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All trials need to recruit participants, but this is often a challenge. Poor recruitment can lead to an underpowered study, which may report clinically relevant effects to be statistically non‐significant. A non‐significant finding increases the risk that an effective intervention will be abandoned before its true value is established, or that there will be a delay in demonstrating this value while more trials or meta‐analyses are done. Underpowered trials also raise an ethical problem: researchers have exposed participants to an intervention with uncertain benefit but may still be unable to determine whether the intervention does more good than harm on completion of the trial. Poor recruitment can also lead to trial extension, higher costs, or trial abandonment.

Investigations of recruitment differ in their estimates of the proportion of studies that achieve their recruitment targets, but it is likely that around half meet their target [, , , , ]. For example, McDonald and colleagues found that only 38 (31%) of 114 trials achieved their original recruitment target and 65 (53%) were extended []. A more recent replication of this work found that the number of trials meeting recruitment targets had increased to around 63% (245/388), but 32% (79/245) of these trials required an extension to their recruitment period to meet the target, meaning approximately 43% of trials recruit to target without an extension []. An additional 22% (86/388) of trials recruited to within 80% of their final recruitment target, with 36% (31/86) of these requiring an extension to their recruitment period [].

Poor recruitment can have significant public health implications []. Evidence from the dexamethasone arm of the COVID‐19 RECOVERY trial suggests that delays in trial completion – such as those caused by slow recruitment – led to avoidable deaths in the UK []. Faster recruitment could lead to earlier trial completion, and if the intervention proves effective, earlier access could benefit more people. Had RECOVERY recruited 50% of eligible participants rather than the typical 15%, nearly 3000 additional lives could have been saved through earlier access to dexamethasone, which was shown to be an effective treatment. The economic implications may also be substantial: increasing recruitment from 15% to 50% at all sites could have delivered an incremental net benefit of 13.9 million pounds sterling (GBP) to the UK from a healthcare system perspective []. These findings highlight the vital importance of efficient trial processes – not only for saving lives but also for maximising the health and economic value of research.

This systematic review updates our previous reviews [, , ]. In addition to updating the literature search, we adjusted the eligibility criteria by excluding quasi‐randomised and hypothetical trials (i.e. where people are asked to imagine whether they would take part in a trial that is not really happening, rather than being invited to a real trial). We also included three new outcomes: cost‐effectiveness of recruitment strategies; impact of recruitment strategies on participant retention; and equity, diversity, and inclusion (EDI) characteristics of the participants.

Primary: to quantify the effects of strategies to improve recruitment of participants to RCTs. Secondary: to evaluate recruitment strategies' cost‐effectiveness and impact on retention, and the equity, diversity, and inclusion (EDI) characteristics of recruited participants.

Since the 2018 update, we amended the protocol in several ways to enhance methodological rigour and address emerging priorities in trial methodology research. We narrowed the inclusion criteria to include only randomised controlled trials. We excluded hypothetical and quasi‐randomised trials to ensure the meta‐analysis reflects high‐certainty, real‐world evidence. We also introduced three new secondary outcomes to provide a more comprehensive evaluation of recruitment strategies: retention rates – to assess downstream effects on trial completion; cost‐effectiveness – to provide practical resource implications; and equality, diversity, and inclusion (EDI) characteristics – to identify representation gaps.

We included randomised Studies Within A Trial (SWATs), including individually randomised and cluster‐randomised designs, that evaluated strategies to improve participant recruitment to randomised trials.

We included any intervention that aimed to improve participant recruitment to a randomised trial, except incentives or disincentives for clinicians to recruit participants, which is covered by another Cochrane review []. We did not impose any restrictions on the number or types of participants included or the study setting. The interventions being studied could be directed at potential participants (e.g. patients being randomised to a trial), collaborators (e.g. clinicians recruiting patients for a trial), or others (e.g. research ethics committees). Examples of eligible interventions include: letters introducing the trial signed by influential people; alternative methods of providing information about the trial to potential participants; additional training for collaborators; monetary incentives for participants; telephone follow‐up after expressions of interest; and modifications to the trial design (e.g. preference designs).

