Sample size calculation for an individual stepped-wedge randomized trial

Aude Allemang-Trivalle<fnref n="1" />,<fnref n="2" />, Annabel Maruani<fnref n="1" />,<fnref n="2" />,<fnref n="3" />, Bruno Giraudeau<fnref n="1" />,<fnref n="2" />

**Correspondence:** Aude Allemang-Trivalle, Centre Hospitalier Régional Universitaire Tours, Clinical Investigation Center 1415, 37044 Tours Cedex 9, France. E-mail: [aude.allemang-trivalle@etu.univ-tours.fr](mailto:aude.allemang-trivalle@etu.univ-tours.fr)

<footnote n="1">¹ Université de Tours, Université de Nantes, INSERM, SPHERE U1246, Tours, France</footnote>

<footnote n="2">² INSERM CIC1415, CHRU de Tours, Tours, France</footnote>

<footnote n="3">³ Department of Dermatology, Reference Center for Genodermatoses and Rare Skin Diseases (Maladies Génétiques rares à Expression Cutanée-Tours), CHRU de Tours, Tours, France</footnote>
# ABSTRACT

In the individual stepped-wedge randomized trial (ISW-RT), subjects are allocated to sequences, each sequence being defined by a control period followed by an experimental period. The total follow-up time is the same for all sequences, but the duration of the control and experimental periods varies among sequences. To our knowledge, there is no validated sample size calculation formula for ISW-RTs unlike stepped-wedge cluster randomized trials (SW-CRTs). The objective of this study was to adapt the formula used for SW-CRTs to the case of individual randomization and to validate this adaptation using a Monte Carlo simulation study. The proposed sample size calculation formula for an ISW-RT design yielded satisfactory empirical power for most scenarios except scenarios with operating characteristic values near the boundary (i.e., smallest possible number of periods, very high or very low autocorrelation coefficient). Overall, the results provide useful insights into the sample size calculation for ISW-RTs.

**Keywords:** Clinical trials, Individual auto-correlation, Individual stepped-wedge randomized trial, Sample size calculation, Stepped-wedge cluster randomized trial

## 1 - Introduction

The individual stepped-wedge randomized trial (ISW-RT), also called randomized placebo-phase design, is a randomized trial in which subjects are allocated to sequences, each sequence being defined by a control period followed by an experimental period. The total follow-up time is the same for all sequences, but the duration of the control and experimental periods varies among sequences. All subjects are exposed first to the control treatment and then to the experimental one, and the date of the switch between the two treatments depends on the sequence to which subjects have been randomly allocated¹. Figure 1 provides an illustration of the ISW-RT. The y-axis indicates periods, and the x-axis indicates sequences.
The ISW-RT can be considered an alternative to the classical two parallel-arm trial in several situations, especially studies of rare diseases.

<figure><img src="image_1.png" /><figcaption>Figure 1. Diagram of the standard individual stepped-wedge randomized trial.</figcaption></figure>

The ISW-RT allows all subjects to receive the tested treatment at the end of the trial. Similar to a classical cross-over design¹,², this approach, where each subject serves as their own control, may exhibit greater statistical power than a conventional two-group parallel design in specific situations, particularly when there is a notably high level of within subject correlation. Although appealing, this design has not been widely used. It has been used in studies of obstructive sleep apnoea³, chronic constipation⁴, fine particulate matter exposure⁵, juvenile idiopathic arthritis⁶, myositis⁷,⁸ or even vascular malformations⁹,¹⁰. However, its use is reviewed among multiple designs addressing challenges in small clinical trials¹¹,¹², to study rare disorders¹³ or studies of fragile populations such as children¹⁴,¹⁵ (for which searchers face
ethical and recruitment difficulties). This design is suitable for studying disease-modifying
treatments in rapidly progressing and challenging diseases and is particularly appropriate in
early development of a new treatment.

