A randomised placebo controlled trial of anakinra for treating pustular psoriasis: statistical analysis plan for stage two of the APRICOT trial

The secondary objectives of the trial include the following:

The primary outcome is the disease activity at 8 weeks measured using the Palmoplantar Pustulosis Psoriasis Area and Severity Index (PPPASI), adjusted for baseline PPPASI.

Secondary outcomes for APRICOT include the following:

Investigator assessed efficacy measures, which include

Participant reported efficacy outcomes, which include

Safety measures, which include

Additional exploratory/mechanistic outcomes will be collected during APRICOT. These outcomes will not contribute to the trial’s main findings and primary results publication, so they do not form part of the main trial statistical analysis plan and will be described in more detail in a separate analysis plan.

The final (stage two) analysis will be performed after all recruited participants have completed 20 weeks of follow-up post-treatment initiation. Analyses will be carried out by the sub-group-blinded trial statistician and will follow the intention-to-treat (ITT) principle. That is, all eligible randomised participants with baseline and at least one recorded outcome (over 8 weeks) will be analysed in the treatment arms to which the participant was allocated, regardless of the treatment subsequently received. The safety set (SS) population consists of all participants who received at least one dose of the assigned intervention and will be used in the analysis to describe adverse events.

All regression analyses will include adjustment for centre where appropriate, as this was a stratification factor in the randomisation; therefore, inclusion of this adjustment is necessary in the analysis to maintain the correct type I error rate [8, 9]. Additionally, for continuous outcomes, the outcome measured at baseline will be included in regression analyses to increase the power [10]. All confidence intervals will be two-sided and at the 95% level. A p-value < 0.05 will be interpreted as statistically significant for the primary outcome.

The number of participants randomised will be summarised by treatment arm and study centre (Appendix in Table 3). To summarise the patient flow through the trial, a Consolidated Standards of Reporting Trials (CONSORT) flow chart will be constructed [11] see (Fig. 1). This will include the number of patients screened, eligible and randomised into the trial, withdrawing from treatment and lost to follow-up, and the number included in the analyses.

Baseline characteristics will be summarised by randomised treatment arm. The variables to be summarised are presented in Appendix in Table 4. Categorical variables will be summarised by number and percentage in each category. Continuous variables will be summarised by mean and standard deviation for approximately normally distributed variables or median and interquartile range for non-normally distributed variables. No formal statistical tests will be performed because any differences between treatment arms at baseline will be the result of chance rather than bias due to randomisation.

The number withdrawing from the trial, including those lost to follow-up, will be reported by treatment arm and time point along with the reasons for the withdrawal. The overall loss to follow-up will be tabulated by treatment arm and visit. The proportions of participants missing PPPASI values (primary outcome) will be summarised in each arm and at each time point for which measurement is planned (see Appendix in Tables 5, 6, 7 and 8).

The number discontinuing the trial drug will be reported by treatment arm and week along with the reasons for the discontinuations (Appendix in Tables 9 and 10). Self-reported treatment adherence, as measured by responses to daily text messages and self-reported by patients using a paper trial diary or verbally self-recalled at study visits, will be reported by treatment arm and week for patients who have not yet discontinued the treatment or withdrawn from the study by the given week (Appendix in Table 11). An injection will be classed as being received if either a SMS response of ‘Yes’ is recorded for the day in question or if self-reported as a ‘Yes’. The adherence to the planned visit windows will also be summarised by treatment arm and visit (Appendix in Table 12).

The proportion of participants using investigator-directed ‘rescue’ medication, as summarised in Table 1, in the form of potent corticosteroid (e.g., mometasone furoate, betamethasone valerate ointment or cream) and the duration of use and amount used will be summarised by treatment arm (Appendix in Tables 13, 14 and 15). We will plot histograms for the number of days of use of rescue therapy by treatment arm, plot the proportion of participants on rescue therapy over time and the cumulative proportion of participants initiated on rescue therapy over time.

Where data allows, we will also summarise the overall proportion of participants using topical therapy during the treatment period, the duration of use and the amount used; histograms for the number of days of use of topical therapy will be constructed by treatment arm, and we will plot the proportion of participants on topical therapy over time.

If any prohibited medications are used (as defined in Table 1), we will also summarise the proportion of participants using prohibited medication, the prohibited medication used, the duration of use and the amount used.

