A Review of the Ring Trial Design for Evaluating Ring Interventions for Infectious Diseases

Abstract

In trials of infectious disease interventions, rare outcomes and unpredictable spatiotemporal variation can introduce bias, reduce statistical power, and prevent conclusive inferences. Spillover effects can complicate inference if individual randomization is used to gain efficiency. Ring trials are a type of cluster-randomized trial that may increase efficiency and minimize bias, particularly in emergency and elimination settings with strong clustering of infection. They can be used to evaluate ring interventions, which are delivered to individuals in proximity to or contact with index cases. We conducted a systematic review of ring trials, compare them with other trial designs for evaluating ring interventions, and describe strengths and weaknesses of each design. Of 849 articles and 322 protocols screened, we identified 26 ring trials, 15 cluster-randomized trials, 5 trials that randomized households or individuals within rings, and 1 individually randomized trial. The most common interventions were postexposure prophylaxis (n = 23) and focal mass drug administration and screening and treatment (n = 7). Ring trials require robust surveillance systems and contact tracing for directly transmitted diseases. For rare diseases with strong spatiotemporal clustering, they may have higher efficiency and internal validity than cluster-randomized designs, in part because they ensure that no clusters are excluded from analysis due to zero cluster incidence. Though more research is needed to compare them with other types of trials, ring trials hold promise as a design that can increase trial speed and efficiency while reducing bias.

Abbreviations

 
• CRCT

  cluster-randomized controlled trial

 
• ICC

  intraclass correlation

 
• RCT

  randomized controlled trial

INTRODUCTION

Infectious disease transmission is inherently heterogenous, with a minority of the population responsible for the majority of transmission (1). This is especially the case in settings of emerging infectious disease and disease elimination, where diseases are rare and strongly clustered within space or contact networks (2–4). These epidemiologic features can pose challenges in randomized trials (2).

Strong spatial clustering and unpredictable timing of outbreaks can compromise baseline balance between trial arms, reducing statistical power and face validity (5, 6). This is particularly true in cluster-randomized controlled trials (CRCTs), which are commonly used to evaluate infectious disease interventions and enroll fewer units than individually randomized trials typically enroll. Although adjusting for baseline covariates may address baseline imbalance, substantive differences in adjusted and unadjusted estimates may undermine trial credibility and replicability (6).

In addition, in studies at the early or waning stages of an outbreak or in elimination settings, rare, clustered outcomes require large numbers of clusters to minimize false-negative results, which may be infeasible and cost prohibitive (2, 7). Individually randomized trials are more efficient than CRCTs, but contamination can prevent valid estimation of the estimand of interest—the effect of individual treatment versus control (8, 9). CRCTs are often used when contamination is a concern (10), among other reasons (e.g., to evaluate group-level interventions, to increase compliance or feasibility) (8). When buffer zones are established between clusters to maintain independence, CRCTs can minimize contamination (8, 11, 12). However, when disease is highly clustered in space or time, disease cases may only occur in a subset of predefined clusters, which may compromise statistical power in CRCTs (7).

Diseases that can be subclinical or asymptomatic pose another challenge to trials (2). For example, malaria and SARS-CoV-2 can be transmitted without symptoms (13), and asymptomatic Zika infection in pregnant women may result in birth defects. For such diseases, it is critical to evaluate asymptomatic infections, but doing so requires outcome measurement in population-based samples instead of, or in addition to, routine surveillance, which can be difficult and costly.

Ring trials are a type of CRCT that may increase efficiency and minimize bias in emerging infection and disease elimination settings (2). This design is well suited for evaluations of ring interventions (e.g., case-area targeted interventions (14–16), targeted interventions (17), focal interventions (18–21), and reactive interventions), which are delivered to individuals in proximity to or with contact with index cases. Ring interventions have been proposed or implemented for a wide range of diseases, including smallpox (4), malaria (22), and COVID-19 (23). In ring trials, as index cases are detected, each “ring” of individuals around the index case is randomized. This design was used to evaluate ring vaccination for the Ebola vaccine (24) and may be effective for ring interventions for other infectious diseases with asymptomatic transmission and high spatiotemporal transmission heterogeneity.

Here, we review ring trial designs, compare them with traditional trial designs, and discuss optimal settings for their use. We also report the findings of a systematic review of ring trials and trials of ring interventions, including published studies and protocols for ongoing studies.

