, but it also includes the theories, scientific evidences, assumptions, and beliefs that support it and the various processes behind it (Logic_model 2022).

For a planned hospital birth, the very first intervention is leaving home, sitting in a car with contractions, finding a car park, waiting for the elevator to the labour ward, and finally meeting the healthcare personnel. Veterinarians seem to have known for a long time that moving animals shortly before birth is counterproductive; it is not allowed to move farm animals in the last tenth of their pregnancy (Bekendtgørelse 2004), which fits fairly well with ‘at term’ in the human species. Recent research in mammals is just beginning to identify the hormonal and epigenetic pathways that might explain such concerns for both humans and other mammals (Uvnäs‐Moberg 2019). (On a side note, we acknowledge that the knowledge about epigenetic pathways is so immature that for women who prefer to be in hospital ‐ and feel safe there because of access to medical staff and facilities, pain relief being available, and not needing to transfer ‐ this may trigger some of the same epigenetic responses, just in the opposite direction). This first part of the journey is without the reassuring and qualified company of a midwife, contrary to what is usually the case when a planned home birth is transferred to hospital. A travel time from home to hospital of 20 minutes or more by car is associated with an increased risk of mortality and adverse outcomes in high‐risk women at term (Ravelli 2011), and may also have negative effects on healthy women. The stress released during transportation may be further increased if the woman's needs are not adequately met upon arrival to hospital, as they sometimes seem not to be (Eri 2015). Even though the couple feel welcomed and have confidence in the safety of hospital birth, staff and empty rooms may be unavailable. The couple may be left alone waiting in an unfamiliar environment and perhaps finally subjected to some standard interventions (e.g. a door‐step cardiotocography (CTG)), provided against the best available evidence (Alfirevic 2017), and against recommendation by WHO (WHO 2018). This might in turn lead to other interventions such as artificial rupture of the membranes in order to observe the colour of the amniotic fluid or to insertion of a scalp electrode and continuation with ST analysis (STAN) monitoring. This very first part of the intervention cascade has been summed up by the WHO: “By medicalising birth, i.e. separating a woman from her own environment and surrounding her with strange people using strange machines to do strange things to her in an effort to assist her, the woman’s state of mind and body is so altered that her way of carrying through this intimate act must also be altered (and the state of the baby born must equally be altered)” (WHO 1985).

Upon arrival in the hospital, perhaps with this altered state of mind, the pregnant woman may soon need additional interventions, partly based on the state of her body and mind, and partly based on hospital routines. Disruption of labour has been defined as “any practice or technology that may disrupt physiological labour e.g. transfer during labour, restricted movements, amniotomy, food restrictions, pushing with closed glottis, and controlled cord traction” (Rydahl 2021). The first two of these disruptions have already taken place as an integral part of the intervention. Interruption of labour may affect the production of oxytocin and slow down labour, and thus women admitted to hospital ‐ particularly in the latent phase of labour (Rota 2018; Miller 2020) ‐ are more likely to experience intrapartum interventions. Sitting and waiting, perhaps far from home, may lead to a desire for ‘something to happen’, leading to amniotomy, thereby increasing the risk of infection and the risk of the cord prolapse without any documented benefits (Bricker 2000). The risk of infection may lead to routine use of antibiotics if the baby is not born within a predefined time limit despite lack of evidence for routine use of antibiotics (Wojcieszek 2014). The first vaginal examination in a series of many may take place at arrival despite the lack of “good evidence of effectiveness, particularly considering the sensitivity of the procedure” (Downe 2013). Even when there are no guidelines prescribing food restrictions, being away from home may still lead to challenges for the partner to find food and drink, mostly desired around the clock. So far, even without involving any medical doctors or any expensive equipment or medicine, a woman starting the journey to a planned hospital birth may very early on in the process experience a cascade of disruptions and interventions disturbing physiological labour. Particularly for first‐time mothers, arriving ‘too soon’ might lead to a cascade of negative experiences described as “embarrassing”, “feeling exposed and ‘naked’”, or “feelings of loneliness, helplessness and sadness” (Eri 2015). Coping with the pain and boredom under these circumstances may be a challenge and lead to a need for epidural analgesia. Popular illustrations of this part of the cascade of interventions can be found in many places on the internet. One shows how epidural analgesia may lead to seven different types of interventions and nine different types of complications that may be interrelated, and all directly or indirectly may lead to caesarean section or postpartum complications, or both (epidural‐flow‐chart‐cascade‐of 2022). Another illustration shows how induction of labour may lead to a mix of 11 interventions and complications that in turn may lead to caesarean section and five postpartum complications (cascade‐of‐intervention‐chart 2022). Many of these interventions (e.g. epidurals) need the presence of highly skilled obstetricians, paediatricians, and anaesthesiologists as well as expensive equipment (Cleese 1983), and may increase the risk of more serious unintended effects in the short, medium, or long term (Sandall 2018). Figure 1 illustrates some suggested or documented pathways in the cascade of interventions often used in healthy low‐risk women with a planned hospital birth rather than a planned home birth along with related complications. The figure should not be taken literally; it is a symbolic representation of an idea. It may be different for nulliparae and multiparae (Petersen 2013), as well as for different hospitals with more or less interventionist policies. If all possible interventions and complications mentioned above ‐ and all possible pathways inbetween ‐ should be included, the figure would end up unmanageable. For example, the dot ‘Augmentation’ could be split into two or more dots including ‘amniotomy’ and ‘syntocinon’ with a possible arrow between them. Most illustrations of the cascade of interventions have been delimited to what takes place in the labour room. In Figure 1, the cascade has been extended to both what happens before arrival in the labour ward and what may happen later, either to the child (blue dots) or to the mother in later pregnancies (red dots). The number of dots and arrows depends on the theories, scientific evidence, and also on assumptions and beliefs that support it and the various processes behind it (Logic_model 2022).

1.

Figure 1. Cascade of interventions and complications

Why it is important to do this review

It is important that pregnant women and public health planners are able to base decisions on the best available evidence. However, still stronger evidence supports the widespread concern that the “increasing medicalization of childbirth processes tends to undermine the woman’s own capability to give birth and negatively impacts her childbirth experience” (WHO 2018), and a multinational, comparative study of variations in use of childbirth interventions in 13 high‐income countries supports this statement, as it was unable to demonstrate reduced rates for any adverse outcomes no matter what the level of intervention was among the very highly variable rates of interventions (Seijmonsbergen‐Schermers 2020). We have updated this review because methodology and references to the evidence in the introduction needed to be updated and put into current context. We have summarised here the currently best available evidence on a number of contextual issues. 

Randomised evidence for effectiveness is lacking

As described in the Cochrane Handbook for Systematic Reviews of Interventions, “Randomized trials are the best study design for evaluating the efficacy of interventions” and “If it is feasible to conduct them […] they must be considered eligible for the review” (McKenzie 2021). The small feasibility study, Dowswell 1996, included in previous versions of this review, Olsen 2012, demonstrated that randomised trials in principle were feasible 25 to 30 years ago, and thus this design type is eligible for this review. We suggested that “Clinicians who are uncomfortable with the quality of the observational or indirect evidence and the lack of direct evidence from randomised trials relating to satisfaction, intervention rates, and morbidity may consider setting up or getting involved in trials” (Olsen 2012). However, the lack of progress in setting up any new trials suggests that neither researchers nor clinicians, nor anybody else has seen it as relevant or possible to set up randomised trials. This is probably reflected by the joint press release stating that "There is strong [sic] evidence that out of hospital birth supported by a registered midwife is safe, and a preferred experience for many mothers" published by the International Confederation of Midwives and the International Federation of Gynecology and Obstetrics (FIGO and ICM 2012), published the very same year and with access to the same evidence as in the previous version of this review, but making a stronger conclusion than in the Cochrane Review (Olsen 2012), thus indicating an agreement that no more evidence from randomised trials was needed. Regarding challenges related to lack of evidence from randomised trials, it is stated in the Cochrane Handbook that “It might be difficult to address some interventions or some outcomes in randomized trials” (McKenzie 2021). In general, “To achieve a balanced perspective, all reviews should try to consider the adverse aspects of the interventions”, and this “is particularly relevant when evidence on the potential for harm has a major influence on treatment or policy decisions” (Peryer 2021). For an intervention in widespread use ‐ as in planned hospital birth for healthy women ‐ for which effectiveness has never been demonstrated in randomised trials, it would be particularly appropriate to include an assessment of unintended side effects based on non‐randomised studies (McKenzie 2021). We remind readers that as long as Cochrane Pregnancy and Childbirth upholds its policy of systematically reviewing only randomised controlled trials (RCTs) (Gates 2012), we only systematically review RCTs in this systematic review.  As in the previous versions of this review and in accordance with Cochrane Pregnancy and Childbirth policy, other types of evidence are only mentioned in this subsection and in the Discussion section; they are not included in the Authors' conclusions. 