While several publications focused on the analysis of ISW-RTs² designs, none, to our knowledge, proposed a sample size derivation. There is a recent study that focused on deriving the optimal allocation of individuals to treatment sequences in ISW-RT designs, considering the nesting of repeated measurements and possible attrition¹⁶. However, it did not address the issue of determining the required sample size and its variations based on different parameters. The ISW-RT is actually a particular stepped-wedge cluster randomized trial (SW-CRT). Indeed, the SW-CRT is defined as a randomized trial in which clusters are randomly allocated to sequences that determine the time for the cluster switch from the control condition to the experimental one¹⁷. Therefore, the ISW-RT can be considered an SW-CRT with clusters of size 1. Different sample size calculation formulas have been proposed in the context of SW-CRTs, thus considering cross-sectional and cohort designs ¹⁸⁻²². A web-based tool called the Shiny CRT Calculator has been developed for easily calculating the required headcount for SW-CRTs²³.

In the present study, we derived a sample size formula for ISW-RTs using results previously
obtained for SW-CRTs and then assessed its accuracy in situations with operating
characteristic values near the boundary with a Monte Carlo simulation study. In Section 2, we
present our motivating example: a clinical trial of rare dermatological pathologies mainly
affecting children. In the third section, we first introduce our statistical model. Then, we
derive the sample size formula for an ISW-RT. The simulation study is reported in Section 4,
and its results are presented in Section 5. We applied our sample size calculation formula to
our motivating example in Section 6. Finally, we conclude with a discussion in Section 7.
## 2 – Motivating example

The ISW-RT design was implemented in the PERFORMUS trial to assess the efficacy of sirolimus in treating low-flow vascular malformations in children¹⁰,²⁴. This was a multicenter, open-label, randomized clinical trial that included 59 children aged 6 to 18 years with low-flow vascular malformation from 2015 to 2018. Patients started the trial with an observational period, then moved to an interventional period during which they received oral sirolimus. The switch date between these two periods was randomized to either 4 or 8 months. The study lasted 12 months for each patient. One of the outcomes was pain, which was assessed with a 0-10 visual analogue scale, 0 indicating no pain and 10 untenable pain. Pain was assessed during 6 visits spread over the 12-month follow-up.

The choice of the ISW-RT design for the PERFORMUS trial was based on several critical considerations. Firstly, this trial focused on a rare disease affecting the pediatric population. Some of the contacted investigators had already administered sirolimus to children based on case reports and were therefore vehemently opposed to participating in a trial where included children might be assigned to a control group without any treatment. The ISW-RT design ensured that all participating children would receive sirolimus before the end of the trial, greatly facilitating recruitment by the investigators. Furthermore, we ruled out the possibility of using a classical cross-over design because we did not know the duration of the treatment's effects and, consequently, the potential impact of the "carry-over" phenomenon. Additionally, this design allowed us to create a control group composed of the same participating children (thus avoiding inter-individual variability and accounting for intra-individual variability). This approach had the advantage of minimizing potential confounding factors and making the trial results more robust.

In summary, the choice of the ISW-RT design for the PERFORMUS trial proved to be judicious due to the nature of the disease under study, the preferences of the investigators, and
the need to ensure equitable participation of all participating children while minimizing sources of bias.

# 3 - Methods

## 3.1 - Statistical model

We consider a normally distributed outcome measure that follows a specific pattern of change over time, referred to as its “trajectory”. This trajectory is characterized by a baseline value $\gamma$ (the average outcome in the control group) and time effects $\tau_t$, $t=0,...,T$, where T is the number of periods, with $\tau_0=0$ for identifiability. To account for the dependence between outcomes for the same participant over time, we introduce a participant-specific random effect in our modeling.

