We included all studies that fulfilled the inclusion criteria and that the authors considered of acceptable methodological quality, according to the critical appraisal tool from JBI SUMARI.41
Data were extracted from the included papers using the standardized JBI data extraction tool.41 Studies selected for retrieval are presented in Appendices II-IV. Appendix II presents general characteristics on included studies. Appendix III presents details on methods for estimation of due date, comparison groups, parity, and induction agents in included studies. Appendix IV presents an overview of outcome measures in included studies. Reasons for exclusion for screened, excluded studies are shown in Appendix V.
Data from the included studies were pooled in a statistical meta-analysis model using RevMan 5 (Copenhagen: The Nordic Cochrane Centre, Cochrane). To minimize errors all pooled statistics were subject to double data entry. Effect sizes expressed as risk ratios (for categorical data) and weighted mean differences (for continuous data) and corresponding 95% confidence intervals (CI) were calculated. Statistical heterogeneity was assessed in the meta-analysis using the I2 and chi-squared statistics, and heterogeneity was considered substantial if I2 >50% and P value < 0.10 in the chi-square test for heterogeneity.42 Subgroup-analysis according to type of study design were performed. Where statistical pooling was not possible the findings have been presented in narrative form, and with tables and figures where appropriate to facilitate interpretation.
Figure 4 shows the results of our search strategy, where 4212 records were identified in the first step. Of these 3442 were identified through database search and 770 from other sources. After abstract reading 33 studies remained for full text-reading, which further excluded 25 studies (Appendix V). We assessed eight full text papers for eligibility and excluded one due to inconsistent methods for due date estimation (i.e. many of the participants in the study had calculation by last menstrual period as the only calculation method). The remaining seven studies were selected for retrieval (Appendix II).
Seven studies were included: two randomized trials33,34 and two quasi-experimental trials13,43 with a total of 5119 participants,13,33,34,43 and three cohort studies with 356,338 participants.44-46
Assessment of risk of bias in randomized and quasi-experimental studies
Table 1 shows the scoring of the included randomized trials and quasi-experimental studies according to the JBI SUMARI critical appraisal tools for RCTs/quasi-experimental studies.41
Comparability at entry (selection bias, confounding) (Q1, Q3, Q6)
Randomization (Q1) and concealment of allocation to allocator (Q3) are important factors in the evaluation of whether the intervention and control groups were comparable at baseline. In two studies,33,34 randomization was conducted via computer or use of opaque sealed envelopes and, thus, scored as truly randomized and with allocation concealed from the allocator. In another study,43 allocation was determined by calendar period meaning that no clinician or researcher could affect allocation to treatment group in the clinical setting. Hence, this study was also considered to have truly random allocation. The Daskalakis study allocation was considered not truly random, as allocation was determined according to the attending physician's preference, and no information was presented as to how the participants were assigned a given physician.13 Question 6 serves to corroborate the randomization in the studies, i.e. only when baseline characteristics turn out to be similar in the two groups is confounding truly minimized, as compared to observational studies. For all four studies, we considered treatment and comparison groups to be comparable at entry. Even though the Daskalakis study only presented a few baseline characteristics (age, parity and ethnicity), the groups were considered comparable, because no statistically significant differences were seen for the examined characteristics.
Blinding (Q2, Q5)
Blinding is used in trials to enhance group comparability and minimize confounding. When the intervention under study is labor induction, concealment of treatment group to participants is not possible. Hence, all included trials were assigned a “no” in Q2, meaning that in none of the studies the participants were blinded to treatment allocation. In the two quasi-experimental studies, the studies were planned and data extracted retrospectively.13,43 Hence, by the time of data collection, neither participants nor clinicians were aware that a comparison would be made between induction and expectant management, and, thus, were not affected by a knowledge of an ongoing trial in the assessment of outcomes. Even so, in the clinical situation the assessment and registration of outcomes for a participant is likely affected by the individual clinician's knowledge on induction vs. expectant management. This poses a risk of bias on the part of clinicians. For the included outcomes, however, we considered lack of blinding by the time of data collection of limited importance due to the character of the outcomes. Concealment of treatment group by the time of analysis is also difficult for labor induction. One study, however, blinded the researcher to some extent by blinding information on tachycardia and hyperstimulation in order to prevent the effects of researcher knowledge of treatment when evaluating outcomes.34
Loss to follow-up and treatment differences (selection bias) (Q4, Q7)
Question 4 addresses selection bias due to loss of follow-up and concerns information on outcome for participants who withdrew from the study. By design, the two quasi-experimental trials could not have any withdrawals and were therefore assigned “not applicable” in Q4. The two RCTs fulfilled this criterion. Question 7 addresses treatment differences between groups other than the intervention of interest, which may induce selection bias. In two studies we considered treatment of participants to be similar in the compared groups.13,33 In one study it was unclear whether groups were treated identically, since deliveries took place during different calendar periods, and no information was given as to any other potential changes in procedures between the two periods.46 The total study period, however, was no longer than three years, and the intervention period followed the control period immediately, indicating a limited risk of important time-dependent bias. In one study, the design allowed for systematic differences in induction methods between groups34 and, thus, we considered groups not to be properly comparable. In this study, the intervention group included deliveries induced by misoprostol medical treatment, oxytocin medical treatment, or Foley-catheter, while those in the expectant group, who had not gone into spontaneous labor at 41+0–6 GW and were induced at 42+0–6 GW, were all treated with misoprostol as induction agent.
