Designing Cluster Randomized Trials: A Practical Guide for Investigators

Abstract

Background:

An important consideration in the design stage of randomized controlled trials is whether individuals within each site should or can be randomized to study arms (an individually randomized controlled trial) or whether entire sites should be randomized (a cluster randomized trial) where the clusters are sites. Recently, cluster randomized trials have grown in popularity; however, investigators have expressed a need for guidelines related to selection of the best design – especially when considering more complex designs such as stepped wedge. This commentary attempts to provide such guidance.

Methods:

In this commentary, we address common misconceptions surrounding the appropriate use of cluster randomization and crossover designs (such as the stepped wedge design). The intracluster correlation coefficients for different levels of clustering are presented, and the impact of different designs on sample size discussed. We provide practical recommendations that are accessible to investigators from all disciplines, regardless of their level of statistical training. Based on these recommendations, we present a flow chart to help researchers identify a suitable trial design for their study. Additionally, we provide a table of commonly used statistical definitions related to cluster randomized trials and a table of design considerations for more complex designs to support effective consultation with a statistician during the design phase.

Conclusion:

Based on these guidelines, it is recommended that researchers prioritize the use of individual randomization and a parallel trial design when the goal of the study is to assess the efficacy or effectiveness of an intervention.

1. Introduction

Randomized controlled trials (RCTs) are considered the gold standard for testing the efficacy or effectiveness of an intervention and often these trials are carried out at multiple sites such as hospitals, primary care clinics, or geographical locations. An important consideration in the design stage of RCTs is whether individuals within each site should or can be randomized – corresponding to an individually randomized controlled trial – or whether entire sites should be randomized – corresponding to a cluster randomized trial (CRT) where the clusters are sites. Randomization aims to create comparable treatment groups so that differences can be attributed to the intervention. When clusters rather than individuals are randomized, the risk of baseline imbalance increases. Despite this, CRTs have grown in popularity, partly because of alternative crossover designs such as stepped wedge, but they require additional considerations in the design and analysis phase. Furthermore, some trials using complex cluster designs encountered problems such that investigators abandoned them in favor of simpler individual-level randomization.¹

Several review articles exist regarding clustered designs^2-8 including guidance for reporting.^9,10 However, despite the growing literature, awareness of these issues remains limited among researchers. This may be because many reviews appear in journals for statistical audiences, limiting accessibility to researchers without formal statistical training. We aim to provide resources that enable researchers to design trials with stronger internal validity and greater rigor in evaluating intervention efficacy or effectiveness.

This commentary addresses best practices for designing CRTs and provides guidelines for their use. Section 2 addresses common misconceptions regarding the use of cluster randomization and provides guidance for appropriate use. Section 3 outlines general design considerations of cluster randomization. Section 4 introduces general CRT designs. Section 5 provides guidance for appropriate use of more complex CRTs. Section 6 discusses the additional design considerations of complex and longitudinal CRTs and Section 7 provides concluding remarks. To aid trial design based on this commentary, we present a flow chart to help researchers collaborate with statisticians in selecting the most suitable study design (Figure 1). Although not discussed, we include individually randomized group treatment trials in which individuals are randomized but the intervention is delivered in a group setting (e.g., group therapy) because they share methodological considerations and analytic approaches with CRTs.^11,12 We also provide a schematic illustration of each CRT design considered in Figure 2 and provide in Table 1 a list of common statistical definitions related to designing CRTs. Finally, common misconceptions regarding the use of cluster randomization and complex cluster designs are summarized in Table 2 and additional design considerations for complex CRTs are provided in Table 3.

Figure 1: Flowchart for Determining When to Use a Cluster Randomized Design and Its Appropriate Level of Complexity.

provides a flowchart to guide researchers in deciding when cluster randomization is appropriate and, if so, whether a simple (i.e., parallel) or more complex design (i.e., standard crossover, stepped wedge, staircase, batched) best fits the study context.

Figure 2: Overview of Common Cluster Randomized Trial Designs.

provides a schematic of commonly used cluster randomized trial designs. Light gray shading denotes the control condition and darker gray shading denotes the intervention condition. The asterisk denotes when the control condition would receive the intervention in a wait-list control setting.

Table 1.

Key statistical definitions related to designing and analyzing cluster randomized trials