METHODS

We conducted a narrative review of articles related to ring trials and ring interventions, focusing on methodological papers and simulation studies. To identify empirical studies, we conducted a systematic review to identify all published studies and registered study protocols reporting trials of ring interventions, including ring trials and other types of trials (PROSPERO registration: CRD42021238932). The remainder of this section focuses on the methods we used in the systematic review.

Inclusion and exclusion criteria

We included studies that 1) were reported as a research article or trial protocol; 2) used a ring trial design or other randomized design to evaluate a ring intervention; 3) measured disease or health-related outcomes; 4) evaluated public health intervention(s); 5) enrolled humans; 6) were reported in English; and 7) were published or registered before August 23, 2021. We defined ring interventions as interventions delivered to neighbors, contacts of index cases, or contacts of contacts of index cases. Index cases may be detected through passive surveillance, in which case patients present at health facilities, or active surveillance, in which case patients are detected through population screening. Typically, interventions are delivered within a relatively short period after index-case detection, when onward transmission to ring members is expected. We distinguished ring interventions from reactive interventions, which are delivered in response to an outbreak but are not restricted to individuals in proximity to or contact with index cases (25–32). We defined a ring trial as a study in which researchers enrolled rings of individuals or households in physical proximity to or in contact with an index case and randomly allocated each ring to study groups. We did not consider interventions to be ring interventions if a single contact of an index case was enrolled or if contacts were enrolled who were possibly exposed to an index case, but trial investigators made no attempt to identify or confirm index cases.

Search strategy

We searched PubMed (MEDLINE) and ClinicalTrials.gov in August 2021. We included the search terms “ring trial,” “responsive target population,” “ring vaccine,” “ring intervention,” “ring vaccination,” “ring treatment,” “ring vaccine,” “responsive target population,” “case area targeted intervention,” “permuted locus,” “reactive case detection,” “reactive focal,” “ring prophylaxis,” “focal mass drug administration,” “targeted mass drug administration,” “household contact,” and “post exposure prophylaxis” independently and in combination with the terms “trial,” “randomized trial,” “randomized controlled trial,” “randomized control trial,” “controlled trial,” and “control trial.” See additional details in the Web Appendix (available at https://doi.org/10.1093/aje/mxac003).

Article selection

Two investigators independently assessed article titles, abstracts, and full-text eligibility. Investigators logged inclusion and exclusion criteria during abstract and full-text review and resolved discordant classifications between each stage; for discordant classifications during title and abstract review, we erred on the side of including records in the full-text review. For trial registrations, 2 investigators reviewed registration eligibility in a single stage.

Data extraction

We extracted the following data from each selected publication: country, year, primary and secondary outcomes, intervention(s), comparison group(s), study design, rationale for the study design, ring definition, randomization unit, randomization type (e.g., stratified randomization), index-case definition, buffer zones, planned study size, power-calculation assumptions, and eligibility criteria. For completed studies, we also extracted results (e.g., study size, compliance, mean response time, parameter estimated, analysis method, outcomes per group, measures of effect).

Risk-of-bias assessment

Investigators independently assessed risk of bias using the revised Cochrane risk-of-bias tool for cluster randomized trials (33). For publications in which multiple analyses were reported, we focused on the primary analysis. We classified the risk of bias in each domain and overall as “low risk,” “some concerns,” or “high risk.” We resolved discordant classifications through consensus.

RESULTS

In the following summary of the findings of studies identified in our systematic review, we highlight features of ring trial design and contrast them with alternative designs, drawing on relevant methods and simulation studies.

Trial selection

We performed a title review of all 849 publications, abstract review of 238 publications, and full-text review of 73 publications (Figure 1). We reviewed 322 ClinicalTrials.gov registrations, of which 20 met inclusion criteria. Initial concordance between investigators was 90% after title review, 92% after abstract review, and 93% after full-text review; we resolved all discordances through consensus. Concordance for ClinicalTrials.gov registrations was 96%. In total, 52 trials (n = 50 publications and 20 registrations) met inclusion criteria.

Trial characteristics

Thirty-one trials were completed, 16 were in progress, 3 were registered and had not started, and registrations for 2 had been withdrawn (Table 1). Twenty-five trials used a ring design (Figure 2A), 7 trials individually randomized contacts of index cases (Figure 2B), and 15 others were CRCTs (Figure 2C). Twenty trials were located in low- or middle-income countries, and 31 studies were located in high-income countries. Studies measured infectious diseases in emergency, outbreak, and emerging infection settings (n = 18), epidemics (n = 15), endemic settings (n = 12), and elimination settings (n = 7).