Outcome assessment (Q8, Q9)
Questions 8 and 9 relate to differences in outcome measurement between groups and reliability in the measurements. For all four randomized trials, we considered outcomes as measured in the same reliable way, including the use of international standardized measures (e.g. CS, Apgar score). In one study, the authors had generated a composite outcome of neonatal morbidity33 that did not rely on solid empirical basis, which may impose some degree of uncertainty about this measure.
Statistical analysis (Q10)
All studies presented intention-to-treat analyses, which is considered a relevant method in RCTs. In one study additional sensitivity analyses were performed.33 The same study also presented analyses with imputation of missing data (e.g. on pH-values in the newborn). The three other studies did not explain how they handled missing data.
Assessment of risk of bias in cohort studies
Table 2 shows the scoring of the included cohort studies according to the JBI SUMARI critical appraisal tools for cohort studies.41
Question 1 concerns generalizability of included cohort studies. For all three studies, we considered study populations to be representative of the background population.
Comparability at entry (selection bias, confounding) (Q2, Q3, Q4)
Question 2 concerns possible differences between groups at study entry. For two studies, we considered groups to be comparable at the time of inclusion.44,46 In one study, it was not clear whether participants in the expectant group were at a poorer health status at 41+0–6 GW than the intervention group, because risk status was assessed at 39+0 GW.45 Authors were approached, but we did not achieve contact. The degree of possible bias was therefore not able to be assessed. Question 3 concerns allocation into the intervention and expectant groups. For all three studies, we found that bias had been minimized with regard to allocation to the two groups. Question 4 asks about proper identification and handling of confounding factors. In two studies we regarded this to be appropriate,44,46 whereas the third study lacked important confounding variables, such as smoking and BMI.45
Follow-up period (Q6)
All studies had follow-up periods long enough to evaluate the outcomes of interest.
Loss to follow-up (Q7)
As was the case for the randomized and quasi-experimental studies, due to the design of the studies and the character of the intervention under study, no participants withdrew, and, thus, all studies were assigned “not applicable” in Question 7.
Outcome measurement (comparability, measurement error) (Q5, Q8)
The questions 5 and 8 regard measurement of outcome. This review includes several different outcomes, and we estimated that the vast majority of these followed objective criteria and were measured in a reliable way in all three studies. One study lacked precise definitions on outcomes, such as birth injury, chorioamnionitis, and labor dystocia,45 but we did not consider this an important limitation to the results.
Statistical analysis (Q9)
We considered all studies to have used appropriate statistical methods for analysis. One study, though, did not perform adjustment for confounders, because such information was not available.44 Even though confounder adjustment is a desirable tool in cohort analyses, we concluded that the authors had used proper statistical tools, given the available data. It should be noted, that none of the three cohort studies presented information on the presence or handling of missing data. It is therefore not possible to evaluate possible biases related to missing information.
Overall, the included studies had fair methodological quality according to their respective study design. None of the experimental studies performed blinding of participants or clinicians to treatment allocation, but since this is not possible for induction of labor, we do not consider this a serious bias source. Generally, we considered treatment groups comparable at entry, though one quasi-randomized and one cohort study might be prone to selection bias. Further, we considered outcomes to be measured appropriately, data analyzed by appropriate methods, follow-up periods to be adequate, and for cohort studies, the study populations were reasonably representative of the background population.
Perinatal and maternal outcomes are presented and evaluated according to induction vs. expectant management, as follows.
Table 3 gives an overview of all pooled risk estimates for perinatal outcomes. Individual meta-analyses are presented in Appendix VI.
Perinatal outcomes (primary)
Routine induction at 41+0–6 GW was associated with an almost doubled risk of low pH (< 7.10) compared to expectant management on pooled data from two RCTs (relative risk [RR] 1.90, 95% CI 1.48, 2.43). No association was observed for low Apgar score (< 7 after 5 minutes).