Term & Definition	Interpretation, example or formula
1. General terms
1.1 Cluster A naturally formed group in which individuals within the same group share similar characteristics and environment.	Example 1: In an educational setting, a classroom can be a cluster and all students in the same classroom share the same teacher, educational materials, and curriculum. Example 2: In the health care setting, a physician can be a cluster and patients who see the same physician will share the same treatment environment, level of knowledge and skills of the physician. Example 3: In an institutional setting, a ward or unit within a hospital or nursing home can be a cluster with patients sharing the same environment and staff.
1.2 Cluster randomized trial (CRT) A type of randomized controlled trial in which clusters are randomized rather than randomizing individuals directly.	Example 1: Different classrooms randomized to either a standard curriculum or a new curriculum aimed at improving student’s competency scores. All students within the same classroom will receive the same educational program. Example 2: Randomizing entire facilities (e.g., hospitals or nursing homes) to either usual care or a staff training program aimed at reducing falls. All patients within the facilities will be monitored for outcomes.
1.3 Level Refers to the hierarchical structure of a cluster randomized trial.	2-level Example: Below we provide an example schematic of a 2-level CRT where individuals are nested in clusters. For example, individuals nested in hospitals. 3-level Example: Below we provide an example schematic of a 3-level CRT where individuals are nested in subclusters which are nested in clusters. For example, individuals could be nested in wards (subclusters) which are nested in hospitals (clusters).
1.4 Intracluster correlation coefficient (ICC) The correlation between participants in the same cluster.	During the design phase, the ICC is ideally estimated using relevant data collected during a similar timeframe from the clusters to be included in the study. Otherwise, the ICC can be estimated from a literature review of relevant cluster trials, with emphasis on studies conducted in comparable settings and assessing similar outcomes. In some instances, investigators could also leverage pilot or preliminary data to help inform their estimate of the ICC; however, only larger pilot studies that produce precise estimates should be used for this purpose. In general, the ICC can be derived from the variance components of a statistical model. When reporting the results of a CRT, investigators should include the model-estimated ICC for all primary outcomes.9 For instance, for a normally distributed outcome variable: Two-level (defined in 1.3): $ICC=\frac{{\sigma }_c^2}{{\sigma }_c^2+{\sigma }_e^2}$, measures the correlation among individuals in the same cluster. ${\sigma }_c^2$: variance across clusters ${\sigma }_e^2$: variance within clusters, across individuals Example: Consider an investigator planning a CRT to evaluate a new intervention for lowering blood pressure in primary care clinics. To estimate the ICC, they first review prior CRTs that measured blood pressure in comparable settings and extract the ICCs reported in those studies. They also have pilot data from ten primary care clinics, which they analyze by fitting a model to estimate the between-clinic and within-clinic variance components, from which the ICC and its confidence interval are derived. The pilot-based estimate is much smaller than the ICCs found in the literature, so the investigator uses the range of ICCs from both sources in the power calculations. Three-level (defined in 1.3): ${\sigma }_c^2$: variance across clusters ${\sigma }_{sc}^2$: variance within clusters, across subclusters ${\sigma }_e^2$: variance within subclusters, across individuals $IC{C}_{cluster}=\frac{{\sigma }_c^2}{{\sigma }_c^2+{\sigma }_{sc}^2+{\sigma }_e^2}$, measures the correlation among individuals for different subclusters within the same cluster (i.e. between subcluster correlation). $IC{C}_{subcluster}=\frac{{\sigma }_c^2+{\sigma }_{sc}^2}{{\sigma }_c^2+{\sigma }_{sc}^2+{\sigma }_e^2}$, measures the correlation among individuals within the same subcluster and same cluster (i.e. within subcluster correlation). Example: Consider an investigator planning a CRT to evaluate a new intervention for reducing back pain in primary care practices. Randomization will occur at the practice level (cluster), with patients nested within primary care physicians (PCPs, subclusters). To estimate the ICCs, the investigator pulls relevant data from the electronic health system of the primary care practices to be included in the study during the same timeframe of the study. Their statistician then fits a statistical model to estimate each variance component and calculates the ICC for each level (practices and PCPs) along with confidence intervals for use in the power calculation. Magnitude of ICC: In most applications, ICC values are small and positive, which also vary substantially among different types of measures and settings and clustering level. For example, for continuous outcomes, the typical ICC values (at the lowest level of clustering) from the literature are listed in the table below.
	Domain	Typical ICC Values	References
	Health and primary care outcomes	0.016 [0.005 to 0.036] (Median interquartile range [IQR])	Stuart B, 202234
	Behavior change intentions	0 to 0.207 (Range)	Thompson DM, 201235
	Patient reported outcomes in the National Cancer Institute Community Oncology Research Program	0.015 to 0.23 (Range)	Snavely AC, 202536
	Mobility performance measures in Community-Dwelling Older Adults	0.05 to 0.10 (Range)	Perera S. 202037