We added the following outcomes for this update. Previous versions of this review did not include any secondary outcomes. Cost‐effectiveness of recruitment strategies, measured using the incremental cost‐effectiveness ratio (ICER), defined as the incremental cost per additional participant recruited. We defined incremental cost as the additional cost of one strategy compared with another, and the ICER as the additional cost per additional participant recruited. Impact of the recruitment strategy on retention rates. We defined retention as the proportion of participants randomised to each SWAT arm who were retained in the host trial (e.g. attended follow‐up visits or completed questionnaires). Where available, we used retention at the host trial's primary outcome time point; otherwise, we used the first reported retention measure. Participant equity, diversity, and inclusion (EDI) characteristics, as reported by trialists, to inform equity‐related assessments of the populations to whom the evidence applies.

To update the review, we re‐screened the 68 previously included studies and searched the following electronic databases, with no language restrictions, for eligible studies published from 1 January 2015 onwards. We searched the following databases on 16 February 2023: Science Citation Index and Social Sciences Citation Index (Web of Science). We added the following databases for this update: Applied Social Sciences Index and Abstracts (ASSIA) (searched to 31 December 2023); CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature; EBSCO) (searched to 31 December 2023); ERIC (EBSCO) (searched to 31 December 2023); Online Resource for Research in Clinical triAls (ORRCA) (searched to 31 December 2019, when it was last updated); PsycINFO (EBSCO) (searched to February Week 2 2023). To ensure global coverage, we also consulted regional sources such as LILACS (Latin American and Caribbean Health Sciences Literature). We did not search the Cochrane Methodology Review (CMR) Group Specialised Register as it has not been updated since July 2012. However, we included eligible papers identified from the CMR Group Specialised Register for the previous review (last search date 11 February 2015) in this review update. details the full search strategies for all databases.

To identify unpublished and ongoing recruitment SWATs [], we issued a call for information via social media and email. On 23 March 2023, we posted on X (formerly Twitter), inviting trial methodology researchers who had conducted randomised recruitment SWATs to share their findings. On 27 March 2023, we circulated a similar request through the Trial Forge SWAT Network, the UK Trial Managers’ Network, the UK Clinical Research Collaboration (CRC) Registered Trials Units Network, the Medical Research Council and National Institute for Health and Care Research (MRC‐NIHR) Trial Methodology Partnership, and the Health Research Board Trial Methodology Network in Ireland. We implemented a study‐integrity audit to identify retractions, expressions of concern, or corrigenda. We checked the digital object identifiers of all eligible studies against the Crossref/CrossMark API and the Retraction Watch database, and used this information to ensure that the results reflected the most up‐to‐date, corrected versions of each included study.

We downloaded the search results to Endnote reference management software for deduplication and then uploaded the records to Covidence to enable screening and data extraction []. Working independently, two review authors screened the titles and abstracts of all records retrieved from searches of the electronic databases. We resolved any disagreements by involving a third author. We retrieved the full texts of studies that appeared to meet the inclusion criteria. Two review authors independently assessed all potentially eligible studies to determine if they met the inclusion criteria. We resolved any disagreements through discussion or by involving a third author. Authors Adwoa Parker, Shaun Treweek, Frank Sullivan, Elizabeth Colement, Mike Clarke, Caroline Fairhurst, and Catherine Hewitt were lead authors or co‐authors of a number of studies included in this review. They were not involved in study eligibility decisions, data extraction, risk of bias assessment, or GRADE assessments for any included studies they authored.