Perinatal outcomes (secondary)
The analysis showed a reduced risk in the induction group of oligohydramnios (RRRCT 0.40, 95% CI 0.24, 0.67), meconium stained amniotic fluid (RRRCT 0.82, 95% CI 0.75, 0.91), and shoulder dystocia (RRRCT 0.28, 95% CI 0.08, 1.00) compared to the expectant group. The latter, however, with substantially broad CI. The analysis on meconium stained amniotic fluid was compromised by substantial heterogeneity.
Perinatal death was not associated with either labor induction or expectant management; data showed a relative risk of 0.22 (95% CI 0.04, 1.32) in the intervention group compared to expectant management based on pooled data from four RCTs. This corresponds to an absolute risk reduction in perinatal death of 0.002 for routine induction at 41+0–6 GW compared to 42+0–6 GW. In other words, one prevented perinatal death per 501 inductions (95% CI 247 to 18,439) or two saved lives per 1000 inductions. Since perinatal deaths are rare, and results based on small numbers may cause important changes in clinical procedures, each perinatal death event should be described and choices on whether to include each of the events in final analysis explained. In this review, it was a criterion for inclusion of participants, that both fetus and mother were healthy and with no known risks at inclusion. This means that perinatal death events that were not related to either induction or expectant management were not included in the analysis. In the following, each perinatal death event in the included primary studies is evaluated: in the Heimstad study, one neonatal death was reported in the expectant group.33 This fatal event occurred during labor after normal cardiotocogram at admission, and cause of death was explained by a true umbilical cord knot. This event was not included in the meta-analysis, because the death reason is not likely to be related to the intervention. Including the event did not change any conclusions (data not shown). In the Gelisen study, one intrauterine death was reported in the expectant group, but no explanation of the cause of death was given.34 The authors were contacted for clarification, but no response was obtained. Despite the lack of explanation, this event was included in the meta-analysis in order to present “worst case scenario”. Finally, the Burgos study comprised three perinatal deaths in the intervention group and seven in the expectant group.43 Four (two in each group) out of the fatal events within the first 28 days after birth were explained by severe congenital malformations. These four events were not included in the present meta-analysis. In the intervention group, we included one pre-labor intrauterine death, and in the expectant management group, we included four prenatal deaths and one neonatal death within the first 24 hours after birth from the Burgos study. From this, follows that the Burgos study contributed with 62% of the data in the meta-analysis and with six of the eight perinatal deaths included. It is unclear whether a relatively high mean age (32.8 years) and proportion of nulliparous women (63–64%) in the study could contribute to the relatively high incidence of perinatal death in the expectant arm compared to other studies on the topic.24,36 We contacted the authors for further details, who confirmed, that the expectant management group had antenatal control with CTG and amniotic fluid at 41+3/4 GW.
Table 4 gives an overview of all pooled risk estimates for maternal outcomes.
Maternal outcomes (primary)
All relative risks for different measures of CS were above 1.00 indicating an increased risk in the intervention group compared to expectant management. Statistical significance was found for overall CS (RRcohort 1.11 95% CI 1.09, 1.14) (one study, n = 74,860), CS due to failure to progress (RRRCT 1.43, 95% CI 1.01, 2.03) (two studies, n = 1038), and CS after previous vaginal birth (RRcohort 1.56, 95% CI 1.05, 2.34) (one study, n = 3165). The RCT-analysis on overall CS showed the same relative risk as the statistically significant cohort-analysis, but the estimate was just non-statistically significant. The analysis on CS due to failure to progress was compromised by substantial heterogeneity. Routine induction at 41+0–6 GW was associated with a 30% increased risk of instrumental vaginal delivery (RRcohort 1.30, 95% CI 1.24, 1.36) (one study, n = 49,628), while pooled data from three RCTs did not show any association.
Maternal outcomes (secondary)
For secondary maternal outcomes, all analyses except vaginal delivery were based on only one of the included studies. We found routine induction at 41+0–6 GW associated with an increased risk of chorioamnionitis (RRcohort 1.13, 95% CI 1.05, 1.21) (one study, n = 75,218), labor dystocia (RRcohort 1.29, 95% CI 1.22, 1.37) (one study, n = 51,473), precipitate labor (RRRCT 2.75, 95% CI 1.45, 5.20) (one study, n = 508), and uterine rupture (RRcohort 1.97, 95% CI 1.54, 2.52) (one study, n = 277,964). The RCT-analysis on labor dystocia suffered from substantial lack of statistical power and could not support any conclusions. None of the other outcomes were associated with the intervention, except for a borderline non-significantly elevated risk of maternal intensive care (RRcohort 1.59, 95% CI 0.96, 2.62) (one study, n = 277,964).