1.5 Variance inflation factor (VIF) or design effect Quantifies how much larger a sample size must be for cluster randomization, relative to individual randomization, to achieve the same level of statistical power.	Example: A VIF of 1.3 indicates that cluster randomization requires 30% more participants than individual randomization to achieve the same level of statistical power. For a normally distributed outcome: Two-level (defined in 1.3): $VIF=1+(n_c-1)ICC$ $ICC$: intracluster correlation coefficient (defined in 1.4) $n_c$: average cluster size, the average number of individuals within a cluster. Example: Consider the example given in 1.4 of an investigator planning a CRT to evaluate a new intervention for lowering blood pressure in primary care clinics. Based on an initial calculation for individual randomization, 350 participants would be required to achieve 80% power. The investigator expects to enroll an average of 25 patients per clinic and, drawing on the literature, estimates the ICC to be 0.02. This yields a VIF of 1.48 (1 + 24×0.02), indicating that 168 additional participants (a 48% increase) are needed under cluster randomization to maintain 80% power. Thus, the total required sample size is 518 participants, corresponding to approximately 21 clinics (518 ÷ 25). Three-level (defined in 1.3): $VIF=1+(n_{sc}-1)IC{C}_{subcluster}+n_{sc}(n_{c^{\ast }}-1)IC{C}_{cluster}$ $n_{sc}$: average subcluster size, the average number of individuals within a subcluster. $n_{c^{\ast }}$: average cluster size (in terms of subclusters), average number of subclusters within a cluster. $IC{C}_{subcluster}$: within subcluster correlation (defined in 1.4) $IC{C}_{cluster}$: between subcluster correlation (defined in 1.4) Example: Consider the example given in 1.4 of an investigator planning a CRT to evaluate a new intervention for reducing back pain in primary care practices. Randomization will occur at the practice level (clusters), with patients nested within primary care physicians (PCPs, subclusters). Based on an initial calculation for individual randomization, 200 participants would be required to achieve 80% power. The investigator expects each PCP to enroll an average of ten patients, with each practice employing an average of eight PCPs. Using the ICC estimates their statistician generated, PCP-level ICC of 0.03 and 0.015 for the practice level ICC, yields a VIF of 2.32 (1 + 9×0.03 + 10×7×0.015), indicating that an additional 264 participants (a 132% increase) are required under cluster randomization to maintain 80% power. The total required sample size is therefore 464 participants, corresponding to approximately six practices (464 ÷ 8 ÷ 10). Note, the effect of clustering depends on the joint influence of both average cluster/subcluster sizes and ICCs. With large cluster/subcluster sizes, even small ICCs can yield a sizeable design effect.
1.6 Effective sample size The contribution of ‘independent sample size’ in clustered samples.	In extreme cases, such as if every individual is perfectly correlated with each other, meaning that all individuals in the cluster act like one individual and have the same outcome, the ‘effective sample size’ is the number of clusters. At the other extreme, if there is no correlation among individuals in the same cluster, meaning everyone in the cluster contributes distinct information, the result will be like an individually randomized controlled trial, and the ‘effective sample size’ is the total number of participants. The effective sample size (ESS) can be calculated: $ESS=\frac{N}{VIF}$ $N$: total number of participants $VIF$: variance inflation factor/design effect (defined in 1.5) Example: Due to clustering, a cluster randomized trial with a total of 518 individuals and a VIF of 1.48 is equivalent to 350 independent observations.
1.7 Coefficient of variation (CV) Quantifies the variation of cluster size	Used to adjust the VIF (or design effect) when the number of participants per cluster (cluster size) is expected to vary. The more variable the cluster sizes are, the larger the sample size needed. $CV=\frac{S{D}_c}{n_c}$ $n_c$: average cluster size, the average number of individuals per cluster. $S{D}_c$: standard deviation of cluster sizes Example: We could adjust the two-level VIF (defined in 1.5) for variable cluster sizes using:38 $VIF=1+\{(C{V}^2+1)n_c-1\}ICC$ If all clusters are the same size, CV=0, then this is the same as the two-level VIF (defined in 1.5). Example: Again, consider the example given in 1.4 of a cluster randomized trial to evaluate a new intervention for lowering blood pressure in primary care clinics. Based on an initial calculation for individual randomization, 350 participants would be required to achieve 80% power. The investigator anticipates variation in clinic size, with an average of 25 patients per clinic and a standard deviation of 5. Based on the literature, the ICC is estimated at 0.02. These values correspond to a CV of 0.2 (5 ÷ 25) and a VIF of 1.5 (1 + [{0.22 + 1}×25 -1]×0.02), indicating that an additional 175 participants (a 50% increase) are required under cluster randomization to maintain 80% power. The total required sample size is therefore 525 participants, corresponding to 21 clinics (525 ÷ 25).
2. Terms specific to longitudinal and crossover designs (using two level design (1.3) for simplicity)
2.1 Cluster-period A single time interval (period) for which a cluster is sampled.	Example: Below is a schematic of a trial with 3 clusters being sampled at 4 different time periods. Each box (such as the one highlighted in red) represents a unique cluster-period.
2.2 Closed-cohort The same individuals within a cluster are measured at each period.	Example: Below is a schematic of a trial with 3 clusters being sampled at 4 different time periods. In cluster 1 we have 2 individuals (blue and pink) measured at period 1 and these same individuals are being measured at each subsequent period. In this example, periods correspond to waves from a typical randomized controlled trial in which individuals are followed over waves of data collection.
2.3 Cross-sectional Different individuals within the same cluster are measured at each period.	Example: Below is a schematic of a trial with 3 clusters being sampled at 4 different time periods. In cluster 1 we have 2 individuals (blue and pink) measured at period 1 and different individuals (denoted by different colors) being measured at each subsequent period.