Interventions

The most common type of interventions were postexposure prophylaxis or preventive chemotherapy delivered to household members or nearby residents of index cases (Table 1). These included postexposure prophylaxis for SARS-CoV-2 (n = 12), influenza (n = 9), common cold (n = 1), meningococcal meningitis (n = 1), cholera (n = 1), tuberculosis (n = 1), pertussis (n = 1), and leprosy (n = 1). Studies also applied focal mass drug administration or focal screening and treatment for malaria (n = 7), focal indoor residual spraying for malaria (n = 2), contact or community-based screening and treatment for tuberculosis (n = 2), and household decolonization for Staphylococcus aureus (n = 1). In 2 studies, researchers evaluated vaccines for Ebola in contacts of index cases and for hepatitis A in household contacts. In a few studies, nonpharmaceutical interventions were evaluated, including handwashing promotion for contacts of case patients with cholera or diarrhea (n = 2), masks and preventive behavior education for household members of case patients with influenza (n = 2) or tuberculosis (n = 1), conditional cash transfers for household contacts of case patients with tuberculosis (n = 1), and notification of partners of case patients with chlamydia or human immunodeficiency virus (n = 2). Different types of ring interventions were compared in several trials (n = 10); in 2 studies, researchers compared ring interventions with population-wide interventions for malaria because the latter are unsustainable, costly, and/or may contribute to drug and insecticide resistance. Most interventions were delivered to all ring members regardless of infection status (n = 49), and some were only delivered to ring members who tested positive for disease (n = 4).

Trial designs

Three types of randomized designs were used to evaluate ring interventions (Figure 2). A ring trial design was used in 26 studies (Table 1, Figure 2A). In 5 trials, researchers enrolled individuals or households in rings around index cases and then randomly allocated units in each ring to intervention or control, stratifying by ring (i.e., a ring-stratified trial) (Figure 2B). Fifteen studies were CRCTs of ring interventions, in which geographic clusters (e.g., health-facility catchment areas) were defined before index case presentation (Figure 2C). Five trial registrations and 1 published trial did not include sufficient information to determine the trial design. CRCTs were the only design used in elimination settings; ring trials were more common in epidemic and emergency or outbreak settings (Table 2).

In trials in which clusters are solely composed of ring members exposed to index cases, ring trials and CRCTs are equivalent. This was the case in many ring trials in which rings were defined as household contacts of index cases. On the other hand, in several CRCTs, researchers defined clusters on the basis of administrative geographic areas, and rings composed a subset of these areas; in these studies, ring trials were a subset of a cluster-randomized design. To make this distinction clear, hereafter, we use “CRCT” to refer to traditional, cluster-randomized trials in which clusters were enrolled before index case presentation.

In ring trials, the ring was the unit of randomization and the unit of intervention (Figure 2A); in ring-stratified randomized trials, the unit of randomization and intervention was the individual, and randomization was stratified by rings for each index case (Figure 2B). In CRCTs, the units of randomization and intervention were clusters, and a single cluster sometimes contained multiple rings that overlapped in location but not in time (Figure 2C). In individually randomized trials, the unit of randomization was the individual, and randomization did not consider ring membership.

Index case ascertainment

In all but 2 studies, index cases were identified through passive surveillance, in which index case patients presented at health care facilities, where infection was confirmed with laboratory tests and then reported to surveillance systems (Web Table 1). Passive surveillance effectiveness depends on the extent of health care use and the robustness of the case reporting system (34–36). In 2 trials, researchers used active surveillance to identify index cases. In 1 study, health workers tested all individuals in study communities for malaria with rapid diagnostic tests and treated positive individuals; in the intervention arm, for household members with any positive tests, all individuals were offered treatment regardless of test results (19). A second trial includes an arm in which nonhousehold contacts of leprosy case patients who test positive for a serological marker of infection will receive treatment (other arms deliver postexposure prophylaxis) (37). In principle, active surveillance could also use serologic surveys to detect prior infections, but if prior infections occurred long before serologic assays, interventions may fail to prevent transmission (26).