Observational studies indicate increased levels of interventions and complications

Assessment of quality of systematic reviews

The two most recent systematic sister‐reviews of observational studies are “based on a published peer‐reviewed protocol”, and together comprise the largest and most comprehensive systematic review comparing outcomes of intended home and hospital birth, and take “study design, parity and jurisdictional support for home birth into account” (Hutton 2014; Hutton 2019; Reitsma 2020). They present an analysis that was called for in the previous version of this review (Olsen 2012). Both reviews are well documented, and the literature search, quality assessment, study selection, and classification into types of integration of the home birth service into the healthcare systems (dichotomised into well‐integrated or less well‐integrated) are meticulously carried out. The only weakness is that in the statistical analyses the unadjusted effect estimates from the original studies are used. We have thus chosen for each outcome reported in at least one of the in total 16 included, quality‐assessed, original studies, Hutton 2019; Reitsma 2020, to quote the adjusted estimate from the largest study reporting that specific outcome. 

Effect estimates from observational studies

The findings can briefly be summarised as follows (for each outcome quoting the adjusted estimate from the largest study reporting that specific outcome): no maternal deaths were reported in any of the groups in any of the studies, and no statistically significant differences were found in perinatal mortality, Apgar < 7 at 5 minutes, or ‐ among nulliparous ‐ in admission to neonatal intensive care unit (NICU) among children born to women routinely referred to hospital birth; among newborn to parous women, the odds for admission to a NICU was significantly increased by around 20% (de Jonge 2015). The odds for the maternal complications postpartum haemorrhage (PPH), Nove 2012, and infection, Janssen 2009, were both statistically significantly increased with more than 50% irrespective of parity. The odds for the interventions oxytocin augmentation, epidural anaesthesia, and episiotomy were all statistically significantly increased with more 50% irrespective of parity (Hutton 2016); the odds for caesarean sections were increased with around 20% (van der Kooy 2017). Although the specific estimates varied between studies, the pattern of doing significantly more harm than good was consistent. No reason is stated for the specific selection of the outcomes presented in the systematic reviews (Hutton 2014; Hutton 2019; Reitsma 2020), but in addition to the obstetric interventions and outcomes presented, a few additional outcomes were reported in the included original studies. For women with a planned hospital birth, electronic fetal monitoring (EFM) was more than three times as common; use of fetal scalp electrode more than twice as common (Janssen 2009); for parous women the rate of severe acute maternal morbidity and the rate of manual removal of placenta was more than doubled (de Jonge 2013); and the rate of failed breastfeeding at days 3 and 10 was at least 50% higher irrespective of parity (Hutton 2016). A list of rare outcomes (e.g. prolapsed cord, need for blood transfusion, fever, etc.) all except one had larger incidence, though the difference was not statistically significant (Janssen 2009). Thus, the previous conclusions about "no statistical difference" in perinatal mortality seem to have been strengthened (Olsen 1997a; Olsen 1998), and the results showing significantly lower morbidity rates related to home birth have become more convincing.

Supporting evidence from randomised studies

Even in well‐controlled observational studies, observed differences (or lack of differences) may be due to uncontrolled confounding and bias. However, a Cochrane Review comparing alternative versus conventional institutional settings for birth all “characterized by a philosophical orientation towards labour and birth as fundamentally normal experiences” did not find any significant difference in various measures of mortality but showed a significantly increased need for intrapartum analgesia/anaesthesia, epidural analgesia, oxytocin augmentation of labour, instrumental vaginal birth, and episiotomy, while decreasing the rate of spontaneous vaginal birth, breastfeeding at six to eight weeks, and very positive views of care in the conventional setting (Hodnett 2012). It thus indirectly supports the findings from the observational studies. The authors had not included EFM as an outcome in the review (Hodnett 2012), although EFM was included in at least one trial, showing a 50% more frequent use in the conventional setting (Begley 2011). Some of the interventions may in turn lead to other interventions and complications (described above as a 'cascade of interventions'). For example, a Cochrane Review showed that women randomised to receive epidural 10 times more often experienced hypotension, motor blockade, and urinary retention that itself might lead to further interventions; labour also lasted on average 48 minutes longer (Alfirevic 2017). Thus parts of the pathway from early interventions to later complications are supported by evidence about similar, Hodnett 2012, or specific interventions, Alfirevic 2017, from randomised trials and Cochrane Reviews.

Women are not informed well about their options and the available evidence

Systematic reviews of other issues related to hospital birth further support why this review is important. Though women’s experience is important (WHO 2018), most qualitative research on women’s experiences of planned hospital versus planned home birth is either focused solely on perspectives in the UK or is outdated (Brunton 2021); the former is probably due to a recently formed national policy to actively support women’s choice of birthplace (Henshall 2016). However, planned hospital birth still seems to be the ‘standard procedure’, and thus in relation to women’s informed choices and decision‐making, the process is only straightforward for women planning to give birth at hospital, while women considering birth at home often “encountered obstacles and described needing to 'counter the negativity' surrounding home birth” (Coxon 2017). Women in search of non‐medicalised childbirth have even brought their case to the UN Committee on the Elimination of Discrimination of Women (CEDAW), CEDAW 2020; CEDAW 2010, and the European Court of Human Rights (Registrar 2010; Judgment 2016).  Despite the increasing research on decision‐making, informed choice is often not well understood. "Policymakers and practitioners alike should examine critically current choice frameworks to ascertain whether they truly allow for flexibility in decision‐making. Health systems should embrace more fluid, personalised models of care to augment service users' decision‐making agency” (Yuill 2020). Midwives are the obvious healthcare professionals to provide such information, but the provision of information and the ensuing shared decision‐making often suffers from organisational pressures (e.g. hospital policies to conform to status quo) and professional norms (e.g. unsupportive attitudes towards home birth) leading to variation in what midwives tell women. "Training in discussion of risk and promotion of homebirth" and leaflets “focusing on birthplace choices for women” seem essential to achieve truly informed choices (Henshall 2016). The mentioned systematic reviews are all very much based on studies from high‐income countries, particularly English‐speaking countries. An analysis of 460 full reports of stakeholders' perspectives on home birth found that only findings from high‐resource countries were sufficiently rich to be synthesised. The two just‐quoted perspectives, respectively women’s, Coxon 2017; Yuill 2020, and midwives’, Henshall 2016, were by far the most common foci, whereas there was a gap in primary research with respect to policymakers (only two studies) (Brunton 2021).