Additional findings: spontaneous onset of labor
Spontaneous onset of labor is a central element in the discussion on how to determine preferable timing of labor induction after due date. Even so, spontaneous onset of labor could not be examined in this review, because, by design, the intervention group will have close to zero spontaneous onsets of labor, and comparison with the expectant group would not make sense. Three studies, however, presented statistics on spontaneous onset of labor in the expectant group.13,33,43 In the RCT by Heimstad, participants were randomized to immediate induction at 41+2 GW (n = 254) or to expectant management up to 42+6 GW (n = 254).33 In the expectant group, 176 went into spontaneous labor (69%), 59 were induced due to medical reasons (most often oligohydramnios), while the remaining 19 women were still pregnant by 42+6 GW and had their labor induced. In the Daskalakis study, participants were selected for induction of labor at 41+1 GW (n = 211) or expectant management until 42+1 GW (n = 227) depending on the attending physician's preference.13 In the expectant group, 168 went into spontaneous onset of labor (74%), 31 were induced due to medical reasons, and 28 were still pregnant, and induced, by 42+1 GW. Finally, the quasi-experimental trial by Burgos found that with a policy of inducing at 42+0 GW, 71% had spontaneous onset of labor.43 This is in line with the pooled statistics from all three studies, where a total of 1584 out of 2227 women (71.4%), who followed expectant management, went into spontaneous labor during the expectant time window.13,33,43 Also, the two quasi-experimental studies13,43 experienced a 20% increase in inductions when using a guideline of recommending induction 41+0–6 GW.
Communicating benefits and harms
Risk differences have been shown to seem greater when presented in relative terms compared to absolute numbers.47,48 Researchers and clinicians need to be aware of this when communication scientific evidence to patients or policy makers. In order to make significant results more comprehensible Table 5 shows absolute risks (AR) and numbers needed to treat (NNT) for all outcomes with statistically significant results in Tables 3 and 4, and where estimates from observational and experimental analyses pointed in the same direction.
Absolute risk reduction (ARR) and absolute risk increase (ARI) are measures of the strength of the association, where the baseline risk in the induction and the expectant groups have been taken into account. For example, low pH will often be presented as RR = 1.90 or as a 90% increased risk after induction at 41+0–6 GW compared to expectant management. Since relative risks do not take into account the prevalence of low pH, it may be difficult for patients and stakeholders to consider the size of the problem. Using absolute numbers brings this aspect into the information given. In the case of low pH, the information could be that for every 1000 induced deliveries, 40 extra children would be born with a low pH compared to expectant management. Or, for every 25 induced deliveries, one extra child will be born with a low pH (with a 95% certainty between 18 and 41), and the last way to explain it is, that labor induction increases the number of children with low pH by 4%.
The aim of this systematic review was to evaluate the effects of induction of labor prior to post-term in low-risk pregnancies. Routine induction at 41+0–6 GW has become a widespread obstetric practice in many Western countries despite a lack of systematic reviews that address both harms and benefits of the intervention. Acknowledging the fact that our analyses are based on a limited number of primary studies, this review qualifies current knowledge and depicts critical methodological aspects in existing research in the field. In the following, we present main findings, discuss the quality of included studies, and describe important methodological problems in systematic reviews on labor induction. Implications for practice from changed guidelines and derived organizational/economic consequences are also touched upon, as well as the communication of systematic review results to patients.
In summary, we found induction at 41+0–6 GW associated with a few beneficial outcomes (e.g. a reduced risk of oligohydramnios and meconium stained amniotic fluid) and several adverse outcomes (e.g. an increased risk of precipitate labor, labor dystocia, CS, uterine rupture, chorioamnionitis and low pH in the newborn) compared to expectant management. As emphasized by the WHO, expected benefits from a medical intervention must outweigh potential harms.3
Overall, previous systematic reviews have found induction associated with a reduced risk of CS, perinatal death, meconium stained amniotic fluid and perhaps meconium aspiration syndrome with induction prior to post-term.6,35,36 Our results largely support previous findings on perinatal outcomes, except for perinatal death and aspiration syndrome. In regard to maternal outcomes, our findings generally do not support those of previous reviews, i.e. we found an increased risk of CS and several adverse outcomes.