Descriptive statistics will be presented for all outcome measures by treatment arm. For each primary and secondary outcome that is recorded at multiple time points, the outcome will be summarised by visit and treatment arm (Appendix in Tables 16, 17, 18, 19, 20, 21, 22 and 23). Summary statistics with 95% confidence intervals will also be plotted in line graphs for each outcome across time by intervention. Only participants with a completely recorded outcome will be used to calculate the summary measures.

Information on adverse events will be collected by means of spontaneous reports from participants and carers, clinical observation and clinical examinations and blood tests. A safety set (SS) population will be used for describing adverse events. This SS population will include all participants who receive at least one injection of study drug or placebo. For each event, local clinical investigators rate the relationship to the study medication as none/unlikely/possible/likely/definite. Adverse Reactions (AR) consist of the subset of non-serious adverse events (AE) rated to have a possible/likely/definite relationship with the study medication. Serious Adverse Reactions (SAR) consist of the subset of serious adverse events (SAE) rated to have a possible/likely/definite relationship with the study medication. If the event is considered related to the study medication, then local clinical investigators will also rate whether the reaction was unexpected (Yes/No). Events will be coded using terms of the clinical investigators choosing with reference to Medical Dictionary for Regulatory Activities (MedDRA) at the ‘Preferred Terms’ level.

Adverse events will be summarised by type (AE, AR, unexpected adverse reactions (UAR, a subset of the ARs), serious adverse events (SAE), serious adverse reactions (SAR, a subset of the SAEs) and unexpected serious adverse reactions (USAR, a subset of the SARs)), and by treatment arm. Adverse events will be tabulated by treatment group for both the number of events and the number of participants with the type of event.

A listing will be produced detailing all Serious Adverse Events (SAEs) and Reactions (SARs). Non-serious adverse events and reactions will be listed by MedDRA preferred term level. Non-serious adverse events will also be summarised by MedDRA system organ class and intensity (subjectively assessed by local clinical investigators as mild/moderate/severe). The number of events related to an infection will be tabulated. Details will be provided for those events related to infection, including the treatment prescribed, where applicable.

No hypothesis testing will be undertaken for adverse event outcomes, but approaches to assess signals for ARs will be explored, as described below (Appendix in Tables 24, 25, 26, 27, 28, 29, 30, 31 and 32). An adverse event of particular interest is injection site reaction. We will also separately analyse serious infections, defined by any infection leading to death, prolonged hospital admission or requiring IV antibiotics, as described below in further detail.

The mean difference in the week 8 PPPASI, adjusted for baseline, between the two treatment groups will be estimated using a mixed-effects linear (Gaussian) regression model. The model will include a random intercept for participants with fixed effects for time, treatment group, time-by-treatment group interaction and baseline PPPASI. Centre will be included in the model either as a random or fixed effect depending on the total number of centres recruiting to the study and the average number of participants recruited from each centre. The estimated treatment effect at 8 weeks will be reported with a 95% confidence interval and corresponding p-value. As the model adjusts for baseline PPPASI, this is equivalent to analysing the change from baseline with adjustment for baseline [12]. The main conclusion of the trial will be based on this analysis time point. We will also report the treatment effect at weeks 1 and 4.

Approximately 15 centres are anticipated to recruit, and therefore, a relatively small number of participants will be recruited per centre. Since random centre effects have been shown to be superior to fixed effects in terms of power and precision when the number of participants per centre is small, and equivalent to fixed effects when the number of participants per centre is larger [9, 13], the default option will be to include centre as a random effect. With centre as a random effect, where Y_ijk denotes the PPPASI measurement for participant i at time j from centre k, the primary analysis model will be model A:

where j = 1 to 3 time points (week 1, 4, and 8), i = 1 to 64 participants, and k = 1 to ~ 15 centres; TRT_i is the dummy variable (TRT_i = 0 or 1) for participant i; \( {PPPASI}_i^0 \) is the baseline PPPASI for participant i; t_x is the dummy variable for time (= 0 or 1) at time point x weeks; Week 1 is represented by t₄ = 0 and t₈ = 0; and \( {b}_{1,i}\sim N\left(0,{\sigma}_{b1}^2\right) \), \( {b}_{2,k}\sim N\left(0,{\sigma}_{b2}^2\right) \), and \( {e}_{ijk}\sim N\left(0,{\sigma}_e^2\right) \),