Thus, let $Y_{ijt}$ be the continuous outcome associated with individual $i$, at time $t$, in sequence $j$:

$$Y_{ijt} = \gamma + \tau_t + A_{jt}\delta + \eta_{ij} + \varepsilon_{ijt} \quad (1)$$

where

$$\eta_{ij} \sim N(0, \sigma_b^2)$$

$$\varepsilon_{ijt} \sim N(0, \sigma_w^2)$$

with the individual random effect $\eta_{ij}$ and the residual random error $\varepsilon_{ijt}$ all being independent of each other, and $A_{jt}$ equal to 1 if participants allocated to sequence $j$ receive the experimental treatment at time $t$, and equal to 0 otherwise.

The treatment effect, denoted $\delta$, is supposed to remain constant once the intervention has been implemented. This assumption is a strong and unusual assumption for individually randomized trials in which we usually consider that the intervention effect 3 months after it has been implemented is different to its effect 6, 9 or 12 months later, for instance. However, because there are an infinite number of options regarding how the effect of an intervention changes over time, our approach, although simplistic, offers the advantage to be manageable.
Finally, the model has a fixed time effect $\tau_t$ that distinguishes change in the outcome over time from change in the outcome due to intervention/treatment.

Under this model, the evaluations of the same participant at different times are considered to have an exchangeable correlation structure with therefore the same correlation, $r$, between the outcomes of any of the two times².

$$r = \frac{\sigma_b^2}{(\sigma_b^2 + \sigma_w^2)}$$

We also define the total variance $\sigma^2$ as

$$\sigma^2 = (\sigma_b^2 + \sigma_w^2)$$

So that $(\sigma^2, r)$ becomes an alternative parameterization of the variance components $(\sigma_b^2, \sigma_w^2)$.

## 3.2 - Sample size calculation

As previously explained, an ISW-RT can be considered a particular SW-CRT with clusters of size 1. To determine $N_{ISW-RT}$, the number of participants needed for an individual stepped-wedge trial, we start from the following formula by calculating the sample size of an SW-CRT $N_{SW-CRT}^{19}$:

$$N_{SW-CRT} = N_0 \times DE_{SW}$$

with $N_0$ being the sample size for a two-parallel group individually randomized trial and $DE_{SW}$ the stepped-wedge design effect. In a closed cohort design (i.e., a design in which participants are included only at the beginning of the trial and followed during the whole trial), $DE_{SW}$ involves the multiplication of two terms: the “Design effect for clustering” ($DE_C$) and the “Design effect for repeated measures on the same cluster” ($DE_R$)¹⁸.

$$DE_{SW} = DE_R \times DE_C$$

with the $DE_C$ formula as follows

$$DE_C = [1 + (m - 1) ICC]$$
where *m* is the number of participants from the same cluster and ICC is the intra-cluster correlation coefficient corresponding to the correlation between two randomly chosen observations in the same cluster. When considering clusters of size 1, we have *m* = 1 and ICC = 0, and the number of participants required for an individual stepped-wedge trial becomes

$$N_{ISW-RT} = N_0 \times DE_R$$

where *DE*<sub>*R*</sub> is the design effect for repeated measures for correlation *r*. According to Hemming et al., for closed cohort designs<sup>23</sup>

$$r = \frac{m \times ICC \times CAC + (1 - ICC) \times IAC}{DE_C}$$

where *CAC* is the cluster autocorrelation and *IAC* the individual autocorrelation coefficient. Hence, *CAC* corresponds to the ratio of the between-period *ICC* to the within-period *ICC*<sup>25</sup> and *IAC* measures the strength of the correlation between two observations on the same participant<sup>23</sup>. Because in an ISW-RT the *ICC* equals 0 and both *m* and *DE*<sub>*C*</sub> equal 1, the correlation coefficient *r* is reduced to the *IAC*. According to Hemming et al.<sup>23</sup>, the *DE*<sub>*R*</sub> formula is

$$DE_R = \frac{3w \times (1 - IAC) \times (1 + (w \times IAC))}{(w^2 - 1) \times (2 + (w \times IAC))}$$

where *w* is the number of sequences that corresponds to the number of periods *T* minus 1: (*T*−1).