2.4 Within-period ICC Correlation of different individuals in the same cluster and period.	Example: The red arrow below represents the within-period ICC which is a measure of the similarity (i.e. correlation) between different individuals in the same cluster-period. During the design phase, the within-period ICC is ideally estimated using relevant data collected during a similar timeframe from the clusters to be included in the study. Otherwise, the within-period ICC can be estimated from a literature review of relevant cluster trials, with emphasis on studies conducted in comparable settings and assessing similar outcomes. In some instances, investigators could also leverage pilot or preliminary data to help inform their estimate of the ICC; however, only larger pilot studies that produce precise estimates should be used for this purpose. In general, the within-period ICC can be derived from the variance components of a statistical model. When reporting the results of a cluster randomized trial, investigators should include the model-estimated within-period ICC for all primary outcomes.10 For instance, in a two-level design (defined in 1.3) with a normally distributed outcome, the within-period ICC is given by, ${\rho }_w=\frac{{\sigma }_{cp}^2}{{\sigma }_{cp}^2+{\sigma }_e^2}$ ${\sigma }_{cp}^2$: variance within clusters in the same period. ${\sigma }_e^2$: patient level residual variance. Equivalent to the ICC for a two-level design given in 1.4 (additional examples provided in 1.4).
2.5 Between-period ICC Correlation of different individuals in the same cluster but different periods.	Example: The red arrows below represent the various between-period ICCs which are a measure of the similarity (i.e. correlation) between different individuals in different cluster-periods (defined in 2.1). In our example schematic below, we have 3 between-period ICCs characterized by the number of periods between the two participants: 1 period apart (${\rho }_b^1$), 2 periods apart (${\rho }_b^2$), and 3 periods apart (${\rho }_b^3$). It is common to assume all between-period ICCs are equivalent (${\rho }_b^1={\rho }_b^2={\rho }_b^3$) or impose a rate of decrease (i.e., decay) (${\rho }_b^{k+1}={\rho }_b^k\times r$ with $0<r<1$, $k=1,2$). In the design phase, the between-period ICC for outcomes measured at periods t and s is typically estimated using,39 ${\rho }_b^{\mid t-s\mid }={\rho }_w\times r_{ts}$ ${\rho }_w$: within-period ICC (defined in 2.4) $\mid t-s\mid$: absolute difference in the number of periods between period t and period s. $r_{ts}$: ratio of between-period to within-period correlation when outcomes are $\mid t-s\mid$ periods apart. This term implies that responses from individuals in the same cluster but at different periods are still similar, just possibly less so. This value is always assumed to be between 0 and 1. A value of 0 implies no between-period correlation and a value of 1 implies the within-period and between-period ICCs are equivalent. Common assumptions for ${\mathit{r}}_{\mathit{ts}}$: The ratio of between-period to within-period correlation is a constant ($r_{ts}=r$). This implies that all between-period ICCs are equivalent ${\rho }_b^{\mid t-s\mid }={\rho }_b$. In this situation r is commonly referred to as the cluster autocorrelation coefficient (CAC). Thus, the general expression for the between-period ICC under this assumption is given by, ${\rho }_b={\rho }_w\times r$ Example: Using our schematic above with 3 clusters and 4 periods, if the within-period ICC is assumed to be 0.2 (${\rho }_w=0.2$) and the CAC is assumed to be 0.5 ($r=0.5$), then this gives us a between-period ICC of 0.1 (${\rho }_b=0.1$) (i.e. regardless of how far apart measures are we assume the same level of correlation: ${\rho }_b^1={\rho }_b^2={\rho }_b^3=0.1$). The ratio of between-period to within-period correlation decays by r (commonly referred to as the decay rate) as outcome measures get further apart (${\rho }_{ts}={\rho }^{\mid t-s\mid }$). Thus, the general expression for the between-period ICC under this assumption is given by, ${\rho }_b^{\mid t-s\mid }={\rho }_w\times r^{\mid t-s\mid }$ Example: Using our schematic above with 3 clusters and 4 periods, if the within-period ICC is assumed to be 0.2 (${\rho }_w=0.2$) and the decay rate is assumed to be 0.5 ($r=0.5$), then this gives us the following between-period ICCs: ${\rho }_b^1$ (when measures are 1 period apart), ${\rho }_b^2$ (when measures are 2 periods apart), ${\rho }_b^3$ (when measures are 3 periods apart). In the analysis phase, the between-period ICC can be derived from the variance components of a statistical model (not included here). When reporting the results of a cluster randomized trial, investigators should include the model-estimated between-period ICC and/or decay rate for all primary outcomes.10
2.6 Intra-subject ICC Correlation of outcomes from the same individual but collected at different periods - only needed if using a closed-cohort design (defined in 2.2).	This is the same concept as the between-period ICC (defined in 2.5) except the outcomes are within the same individual instead of different individuals. If using a cross-sectional design (defined in 2.3), then this ICC is not needed since different individuals are measured at each cluster-period (defined in 2.1). Example: The red arrows below represent the various intra-subject ICCs in a closed-cohort (defined in 2.2) cluster randomized trial. In our example schematic, we have 3 intra-subject ICCs characterized by the number of periods between the two measures: 1 period apart (${\rho }_a^1$), 2 periods apart (${\rho }_a^2$), and 3 periods apart (${\rho }_a^3$). It is common to assume all intra-subject ICCs are equivalent (${\rho }_a^1={\rho }_a^2={\rho }_a^3$) or impose a rate of decrease (i.e. decay) (${\rho }_a^{k+1}={\rho }_a^k\times r$ with $0<r<1$, $k=1,2$). Typically, the same assumptions used for the between-period ICC (defined in 2.5) are applied to the intra-subject ICC. For instance, if all between-period ICCs are assumed to be equivalent, then all intra-subject ICCs would be assumed to be equivalent. If the between-period ICC is assumed to decrease as measures get further apart with a decay rate of r, then we would assume the intra-subject ICC would also decay at a rate of r. In the analysis phase, the intra-subject ICC can be derived from the variance components of a statistical model (not included here). When reporting the results of a cluster randomized trial, investigators should include the model-estimated intra-subject ICC and/or decay rate for all primary outcomes.10