Regarding perinatal outcomes, our findings are aligned with a systematic review by Caughey et al. 6 finding that evidence was insufficient to form conclusions for many of the key neonatal outcomes (e.g. neonatal death, fetal distress and asphyxia). As for perinatal death, our data indicated two possibly prevented fetal deaths per 1000 inductions with routine induction at 41+0–6 GW. However, conclusions could not be drawn due to lack of statistical power illustrated by a very broad CI in relative numbers (RR 0.22, 95% CI 0.04, 1.32) and, in absolute numbers, a range of 247 to 18,439 inductions to be performed to prevent one perinatal death. A Cochrane meta-analysis on induction of labor at or beyond term35 found that a policy of labor induction was associated with fewer (all-cause) perinatal deaths (RR 0.31, 95% CI 0.12, 0.88), and Wennerholm et al. 36 found a decreased risk of perinatal death (RR 0.33, 95% CI 0.10, 1.09), even though it was not statistically significant. In the Wennerholm study, only pregnancies beyond term were included, which makes this review more comparable to ours. Wennerholm et al. 36 found meconium aspiration syndrome to be reduced (RR 0.43, 95% CI 0.23, 0.79), and Caughey et al. and Gulmezoglu et al. found similar conclusions.6,35 Our data showed a decreased risk of meconium stained amniotic fluid, but we found no association with meconium aspiration syndrome. Further, we found an increased risk of pH < 7.10 in the newborn, which can be a serious acute condition and is associated with long-term consequences, such as cerebral palsy. On the other hand, we did not find low Apgar score associated with induction prior to post-term.
Regarding maternal outcomes, Wennerholm et al. 36 found a 13% decreased risk of CS after induction (RR 0.87, 95% CI 0.80–0.96), and the findings are supported by a Cochrane review35 and Caughey et al. 6 In the present review, we found an 11% increased risk of CS. We believe this is due to differences in methodology, which will be discussed below. The pooled RR for CS was statistically significant in the cohort analysis, but not in the analysis including four RCTs. The largest RCT, however, by Burgos43 which weighs 54%, found a significant increase in CS, which supports the conclusions from our cohort analysis. Cesarean section has been associated with an increased risk of excessive bleeding, pain, bladder disorders, hysterectomy, and neonatal death, and, in subsequent pregnancies, placenta previa, fetal death and uterine rupture.49-51 Finally, we found chorioamnionitis, labor dystocia, precipitate labor and uterine rupture associated with induction prior to post-term. Uterine rupture is a rare, but potentially life-threatening condition, and it imposes severe risks in subsequent pregnancies.52 Unfortunately, even though several adverse birth outcomes are associated with long-term risks, we were not able to evaluate such effects, since none of the primary studies included long-term outcomes.
Overall, the methodological quality of the included studies was considered high when assessed according to the JBI SUMARI critical appraisal tools for RCTs/quasi-experimental studies and observational studies, respectively. This was expected, because one of the main purposes of this review was to restrict data to updated studies. Generalizability and length of follow-up period (both relevant only for cohort studies), measurement and assessment of outcome and statistical analysis were the items best covered in the included studies. Comparability of groups at entry was not satisfactory in two out of seven studies. For example, in one quasi-experimental trial, assignment to treatment groups was determined according to the attending physician's preference. Selection bias due to loss of follow-up was minimal in the two RCTs that this criterion applied to, whereas one of the two RCTs was prone to selection bias due to treatment differences, because induction agents differed between groups.
The question(s) addressed in systematic reviews are said often to be (too) simple and (too) general, e.g. a title like “Elective Induction of Labor Versus Expectant Management of Pregnancy”6 may include all varieties of women, a broad variation in gestational age, different induction agents etc. This is the reason why careful attention should be paid to inclusion criteria, when systematic reviews are interpreted. Systematic reviews form the main evidence base for clinical guidelines today, and it is crucial that policy makers and stakeholders pay careful attention to the criteria for inclusion of studies, because inclusion criteria are central for a review's external validity and relevance.53
Regarding gestational age criteria, even though our literature search resulted in a large amount of papers on induction of labor versus expectant management, only a few studies compared the relatively tight timeframes of 41+0–6 GW and 42+0–6 GW, which reflects the new routine versus the old standard in many Western countries. Tight timeframes for comparison of the groups were chosen in the present review, because they reflect this change in practice. In the Cochrane review, only three of 22 randomized studies met this criterion, while the remaining 19 studies included variations from 37 GW up to expectant management with no upper time limit.35 In the present study, we only identified four RCTs or quasi-randomized trials (n = 5109) and three cohort studies (n = 356,338), that met our criteria regarding gestational age. We argue that meta-analyses that use broad criteria for gestational age in the expectant group are likely to overestimate poor fetal or maternal outcomes from expectant management. The main reason for this is that the expectant group includes excessively long pregnancies with correspondingly increased complication risk.6,35,36 We further argue that conclusions from such studies may contribute unfairly to evidence, because this does not reflect usual practice, where expectant management beyond 42+6 GW is close to non-existent. All of the above mentioned systematic reviews by Wennerholm et al.,36 Gulmezoglu et al.,35 and Caughey et al. 6 include studies with excessively long expectant management, e.g. one of the studies weighting the most in the systematic reviews uses expectant management until 44+0 GW.28
Regarding temporal criteria, the cited reviews included studies dating back to the 1960s and 1970s. At this time, fetal surveillance was less developed, induction agents were different from today, and both induction and CS rates were much lower. Caughey et al. describes restriction of studies to include only those “published from 1966 and beyond to represent modern obstetric practice”.6 (p253) We do not agree with the authors and find that obstetric practice (e.g. induction agents, CS rates and possibilities of monitoring pregnancy and childbirth) has changed substantially since 1966. Further, population characteristics have changed over this time. One could ask if it is reasonable to base a contemporary guideline on studies that are 40–50 years old. We suggest not, and have restricted publication dates of included studies to the last 20 years. The price to pay is fewer studies but with greater relevance.