Detrimental effects at the systemic level

Beyond potential harms and benefits at the individual level, a healthcare system based on hospitalisation and medicalisation of healthy women may also cause harms and benefits at systemic levels (Thomas 2021). Midwives have increasingly been leaving the profession (Curtis 2006; Lind 2021; Svensson 2021), describing the situation at the hospital as “war like” (Geraghty 2019), or describing themselves as working “in a highly strained, factory‐like, over‐medicalised context with high demands and lack of organisational resources and support systems” (Hansson 2020), issues that have led to a high turnover, with more than one‐third of all newly educated midwives leaving the labour ward within four to five years (Lind 2021), and midwifery students stating that “Current maternity care is medicalized and managed from a pathological point of view. Midwives flee maternity care because they are not allowed to be midwives”(Svensson 2021).

Similarly, a small but increasing number of women seem so dissatisfied with current maternity care that they reject the service completely and give birth without any qualified birth attendant (Lynch 2007). This in turn has led to an exponential growth in research interest in so called ‘freebirth’, starting in 2007 (Lynch 2007; Macdonald 2019; Feeley 2015). A meta‐narrative review concluded that motivations for freebirth “frequently related to women's previous negative maternity experiences and the type of maternity care available, for example medicalised and hospital‐based” (McKenzie 2020). A meta‐thematic synthesis suggested that “the gulf between the midwifery philosophy of care and that which is currently practised needs radical attention” (Feeley 2015); a follow‐up study specifically concluded that midwives need to restore relationships with women (Feeley 2016). A system of maternity care based on hospital birth, where an increasing number of women do not want to give birth, midwives cannot practise midwifery, and an increasing number of midwives leave the labour ward, seems unsustainable.

Planned hospital birth more costly 

A systematic review compared the cost of planned hospital to the cost of planned home birth. The included studies varied considerably in terms of sample size and methods, but the three larger studies concluded that home birth was less costly, and the fourth, smaller study found no difference in cost (Scarf 2016). Three later studies have findings in line with this (Hitzert 2017; Scarf 2020; Scarf 2021).

Planned hospital birth may not be sustainable in the future

The context in which birth takes place may change over time. Since the latest version of this review, WHO has raised concerns that “Antibiotic resistance is rising to dangerously high levels in all parts of the world” and that “caesarean sections [will] become much more dangerous without effective antibiotics” (WHO 2020). An increased rate of caesarean sections for planned hospital births was reported in the studies above, but none of them reported on the use of antibiotics. Often the use of antibiotics is part of, or a consequence of, a general interventionist hospital regimen including pre‐labour rupture of membranes, frequent vaginal examinations, instrumental delivery, caesarean section, etc., some of which are reported in the studies above, while some will only occur in the labour notes. Meta‐analysis of data from observational studies shows a more than doubled risk for maternal antibiotic treatment among women having epidural analgesia (Jansen 2020). It also seems as if spontaneous birth beyond 41 weeks can no longer be managed safely at hospitals without induction, whereas inclusion of spontaneous birth beyond 41 + 0 weeks seems not to increase risk among planned home births (de Jonge 2015; Hutton 2016). It has been proposed that one way to reduce the need for the cascade of interventions is to reinvigorate the classical core midwifery skill ‘watchful attendance’, where the midwife “uses all her senses to observe a woman’s wellbeing and labour progress” and to instil “a feeling of trust and safety” (de Jonge 2021), skills which seems increasingly difficult to uphold within the organisational norms and bureaucratic imperative of the modern hospital.

Power calculations

According to the protocol the objective was "to determine if the above results [from observational studies] are reproducible in randomised trials". If an equivalence trial – despite the above‐mentioned potential harms and costs ‐ were to be set up in order to demonstrate that planned hospital birth is at least as safe as planned home birth for low‐risk women assisted by an experienced midwife with collaborative medical backup, trialists would need to determine a minimal clinically important difference in maternal mortality (D’Agostino 2003). If a minimal clinically meaningful difference is set to 10% or 20% difference in the efficacy measure (D’Agostino 2003), then for maternal mortality, 10 to 50 million women would be needed in such a trial depending on the exact circumstance. In order to demonstrate a 50% reduction in maternal mortality, “only” 1 to 2 million women would be needed. More than 100,000 women would be needed in order to demonstrate a lower perinatal mortality. Some may still think there is a strong need for a large randomised trial to assess whether routine hospitalisation is doing more good than harm. Whether or not a such randomised trials will ever be carried out, the need to systematically summarise the best available evidence will prevail, and this review will remain an important place to do so.

Regions with remote hospitals  

In the future it might be worthwhile to prepare a protocol for a separate review focusing on pregnant women who live in areas of the world where hospitals, even though adequate in numbers, are not distributed “within easy reach of all the women and newborns who need them" (SOWMY 2011). Assessments in more than 50 countries have revealed that a deficit of health facilities offering Basic Emergency Obstetric and Newborn Care (BEmONC) is an even larger problem than the lack of hospitals. In areas where both levels of care are available, it might be worthwhile to consider if resources are better spent maintaining home births in areas within reach of BEmONCs rather than spending all resources on “concentrating staff, equipment, drugs and supplies in a health facility that is open 24 hours a day, 7 days a week” (SOWMY 2011).

Objectives

To compare the effects of planned hospital birth with planned home birth attended by a midwife or others with midwifery skills and backed up by a modern hospital system in case a transfer should turn out to be necessary. The primary focus is on women with an uncomplicated pregnancy and low risk of medical intervention during birth.

Methods

Criteria for considering studies for this review

Types of studies

We included randomised controlled trials (RCTs). We would have included cluster‐RCTs if available. We excluded cross‐over trials. We would include data from abstracts only if sufficient information was available to assess risk of bias.

Types of participants

Low‐risk pregnant women as defined by local legal regulations or as defined by trialists, for example "who had no medical indication for hospital birth", no "medical or obstetric risk factor before labour" and with "spontaneous onset of labour [...] between 37 and 42 weeks gestation" and a "single baby" (de Jonge 2015).

Types of interventions

We compared planned hospital birth and planned home birth.

• A planned hospital birth is a birth planned prior to labour to take place at a hospital; we would include any type of hospital without restriction, e.g. whether the labour ward is midwifery‐led or not, whether it has a paediatric department or not, etc.

• A planned home birth is a birth planned prior to labour to take place at home and planned to be attended by a midwife or others with midwifery skills (UNFPA 2012), who in turn are backed up by a modern hospital system.

We did not consider stand‐alone midwifery units and any other institutional settings 'home'.

Births that had not been planned to take place either at a hospital or at home (or any other adequate private address, e.g. a summer cottage or a friend's home) prior to labour were not considered planned births. 

Types of outcome measures

Reporting the outcome measures listed below was not a criterion for study inclusion. 

Primary outcomes

• Maternal mortality                                  

• Perinatal mortality (non‐malformed)      

• Apgar < 7 at 5 minutes

• Transfer to neonatal intensive care unit (NICU)

• Caesarean section                          

• Baby not breastfed                       

• Maternal satisfaction                    

Secondary outcomes

Secondary outcomes

As low‐risk birth is not a disease; as both home and hospital birth can have many diverse physiological and psychosocial effects and side effects (both short term and long term); and as the aim of the review was to assess the “price paid” for a general policy based on the belief that planned hospital birth is always the safest for all women including low‐risk women (Olsen 1997b), the list of secondary outcomes must be long, as follows.

• Transportation

• Doorstep cardiotocography (CTG)

• Vaginal exploration 

• Medical augmentation

• Epidural

• Other medical pain relief (non‐epidural)

• Non‐medical pain relief

• Assisted vaginal birth

• Episiotomy 

• Perineal trauma

• Caesarean section

• Absence of immediate skin‐to‐skin contact between mother and newborn 

• Resuscitation

• Early cord clamping

• Haemoglobin concentrations (24 to 48 hours)

• Iron stores in infants (3 to 6 months)

• Jaundice

• Other short‐term neonatal morbidity 

• Long‐term child morbidity (i.e. diabetes, atopy) 

• Haemorrhage more than 1000 mL

• Other short‐term maternal morbidity

• Disrespectful care

• Placenta accreta in next pregnancies

• Operational delivery in next pregnancies

• Other complications in next pregnancies

• Maternal mortality in next pregnancies

• Neonatal mortality in next pregnancies

Search methods for identification of studies

Electronic searches

For this update, we received search results from the Cochrane Pregnancy and Childbirth’s Trials Register via their Information Specialist (16 July 2021).