So, the number of participants in an ISW-RT is as follows

$$N_{ISW-RT} = N_0 \times \frac{3(T-1) \times (1-r) \times (1+((T-1) \times r))}{((T-1)^2-1) \times (2+((T-1) \times r))} \quad (2)$$

where *w* is the number of sequences that corresponds to the number of periods *T* minus 1: (*T*−1).
To achieve a balanced design, round up this $N_{ISW-RT}$ value to $N^*_{ISW-RT}$ so that $N^*_{ISW-RT}$ is a multiplier of (T−1). This adjustment enables the attainment of a balanced design with a consistent number of participants in each sequence.

# 4 – Simulation study specification

To assess the accuracy of formula (2) in extreme situations, we conducted a Monte Carlo simulation study. We were interested in verifying this result in situations of low correlation (0.05) or high correlation (0.95). We also varied the number of periods *T* and tested the formula for low number of periods (*T*=3), corresponding to only 2 sequences.

Data were generated according to the previously described model (1) with $\gamma = 0$, $\tau_t = 0$ and $\sigma_b^2 + \sigma_w^2 = 1$, which remained fixed, without loss of generality.

## 4.1 – Specification of simulation scenarios

1. Calculate $N_0$ using the two-group independent sample t-test method for a given combination of *T*, $\delta$ and power parameters. The formula used is: $n = (\delta^2 / (Z_{(1-\alpha/2)} + Z_{(1-\beta)})^2 * (s1^2 + s2^2))$ where: *n* is the total sample size (per group), $Z_{(1-\alpha/2)}$ is the quantile of the standard normal distribution for the confidence level (1-α/2), $Z_{(1-\beta)}$ is the quantile of the standard normal distribution for the power (1-β), *s1* and *s2* are the standard deviations of the two groups, $\delta$ is the minimum difference you want to detect between the means of the two groups.

2. Calculate the sample size $N_{ISW-RT}$ from equation (2), for given *r*. Round up this $N_{ISW-RT}$ value to $N^*_{ISW-RT}$ so that $N^*_{ISW-RT}$ is a multiplier of (T−1).

3. Calculate the standard deviation parameters $\sigma_b$ and $\sigma_w$ as $\sigma_b = \sqrt{r}$ and $\sigma_w = \sqrt{1-r}$.
## 4.2 – Simulation and results.

4. For each sequence $j$, consider the subject $i$ ($i= 1 ... N*_{ISW-RT}/(T-1)$):

a. On an individual subject level, for each subject $i$ from sequence $j$, generate a subject random effect $\eta_{ij}$ from a normal distribution with mean of 0 and standard deviation $\sigma_b$.

b. Then, at the period level, for each period $t$, embedded in subject $i$ from sequence $j$, generate a residual error term $\varepsilon_{ijt}$ from a distribution following a normal distribution with mean of 0 and standard deviation $\sigma_w$.

c. Finally, calculate $Y_{ijt}$ from equation (1).

5. Fit model (1) using a linear mixed-effects regression - incorporating time effects $\tau_t$ - and record both the count of models that do not converge and the two-sided P-value for those for which convergence was obtained.

6. Repeat steps 4 and 5 for 5000 times for each combination of the simulation parameters.

7. The empirical power $\phi$ of the design is the fraction of p-values that are < 0.05 on the 5000 simulations.

The following combinations of the simulation parameters were pre-specified: $r=0.05, 0.2, 0.5, 0.9, 0.95^{18}$; $\delta= 0.25, 0.5$; $T=3, 6, 10$. This 5×2×3 factorial design scheme yielded a total of 30 combinations of these parameters. The set nominal power was 80%. The Monte Carlo precision for the empirical power at the 95% confidence level was ± 0.01. We conducted these simulations using R v4.3.1.

# 5 – Simulation study results

## 5.1 – Convergence
We found convergence issues only when the within-patient correlation *r* was low (i.e., when *r*=0.05; see Table I). At most, 870 of 5000 simulations did not converge (for the scenario with *δ*= 0.5, *T*=3 and *r*=0.05).