Regarding estimation of due date, when the aim is to compare policies for induction of labor according to gestational age, the estimation of due date is paramount, and, consequently, the methods for estimation should be comparable. Previous reviews included studies with varied methods for estimating due date. Since EDD tends to differ between early ultrasound estimation and calculation by last menstrual period, this approach introduces a possible bias source to the analysis. Hence, in the present review we restricted data to studies using early ultrasound estimation.
In the present review, we allowed only for generally known methods of induction to be included (prostaglandins, balloon, oxytocin and artificial rupture of membranes). Even so, the included studies use different induction agents, and, thus, the external validity may be compromised. Furthermore, it was not possible to stratify on parity or rupture of membranes due to lack of information in the studies, and hence, both might be relevant. These factors might bias the results and we suggest the clinicians and stakeholders look thoroughly into individual studies before making local recommendations.
As described in the Methods section, the analytical approach for comparing groups is crucial to obtain a realistic scope for deciding recommendations for low-risk pregnancies past due date.25 Two different courses of action were compared in the present review: an active induction regimen and an expectant management, and data were restricted to a maximum expectancy up to 42+6 GW, since this reflects common practice, due to the increased risk of adverse outcome beyond that point. Our data showed that when women in the expectant arm were left without induction during week 41+0–6, a large proportion (∼70%) did in fact go into spontaneous labor before induction was recommended.13,33,43 However, the cited systematic reviews include studies that failed to include this sizable group of women in their analysis.6,35,36 When those in the expectant arm who gave birth during week 41+0–6 are excluded from analysis, the expectant arm is composed only of those who have reached 42+0 GW of pregnancy without the spontaneous onset of labor. Pregnancies that last beyond 42+0 GW are beyond the normal range of gestational time and are associated with an increased risk of complications. Therefore, comparison of outcomes between an induction arm composed of low-risk, healthy women whose labor was induced at 41+0–6 GW, and an expectant arm composed of women who have reached 42+0 GW and are therefore at heightened risk of complications is likely to bias the results in favor of induction. The risks associated with expectant management are likely to be overestimated. The problem can be circumvented if the large group of women in the expectant arm who go into spontaneous labor before 42+0 GW are included. Then a more accurate comparison can be made as to the effects of induction 41+0–6 GW versus expectant management, which, as has been noted, will in many cases result in spontaneous onset of labor before 42+0 GW. Therefore, in the present review, we draw only upon studies that include data on all participants in the expectant arm, including those who give birth between 41+0–6 and 42+0 GW. This will more correctly reflect the implications of using the two different guidelines, induction versus expectant management, and is probably the explanation as to why we found an increase in CS when performing routine induction in 41+0–6 GW, while other reviews found otherwise. We hope that issuing this topic will make stakeholders or authors of guidelines more attentive to the methodologies of the studies on which their recommendations are based.