This Register is a database containing over 34,000 reports of controlled trials in the field of pregnancy and childbirth. It represents over 30 years of searching. For full current search methods used to populate Pregnancy and Childbirth’s Trials Register including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link.

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

• monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL) (which includes Cochrane's centralised search of the WHO International Clinical Trials Registry Platform (ICTRP));

• weekly searches of MEDLINE (Ovid);

• weekly searches of Embase (Ovid);

• monthly searches of CINAHL (EBSCO);

• handsearches of 30 journals and the proceedings of major conferences;

• weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.

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

In addition, we searched ClinicalTrials.gov for unpublished, planned, and ongoing trial reports (16 July 2021) using the search methods detailed in Appendix 1.

Searching other resources

We searched the reference lists of retrieved studies. We did not apply any language or date restrictions.  We also revisited all studies included and awaiting classification from the previous published version.

Data collection and analysis

For methods used in the previous version of this review, see Olsen 2012.

Screening eligible studies for trustworthiness

All studies meeting our inclusion criteria were evaluated by the two review authors against predefined criteria to select studies that, based on available information, were deemed to be sufficiently trustworthy to be included in the analysis. Cochrane Pregnancy and Childbirth have developed a Trustworthiness Screening Tool (CPC‐TST), which includes the following criteria.

Research governance

• Are there any retraction notices or expressions of concern listed on the Retratction Watch Database relating to this study?

• Was the study prospectively registered (for those studies published after 2010) If not, was there a plausible reason?

• When requested, did the trial authors provide/share the protocol and/or ethics approval letter?

• Did the trial authors engage in communication with the Cochrane Review authors within the agreed timelines?

• Did the trial authors provide individual patient data (IPD) data upon request? If not, was there a plausible reason?

Baseline characteristics

• Is the study free from characteristics of the study participants that appear too similar (e.g. distribution of the mean (standard deviation) excessively narrow or excessively wide, as noted by Carlisle 2017)?

Feasibility

• Is the study free from characteristics could be implausible? (e.g. large numbers of women with a rare condition (such as severe cholestasis in pregnancy) recruited within 12 months);

• In cases with (close to) zero losses to follow‐up, is there a plausible explanation?

Results

• Is the study free from results that could be implausible? (e.g. massive risk reduction for main outcomes with small sample size)?

• Do the numbers randomised to each group suggest that adequate randomisation methods were used (e.g. is the study free from issues such as unexpectedly even numbers of women ‘randomised’ including a mismatch between the numbers and the methods, if the authors say ‘no blocking was used’ but still end up with equal numbers, or if the authors say they used ‘blocks of 4’ but the final numbers differ by 6)?

Studies assessed as being potentially ‘high risk’ were not included in the review. Where a study was classified as ‘high risk’, we attempted to contact the study authors to address any possible lack of information/concerns. We planned that in cases where we could not obtain contact details for the study authors, or where there was still inadequate information, we would add the study to ‘awaiting classification’ and describe the reasons for this categorisation and communications with the author (or lack of) in detail.

Abstracts

We planned to include data from abstracts only if, in addition to the trustworthiness assessment, the study authors had confirmed in writing that the data to be included in the review had come from the final analysis, and would not change. If such information was not available/provided, the study would remain in ‘awaiting classification’ (as above).

Please see Figure 2 for details.

2.

Applying the Cochrane Pregnancy and Childbirth Trustworthiness Screening Tool

Selection of studies

The two review authors, working independently, selected trials for inclusion in the review. We planned that any disagreements would be resolved by discussion.

Data extraction and management

Two review authors extracted data from the included studies onto a pre‐designed, agreed‐upon data extraction form. Any disagreements were resolved by discussion. When information regarding any of the above was unclear, we contacted authors of the original reports to provide further details. We entered these data into RevMan Web (RevMan Web 2022), and checked the data for accuracy. 

Assessment of risk of bias in included studies

Two review authors independently assessed risk of bias for each study using the the revised Cochrane Pregnancy and Childbirth Group (CPCG) template data extraction form, supplemented with the CPCG methods standard text, Gates 2010, and criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved any disagreements by discussion.

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

We described for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We assessed the method as:

• low risk of bias (any truly random process, e.g. random number table; computer random number generator);

• high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);

• unclear risk of bias.

(2) Allocation concealment (checking for possible selection bias)

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

We assessed the methods as:

• low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes);

• high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);

• unclear risk of bias.

(3.1) Blinding of participants and personnel (checking for possible performance bias)

We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered studies to be at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect the results. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed the methods as:

• low, high, or unclear risk of bias for participants;

• low, high, or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

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

We assessed methods used to blind outcome assessment as:

• low, high, or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature, and handling of incomplete outcome data)

We described for each included study, and for each class of outcomes, the completeness of data including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. To be included in the review, data on a given outcome had to be available for at least 80% of those who were originally randomised. We recognise that for outcomes collected post‐hospital discharge, follow‐up can be difficult. Therefore, we included data if the response rate was higher than 75% and there was no obvious imbalance in groups. Where sufficient information was reported, or could be supplied by the trial authors, we planned to re‐include missing data in the analyses. We assessed methods as:

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

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);

• unclear risk of bias.

(5) Selective reporting (checking for reporting bias)

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

We assessed the methods as:

• low risk of bias (where it was clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review had been reported);

• high risk of bias (where not all of the study’s prespecified outcomes had been reported; one or more reported primary outcomes were not prespecified; outcomes of interest were reported incompletely and so could not be used; the study failed to include results of a key outcome that would be expected to have been reported);

• unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

We planned to describe for each included study any important concerns we had about other possible sources of bias, including, for example, whether the trial was stopped early due to a data‐dependent process; there was evidence of extreme baseline imbalance; or there had been claims of fraud or misconduct. We assessed whether each study was free of other problems that could put it at risk of bias as:

• low risk of other bias;

• high risk of other bias;

• unclear whether there is risk of other bias.

(7) Overall risk of bias [See table 8.5c in the Handbook]

We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the CochraneHandbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it likely to impact on the findings. 

Measures of treatment effect

Dichotomous data

One of our primary outcomes was satisfaction, a variable that in some studies is measured as ‘satisfaction’ (Waldenström 2000), and in other studies as ‘dissatisfaction’ (Hodnett 2010). A similar ‘reversal of scale’ may be seen in other outcomes with a high incidence. As the odds ratio (OR) is invariant and equally valid in such cases irrespective of direction, and because we had many sparse data, we presented results as summary Peto odds ratios with 95% confidence intervals (CIs).

Continuous data

We encountered no continuous data among the prespecified outcomes.

For continuous data in forthcoming studies, we will use the mean difference (MD) if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measure the same outcome but that use different methods.

Unit of analysis issues

Cluster‐randomised trials

Had we found cluster‐randomised trials, we would have included them in the analyses along with individually randomised trials. We planned to adjust the sample sizes of cluster‐randomised trials using the methods described in Chapter 23 of the Cochrane Handbook (Higgins 2022), employing an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), from a similar trial, or from a study of a similar population. Had we used ICCs from other sources, we would have reported this and conducted sensitivity analyses to investigate the effect of variation in the ICC. In future updates, if we identify both cluster‐randomised trials and individually randomised trials, we will synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between study designs, and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely. We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Dealing with missing data

We noted levels of attrition in the included studies. For outcomes that occurred prior to hospital discharge, we only included data if they were available for at least 80% of those originally randomised. For outcomes collected post‐hospital discharge, we included data if the response rate was higher than 75%, and there was no obvious imbalance in groups. Had we found studies with high levels of missing data, we would have explored the impact of including them in the overall assessment of treatment effect using sensitivity analysis.