Table 2:

Common misconceptions regarding the use of cluster randomization and cluster crossover designs

Misconception	Reasoning	Solution
Cluster randomization…
is more pragmatic.	How pragmatic a trial is depends on several factors such as eligibility criteria and the setting of the trial, not on the unit of randomization.	Use the PRECIS-2 tool13 to assess how pragmatic a trial is. Note that the unit of randomization is not a criterion.
improves generalizability.	Generalizability depends on sample representativeness and trial conduct, not the unit of randomization.	Use individual randomization. Consider your study population, develop strategies to enroll a representative sample, and work with collaborators to ensure the study design will maximize generalizability.
does not require informed consent.	Even in the instance of minimal risk, if interventions are delivered to patients, informed consent may be required.	If cluster randomization is necessary, use the guidelines provided in the Ottawa Statement on the ethical design and conduct of cluster randomized trials.14
should be used if there is any risk of contamination.	Cluster randomization introduces correlation and potential issues of confounding and bias. Only when the risk of contamination is severe should cluster randomization be considered.	Use individual randomization and develop strategies to minimize contamination, to measure contamination during the study, and adjust the sample size for potential contamination. Researchers can also utilize analytical expressions provided in Hemming et al. (2021)16 to determine whether cluster randomization is more efficient (meaning, requires fewer total participants) than individual randomization adjusted for contamination.
A crossover design should be used…
when it would be unethical to withhold the intervention (used for stepped wedge).	If this is true, then it is unethical to withhold the intervention until a trial begins or make one or more clusters wait until the last study period.	Consider a parallel design with a wait-list control (Figure 2).
when a staggered rollout is needed (used for stepped wedge).	Crossover designs are not the only designs that allow a staggered rollout.	Consider a parallel design with a staggered rollout (Figure 2).
to reduce the potential for confounding because clusters serve as their own control.	Crossover designs mitigate time-invariant confounding but introduce time-varying confounding—and, in some cases, time itself—as a potential confounder. Thus, researchers may be trading one source of confounding for others that are often more difficult to address.	Use a parallel design and utilize strategies such as covariate-constrained randomization to increase the likelihood of balance between arms at baseline. Also consider collecting a baseline outcome to account for potential imbalances in the analysis.

Table 3:

Pros and cons of various cluster randomized crossover designs

Design	Pros	Cons
Standard crossover	Number of control and intervention outcomes collected are balanced over time. Can incorporate a staggered rollout.33	May not be possible to “turn off” the intervention. Potential carryover effects – even when a washout period (i.e., time to allow the current treatment effects to dissipate before crossing over) is used. Conditions of the participants must be stable over time (e.g., if studying participants with a certain disease, then disease status should not change over time. For instance, if a participant can be cured in the first period of the study, then they have no reason to participate in subsequent periods).32
Stepped wedge	Under certain situations is more statistically powerful than a longitudinal parallel design. For example, when the number of clusters is limited and the ICC is expected to be large.	All clusters need to be recruited by the start of the study. Repeated sampling could create a heavy burden or increase attrition.
Batched stepped wedge	Not all clusters need to be recruited before the start of the study. More robust to trial disruptions if they occur between batches (i.e. trial delays between batches are not problematic).	Need to consider batch effects. May require a longer study duration.
Staircase	Fewer measures are collected within each cluster reducing the data collection burden and reducing the risk of attrition. Under certain situations is more statistically powerful than a stepped wedge design.30	All clusters need to be recruited by the start of the study. Statistical power depends on how time is considered (continuous or categorical) – treating time as categorical yields a more conservative power estimate.18

In all the designs listed above, researchers must consider time as a potential confounder and consider two to three sources of correlation: a within-period ICC, between-period ICC(s), and intra-subject ICC(s) (if closed-cohort design).

2. When to use cluster randomization

2.1. Common misconceptions

There are several misconceptions about when cluster randomization is appropriate (Table 2). One common misconception is that CRTs are better suited for evaluating intervention performance in real-world practice – that is, that cluster randomization is more pragmatic or improves generalizability. To assess the degree of pragmatism of a trial researchers can utilize the PRagmatic-Explanatory Continuum Indicator Summary (PRECIS-2) tool¹³ which examines various factors such as the eligibility criteria and the setting of the trial and does not include the unit of randomization as a criterion. Overall, generalizability depends on sample representativeness and trial conduct, not on the unit of randomization.