Ring enrollment

The most common type of ring was household contacts (or nursing home contacts) of index case patients, especially in endemic, epidemic, and emergency settings (Table 2, Web Table 1). Studies of Ebola, influenza, COVID-19, chlamydia, and human immunodeficiency virus defined rings of contacts and/or contacts of contacts of index cases or household members of an index case. The only trials in which rings were defined on the basis of geographic proximity (e.g., 100–500 m) of index cases, researchers used cluster-randomized designs (Table 2). In future ring trials of environmentally transmitted or vector-borne disease, researchers could define rings on the basis of geographic proximity to index cases (7). In studies enrolling contacts of index cases, it may be difficult to identify contacts within the desired response window if the contact tracing system is not robust. Complete contact tracing and enrollment may be more difficult for stigmatized diseases, such as human immunodeficiency virus and Ebola (38). In trials in which rings are defined by geographic proximity, it may be difficult to enroll ring members in a timely fashion in the absence of a baseline geographic census identifying the location of all households.

Observation period

Outcomes within predefined observation periods were measured on the basis of the disease incubation period and the expected duration of intervention effectiveness (Web Table 1). For example, observation periods of 10–14 days were used in most influenza and COVID-19 studies, and malaria interventions used observation periods of 35 days or longer for ring mass drug-administration interventions and up to 24 months for reactive, indoor residual spraying, which is expected to have a longer effect duration. In some trials, intervention effects were expected to be transient, and participants could be enrolled in ring interventions more than 1 time. For example, in 2 trials of reactive focal mass drug administration, researchers defined observation periods of 5–8 weeks after the start of an intervention; after this period, if additional index cases occurred in the same area, the intervention was repeated around the new index case (20, 21).

A simulation study of ring trials showed the importance of carefully defining observation periods (39). Starting the observation period before the intervention is effective may attenuate effect estimates toward the null. This is because cases occurring soon after index case presentation may result from transmission prior to intervention. Longer follow-up periods will capture initial intervention effects on recipients as well as reductions in secondary transmission, which may be desired. For interventions with short-lived effects, ending the observation period too late could also attenuate effects toward the null because effects on onward transmission would be expected to be smaller. In vaccine trials, intention-to-treat effects are estimated according to randomized intervention assignment and define the observation period from the time of randomization, which may include the incubation period and time in which vaccinated individuals develop an immune response; per-protocol effects are estimated according to vaccination status, and the observation period starts after the incubation period and development of an immune response (40, 41). For example, in their primary analysis, researchers conducting a ring trial of the Ebola vaccine used a per-protocol approach that included outcomes 10 days or more after randomization (24, 42).

Response time

For infectious diseases with short serial intervals, rapid intervention delivery after index case detection is crucial to ring intervention effectiveness. Trials of influenza and SARS-CoV-2 postexposure prophylaxis typically had response times close to 1 day; response times were longer in other trials (Web Table 2). Response times longer than planned can result in secondary and possibly tertiary transmission before interventions take effect (43, 44). For example, in 2 malaria trials, researchers reported that longer-than-planned response times in some clusters might have limited intervention effectiveness and that response time differed between intervention arms (20, 21). If response time differs between arms, effect estimates may be biased.

Parameter of interest

CRCTs are amenable to estimation of total effects, spillover effects (i.e., indirect effects), and overall effects, each of which provides different information (45–47). Total effects are used to make inferences about effects on intervention recipients, and spillover effects are used to make inferences about untreated individuals in proximity to interventions and may reflect impacts on disease transmission in the study population. Overall effects are used to make inferences about effects on the general population and average across total effects and spillover effects. In all completed CRCTs and ring-stratified RCTs, researchers estimated overall effects, comparing all individuals in treatment clusters (including those outside of rings) with all individuals in control clusters (17, 20, 21, 48–50). In the ring trial of the Ebola vaccine, the primary analysis estimated total effects, comparing outcomes among vaccinated individuals in immediate versus delayed vaccinated groups; a secondary analysis estimated overall effects among all eligible individuals in each arm, including unvaccinated individuals (24). No trials estimated spillover effects among untreated individuals in treatment versus control clusters (45).

In CRCTs, it is common to estimate an overall effect, comparing cluster-level outcomes in treatment versus control clusters. However, when ring members compose a small proportion of study clusters, the overall effect can differ substantially from the total effect because study clusters include a large number of untreated individuals. This result may be more likely in elimination and emergency settings, where index cases typically occur in spatiotemporal clusters. For example, in 2 CRCTs in malaria elimination settings in which researchers estimated overall effects, the proportion of cluster members that participated in ring interventions ranged from 2% (20) to 27% (21). On the other hand, in endemic settings, index cases may be more evenly distributed within the study population, and ring members may compose a larger proportion of the study population; in this case, overall effects and total effects may be more similar. Future trials of ring interventions may benefit from estimating each type of effect (total effect, overall effect, and spillover effect, if possible) to shed light on intervention impacts in different subpopulations.