For all outcomes, we have carried out analyses, as far as possible, on an intention‐to‐treat basis, that is we attempted to include all participants randomised to each group in the analyses, and all participants were analysed in the group to which they had been allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial was the number randomised minus any participants whose outcomes were known to be missing.

Assessment of heterogeneity

In future updates of this review, if we include more than two trials with more than 20 participants in total contributing informative data to this review, we will follow standard advice as published in the then current Cochrane Handbook for Systematic Reviews of Interventions. Should this happen in the near future, we will assess statistical heterogeneity in each meta‐analysis using the Tau², I², and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either Tau² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity.

Assessment of reporting biases

If in future updates of this review there are 10 or more studies in the meta‐analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

We carried out statistical analysis using RevMan Web (RevMan Web 2022). We planned to use fixed‐effect meta‐analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect, that is where trials were examining the same intervention, and the trials’ populations and methods were judged sufficiently similar. If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or if substantial statistical heterogeneity was detected, we would use random‐effects meta‐analysis to produce an overall summary if an average treatment effect across trials was considered clinically meaningful. We planned to treat the random‐effects summary as the average of the range of possible treatment effects, and discuss the clinical implications of treatment effects differing between trials. We planned that if the average treatment effect was not clinically meaningful, we would not combine trials. If we used random‐effects analyses, we would present the results as the average treatment effect with 95% CIs, and the estimates of Tau² and I².

Subgroup analysis and investigation of heterogeneity

If in future updates more than two trials with more than 20 participants in total are identified and there is substantial heterogeneity, we will investigate the heterogeneity using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random‐effects analysis to produce it. Under these conditions we plan to carry out subgroup analyses for parity. In order to avoid too many chance findings and a great amount of non‐informative subgroup analyses, we will perform subgroup analyses for any primary outcome only when the individual outcome has more than 20 events (counted from either end of the scale) in total. We will assess subgroup differences by interaction tests available within RevMan Web (RevMan Web 2022). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.

Sensitivity analysis

We plan that as soon as a new trial has been announced in a trial database, we will follow standard advice as published in the then current Cochrane Handbook for Systematic Reviews of Interventions. As it is stated in the now current version of the Cochrane Handbook: “Some sensitivity analyses can be pre‐specified in the study protocol, but many issues suitable for sensitivity analysis are only identified during the review process where the individual peculiarities of the studies under investigation are identified” (Higgins 2022). Currently, no certain conclusions can be drawn based on the very small included feasibility trial. Any sensitivity analysis with any subset of the only included trial or any subset of its 11 observations will reach the same conclusion as the main analysis: the evidence is uncertain. Given the speed of progress (none) in setting up new trials in recent decades, a detailed description of possible sensitivity analyses is not currently meaningful. However, should Cochrane Pregnancy and Childbirth decide to widen the fifth eligibility criterion, study design, described in Section 10.14 of the Cochrane Handbook, and allow non‐randomised studies to be included, serious sensitivity analyses could be carried out. We will plan these sensitivity analyses in detail if and when Cochrane Pregnancy and Childbirth decides to widen the range of design types.

Summary of findings and assessment of the certainty of the evidence

We assessed the certainty of the evidence for the following outcomes using the GRADE approach as outlined in the GRADE Handbook (Schünemann 2013). 

• Maternal mortality                                  

• Perinatal mortality (non‐malformed)      

• Apgar < 7 at 5 minutes

• Transfer to neonatal intensive care unit (NICU)

• Caesarean section                          

• Baby not breastfed                       

• Maternal satisfaction   

We used GRADEpro GDT (GRADEpro GDT), along with RevMan Web (RevMan Web 2022), to create a summary of findings table. We produced a summary of the intervention effect and, where possible, a measure of certainty for each of the above outcomes using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the body of evidence for each outcome. Randomised controlled trial data are initially considered to be high‐certainty evidence. Evidence can be downgraded by one level for serious (or by two levels for very serious) limitations, depending on assessments of risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates, or potential publication bias.

Results

Description of studies

Results of the search

For this update, the July 2021 search did not identify any new RCTs. There were no new trial reports in the Cochrane Pregnancy and Childbirth Trials Register, and the additional trials registry search did not retrieve any relevant unpublished or ongoing trials. We reassessed and excluded Hendrix 2009, which was awaiting classification in the previous version of the review. 

The electronic searches retrieved six references for full‐text assessment for the first version of this review (Olsen 1998). In 2009, an additional reference was identified and was assessed as awaiting classification (Hendrix 2009); on closer investigation we found that it referred to a trial not previously identified. We excluded the Hendrix 2009 study in the current update (see Excluded studies). The current review includes one study that was reassessed and met our criteria for trustworthiness (Dowswell 1996); for details, see Characteristics of included studies. (See: Figure 3 ).

3.

Study flow and jump diagram.

Included studies

The included study was conducted in the UK and recruited multiparous women judged to be at low obstetric risk by a consultant obstetrician (n = 71) and likely to have suitable home support and home circumstances (n = 11) (Dowswell 1996). Recruitment was carried out by one consultant obstetrician in an area where planned home birth was otherwise uncommon (0.5% to 1%). The midwives assisting the home births were community midwives who spent a few days each month in hospital; all UK midwives are trained to do home births, but the ones in the trial were probably not experienced with home birth. The hospital births were standard hospital care with intermittent auscultation at a university hospital with consultant obstetrician on call (but not called routinely) and full neonatal facilities. One midwife served one to two women in single rooms; she used intermittent auscultation and was not continuously present. Dates of the study, funding sources, and declarations of interest of primary researchers were not reported by the trial authors.

Studies awaiting classification

No studies are awaiting classification.

Excluded studies

We excluded a total of six studies, five that had been excluded in the previous version of this revew (Bateman 1994; Berghs 1995; MacVicar 1993; O'Connor 1986; Truffert 1998), and one newly excluded for this update (Hendrix 2009).  The newly excluded study was previously in awaiting classification (Hendrix 2009); it has now been excluded because only one woman was randomised, and after investigating women's reasons for not participating in the RCT, the trialists decided to stop the RCT and continue the study as a cohort study (van Haaren‐ten 2015). The randomised woman was informed of this and eventually included in the cohort study and allowed to choose where she wanted to give birth. The trialists have been contacted but cannot provide any outcomes specifically from the woman randomised. 

Five studies were identified via a previous search of CENTRAL/CCTR with the MeSH term Home Childbirth. Four studies were not RCTs or clinical controlled trials (Bateman 1994; Berghs 1995; O'Connor 1986; Truffert 1998), and the fifth study compared "simulated home delivery in hospital" with hospital birth and thus did not fulfil the criteria to be labelled with the MeSH term Home Childbirth, nor did it fulfil the inclusion criteria of this review (MacVicar 1993).

Risk of bias in included studies

The included study was at high risk of bias for four out of seven domains (Figure 4; Figure 5). For details, see Characteristics of included studies.

4.

'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.

5.

'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.

Allocation

Random sequence generation

On correspondence with one of the trial authors, it was confirmed that the sequence was computer‐generated. Randomisation was in the ratio 1:1 in balanced blocks of eight. We thus assessed risk of bias as low.

Allocation concealment

Numbered, opaque, sealed envelopes contained the trial allocation. We thus assessed risk of bias as low.

Blinding

There was no blinding of participants and personnel or outcome assessors. We thus assessed risk of bias as high. 

Incomplete outcome data

One woman allocated to delivery at home was excluded after randomisation because she was found to have had a previous postpartum haemorrhage. Intention‐to‐treat analysis of obstetric outcomes was carried out. The excluded woman was not included in the analysis of questions regarding satisfaction. The one woman with partially missing data constituted less than 20% of the entire sample. We thus assessed risk of bias as low.

