Types of studies

We included randomized controlled trials (RCTs), irrespective of blinding, language, publication status, or sample size. We did not include controlled clinical trials (CCTs) that used non‐random methods of assigning participants to treatment, such as by alternation, by birth date, or by medical record number, as they may be subject to high risk of bias.

Types of participants

Postpartum people who requested a long‐acting reversible contraceptive method and were recruited before hospital discharge.

Types of interventions

Contraceptive implants:

• immediate postpartum insertion of contraceptive implants (after delivery and before hospital discharge) compared to delayed postpartum insertion (during a postpartum visit after hospital discharge), which is often referred to as standard, or interval, insertion.

IUDs:

• immediate postpartum insertion, including both immediate postplacental insertion (within 10 minutes of placenta delivery, following vaginal or cesarean delivery) and early postpartum insertion (10 minutes after delivery to hospital discharge), compared to delayed postpartum insertion (during a postpartum visit four or more weeks after hospital discharge), which is often referred to as standard, or interval, insertion.

Types of outcome measures

Electronic searches

We searched the following electronic databases:

• Cochrane Central Register of Controlled Trials (via Ovid EBM Reviews, CENTRAL, 2020, issue 12);

• MEDLINE ALL (Ovid) (1946 to December week 2, 2020);

• Embase.com (1980 to December 2020);

• POPLINE (1970 to December 2020).

We have provided the search strategies in Appendix 1.

Searching other resources

We checked the citation lists of included studies, key textbooks, and systematic reviews for potentially relevant references. We searched the WHO International Clinical Trials Registry Platform (WHO ICTRP) (www.who.int/ictrp/en) and ClinicalTrials.gov to identify ongoing trials. We applied modified versions of the same search strategy to check the following databases for grey literature: OpenGrey, GreyNet, Scirus, Social Care Online, National Research Register, NIHR portfolio database, and Index to theses.

Selection of studies

Before examining the identified trials for possible inclusion, we developed and piloted a data collection form, as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019). We downloaded all titles and abstracts retrieved by electronic searching. After removal of duplicates, all references were transferred to Covidence. Two review authors, JS and SK, independently screened the titles and abstracts of the remaining studies. We excluded studies that clearly did not meet the inclusion criteria. We obtained full‐text copies of potentially relevant studies. Two review authors, JS and SK, independently assessed the eligibility of the retrieved reports and publications. We resolved any disagreement through discussion or, if required, we consulted a third review author (PL, SA or PP). We identified and intended to collate multiple reports of the same study so that each study, rather than each report, was the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009), and a.'Characteristics of excluded studies table.

Data extraction and management

Two review authors, JS and SK, independently extracted study characteristics and outcome data from the included studies using a piloted data collection form. When the included trials did not report outcome data in a usable way, we noted in this the Characteristics of included studies table. We then contacted the trial authors for further information. We resolved disagreements by consensus or by involving a third review author (PL, SA or PP). One review author, PP, entered data into Review Manager 5 (RevMan 5) (RevMan 2014). We double‐checked whether data were entered correctly by comparing the data presented in the systematic review with the study reports. A second review author (PL or SA) checked all study characteristics for accuracy against the trial report.

For included studies, we extracted the following data:

• author, year of publication, and journal citation (including language);

• country;

• setting;

• inclusion and exclusion criteria;

• study design and methodology;

• study population;

• study outcomes and their related summary statistics.

Assessment of risk of bias in included studies

We assessed and reported on the methodological risk of bias of included studies in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019), which recommends an assessment is made for each of the following domains for RCTs:

• selection bias: random sequence generation and allocation concealment;

• performance bias: blinding of participants and personnel (participants and treatment providers);

• detection bias: blinding of outcome assessors;

• attrition bias: incomplete outcome data;

• reporting bias: selective reporting of outcomes.

Two review authors, JS and SA, independently applied the risk of bias tool (ROB 1) to each included study and resolved differences by discussion or by consulting a third review author (PL or PP). SA was a study author on two studies, so other review authors assessed these studies for risk of bias (JS and PL). We judged each item as at being at either 'high’, 'low’, or 'unclear’ risk of bias, as set out in the criteria provided by Higgins 2019, and provided a quotation from the study report or a statement as justification for the judgement for each item in the risk of bias table. We summarized the results in both a risk of bias graph and a risk of bias summary. When we interpreted treatment effects and meta‐analyses, we took into account the risk of bias for the studies that contributed to that outcome. Where information on risk of bias was related to unpublished data or correspondence with a trial author, we noted this in the risk of bias table.

Measures of treatment effect

We used the following measures of the effect of treatment.