Within model A,b_{1, i} and b_{2, k} are random intercepts at the participant level and centre level, respectively. Each of b_{1, i}, b_{2, k} and e_ijk are assumed to follow normal distributions. An unstructured covariance matrix will be used [14]. The treatment effect at 8 weeks, β₁ + β₆,will be of primary interest. If, however, the variation between centres is low and the model fails to converge, then centre will be treated as a fixed effect instead. With centre as fixed, where y_ijk denotes the PPPASI measurement for participant i at time j from centre k, the primary analysis model will be model B:

where j = 1 to 3 time points (week 1, 4, and 8) and i = 1 to 64 participants; TRT_iis the dummy variable (TRT_i = 0 or 1) for participant \( i;{PPPASI}_i^0 \) is the baseline PPPASI for participant i;

t_x is the dummy variable for time (= 0 or 1) at time point x weeks; Week 1 is represented by t₄ = 0 and t₈ = 0; β_7k is a dummy variable for each centre k; for centre 1, β_7k will be constrained to be 0; and\( {b}_{1,i}\sim N\left(0,{\sigma}_{b1}^2\right) \) and \( {e}_{ijk}\sim N\left(0,{\sigma}_e^2\right) \),

Within model B, b_{1, i} is a random intercept at the participant level. Both e_ijk and b_{1, i} follow normal distributions. An unstructured covariance matrix will be used. The treatment effect at 8 weeks, β₁ + β₆,will be the mean treatment effect of primary interest.

Models will be fitted using restricted maximum likelihood (REML). Both models make assumptions about random effects distributions, correlation structure and residuals, which will all be investigated. If including centre as a fixed effect results in unstable model estimates, e.g., if a number of sites (> 1) have very few randomisations (≤3), we will exclude centre from the model (model C). Stata code for the primary outcome analysis is displayed in Table 2.

Every effort will be made to obtain follow-up data for all participants including those who stop treatment. The primary analysis will include all observed data and employ maximum likelihood estimation.This approach is efficient for handling missing outcome data under the missing-at-random assumption (MAR). That is, the probability of missing data is assumed to not be dependent on the values of the unobserved data themselves, but instead conditional on the observed values of the variables included in the analysis model.

Sensitivity analyses addressing the impact of missing data will explore departures from the main MAR analysis assumption and potential missing not at random (MNAR) mechanisms using Multiple Imputation (MI) and a pattern mixture approach (Carpenter and Kenward, 2008) for all patients on the primary outcome following the ITT principle. Imputation under MAR will initially be performed separately within each treatment arm using chained equations following the guidance suggested by White et al. [15]. The variables in the imputation model will be the same as those in the analysis model without including more auxiliary variables after taking into account the relatively small sample size of this study [16]. Imputations will then be modified to investigate the impact of a better or poorer response than that predicted by MAR (lower/higher PPPASI scores) for participants with missing data. To do this, we will define δ as the postulated mean difference in the rate of change of the PPPASI score between the observed and unobserved cases for each week unobserved. For each participant in each intervention arm, we will then modify the MAR imputed observations accordingly by δ. Imputed data sets will be analysed using the primary analysis model. Results will be combined across imputed data sets using Rubin’s rules. We will repeat the analysis for a range of δ corresponding to +/− 10, 20, 30, 40 and 50% of the rate of change of the PPPASI over 8 weeks in all observed participants. We will also consider the possibility that data is missing informatively in one arm only. Only imputations for active arm participants will be modified for a range of δ corresponding to +/− 10, 20, 30, 40 and 50% of the rate of change of the PPPASI observed over 8 weeks in the active arm and the primary analysis repeated. Subsequently, only imputations for placebo participants will be modified as described above. Fifty imputations will be run for each MI analysis.

Four supplementary analyses are pre-planned for the trials primary outcome:

Continuous secondary outcomes (fresh pustule count, total pustule count, plaque-type psoriasis - PASI, palmoplantar quality of life instrument and EQ5D-3 L utility score) will each be analysed in a similar fashion to the primary PPPASI outcome using a linear mixed effects model. Similar to the primary analysis model, each model will include fixed effects for treatment group, time, treatment group-by-time interaction and baseline value of the associated outcome. A random patient intercept will also be included in each of the models. If convergence problems are experienced, the approach outlined for the primary outcome will be followed.

Binary secondary outcomes (clear on PPP-IGA, development of disease flare, serious infection, and neutropenia) will each be analysed with a mixed logistic regression model. The models will include a fixed effect for treatment group and centre as a random intercept. If convergence problems are experienced, the approach outlined for the primary outcome will be followed. The treatment odds ratio (OR) will be reported with 95% CI.