Selective reporting

Not all outcomes registered in the trial were published, and data now seem to have been lost. This is a concern in terms of bias, since it is unclear which data were lost and if, for example, these data might have shown large or small effects for either arm of the study. We thus assessed risk of bias as high.

Other potential sources of bias

No other sources of bias were identified.

Effects of interventions

See: Table 1

The one included small feasibility trial, Dowswell 1996, did not report on five of the seven primary outcomes, reported zero events for one primary outcome (caesarean section), and non‐zero events for the remaining primary outcome (baby not breastfed). Maternal mortality, perinatal mortality (non‐malformed), Apgar < 7 at 5 minutes, transfer to neonatal intensive care unit (NICU), and maternal satisfaction were not reported.

The small feasibility trial, Dowswell 1996, with reported outcomes, was too small to draw any reliable conclusions. For the two primary outcomes that were reported, the evidence was found to be very uncertain: caesarean section (odds ratio (OR) not estimable due to zero events; very low certainty evidence; Analysis 1.1) and baby not breastfed (OR 1.84, 95% confidence interval (CI) 0.15 to 23.38; very low certainty evidence; Analysis 1.2). The evidence was also very uncertain for the following secondary outcomes: other (non‐epidural) medical pain relief (Analysis 1.3: nitrous oxide and oxygen OR 0.54, 95% CI 0.04 to 6.89; pethidine OR 6.25, 95% CI 0.12 to 320.40) and assisted vaginal birth (OR not estimable due to zero events; Analysis 1.4). In addition, three other, non‐prespecified outcomes were reported, and these are also included here, again all with very low certainty evidence: perineal sutures (OR 1.44, 95% CI 0.15 to 14.00; Analysis 1.5); mother disappointed about allocation (OR 12.18, 95% CI 1.05 to 141.17; Analysis 1.6); and father did not state that he was relieved (OR 0.19, 95% CI 0.00 to 10.32; Analysis 1.7).

1.1. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 1: Caesarean section

1.2. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 2: Baby not breastfed

1.3. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 3: Other (non‐epidural) medical pain relief

1.4. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 4: Assisted vaginal birth

1.5. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 5: Perineal sutures 

1.6. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 6: Mother disappointed about allocation

1.7. Analysis.

Comparison 1: Planned hospital birth versus planned home birth, Outcome 7: Father did not state that he was relieved

No data were identified for our other prespecified outcomes or for any unintended effects that might be encountered as part of the 'cascade of interventions'.

Discussion

Summary of main results

The included study was at high risk of bias for four out of seven domains and with evidence for outcomes either absent, not estimable, or of very low certainty. It is impossible to balance important benefits against important harms as described in the Background section as long as only evidence from randomised studies is acceptable (Gates 2012); it will probably remain so for the next many years. 

Overall completeness and applicability of evidence

The included study cannot sufficiently address the objectives of this review.  

The most important finding at the time the trial was carried out was that it was possible to randomise women to either home or hospital birth in areas where home birth was available as part of the general maternity care but at the same time was not a commonly known option (Olsen 2012). On the other hand, it seems impossible to randomise women in areas where women already are well‐informed about the possibility of home birth (Olsen 2011). Considering that the observational evidence against planned hospital birth has strengthened since the feasibility trial (Dowswell 1996), it is probably no longer ethical to set up trials anywhere in the world where an established home birth service exists, nor would well‐informed women be expected to volunteer to be randomised.

Quality of the evidence

The majority of primary outcomes were not reported and thus not assessed for certainty. The overall certainty of the evidence for the remaining two primary outcomes was very low according to our GRADE assessment (downgraded by two levels for substantial imprecision and two levels for high overall risk of bias, the latter due to lack of blinding, high risk of selective reporting, and inability to check for publication bias; see Table 1). It is impossible to draw any firm conclusions. Further research is unlikely to provide better data in the foreseeable future and thus alter our overall conclusion.

Potential biases in the review process

The inclusion of only randomised trials prevents bias towards strong but misleading conclusions. However, this restriction excludes a large body of evidence from observational studies of a fairly high quality, potentially introducing the misleading impression that almost nothing is known about the potential effects of planned hospital versus planned home birth (Berghella 2008). In general, over‐reliance on only RCTs should be avoided (Abbasi 2022; Jadad 2007), and this review may provide a good example of a field where evidence from good observational studies is a sine qua non.

Agreements and disagreements with other studies or reviews

The weak evidence from one not fully reported randomised trial, Dowswell 1996, does not contradict evidence from the largest observational studies, de Jonge 2015; Nove 2012; Hutton 2016; de Jonge 2013;  Janssen 2009, identified in the most recent systematic reviews (Hutton 2019; Reitsma 2020); nor does it contradict the results of Cochrane Reviews of elements of care typical for hospital birth, Hodnett 2012; Downe 2013; Alfirevic 2017; Bricker 2000; Wojcieszek 2014, or of systematic reviews of qualitative studies related to planned hospital birth (Coxon 2017; Yuill 2020; Henshall 2016).

Authors' conclusions

Implications for practice.

This review shows that for selected, low‐risk pregnant women, the evidence from randomised trials to support that planned hospital birth reduces maternal or perinatal mortality or any other critical outcome is uncertain. 

The relative value of the benefits and harms of a planned hospital birth compared to a planned home birth attended by a midwife backed up by a modern hospital system (in case a transfer should turn out to be necessary) is likely to be highly relevant to individual women and couples making decisions about where to plan a forthcoming birth. Consulting with healthcare professionals during pregnancy will also be important to be reassured that both the woman’s health and her pregnancy are developing towards an expected normal birth. Finally, availability of a well‐organised home birth system as an alternative to a hospital birth is crucial. 

In addition to the relative benefits and harms, legislation and resource issues are factors that are likely to be relevant to decision‐making among healthcare providers and policymakers. With respect to legislation, the European Court of Human Rights in Strasbourg handed down a judgement stating that “the right to respect for private life includes the right to choose the circumstances of birth”. Thus, it is the woman's own decision to decide where to give birth, no matter the circumstances (Registrar 2010). If cost‐effectiveness in general is of critical importance in considering the organisation of maternity care, this issue might also be taken into consideration when deciding whether to de‐implement hospital birth as a first choice for healthy women with an expected normal birth, and instead consider establishing home birth services with collaborative medical backup and offer low‐risk pregnant women information about the available evidence and the possible choices.

Implications for research.

The small trial conducted in the UK, Dowswell 1996, showed that randomising women to home or hospital delivery was feasible at that time (11/71 (15%) of the invited women accepted to be randomised), whereas the excluded Dutch trial, Hendrix 2009, showed that in a place where home birth at the time of the trial was part of standard care and where women were already well‐informed about the two options (Thomasson 2008), women did not wish to be randomised.

Evidence from observational studies suggests that planned hospital birth does not reduce mortality but may lead to more interventions, more complications, and more neonatal problems. If maternal or perinatal mortality is of prime concern, extremely large trials are required to definitively demonstrate with sufficient power that planned hospital birth reduces mortality as has been believed for many years; this will hardly ever be achievable, nor would it be ethical considering the lack of equipoise on a multitude of other outcomes. Midwives and obstetricians also seem not to see a need for randomised trials (FIGO and ICM 2012). Because systematic reviews of observational studies about home versus hospital birth based on a published protocol in which all steps were prespecified, most importantly inclusion criteria with regard to study design, population, type of intervention and relevant outcome measures as proposed in the previous version of this review (Olsen 2012), have been conducted (Hutton 2019; Reitsma 2020), the best way forward would probably be to systematically search for and critically assess such systematic reviews and include the results in this review, so that this review and the Cochrane Library continue to be the place to look for the best available evidence.