<table><caption>Table I. Description of non-convergent scenarios</caption><thead><tr><th colspan="7">Number of non-convergent scenarios / 5000 iterations</th></tr><tr><th>δ</th><th>T</th><th>r= 0.05</th><th>r= 0.2</th><th>r= 0.5</th><th>r= 0.9</th><th>r=0.95</th></tr></thead><tbody><tr><td rowspan="3">0.25</td><td>3</td><td>147</td><td>0</td><td>0</td><td>0</td><td>0</td></tr><tr><td>6</td><td>80</td><td>0</td><td>0</td><td>0</td><td>1</td></tr><tr><td>10</td><td>19</td><td>0</td><td>0</td><td>0</td><td></td></tr><tr><td rowspan="3">0.5</td><td>3</td><td>870</td><td>1</td><td>0</td><td>1</td><td>0</td></tr><tr><td>6</td><td>691</td><td>1</td><td>0</td><td>0</td><td></td></tr><tr><td>10</td><td>507</td><td>2</td><td>1</td><td></td><td></td></tr></tbody></table>

*δ* = treatment effect size; *T* = number of periods; *r* = individual auto-correlation coefficient

## 5.2 – Empirical power

Empirical power results are presented in Figure 2 and Table S1. Our formula was satisfactory in most scenarios. The formula worked particularly well for number of periods *T*=6 and treatment effect *δ*=0.25 whatever the correlation coefficient *r*. For all scenarios with *T*=3, except with *r*=0.05 and *δ*=0.5, the calculated empirical powers were lower than the targeted nominal power. In these cases, we therefore investigated whether adding one subject per sequence allows achieving the nominal power. In light of the findings outlined in Table S2, the inclusion of one additional observation per sequence exhibited an enhanced effect on statistical power, particularly evident in scenarios with higher correlation coefficients (*r*= 0.5, 0.9, and 0.95), i.e. scenarios for which the required sample size was found to be very small. Conversely, scenarios with lower correlation coefficients (for which large sample size are required), are, unsurprisingly, not impacted by the adjunction of one observation per sequence.
<figure><img src="image_2.png" /><figcaption>Figure 2. Empirical power according to the individual autocorrelation coefficient (r), number of periods (T) and effect size (δ). The first line corresponds to δ = 0.25 and the second to δ = 0.5.</figcaption></figure>

In the extreme situation of very low correlation coefficient (r=0.05) and high treatment effect
(δ=0.5), the simulated empirical power was very high (> 0.9). These results were surprising.
Consequently, we conducted further investigations by simulating new scenarios and varying
the value of the treatment effect δ. We obtained similar results. For instance, with r=0.05 and
δ=0.4, we achieved power values of 0.898, 0.928, and 0.924 for T=3, 6, and 10 periods,
respectively. We opted to examine Type I error for each scenario using a sample size of 50
subjects and an intervention effect δ set to 0. The results, displayed in Table S3, revealed
inflation specifically when r=0.05. We investigated whether a Kenward and Rogers²⁶
correction, as usually done for SW-CRTs when the number of clusters is low, changed the
results. We observed very similar results (Table S4), probably because we also observed that
the Kenward and Rogers correction did not allow to achieve correct type I error rates when
r=0.05 (Table S5). We have not been able to find any explanation for this phenomenon,
except that the model may not perform well in these extreme cases. Of note, the most
significant problem of convergence also occurred in these scenarios. Thus, in these situations
of r=0.05 and δ =0.5 (or 0.4), the statistical approach may not be well adapted. Nevertheless,
these situations are of low plausibility because a 0.05 correlation value seems to be very low.

Also, the calculated empirical power was greater 0.9 when the number of periods was T=10,
with r=0.5 and δ=0.5. This extremely high power can be explained by the increase in the
sample size when rounded to the upper integer to be a multiple of the number of sequences. In
fact, in this situation, the number of subjects required increased from 19 to 27.