Working independently, two review authors extracted data from each included study using a data extraction form designed for the purpose. We resolved any differences in data extraction through discussion. We extracted data on: country in which the study was carried out; number and proportion of participants in the SWAT intervention and comparator groups; participant characteristics, including age, sex, gender, ethnicity, socioeconomic status, and geographic location, using the PRO EDI tool []; proportion of participants or clusters retained. For the cost‐effectiveness analysis, we extracted cost data from newly included studies, where available. We also extracted cost data from previously included studies identified in a systematic review of economic evaluations conducted alongside SWATs []. For each study, we recorded the costs of the intervention and comparator strategies, and any reported incremental costs. Where incremental costs were not reported, we estimated them by attributing relevant unit costs to each strategy and calculating the difference.

We assessed risk of bias in the included studies using the original Cochrane risk of bias tool [], for consistency with previous versions of the review []. We adapted the assessment to reflect the methodological nature of the interventions evaluated. Working independently, two review authors performed a blinded risk of bias assessment of each study before comparing assessments. We resolved any discrepancies through discussion. We assessed random sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, selective reporting, and other potential sources of bias. We judged each domain as low, high, or unclear risk of bias. We considered a study to be at low overall risk of bias if all domains were judged to be at low risk of bias, at high overall risk of bias if one or more domains were judged to be at high risk of bias, and otherwise at unclear risk of bias.

We did not exclude studies judged to be at high overall risk of bias from the meta‐analyses (). However, because we have lower confidence in these studies' evidence, we do not discuss them individually in the Results or Discussion, except where their data contribute to a meta‐analysis and can be considered alongside evidence from studies at lower risk. We suggest that readers should not draw conclusions about intervention effects solely from the results of studies at high overall risk of bias. Rather, these studies may help identify interventions that warrant further evaluation using more rigorous methods. Methodological quality data for all included studies are presented in the risk of bias graph ().

For recruitment SWATs that randomised individuals and clusters, the unit of analysis was the participant. We included cluster‐randomised trials in meta‐analyses only when sufficient data were available to adjust for clustering (e.g. intra‐cluster correlation coefficients or cluster‐adjusted estimates). When cluster‐adjusted risk differences (RDs) or risk ratios (RRs) were not available, we used odds ratios (ORs) as the summary effect measure.

We contacted study authors to request missing data needed for the risk of bias assessment, the number of participants randomised to each group, and the number of participants recruited.

We sought statistical evidence of heterogeneity of results using the Chi 2 test for heterogeneity, and we quantified the degree of heterogeneity using the I 2 statistic []. The I² is independent of the number of studies and reflects variation based on the treatment effect. Where we detected substantial heterogeneity, we informally investigated possible explanations and summarised the data using a random‐effects meta‐analysis.

We used the Online Resource for Recruitment research in Clinical triAls (ORRCA) project's taxonomy of recruitment interventions to classify the interventions included in this review []. We split one ORRCA category ('Recruitment information needs') into two to distinguish interventions aimed at the consent process from those aimed at more general participant information. Our seven categories are as follows. Category A: design: changes to the general design of the trial made specifically to increase recruitment. Category B: pre‐trial planning: work done before the trial starts (possibly in a separate study) to explicitly make it more likely that recruitment will be successful. Category C: trial conduct changes: initiatives implemented once the trial has started, including better ways of identifying participants, changes to how data are collected, changes to the type of data collected, and tailoring recruitment to different types of participants. Category D: modifications to the consent process: changes to the personnel obtaining consent, the timing of consent, what sort of consent information is presented and how it is presented. Category E: modifications to the information given to potential participants about the trial: including who provides it, when, where, what sort of information is presented, and how the information is presented.

Category F: interventions aimed at the recruiter or recruitment site: any interventions aimed at the recruiter or recruitment site staff, such as changes to training. Category G: incentives: monetary and other incentives for participants (but not staff, which is covered in a separate review []). We conducted random‐effects meta‐analyses when at least two studies evaluated the same recruitment strategy. Unlike previous versions of this review, which used fixed‐effect models in the absence of substantial heterogeneity, we used random‐effects models throughout because we anticipated substantial heterogeneity across most comparisons. In accordance with updated guidance in the Cochrane Handbook for Systematic Reviews of Interventions [], we estimated between‐study variance using the restricted maximum likelihood (REML) method. We calculated confidence intervals for the summary effect using the Wald‐type method by default. However, when the estimated between‐study variance was greater than zero and more than two studies contributed to a comparison, we used the Hartung‐Knapp‐Sidik‐Jonkman (HKSJ) method.