It is well known that it is a great challenge to conclude and act appropriately when "there is inconclusive evidence” (Schünemann 2011), and that the most difficult thing seems to be to say ‘I do not know’ (Chalmers 1983). As long as:

• the available evidence is considered too weak to provide strong advice; 

• systematic reviews of qualitative studies show provision of information and shared decision‐making relating to planned place of birth often suffer from organisational pressures and professional norms (Henshall 2016), rather than being evidence‐based and patient‐centred; 

• planned hospital birth remains the ‘standard procedure’ and women considering birth at home often encounter obstacles and need to 'counter the negativity' surrounding home birth (Coxon 2017); 

it might be worthwhile initiating action research projects primarily involving women and midwives but also involving change facilitators (Changing Dojo 2016; Lessard 2016), policymakers, healthcare providers and obstetricians, with a focus on participation and involvement (Armenakis 2002; Greenhalgh 2006), facilitation of de‐implementation, and other types of change (Lessard 2016), description of change (Greenhalgh 2006), and eventually measurement of effectiveness and satisfaction, as well as to initiate various types of public deliberation processes demonstrated in an RCT to be effective in increasing participants' knowledge of evidence and shifts in participants' attitudes regarding the role of evidence in decision‐making (Carman 2015).

Even though "[a]bandoning ineffective medical practices […] has the potential to improve outcomes for patients, and mitigate the unsustainable rise in healthcare costs" (Prasad 2014), "[d]e‐implementation […] is an emerging area of study in healthcare" (Parker 2022), and "there is a limited understanding of the individual and social behavioral aspects of de‐implementation" (Parker 2022). "Many barriers to evidence‐based de‐implementation have been identified on both systemic and individual levels, and much more research is needed to provide an evidence base for effective strategies for de‐implementation […] To tackle these issues, a broad collaboration needs to be established […] underpinned by better understanding of the perspectives and challenges for each of the stakeholders in the pathways between evidence and practice" (Clarke 2021).

It thus begs the question whether randomised trials are the most needed type of study. It might be worthwhile for Cochrane Pregnancy and Childbirth to consider whether some evidence from observational studies could successfully be included in some reviews under their control (e.g. reviews including only low‐risk pregnant women and only for very rare outcomes) on the condition that the guidelines in the Cochrane Handbook for Systematic Reviews of Interventions are followed.  Given that 'first do no harm' is a basic principle in health care and as long as low‐risk women giving birth at hospital are exposed to overuse of interventions with potentially harmful effects (Cochrane 1979; Chalmers 1989; EURO‐PERISTAT 2008; Sakala 2008; Seijmonsbergen‐Schermers 2020), all of the above research is needed. As values are so different among and between women, clinicians, scientists, and policymakers, it is difficult to prioritise between the research approaches. They are probably best undertaken in tandem.

Feedback

Feeback from Robin Kidder, 27 August 2013

Summary

The review text states: "Two trials met the inclusion criteria but only one trial involving 11 women provided some outcome data and was included. The evidence from this trial was of moderate quality and too small to allow conclusions to be drawn."

If this is the case, how can the review authors draw conclusions? As you say, the evidence is of moderate quality and too small to allow conclusions.

Comments submitted by Robin Kidder, August 2013

Reply

Thank you for reading the text of our review so carefully. The sentence you refer to is at from the results section of the abstract, and it refers to the “effects of interventions” section of the main review results. The Cochrane Handbook section “11.8 Writing an abstract” states that “Abstracts to Cochrane reviews are published in MEDLINE and the Science Citation Index, and are made freely available on the internet. It is therefore important that they can be read as stand‐alone documents”. We realize that we haven’t fully achieved this. Thus, in order to clarify the text we have amended this sentence in the abstract to “The evidence from this trial was of moderate quality and too small to allow conclusions about the effects of the interventions to be drawn”.

Contributors

Response from Ole Olsen and Jette Aaroe Clausen, February 2014

What's new

Date	Event	Description
7 March 2023	New search has been performed	Search updated. Did not identify any new RCTs.
7 March 2023	New citation required and conclusions have changed	No new studies have been included. However, because the methodological and clinical context has changed combined with the increasing emphasis on patient rights, the implications for practice from the one very tiny included trial has ‐ somewhat surprisingly ‐ changed.

History

Protocol first published: Issue 2, 1997
Review first published: Issue 3, 1998

Date	Event	Description
10 April 2014	Feedback has been incorporated	Response to Feedback 1 from Ole Olsen and Jette Aaroe Clausen
27 August 2013	Feedback has been incorporated	Feedback 1 received from Robin Kidder.
25 January 2013	Amended	External source of support added.
30 March 2012	New search has been performed	Search updated.
7 August 2011	New citation required and conclusions have changed	A new trial has been identified and is awaiting classification (Hendrix 2009). All sections have been almost completely rewritten. A new second author has replaced the previous second author.
25 September 2009	New search has been performed	Search updated. No new trials identified.
3 September 2008	Amended	Converted to new review format
30 April 2006	New search has been performed	Search updated, but no new trials identified.

Appendices

Appendix 1. Search methods for ClinicalTrials.gov

Advanced search 

(16 July 2021)

Interventional Studies | home birth

Data and analyses

Comparison 1. Planned hospital birth versus planned home birth.

Outcome or subgroup title	No. of studies	No. of participants	Statistical method	Effect size
1.1 Caesarean section	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	Not estimable
1.2 Baby not breastfed	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	1.84 [0.15, 23.38]
1.3 Other (non‐epidural) medical pain relief	1		Peto Odds Ratio (Peto, Fixed, 95% CI)	Subtotals only
1.3.1 Nitrous oxide and oxygen	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	0.54 [0.04, 6.89]
1.3.2 Pethidine	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	6.25 [0.12, 320.40]
1.4 Assisted vaginal birth	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	Not estimable
1.5 Perineal sutures	1	11	Peto Odds Ratio (Peto, Fixed, 95% CI)	1.44 [0.15, 14.00]
1.6 Mother disappointed about allocation	1	10	Peto Odds Ratio (Peto, Fixed, 95% CI)	12.18 [1.05, 141.17]
1.7 Father did not state that he was relieved	1	10	Peto Odds Ratio (Peto, Fixed, 95% CI)	0.19 [0.00, 10.32]

Characteristics of studies

Characteristics of included studies [ordered by study ID]

Dowswell 1996.