• For dichotomous outcomes, such as the rates of contraceptive implantation and IUD initiation, we used number of events and number of participants assessed for both the intervention and comparison groups to calculate the risk ratio (RR) and 95% confidence interval (CI).

• For continuous outcomes, such as satisfaction rate, we used mean, standard deviation (SD), and the number of participants assessed for both the intervention and comparison groups to calculate mean difference (MD) with 95% CI.

Unit of analysis issues

We intended to include studies where postpartum people were randomized individually and also cluster‐randomized studies where, for example, the hospital was the unit of randomization. However, we did not find any relevant cluster‐randomized studies. In future updates of this review, if we identify studies that use a cluster‐randomized design but do not have any information related to the design effect, we will estimate the design effect based on a fairly large assumed intra‐cluster correlation of 0.10. We will base this assumption by analogy on studies about implementation research (Campbell 2000; Ukoumunne 1999).

Dealing with missing data

We did not impute any missing outcome data and we tried to contact the trial authors for missing data.

Assessment of heterogeneity

We assessed heterogeneity by visual inspection of the forest plots. We also assessed statistical heterogeneity in each meta‐analysis using the I² statistic and Chi² test. We regarded heterogeneity as substantial if the I² statistic value was greater than 50%, or there was a low P value (less than 0.10) in the Chi² test for heterogeneity (Deeks 2001).

Assessment of reporting biases

We considered all 16 studies to be at low risk of selective reporting bias, since all relevant outcomes were reported by all included studies.

Data synthesis

We undertook meta‐analysis for all the outcomes where suitable data were available. We described skewed data reported as medians and interquartile ranges narratively.

Using RevMan 5, we performed statistical analyses (RevMan 2014). We used a fixed‐effect model to combine data where it was reasonable to assume that studies were estimating the same underlying treatment effect, that is where studies were examining the same intervention, and we judged the studies' populations and methods to be sufficiently similar. If there was unexplained clinical heterogeneity sufficient to expect that the underlying treatment effects differed between studies, or if we detected substantial statistical heterogeneity, we used a random‐effects meta‐analysis to produce an overall summary, but only where it was possible to derive a meaningful meta‐analysis. For example, population differences (high‐income and low‐ and middle‐income countries), type of IUDs (non‐hormonal IUDs, hormonal IUDs, and any other type of IUD). When we used random‐effects meta‐analysis, we treated the pooled treatment effect as the average range of possible treatment effects, and discussed the clinical implications of treatment effects differing between studies. When we used random‐effects analyses, we presented the results as the pooled treatment effect with 95% CIs, and estimates of the T² and I² statistic (DerSimonian 1986). We prepared a summary of findings table to present the results of meta‐analysis, based on the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011). For the data that we were unable to pool for meta‐analysis, we conducted a narrative synthesis of the results.

Subgroup analysis and investigation of heterogeneity

We planned to perform subgroup analyses according to:

• age of participants (teens (13‐19 years old) versus non‐teens);

• type of IUDs (non‐hormonal IUDs versus hormonal IUDs); and

• population differences (high‐income versus low‐ and middle‐income countries, according to World Bank 2020).

We performed subgroup analyses for the primary outcome of rate of insertion at first postpartum visit (six to eight weeks postpartum) to assess:

• population differences for contraceptive implants, and

• types of IUDs.

We did not perform subgroup analyses according to age as the number of included studies that would allow this subgroup analysis was limited.

Sensitivity analysis

We performed the following sensitivity analyses in order to determine the impact of the following factors on effect size:

• repeating the analysis excluding unpublished studies (if any);

• repeating the analysis excluding trials rated as 'high' or 'unclear' for risk of selection bias.

Summary of findings and assessment of the certainty of the evidence

Two review authors working independently prepared a summary of findings table, and disagreements were resolved by consensus. The following outcomes were reported in the table reporting on contraceptive implants:

• rate of initiation;

• utilization rate at six months postpartum;

• utilization rate at 12 months postpartum;

• adverse effects of contraceptive implants: prolonged vaginal bleeding within six weeks postpartum;

• adverse effects other than prolonged vaginal bleeding;

• unintended pregnancy rate at 12 months postpartum; and

• any breastfeeding at six months postpartum.

The following outcomes were reported in the table reporting on IUDs:

• rate of initiation;

• expulsion by six months postpartum;

• utilization rate at six months postpartum;

• utilization rate at 12 months postpartum;

• unintended pregnancy rate at 12 months postpartum; and

• any breastfeeding at six months postpartum.

We used the GRADE approach (consideration of study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of the evidence (GRADEproGDT 2014). We used methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019). We justified all decisions to downgrade the certainty of evidence, using footnotes.