A second misconception is that obtaining informed consent is not needed in CRTs. Whether informed consent is needed and by whom can be challenging to discern under a CRT design. The Ottawa Statement on the ethical design and conduct of CRTs provides explicit guidelines.¹⁴ Generally, informed consent is required when individual cluster members are the direct recipients of study interventions, even in the instance of minimal risk. Consent is not only to inform about risks but also to preserve patient autonomy and the trust of patients and members of the public in research. RCTs including individuals with cognitive incapacity may require obtaining consent from family members or guardians. Waivers of consent may be appropriate when interventions are inherently cluster-level interventions (for example, programmatic interventions such as staff training in fall prevention).

A third misconception is that cluster randomization should necessarily be used whenever there is a potential risk of contamination. For instance, consider a dietary RCT where patients are individually randomized to a new nutritional counseling intervention or standard counseling at various clinics. Potential risks of contamination include: (1) participants may interact in waiting rooms and share details about their counseling sessions or materials; (2) clinicians or staff delivering the intervention might inadvertently deliver aspects of the new counseling approach to control participants; (3) educational materials or discussions regarding the intervention might be visible or overheard in shared spaces. Such contamination would cause the outcomes in the two groups to become more similar, reducing the apparent effect of the intervention and increasing the likelihood of a negative trial. When faced with potential contamination researchers should not default to cluster randomization; instead, they should consider retaining individual randomization, develop strategies to mitigate the risk, measure contamination during the study, and adjust power analyses.¹⁵ In the dietary RCT, some strategies to mitigate contamination include: (1) training staff to strictly adhere to protocols and assigning different staff to deliver each treatment condition and separate staff to collect evaluation data; (2) scheduling intervention and control participants at different times or days; (3) using different rooms for each treatment condition; (4) limiting access to intervention materials outside of sessions. Only in the case of severe contamination should cluster randomization be considered. For example, if the dietary RCT involved participants from the same household but randomized to different treatment conditions, then the shared environment would substantially increase the risk of contamination. Instead, researchers need to enroll one person per household or consider randomizing households. In terms of total sample size, Torgerson¹⁵ estimated that cluster randomization becomes more efficient – that is, requires fewer participants to achieve the same statistical power – than individual randomization adjusted for contamination when contamination exceeds 30%. Hemming et al.¹⁶ later derived analytical expressions to determine the exact contamination rate at which cluster randomization becomes more efficient.

2.2. Appropriate reasons

The necessity for cluster randomization typically arises from the nature of the intervention. For example, if the intervention is a policy change for hospitals, it would be infeasible to randomize individuals within each hospital to different policy conditions. The level of contamination or financial, logistical, or feasibility constraints may make cluster randomization the only practical option, despite its tradeoffs.

Finally, if a CRT design is used, researchers should report their results according to the Consolidated Standards of Reporting Trials (CONSORT) guidelines for CRTs.⁹

3. General considerations of cluster randomization

Because individuals within a cluster tend to be more similar to one another than to individuals in different clusters, outcomes within a cluster are correlated. This correlation is quantified by the intracluster correlation coefficient (ICC). CRTs must consider the ICC in the design and analysis stage. Not considering the ICC in the design stage could lead to an underpowered trial and not considering the ICC in the analysis stage could lead to overconfident estimates. It is also possible to have more than one level of clustering, for example entire hospitals could be randomized with participants nested within wards. Considering each level of clustering in the design and analysis phase would require a separate level-specific ICC (examples are provided in Table 1). Due to the correlation induced by cluster randomization, individually randomized trials are always more statistically powerful for a given number of individuals. In fact, even very small ICC values (ICC<0.01) can substantially reduce power. Researchers can utilize the variance inflation factor (VIF, also called the design effect, Table 1), which is the sample size inflation factor for using cluster randomization over individual randomization, as a tool for quantifying the impact of clustering on their study. Additional statistical terms used in designing CRTs, including effective sample size and the coefficient of variation are provided in Table 1. In general, the power of CRTs is driven primarily by the number of clusters rather than the number of individuals within a cluster (i.e., the cluster size). Therefore, in the case of multiple levels of clustering (e.g., patients nested in wards nested in hospitals), researchers should prioritize randomizing at the lowest level possible given their intervention (e.g., randomizing wards if possible) to maximize the number of clusters. In addition to the increased power, larger numbers of clusters result in more accurate parameter estimation, including standard errors. Depending on the ICC, the power of a CRT can be sensitive to the cluster size. For a fixed number of clusters, power gains are greatest as cluster size increases from 1 to about 1/ICC, with further increases having only modest impact.³ For example, with an ICC of 0.02, cluster sizes above 50 may offer little additional gain in power. If enrolling all individuals in each cluster who meet study criteria is not feasible, investigators should use sampling strategies for individuals that minimize selection bias, such as random sampling of individuals within randomized clusters.³