6 – Application

We applied our sample size calculation formula (2) to our motivating example. Consider the
situation of planning a trial similar to the PERFORMUS trial, with pain as the primary
outcome. For a classical individually randomized trial with two parallel arms, we would need
199 participants (N₀) to demonstrate an effect size δ of 0.4, with power 0.80 and two-sided
type I error α 0.05.

Consider planning 6 visits (T=6 periods) and an r of 0.5. Using equation (2), we would need
49 participants to achieve a minimum power of 0.80. By rounding up, 50 participants would
be needed to have 10 participants per sequence. In doing so, the empirical power is estimated
at 80.7%.
# 7 – Discussion

In this study, we derived a sample size calculation formula for an ISW-RT design and studied its accuracy. Overall, our formula presented good results, particularly for realistic values of *r* (0.2 and 0.5) and number of periods *T*=6. It worked less well with extreme values, for example, when the autocorrelation coefficient was extremely low (*r*=0.05) or extremely high (*r*=0.95) but also when the number of periods was very low (*T*=3), which thus corresponds to two sequences. In the latter case, adding one additional subject per sequence might be advisable. However, our formula may not be optimal in situations with only two sequences.

Our statistical model assumes an “exchangeable” correlation structure within individuals over time. Therefore, we assumed that the *r* remains the same between whatever time points, for all participants. Although debatable, exchangeability assumptions are common to most approaches to sample size calculation for longitudinal randomized trials¹⁸. Moreover, our findings also depend on the assumption that the effect of the intervention is independent of the time when a participant crosses over from the control to the intervention, which is also a strong assumption. However, if an intervention's impact undergoes fluctuations over time, it could exhibit either a linear or non-linear pattern of increase or decrease. It is highly unlikely that the principal investigator of a trial will possess an a priori understanding of these dynamics. Consequently, our firm assumption of a consistent intervention effect, while acknowledged as a limitation, may prove challenging to overcome due to the inherent complexity of predicting such variations.

In the context of treatment comparisons across different periods, the need to address both carry-over effects and time-trends becomes paramount. Consequently, our proposed design is particularly well-suited for cases involving stable pathologies. It is crucial to ensure that there
are no lingering effects from the first treatment when the second treatment is administered.
This may involve implementing a wash-out period to minimize the risk of carry-over effects.
Moreover, it is imperative that the effects of the treatment given during the first period can be
reversed, ensuring that subjects return to a state similar to their initial condition at the start of
the second period. Another effective strategy to mitigate carry-over effects in ISW-RT is the
utilization of an observational control period. Furthermore, it's essential that the disease does
not exhibit significant progression between the two periods, avoiding spontaneous healing or
deterioration before the conclusion of the second period. This consideration often limits the
practical applicability of crossover designs and other study designs where interventions are
staggered over time²⁷.

Furthermore, we opted for a uniform allocation of participants to each sequence. However,
Moerbeek's study¹⁶ demonstrated that uniform allocation is not necessarily the most optimal
and depends on the correlation rate as well as the attrition rate (which we assumed to be
absent in our study). It is therefore advisable to consider an imbalanced allocation in certain
specific situations, by increasing the number of participants allocated to certain sequences
(typically the first and the last ones in particular).

In conclusion, our proposed sample size calculation formula for an ISW-RT design yielded
satisfactory empirical power for various scenarios but may underestimate the necessary
sample size under certain conditions, particularly for low number of periods.

## DATA AVAILABILITY STATEMENT

Our full simulation results are available as supplementary material for this article.

## CONFLICT OF INTEREST

The authors have declared no conflict of interest.
ORCID

Aude Allemang-Trivalle: https://orcid.org/0000-0001-5311-1191

Annabel Maruani: https://orcid.org/000000-0003-3734-810X

Bruno Giraudeau: https://orcid.org/0000-0003-3031-8258
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