The main limitation in this review concerns the limited number of included studies. It would, however, not be appropriate to rely on studies that do not include the gestational weeks under investigation, are up to 50 years old, use different methods for estimation of due date, or exclude the vast majority of women that go into spontaneous labor under an expectant management of pregnancies. We discussed problems with the wide variations in current systematic reviews and described how we have attempted to overcome the problem by defining strict criteria for inclusion. This decision had a major implication concerning the power of our analysis, as only seven studies were found to be eligible. To summarize, as Greenhalgh states: “any numerical result, however precise, accurate, ‘significant,’ or otherwise incontrovertible, must be placed in the context of the painfully simple and often frustratingly general question which the review addressed”.53 (p.674) Also, we were only able to separate groups by the number of weeks, even though different regimens should ideally be compared according to single days. Some guidelines recommend that the women deliver before 42+0 GW, which means that induction is not initiated until 41+3–5 GW.18,19 In practice, this implies that a considerable number of women will have time to go into spontaneous labor before reaching the time for recommended induction. As we compile data on a weekly basis, our findings may overestimate the effects regarding both benefits and harms if the groups in reality are only separated by a few days.
Finally, none of the studies included indicators of long-term effects on the child, such as cerebral palsy or hypoxic-ischemic encephalopathy. Therefore, we included pH < 7.10 as the best available proxy measure for possible long-term offspring outcomes. This is a deviation from the original protocol.37
The objective of this systematic review was to compare the effect of routine labor induction between one and two weeks past EDD to the practice of awaiting spontaneous onset of labor until two weeks past EDD. The review included seven primary studies. We found routine induction at 41+0–6 GW associated with a decreased risk of meconium stained amniotic fluid and oligohydramnios and with an increased risk of CS, labor dystocia, chorioamnionitis, precipitate labor, uterine rupture and low pH in the newborn. No conclusions could be drawn on perinatal death due to lack of statistical power. For perinatal outcomes, our findings largely support previous meta-analyses, except for perinatal death. For maternal outcomes (including outcomes related to the course of labor), routine induction was associated with several adverse outcomes, including an increased risk of CS, which is not in line with previous reviews. The current review used stricter inclusion criteria than most of the previous reviews, which is potentially the main reason for discrepancies from previous findings. These restrictions were applied in order to enhance the methodological quality and increase the relevance for contemporary maternity care. Our findings do not support the widespread use of induction prior to post-term, and they highlight the importance of discussing whether the threshold has been reached where risks related to the procedure of induction outweigh potential harms from the ongoing pregnancy, and whether induction of labor should be applied to large populations of low-risk women. If an intervention cannot demonstrate a positive association between higher intervention rates and an improved perinatal outcome, and evidence exists that the intervention itself may impose maternal and perinatal risks, it is normally decided to strive for the lowest intervention rates. In the case of routine induction prior to post-term, the challenge is how to prevent fetal demise leading to poor fetal outcome and in few occasions of fetal death. Nevertheless, one might ask if routine induction of labor on larger populations of healthy women and fetuses is the answer to this task, when – as demonstrated in this review – the intervention is associated with several iatrogenic effects.
Recommendations for practice
As much as the above discussion on research methodology and inclusion criteria in systematic reviews may appear as a purely academic one, it affects clinical daily life. Since clinical guidelines mainly rely on systematic reviews, and since systematic reviews are justified by their ability to weigh and sum up relevant research on a given subject, such discussions are highly relevant for practice. In the current review, we used stricter criteria for inclusion, and we found that doing so changed the conclusions from previous reviews. We suggest increased awareness of inclusion criteria in systematic reviews as they can reflect contemporary clinical practice, and the findings can be applied to guidelines and practice. We also suggest that clinicians and stakeholders look into original individual studies before making local guidelines.
The current review revealed several adverse outcomes associated with routine induction, which may not be prioritized in the information given before consent to labor induction.54 It is of the utmost importance that women are thoroughly informed about benefits and harms before making their decision on induction by routine, as described in general requirements of health legislations. In order to present balanced and understandable information, absolute numbers may also be needed. The current review presents absolute numbers to raise awareness of the communication of scientific evidence among users and policy makers. As health professionals, we should be aware that our choice of which risk measures to present works as a tool by which we can influence people's decisions regarding routine induction or not. We suggest that future research and clinical practice include absolute numbers and absolutes risks in addition to the usual relative estimates.
According to Joanna Briggs Institute Grades of Recommendations, our findings do not support the obstetric practice for low-risk pregnancies with routine labor induction at 41+0 to 41+6 GW when compared to expectant management (routine labor induction at 42+0 to 42+6 GW), because desirable effects do not appear to outweigh undesirable effects of such practice. There is not strong evidence supporting its use, and there does not seem to be any resource benefits from following this practice (Grade B). Values, preferences and the patient experience have not been taken into account.