Internal validity

We assessed the risk of bias of 33 completed studies. There was a low risk of bias in 22 studies, some concerns about 8 studies, and high risk of bias in 1 study (Web Table 3). In the following paragraphs, we highlight potential risks of bias specific to ring trials and CRCTs of ring interventions, some of which were not identified during the formal risk-of-bias assessment.

Blinding.

The most common threat to internal validity identified in the risk-of-bias assessment was due to lack of blinding; in 11 trials, participants were blinded to their intervention status (51–61); the remainder were unblinded, typically because of the nature of the interventions. Unblinded studies are often more susceptible to measurement bias, particularly if outcome measurement is subjective, and may have lower retention or compliance (62).

Baseline balance.

In all but 2 ring trials (60, 63), all ring-stratified trials, and all but 1 CRCT (20), baseline characteristics were balanced between study arms. In 22 trials, researchers used stratified randomization to support baseline balance (Table 1). In CRCTs, if the number of clusters is relatively small, it can be difficult to account for baseline imbalances, even in covariate-adjusted analyses (64). Ring trials and ring-stratified trials are likely to have better baseline balance than CRCTs because randomization occurs after index case detection. This implicitly stratifies study arms by both location and by time, both of which may strongly influence disease incidence. Performing randomization after ring definition was typical in ring trials and ring-stratified trials, with some exceptions (60), but in all CRCTs, cluster randomization was performed prior to ring enrollment. In settings with strong spatiotemporal clustering, ring trials and ring-stratified trials can deliver interventions in the same geographic area, which can improve balance, whereas CRCTs are more vulnerable to imbalances in the number of index cases that occur during follow-up (Figure 2).

Contamination.

If there is inadequate social or physical distance between individuals with different treatment assignments, contamination may bias effect estimates toward the null. No ring trials or ring-stratified trials included social or physical buffer zones; however, contamination between rings may be unlikely in household- or facility-based ring trials. Ring-stratified randomized trials (Figure 2B) may be particularly vulnerable to contamination because individuals in the same ring may have different treatment assignments. In rings defined as households or nursing homes, contamination is more likely. Three of 15 CRCTs included geographic buffer zones between clusters to minimize contamination; none included buffer zones inside rings or clusters (Web Table 1). In 1 CRCT in which buffer zones were not included between clusters, researchers assessed possible contamination and did not find evidence of it (20), and in 1 ring trial in which households with index cases were enrolled, researchers reported contamination in which control households adopted intervention behaviors (65). It may be more feasible to include buffers in ring trials than in CRCTs using fixed geographic areas because ring trials are conducted in a small geographic footprint around index cases, leaving more space for buffers. On the other hand, researchers conducting CRCTs in rare-disease settings may need to enroll participants within very large geographic areas to obtain sufficient statistical power, leaving minimal space for buffers. The same principles apply to studies in which rings of participants are enrolled on the basis of contact networks: rings need to be separated by a reasonable number of network nodes to prevent contamination.

Noncompliance.

In practice, compliance with random intervention assignment is often imperfect. In trials of ring interventions, noncompliance included 1) eligible index cases did not trigger interventions (incomplete index case coverage); 2) ring members did not receive their assigned intervention (incomplete target population coverage); and 3) ring members received the incorrect intervention. In CRCTs, the level of noncompliance (cluster vs. individual) affects the magnitude of bias (66). Index case coverage ranged from 58% to 100%, and target population coverage ranged from 27% to 100%; both types of coverage were at least 80%, according to most study reports (Web Table 2). In 3 trials, some participants or clusters received the incorrect intervention, but in 2 of these trials, the proportion receiving the incorrect intervention was very small (20, 67, 68).

Ring trials require nimble implementation teams to deliver interventions to any study site location within a short response time. In CRCTs in which clusters are defined in existing administrative areas, it may be easier to establish intervention delivery infrastructure within each cluster, increasing compliance. Even so, compliance can remain a challenge in CRCTs; for example, in 1 trial report, authors stated that staffing and transportation limitations reduced compliance (20).