4. Common cluster randomized trial designs

A schematic illustration of each CRT design is provided in Figure 2. The simplest CRT design is a parallel design, in which clusters are randomized at baseline to a treatment condition and the clusters remain in their assigned arm for the entire study. A parallel design can be longitudinal, meaning data are collected at multiple time points (or waves) within the same cluster. Another common type of design is the crossover design in which clusters switch from one treatment condition to another. A standard crossover design begins with a parallel design in the first period and then all clusters switch to the other treatment condition in subsequent periods. Stepped wedge designs have grown increasingly popular. In this design, all clusters start in the control condition and each subsequent period more clusters cross over to the intervention. Once clusters transition to the intervention they remain in the intervention until the end of the study. Thus, by the end of the study all clusters have received the intervention. Recently, batched stepped wedge designs have been proposed which are essentially multiple stepped wedge designs in a single trial.¹⁷ Incomplete stepped wedge trials, such as the staircase design, do not require all clusters be sampled at every period. Instead, clusters are sampled for a number of control periods followed by intervention periods and this is carried out in a staggered fashion until all clusters have been sampled.¹⁸ Although not a focus here, variations of these designs exist, such as the hybrid parallel stepped wedge design.¹⁹

5. When to use a crossover cluster randomized trial design

5.1. Common misconceptions

There are several misconceptions regarding when a crossover design is appropriate (Table 2). One common misconception used to justify a stepped wedge design is that if an intervention is believed beneficial, it is unethical to withhold it, rendering designs that give all clusters the intervention ethically necessary. However, if withholding the intervention is unethical, it would also be unethical to delay its provision until the trial starts – or even longer for clusters randomized to receive it last. Furthermore, if the intervention’s benefit is uncertain, a stepped wedge design exposes more participants to a potentially ineffective treatment which raises ethical concerns.²⁰ If there are valid reasons to ensure all clusters receive the intervention (e.g., to facilitate cluster recruitment), a more appropriate option may be a parallel design with a wait-list control (Figure 2). In this approach, the study is conducted as a parallel RCT, and the control group receives the intervention after all data collection is completed or after the intervention has been shown to be beneficial. A variant of this design is to offer only key elements of the intervention to the control after the study ends; however, the latter is only appropriate for programmatic or training interventions, for which key elements have been identified. Because stepped wedge designs usually require a longer study time compared to a parallel design, using a parallel design with a wait-list control may allow all clusters to receive the intervention sooner.²⁰

A second misconception is that a staggered rollout of the intervention necessitates a design like stepped wedge, which is defined by this feature. In practice, a staggered rollout may be required due to logistical or feasibility constraints - for example, if the intervention arm requires hospital staff to be trained but only one or two hospitals can be trained at a time due to limited resources or budget constraints. However, there are ways to incorporate a staggered rollout under a parallel design while maintaining balance between treatment groups over time²¹ (Figure 2). An additional advantage of the staggered parallel design is that clusters can be enrolled and randomized over time (i.e., rolling enrollment of clusters) versus a stepped wedge design that requires all clusters be enrolled and randomized at the beginning of the study.

A third misconception is that crossover designs reduce confounding because clusters serve as their own control, making them preferable when the number of clusters is small or characteristics differ substantially. This is partially true for time-invariant cluster-level confounders; however, abandoning the parallel design for a crossover design simply trades one source of confounding for another. Specifically, crossover designs are susceptible to time-varying confounding since treatment groups are not balanced over time (e.g., seasonal effects or fluctuations in hospital admissions) and are more sensitive to trial disruptions (e.g., pandemics or policy changes). Furthermore, in designs like stepped wedge – where most control outcomes are collected earlier and most intervention outcomes later – time becomes a confounder by design. Instead, researchers should prioritize parallel designs and make efforts to balance clusters at baseline. For instance, researchers could utilize stratification, matching, minimization, and covariate-constrained randomization to increase the likelihood of baseline balance.²² Researchers could also include a baseline outcome measure in a parallel design – either by incorporating a baseline period (Figure 2) or by collecting the outcome along with other baseline characteristics at enrollment. The advantage is that between-cluster variability in the outcome, which can cause baseline imbalances, can be directly accounted for in the analysis.²³ Furthermore, incorporating a baseline outcome can improve statistical efficiency and increase power.^24-26

5.2. Appropriate reasons

One reason an investigator might use a crossover design is that the study would not be possible otherwise. For example, when the number of clusters is limited and the ICC is expected to be large, a crossover design will likely yield more power than a parallel design. However, this gain in power comes from the increased number of outcomes collected (i.e., additional waves of data collection), not from any inherent property of the crossover design.²⁰ Therefore, if the number of clusters cannot be increased, we recommend adapting the parallel design to increase power – for example, by adding a baseline outcome and/or using a longitudinal parallel design. Given that crossover trials with a small number of clusters (about 6 or fewer) are not uncommon,²⁷ we caution that regardless of the CRT design, there is an increased risk of chance imbalances, insufficient power to detect an intervention effect, and potentially inflated type I error.^28,29 Therefore, the rationale for using a small number of clusters should be well justified and analyses should be adjusted accordingly.²⁷

Finally, if a crossover CRT design is used, researchers should report their results according to the CONSORT extension for stepped wedge trials,¹⁰ which, although developed for stepped wedge designs, is applicable to the crossover designs discussed in this commentary.