Study characteristics
Methods	Randomisation was in the ratio 1:1 in balanced blocks of 8 and performed by opening the next in a series of numbered, opaque, sealed envelopes containing the trial allocation. No blinding. 1 woman allocated to delivery at home was excluded after randomisation because she was found to have had a previous postpartum haemorrhage. Intention‐to‐treat analysis of obstetric outcomes; in the analysis of questions regarding satisfaction, the excluded woman was not included.
Participants	11 multiparous women (5 experimental and 6 control) judged to be at low obstetric risk by a consultant obstetrician and likely to have suitable home support and home circumstances.
Interventions	Planned delivery at home or in hospital. (More detailed unpublished data were sought in 1997 for first version of the review, in 1998 for the next update and again in 2010 and 2011 for this update. The information has now been supplied by the consultant obstetrician according to his memory.) The midwives assisting the home births were community midwives who spent a few days each month in hospital but were probably not experienced with home birth. All UK midwives are trained to do home births and legally bound to assist a woman who asks for one. However, in practice some feel much more secure than others. So for planned home births midwives tend to self‐select enthusiasts. Home birth was generally available in the area to those who asked for it, but not routinely offered. The home birth rate in Leeds at that time was between 0.5% and 1%. The home birth midwives were different from the midwives taking care of the hospital births. Hospital birth was normal hospital care with intermittent auscultation, at a university hospital with consultant obstetrician on call (but not called routinely when the child was born) and full neonatal facilities. One midwife who was not continuously present served 1 to 2 women in single rooms.
Outcomes	The following seven outcomes are reported in the trial report: operative delivery, perineal sutures, nitrous oxide and oxygen, pethidine, baby not breastfed, mother disappointed about allocation, father did not state that he was relieved. The first five variables are presented in Table 1 of the trial report whereas the two latter outcomes are reported in the main text in the following way: “The four women allocated home birth who delivered at home were pleased with the allocation. However, four of the six women allocated delivery in hospital were disappointed, though one husband stated that he was relieved." (Unpublished data were sought in 1997 for first version of the review, in 1998 for the next update and again in 2010 and 2011 for this update; however, the trialists now consider data to be lost.)
Notes	Dates of study: This information is not reported by the trial authors. Funding sources: This information is not reported by the trial authors. Declarations of interest: This information is not reported by the trial authors.
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Low risk	Computer generated according to correspondence with trial author "I’m sure it was by computer. Andy Vail generated the sequence for us". Mail reply from J Thornton, 7 July 2011
Allocation concealment (selection bias)	Low risk	"Randomization was in the ratio 1:1 in balanced blocks of eight and performed by opening the next in a series of numbered opaque sealed envelopes containing the trial allocation."
Blinding of participants and personnel (performance bias) All outcomes	High risk	Impossible to blind
Blinding of outcome assessment (detection bias) All outcomes	High risk	Not blinded
Incomplete outcome data (attrition bias) All Outcomes	Low risk	One woman allocated to delivery at home was excluded after randomisation because she was found to have had a previous postpartum haemorrhage. Intention‐to‐treat analysis was carried out for the obstetric outcomes operative delivery, perineal sutures, nitrous oxide and oxygen, pethidine, and baby not breastfed. In the analysis of the outcome mother disappointed about allocation the excluded woman was not included. The one woman with partly missing data constituted less than 20% of the entire sample. We thus assessed the risk of bias as low.
Selective reporting (reporting bias)	High risk	Complications recorded according to the text but not reported in table. Data presumably lost according to trialist (mail reply from T Dowswell, Dec 21, 2010). Comment: the reported outcomes are fairly standard and seem to be a fair choice of outcomes considering it is a feasibility trial not published as a full report. So we do not suspect selective reporting though we cannot be sure.
Other bias	Low risk	No reasons to suspect other types of bias.

Characteristics of excluded studies [ordered by study ID]

Study	Reason for exclusion
Bateman 1994	This is a retrospective study of unplanned and unattended home births. It is not a trial.
Berghs 1995	This is an observational study, not a trial.
Hendrix 2009	When the trialist realised that only one woman was randomised, and after investigating women's reasons for not participating in the RCT (Hendrix 2009), the trialists decided to stop the RCT and continue the study as a cohort study (van Haaren‐ten 2015). The randomised woman was informed of this and eventually included in the cohort study and allowed to choose where she wanted to give birth. The trialists have been contacted but cannot provide any outcomes from the randomised woman specifically. The trial is therefore excluded.
MacVicar 1993	The trial is not studying true home birth but "simulated home delivery in hospital".
O'Connor 1986	The trial is not studying home birth but vitamin K1.
Truffert 1998	This is an observational study and not a trial.

RCT: randomised controlled trial

Differences between protocol and review

2022 update

During peer review of the previous update the title of the review was changed from 'Home versus hospital birth' to 'Planned hospital birth versus planned home birth', making planned hospital birth the experimental intervention (as it was also reasoned by Archie Cochrane when he awarded obstetrics the wooden spoon). This change of title and viewpoint was not fully reflected in the previous update of the review; we have thus made a minor change in the Objectives, and partly for this reason also more substantial changes in the Background section.

Since the previous update there have been increasing concerns that the “increasing medicalisation of childbirth processes tends to undermine the woman’s own capability to give birth and negatively impacts her childbirth experience” (WHO), while at the same time the knowledge about these and other negative effects of this increasing medicalisation has increased tremendously. Additionally, there have been increasing concerns that standard hospital procedures like caesarean sections may be under threat due to increasing prevalence of infections with bacteria resistant to most antibiotics (WHO). These changes are reflected in our very thorough update of the Background and Authors' conclusions.

Changes in review questions: as a consequence of the earlier change in the title, the first sentence in the Objectives has been modified (10 words moved). 

With respect to changes in methods, we have provided a more detailed description of types of studies not currently included in the review (as requested by the editorial office); a more detailed description of types of participants; and a more detailed description of types of intervention. We were also asked to reduce the number of primary outcomes dramatically. Considering the increasing medicalisation and the ensuing cascade of negative effects, this has been a challenging and not fully meaningful task. We have thus moved the deleted primary outcomes to the list of secondary outcomes and concomitantly updated the introductory text in order to relate the additionally added secondary outcomes to the updated section How the intervention might work. The following outcomes are now listed as secondary outcomes.

• Transportation

• Doorstep cardiotocography

• Vaginal exploration 

• Medical augmentation

• Epidural

• Other medical pain relief (non‐epidural)

• Non‐medical pain relief

• Assisted vaginal birth

• Episiotomy 

• Perineal trauma

• Caesarean section

• Absence of immediate skin‐to‐skin contact between mother and newborn 

• Resuscitation

• Early cord clamping

• Haemoglobin concentrations (24 to 48 hours)

• Iron stores in infants (3 to 6 months)

• Jaundice

• Other short‐term neonatal morbidity 

• Long‐term child morbidity (i.e. diabetes, atopy) 

• Haemorrhage more than 1000 mL

• Other short‐term maternal morbidity

• Disrespectful care

• Placenta accreta in next pregnancies

• Operational delivery in next pregnancies

• Other complications in next pregnancies

• Maternal mortality in next pregnancies

• Neonatal mortality in next pregnancies

We assessed the one included trial for trustworthiness and decided that it was trustworthy.

To comply with new terminology and the new tool for risk of bias assessment, we have reassessed the included trial using this new tool. This revision did not lead to any appreciable changes in the certainty of the evidence, only to use of an updated terminology.

We were also asked to report our results within the context of our GRADE assessments in line with the GRADE guidelines 26 (GRADE 2020). 

2012 review

The Background section has been updated and restructured according to the most recent guidelines in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The primary objective is the same as in the protocol for the first version of the review (except that types of people or problem and secondary analysis which were lacking have been added). The Methods section has been amended to be in accordance with the Cochrane Handbook for Systematic Reviews of Interventions and the Cochrane Pregnancy and Childbirth Group: Methodological Guidelines (Gates 2010).

Contributions of authors

Ole Olsen and Jette A Clausen both contributed to writing the text of this and the previous version of the updated review.

For the first version of this review, Ole Olsen performed the search, selected the trials, assessed trial quality, extracted data, wrote the draft review, and contacted study authors for additional information. David Jewell independently selected the trials to be included, checked the trial quality assessment and the extracted data, and suggested improvements to the manuscript.

Ole Olsen was sole author of the protocol and first author of the first version of the review.

Sources of support

Internal sources

• H:S Rigshospitalet, Denmark

  Salary for the first author for the first version of the review 

• National Research Centre for the Working Environment, Denmark

  Salary for the first author for the first update of the review

• The Research Unit for General Practice and Section of General Practice, Department of Public Health, University of Copenhagen, Denmark

  Part time salary and IT‐support for the first author for this update of the review

External sources

• National Institute for Health Research, UK

  NIHR Programme of centrally‐managed pregnancy and childbirth systematic reviews of priority to the NHS and users of the NHS:10/4001/02

Declarations of interest

Ole Olsen: In the 36 months prior to the RevMan file was made available for us to work on for our updated review and until our draft was accepted for publication I may have published opinions relevant to place of birth in two medical journals (Practicus and Månedsskrift for Almen Praksis).

Jette A Clausen: In the 36 months prior to the RevMan file was made available for us to work on for our updated review and until our draft was accepted for publication I may have published opinions relevant to place of birth in one medical journal (Women Birth).

New search for studies and content updated (conclusions changed)