When noncompliance depends on participant characteristics or is correlated with loss to follow-up, intention-to-treat estimates that ignore noncompliance are biased (69, 70). Two trials investigated this possibility (20, 21); disease incidence in 1 was inversely associated with target population coverage (21). In any trial, when noncompliance occurs, analysis methods must account for posttreatment measures of compliance (66).

External validity

A common critique of trials is that they have poor external validity (71). Indeed, authors of some of the trial reports included in this review cited the need to evaluate ring interventions in multiple sites because benefits of ring interventions may differ between populations (17, 18, 20). Although CRCTs are often considered to have higher external validity than individual randomized controlled trials (RCTs) (72), this is not necessarily the case for trials of ring interventions, because the interventions are delivered to high-risk individuals. External validity of ring trials may be high when the majority of the study population is susceptible and eligibility criteria are inclusive, as was the case in most of the household postexposure prophylaxis studies and other ring trials, such as the Ebola vaccine trial (42). On the other hand, CRCTs of malaria ring interventions were predominantly conducted in low-transmission elimination settings, where infection occurred in hot spots driven by environmental factors and migration (17, 18, 20, 21). Thus, these trials’ findings may generalize only to populations with similar spatiotemporal infection patterns, environmental risk factors, and proportions of immune individuals.

Publication bias

All study registrations for studies that had been completed for at least 1 year had published a corresponding preprint or manuscript, suggesting that publication bias was not present.

Statistical power

Factors that affect statistical power of CRCTs are well established (73). Here, we focus on factors that affect power of ring trials and CRCTs of ring interventions. For several studies included in this review, researchers described insufficient statistical power (20, 49–51, 61, 74, 75). In CRCTs, the number of clusters required per arm commonly is estimated on the basis of the assumed baseline incidence, intraclass correlation (ICC), and true intervention efficacy. In ring trials, additional factors that affect statistical power include the starting day of the follow-up period, probability of case detection, intervention response time, and the force of infection from individuals outside of the ring (39). In a simulation study in which researchers used a mathematical model to investigate sample size requirements for immediate versus delayed Ebola ring vaccination, the factors that had the strongest effect on sample size were the baseline attack rate and the follow-up start day (39).

Probability of case detection.

If all detected cases trigger interventions, increasing probabilities of case detection require larger sample sizes, because more frequent intervention will cause incidence to decline if the intervention is effective (39). However, increasing case-detection probabilities may not require larger sample sizes in trials that do not repeat interventions if subsequent index cases occur during the observation period (20, 21).

Baseline incidence.

The assumed baseline incidence in sample-size calculations was low for elimination settings and studies during the late stage of an outbreak and was higher in other settings (Web Table 4). The illness rate of contacts, rather than the baseline incidence rate, was used in the power calculations in some studies of Ebola, influenza, and SARS-CoV-2 (24, 63, 65, 76, 77). An advantage of using ring trials rather than CRCTs when evaluating ring interventions in low-incidence settings is that individuals with the highest incidence in a population are enrolled in the former, which may translate to greater statistical power. In reports on 4 trials, including 3 CRCTs, authors stated that statistical power was low due to lower-than-expected incidence during the study period (49, 51, 61, 74). A shared feature of these trials, in contrast to ring trials, is that researchers enrolled a fixed number of individuals or clusters at baseline instead of at the time of index case presentation. By enrolling rings as index cases occur, ring trials are less susceptible to reductions in statistical power resulting from unexpected decreases in incidence. Simulation studies are needed to investigate whether there is a certain incidence level above which a CRCT is more efficient than a ring trial design.

Compliance.

Incomplete intervention coverage, longer-than-intended response time, and incorrect intervention delivery may compromise statistical power (78). Even in analyses that account for noncompliance (e.g., as treated, per protocol, instrumental variables), higher levels of noncompliance reduce statistical power (66). Authors of 1 study cited unexpectedly low intervention coverage as a potential explanation for limited statistical power (20). Authors of a modeling study found that a rapid response time was critical to ring intervention efficacy, especially at higher values of R₀ (44).

Ring size.

As in any CRCT, for ring trials, the number of clusters (rings) has a larger impact on statistical power than the number of individuals recruited per ring (8, 39). One consideration unique to ring trials is that increasing the ring size (e.g., diameter around the index case or degree of contact network connections enrolled per ring) may reduce the average risk in ring members. If so, increasing the ring size may have little to no benefit to statistical power. To our knowledge, this has not been formally investigated in simulation studies. More research is needed to evaluate the effect of ring size and membership on statistical power.

Intraclass correlation.