6. Design considerations in longitudinal and crossover cluster randomized trial designs

6.1. General considerations

Given the repeated sampling of clusters over time, longitudinal CRTs must account for multiple sources of correlation. First, individuals measured within the same cluster and period are correlated (within-period ICC), analogous to the ICC described in Section 2. Second, individuals from the same cluster but measured in different periods may also be correlated (between-period ICC). Third, in closed-cohort designs, where the same individuals are followed over time, repeated measurements within individuals introduce an additional correlation (intra-subject ICC) that must be considered. The intra-subject ICC is generally the largest, followed by the within-period ICC, while the between-period ICC is usually the smallest. The number of periods in a longitudinal CRT determines the number of distinct between-period and intra-subject ICCs that could be considered. For example, in a study with three periods, one must account for correlations between measurements taken one period apart and two periods apart—for both between-period and intra-subject ICCs (examples provided in Table 1). Rather than estimating each ICC separately when conducting power calculations, investigators often make simplifying assumptions. A common approach is to assume that all between-period ICCs are equal, resulting in a single parameter to estimate—typically via the cluster autocorrelation coefficient (CAC; Table 1). Alternatively, the between-period ICC may be assumed to decrease (i.e., decay) at a fixed rate as the time between measurements increases. Similar assumptions are usually applied to intra-subject ICCs. Together, the assumptions about between-period and intra-subject correlations define the overall correlation structure of study participants (see Tables 1 and 2, Supplemental Digital Content, for illustrations and additional details). Depending on the anticipated values of the ICCs, only one type of crossover design might provide sufficient power. For instance, despite the substantial decrease in the number of outcome measures collected, there are situations where a staircase design is more statistically powerful than a stepped wedge design.³⁰ In the case of stepped wedge designs, it is well established that allowing the within-period correlation to differ from the between-period correlation at the design stage is crucial to avoiding an underpowered trial.^28,31 One common misconception when estimating the ICCs during the design stage is that higher values always produce more conservative power estimates. This applies only to the within-period ICC; for the between-period ICC, smaller values typically yield more conservative estimates.^28,31 Therefore, researchers should consider larger within-period ICCs and both larger and smaller between-period ICCs to properly assess the sensitivity of power estimates.

6.2. Design specific considerations

In a standard crossover design, researchers must assess whether the intervention can be “turned off”. For instance, if the intervention involves educating physicians, the knowledge gained cannot be removed in subsequent periods. In contrast, if the intervention involves use of a removable device, a standard crossover design may be appropriate. Researchers should also consider the expected duration of treatment effects and include washout periods to minimize carryover effects (when the effects of a treatment persist into subsequent periods). Finally, participant conditions should remain stable over time – for example, in studies of a specific disease, disease status should not change over time.³²

A general consideration of crossover designs is logistical and feasibility constraints. For example, the stepped wedge design requires all clusters be recruited and randomized to a crossover point by the beginning of the study and be repeatedly sampled throughout the study. This could create a heavy burden on clusters and/or study participants (if using a closed-cohort design) and could lead to issues with attrition especially in clusters randomized to receive the intervention at later time points.²⁰ Staircase designs (defined earlier) were proposed to combat this issue of attrition and data collection burden but still requires all clusters be enrolled at the beginning of the study because clusters will be randomized to a time at which they will begin data collection. If it is more feasible to recruit clusters during the study (i.e., rolling enrollment of clusters), maybe due to limited resources, then a standard crossover design³³ or a batched design could be useful. An additional benefit of the batched stepped wedge design is that the commencement of subsequent batches can easily incorporate delays. However, using a batched design would likely require a longer study time and the design and analysis would need to consider possible batch effects.¹⁷ These design considerations are summarized in Table 3.

7. Discussion

The aim of this commentary was to provide general design guidelines for CRTs, accessible to researchers regardless of their statistical training. When feasible, researchers should use individual randomization over cluster randomization due to the increased power and reduced risk of confounding and bias. When cluster randomization is necessary, then researchers should start with a parallel design and only consider crossover designs if there is a clear rationale (e.g., insufficient statistical power). Although parallel cluster trials may be more prone to confounding from baseline imbalances than crossover trials, methods such as covariate-constrained randomization and the collection of a baseline outcome can help mitigate this risk. Compared to parallel trials, crossover trials are more prone to confounding by time and time-variant imbalances and are more sensitive to trial disruptions.

This commentary is not a substitute for formal statistical consultation. We encourage investigators to engage with a statistician early in the design phase to determine the most appropriate trial design. We hope this commentary and the accompanying materials will contribute to the design of more robust clinical trials with enhanced internal validity and greater scientific rigor.

In conclusion, it is recommended that researchers prioritize the use of individual randomization and a parallel trial design when the goal of the study is to assess the efficacy or effectiveness of an intervention.^{34,35,36,37,38,39}