Ordinal secondary outcomes (PPP-IGA, PGA) will be analysed with mixed ordinal logistic regression models. The models will include a random intercept for participant and fixed effects for time, treatment group, time-by-treatment group interaction and baseline value of the outcome. Centre will be included as a random effect initially, but if non-convergence occurs, centre will be treated as a fixed effect or will be excluded if unstable model estimates occur. We will report the change in odds of a one-category increase in the outcome for patients in the active arm relative to placebo. The ordinal logistic regression model makes assumptions about proportional odds which will be checked for each outcome. If the proportional odds assumption appears to be strongly violated, a mixed effect multinomial logit model may alternatively be fitted.

For the time to event outcomes (time to response of PPP, time and to relapse), we will initially plot Kaplan Meier curves to visualise the unadjusted response rate over time by treatment group. Since outcomes are observed at relatively few discrete time intervals (week 1, 4, 8 and 12) random-intercept complementary log-log models will be used to estimate the treatment effects for the time to event outcomes. The model will include treatment group as a fixed effect and a random intercept for centre. The subject specific (conditional) hazard ratio for the treatment group will be reported with 95% CI. If convergence problems are experienced by including centre as a random effect, the approach outlined above will be followed. The complementary log-log model is appropriate for the discrete nature of the survival data [17]. The model corresponds to proportional hazards in continuous time. The proportional hazards assumption will be checked. If this assumption is violated, an alternative parameterisation will be used e.g., including a treatment-by-time interaction that varies the effect by time or restrictsing the observation time.

For adverse events and reactions, a volcano plot, constructed as described in [18], which plots the risk difference of the non-serious adverse events and reactions by the MedDRA preferred term between the treatment arms against the p-value from a Fishers’ exact test, will be examined to identify the events with the strongest evidence for between arm differences. A volcano plot will also be constructed to examine non-serious adverse events and reactions by MedDRA system organ class. Because few SAEs are anticipated, the SAEs will be evaluated individually, but they may also be included in these plots if thought to aid review. Where useful negative binomial or zero-inflated Poisson regression models will be used to estimate relative risks, risk differences and incidence rate ratios of non-serious events by MedDRA preferred term and/or system organ class. Where suitable, the timing of adverse events (using hazard plots) by treatment arm will be examined.

A longitudinal analysis will be undertaken using a linear (Gaussian) mixed model to determine the treatment difference in PPPASI at 12 weeks. The analysis model will be the same as in the primary analysis but will include additional data at 12 weeks. The treatment effect for PPPASI at 12 weeks will be estimated and reported with 95% CI.

Since palmar disease may respond more quickly than plantar disease, exploratory analysis will separately estimate the efficacy of anakinra on the (i) disease activity at 8 weeks, measured using fresh pustule count on the palms, adjusted for baseline compared to placebo and (ii) disease activity at 8 weeks, measured using fresh pustule count on the soles, adjusted for baseline compared to placebo. For each of the palms and soles fresh pustule counts, a linear mixed effects model will be used, which includes fixed effects for treatment group, time, treatment group-by-time interaction, and baseline value of the associated outcome. A random patient intercept will also be included in each of the models. If convergence problems are experienced, the approach outlined for the primary outcome will be followed.

Missing baseline data are unlikely to be problematic for the analysis because the baseline values will be collected at the first clinic visit and centre will naturally be complete. However, if baseline values are missing, to avoid a loss of power within the analyses which adjust for baseline values, these values will be imputed with the mean baseline value calculated from the non-missing values using pooled data from both treatment groups. This technique improves the statistical efficiency in the estimation of the treatment effect and is justifiable since randomisation ensures that baseline values are independent of treatment group [19, 20].

The primary analysis will use all observed outcome data and will be conducted under the MAR assumption. As detailed above, we will conduct sensitivity analysis to assess the impact of departures from the MAR assumption on the results of the primary analysis. Secondary analyses will use all available outcome data and will also be conducted under the MAR assumption.

The IDMC will review safety and efficacy data at time points of their choosing. No statistical hypothesis testing will be completed for the IDMC. Stage one analysis did not involve formal statistical hypothesis testing; as a result, no adjustment for interim analyses has been made.

No multiplicity adjustments will be performed for the analysis of secondary outcomes, and results will be viewed as hypothesis-generating.