In CRCTs, the extent of clustering can have a large influence on required sample sizes (79). Accurate ICC estimates are often difficult to obtain during trial planning, especially in emerging infection or emergency settings (39, 72). For example, in the Ebola ring vaccine trial, the observed ICC of 0.14 was substantially higher than the expected ICC of 0.05 (24). For ring trials, ICCs within the ring around index cases are most relevant and may be especially difficult to obtain. Observational studies in which ICCs are estimated in populations adjacent to index cases would support the design of future ring intervention trials (80, 81).

Network structure within and between rings.

In none of the studies included in this review was transmission network structure considered in sample size calculations, but in 1 simulation study, researchers showed that transmission network structure can strongly affect statistical power in CRCTs (82). Statistical power reached 0 as the proportion of network connections shared between treatment and control clusters approached 50% (82). These findings may apply to ring trials as well, particularly for ring trials of directly transmitted diseases, and underscore the value of collecting data on spatial and network structure to support sample size calculations. In addition, studies may benefit from using simulations to inform sample-size selection, because using ICCs alone may overestimate statistical power when individuals share contacts between rings (83).

Ring trials versus CRCTs.

We note 3 critical differences between ring trials and CRCTs of ring interventions that we would expect to influence study power. First, the numbers of interventions and ring members per arm are balanced by design in ring trials but may be imbalanced in CRCTs when there is high spatiotemporal clustering and unpredictable fluctuations in incidence (e.g., emergency and elimination settings). In 4 CRCTs of ring interventions in which participants composing village or health-facility clusters were enrolled, the number of interventions per arm was not balanced, because the number of index cases varied between arms (20, 21, 48, 61). In 2 of these studies, researchers noted limited statistical power (20, 61). On the other hand, ring trials tended to have balanced numbers of index cases in study arms.

Second, as noted above, ring members may comprise a much smaller proportion of the study population in CRCTs than in ring trials. This is especially the case when index cases cluster spatiotemporally, as is common in emergency and elimination settings. For example, in a ring trial of the Ebola vaccine, the proportion of ring members was 76%, whereas in 3 CRCTs conducted in malaria elimination and meningitis outbreak settings, the proportion ranged from 2% to 27% (20, 21, 48).

Third, by definition, all clusters in ring trials include an index case and are included in analyses; in CRCTs, because clusters are randomized before index case detection, some clusters may have 0 index cases during follow-up and must be excluded from analyses. Exclusion of some clusters can reduce power in any setting with a rare outcome. For example, in a CRCT in a malaria elimination setting, only 61% of clusters had at least 1 index case, limiting statistical power (20). In a CRCT of influenza in nursing homes, the small number of outbreaks resulted in many clusters having no index cases, increasing the length of the study and reducing study power (61). We did not identify any simulation studies that directly compared statistical power of ring trials versus CRCTs of ring interventions, and this is an important topic for future research.

Ethics

The ethical guidelines for CRCTs largely apply to ring trials (84). We have outlined some ethical considerations unique to ring trials.

Informed consent.

In community-based CRCTs, consent is often required both at the cluster and individual levels (84, 85). In low- and middle-income countries, when the cluster is a community, obtaining group-level consent can be difficult, particularly if there is not an elected community leader to provide consent (86). In ring trials, this is complicated because ring members around each index case often do not compose an extant group, such as a school or village. Of the 8 completed trials in which participants composing village clusters were enrolled, both group and individual consent was obtained in 4 (17, 21, 24, 48). In the Ebola ring vaccine trial, researchers obtained from local leaders consent to administer ring vaccination in potential ring sites prior to enrolling ring members (42). Although it may still be important to obtain the support of local leaders to perform a trial, whether it is ethical to obtain consent from them depends on study circumstances. In addition, in CRCTs, individuals often provide consent to participate after clusters have been randomized for logistical reasons, so it is not possible to obtain consent for randomization (84, 86). In the Ebola ring vaccine trial, investigators sought informed consent from ring members after randomization and notified participants of their treatment assignment after consent was given (24).

Beneficence.

In the process of enrolling ring members, ring trials must balance the risk of potentially disclosing index case infection status, which could be harmful for stigmatized diseases, with the potential benefits of the ring intervention. This may be particularly difficult for ring trials in which ring members could be identified through contact tracing. In addition, for ring interventions that involve presumptive treatment of individuals without confirmed infection status (e.g., reactive focal mass drug administration), the potential risk of adverse side effects against benefits must be weighed, considering that some participants who experience such side effects may be otherwise healthy. Investigators frequently cited minimization of adverse outcomes as a potential benefit of ring interventions in comparison with interventions delivered to an entire population, and several studies monitored adverse effects as a secondary outcome.