To synthesise cost‐effectiveness evidence across studies within each comparison, we reported the incremental cost‐effectiveness ratio (ICER), defined as the additional/incremental cost of the intervention strategy compared with the control strategy per additional participant recruited. We measured incremental effectiveness using the RD, defined as the number of additional participants recruited, and defined incremental cost as the difference in cost between the intervention and control strategies. When all studies in a comparison reported cost data, the RD used in the cost‐effectiveness analysis matched the RD estimated from the pooled effectiveness results. When only a subset of studies reported cost data, we re‐estimated the RD using data from those studies only. For single‐study comparisons, we estimated RDs using fixed‐effect meta‐analysis with Mantel‐Haenszel weighting []. For comparisons involving multiple studies, we conducted random‐effects meta‐analyses using inverse‐variance weighting [].

For comparisons with cost data from multiple studies, incremental costs were weighted according to the same weights applied in the estimation of the RD. This approach enabled us to estimate the overall incremental cost of each recruitment strategy. We were unable to synthesise incremental costs using single‐arm meta‐analysis methods because the included SWATs did not report cost variability data. We calculated ICERs only when both incremental cost and incremental effectiveness data were available for a given strategy. All ICERs are reported in pounds sterling (GBP) at 2023 price levels. For studies reporting cost data in GBP at price levels other than 2023, we adjusted costs to 2023 values using the UK Consumer Price Index (CPI) []. For studies reporting cost data in other currencies and price years, we first adjusted costs to 2023 values using the CPI for the relevant country [], and then converted the figures to GBP using the UK integrated tariff exchange rates [].

We planned to explore the following factors in subgroup analyses for our primary outcome (proportion of eligible participants recruited). We assumed sufficient studies would be identified for these analyses and that these factors represented plausible explanations for any observed heterogeneity. Type of allocation concealment used to evaluate recruitment strategies (adequate versus inadequate or unclear). Setting of the study recruiting participants (e.g. primary versus secondary care; healthcare versus non‐healthcare settings). Type of health condition in healthcare studies (e.g. cancer versus lifestyle change). Design of the study recruiting participants (e.g. open‐label versus blinded studies, trials with placebo arms versus those without). Target group (e.g. ethics committees, clinicians, patients). However, there were too few studies to permit subgroup analysis except for one strategy (monetary incentive versus no incentive – detailed in the ).

We did not perform sensitivity analyses because the limited number of replications for most strategies precluded a meaningful assessment of the robustness of the results. If the evidence base for specific recruitment strategies expands in future review updates, we will consider the feasibility of conducting sensitivity analyses.

We used the GRADE framework to assess the certainty of the evidence for our primary outcome (proportion of eligible individuals or centres recruited), and where data were available, our secondary outcomes (cost‐effectiveness, retention, participant EDI characteristics) []. We present GRADE assessments for meta‐analysed comparisons in the corresponding summary of findings tables []. These tables compare specific recruitment strategies with standard practice or alternative interventions and report the primary and secondary outcomes. As all included studies were randomised SWATs, we started each GRADE assessment at high certainty and considered downgrading the evidence for risk of bias, inconsistency, indirectness, imprecision, and publication bias [, ]. For all comparisons, we assessed: risk of bias, downgrading by one level when studies were judged to have an overall high or unclear risk of bias. This differs from previous versions of the review, in which we automatically downgraded studies at high overall risk of bias by two levels; inconsistency, downgrading when there was substantial unexplained heterogeneity across studies; indirectness, downgrading when there were key differences across study interventions or methods; imprecision, downgrading when confidence intervals were wide or crossed the line of no effect (risk difference = 0);