Recommendations for research
The current review revealed important methodological weaknesses in existing systematic reviews on labor induction prior to post-term. One important problem is the use of studies with improper gestational timeframes in the comparison group. Another problem is the use of old studies. Obstetric practice (fetal surveillance, induction agents, clinical procedures, intervention rates etc.) as well as population characteristics have changed substantially since the 1960s–1980s. It is questionable whether findings from studies of such age can be extrapolated to a contemporary setting. A third problem is the use of studies with different methods for estimating due date and/or different induction agents within or across studies. The above aspects are all likely to bias the conclusions reported in some of the key scientific papers behind existing clinical guidelines. In the current review, we used stricter criteria for inclusion of studies in order to overcome some of the above flaws. This approach has resulted in a generally positive assessment of the methodological quality of the included studies, but the consequence has been a smaller sample size than in most previous reviews. We suggest that systematic reviews, with all their best efforts to promote evidence-based decision-making, should be studied carefully by stakeholders for external validity, since only few studies in a review may be relevant for the given clinical decision-making process.
The review process revealed a focus on few, selected outcomes in labor induction studies. Cesarean section and perinatal death have gained much focus so far, while e.g. hyperstimulation, tachysystole, and precipitate labor are understudied. This is of interest, because routine induction is performed on a healthy low-risk population, and in such cases, only a low risk of iatrogenic effects is usually accepted. We also found that several central aspects were generally not covered or inadequately accounted for in existing research. For example, it was not possible to evaluate long-term effects, the need for care, economic resources, or the experience of birth when artificially induced compared to being in a tight surveillance regimen awaiting spontaneous onset of labor. Long-term effects in the child may include cerebral palsy, brachial plexus injury, or hypoxic-ischemic encephalopathy. Even though pH < 7.10 and resuscitation may be indicators for such long-term effects, we suggest that future studies include a broad selection of both short- and long-term outcomes when evaluating the procedure of routine induction prior to post-term.
The current review revealed a 20% increase in inductions when using a guideline of recommending induction 41+0–6 GW, which affects workload in the labor ward. Inductions require extra attention compared to spontaneously initiated deliveries, and these resources may be drawn away from other laboring women. We suggest that future studies focus on economic consequences of new routines as well as health outcomes related to busy staff.
We thank Bodil K. Møller (Head of Midwifery Programme), Anna Møbjerg (Search Librarian), and Christina Ruggiero-Corliss (Visiting Student), University College Copenhagen, Copenhagen, for help and support.
Appendix I: Individual search strategies
PubMed (pubmed.gov): searched on 18/06/2018
CINAHL (EBSCO): searched on 18/06/2018
Embase (Elsevier): searched on 18/06/2018
Scopus (Elsevier): searched on 18/06/2018
Swemed+: searched on 15/03/2018
POPLINE (K4health): searched on 15/03/2018
Cochrane Library: searched on 18/06/2018
TRIP Medical Database: searched on 14/03/2018
Current Controlled Trials: searched on 14/03/2018
Web of Science: searched on 14/03/2018
MedNar: searched on 15/03/2018
Google Scholar: searched on 15/03/2018
OpenGrey: searched on 15/03/2018
ProQuest Nursing and Allied Health Source: searched on 20/03/2018
National Institute for Health and Care Excellence, World Health Organization, Royal College of Obstetricians and Gynaecologists, American College of Obstetricians and Gynecologists, and Society of Obstetricians and Gynaecologists of Canada. Searched on 15/03/2018
Appendix II: General characteristics of included studies
Appendix III: Details on comparison groups in included studies
Appendix IV: Outcome measures in included studies
Appendix V: Excluded studies
Appendix VI: Meta-analyses
Analysis 1. Admission to neonatal intensive care unit. Quasi- or randomized studies
Analysis 2. Apgar score (less than 7 after 5 minutes). Quasi- or randomized studies
Analysis 3. Macrosomia >4500 g. Quasi- or randomized studies
Analysis 4. Meconium aspiration syndrome. Quasi- or randomized studies
Analysis 5. Meconium stained amniotic fluid. Quasi- or randomized studies
Analysis 6. Perinatal death. Quasi- or randomized studies
Analysis 7. pH <7.10. Quasi- or randomized studies
Analysis 8. Shoulder dystocia. Quasi- or randomized studies
Analysis 9. Cesarean Section. Quasi- or randomized studies
Analysis 10. Cesarean Section for failure to progress. Quasi- or randomized studies
Analysis 11. Cesarean Section for fetal distress. Quasi- or randomized studies
Analysis 12. Instrumental vaginal delivery. Quasi- or randomized studies
13. Vaginal delivery. Quasi- or randomized studies
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Keywords:© 2019 by Lippincott williams & Wilkins, Inc.
41 gestational weeks; 42 gestational weeks; expectant management; labor induced; perinatal mortality