Equipoise.

The comparison group for a ring intervention must be chosen to ensure equipoise, especially when there is evidence of intervention effectiveness if it is delivered at the individual level in a clinical setting. For example, in 3 malaria trials, researchers investigated whether treating all individuals near index cases was more effective than treating individuals near index case patients who tested positive according to a rapid diagnostic test (the standard of care) (18, 20, 21). Even though prior trials demonstrated the effectiveness of antimalarials delivered to individuals (87, 88) or through mass drug administration (89, 90), there was not clear evidence about the effectiveness of the potential ring intervention relative to the standard of care; thus, equipoise was present.

Equity.

Because ring trials are particularly useful in emergency settings, after trial completion, investigators may consider offering all participants interventions shown to be effective, to ensure equity. This consideration is particularly important in trials in low- and middle-income countries, where participants may have less access to care and cutting-edge therapies (85). In the Ebola ring vaccine trial, delayed vaccination was provided to the control group to assuage potential concerns of withholding treatment (24, 91). Future ring trials could be used in concert with stepped-wedge designs to ensure equity in study populations. Another potential advantage of ring trials, particularly for outbreak and emergency settings, is that ring interventions can immediately be implemented after trial discontinuation, as was done after the Ebola vaccine ring trial (92).

Extensions

Alternative designs.

Ring trials are amenable to additional design modifications, such as adaptive designs (93), as were used in the Ebola ring vaccine trial (42), and stepped-wedge designs (94).

Noncommunicable diseases.

Although we only identified ring intervention trials with infectious disease endpoints, in principle, ring trials could also be appropriate for noncommunicable diseases or health behaviors that diffuse through networks (e.g., gun violence (95, 96)). Offering interventions to individuals connected to index cases could be particularly useful for outcomes that are stigmatized or underreported (e.g., opioid-use disorders (97)). In addition, ring trials could be used for noncommunicable, vector-borne or environmentally transmitted diseases that tend to cluster spatially or temporally (e.g., Lyme disease, coccidioidomycosis). The design could be particularly useful for studying interventions in populations where climate change results in the introduction or reintroduction of diseases with environmental risk factors.

Limitations

Our search strategy may not have included all possible terms used to describe ring interventions, so our results may not encompass all prior trials of ring interventions. In our narrative review, we only identified a small number of simulation studies investigating ring interventions; only 1 investigated a ring trial design (39). We consider the paucity of research on this topic an important finding in itself that motivates future research.

CONCLUSION

Ring interventions are well suited to infectious diseases with asymptomatic and heterogeneous transmission. We identified multiple potential advantages of ring trials over ring-stratified trials and CRCTs for evaluating ring interventions. Although each type of trial has its limitations, overall, we identified in this review more potential threats to validity and statistical power in CRCTs of ring interventions and ring-stratified trials than in ring trials, especially in settings with rare and strongly clustered infections. Additional simulation studies are needed to formally compare design features and statistical power of these trial designs. We believe that ring trials hold promise, particularly for evaluations of ring interventions during public health emergencies, seasonal outbreaks, early or waning stages of an epidemic, and disease elimination or eradication settings. To date, novel trial designs have been adopted slowly, particularly in low- and middle-income countries (98). The COVID-19 pandemic has further underscored the urgent need for novel designs, such as the ring trial, that have the potential to maximize investments, reduce cost, and produce rapid, robust results (99).

ACKNOWLEDGMENTS

Author affiliations: Division of Epidemiology, School of Public Health, University of California, Berkeley, Berkeley, California, United States (Zachary Butzin-Dozier); and Department of Epidemiology and Population Health, School of Medicine, Stanford University, Stanford, California, United States (Tejas S. Athni, Jade Benjamin-Chung).

This work was funded by National Institute of Allergy and Infectious Diseases grant K01AI141616.

The data set is available from the corresponding author.

We thank the authors, participants, and coordinators of the studies included in this systematic review.

The content is solely the responsibility of the authors and does not necessarily represent the official views of the National Institutes of Health.

Conflict of interest: J.B.-C. is co-first author of reference 20. Because of this potential conflict of interest, she recused herself from evaluation of this study’s risk of bias.

REFERENCES