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Statistical analysis plan

Before starting analysis we developed our analysis plan for approval by the DMEC (seeAppendix 5). Trial populations

‘Analysed’population

Randomisation allocated all participants to one of the two treatments. The CONSORT guidelines require that the main analysis be‘by treatment allocated’. Ideally, therefore, this population should comprise all randomised participants. In practice only participants who contributed at least one BDI-II measured after baseline can usefully contribute. To get the most from their data, we used established methods to impute their missing data.

Complete case population

This population comprises only those participants whose outcome data are complete. It provides a sensitivity analysis of two issues: whether primary and secondaryfindings are sensitive to the absence of missing data, and the methods we used to impute those missing data.

‘Randomised’ population

Atfirst sight it is difficult to draw inferences about this population because some contributed no data after baseline, even on the BDI-II. Because we know the baseline characteristics of all these participants,

however, it is possible to reweight the‘analysed population’so that they match the characteristics of the randomised population, notably allocated treatment, stratifying variables and baseline BDI-II.

Imputation of missing data for ‘analysis by treatment allocated’

We excluded participants without follow-up data from the primary analysis‘by treatment allocated’. For each variable we summarised missing data by reason (mainly participant withdrew; questionnaire not returned; page missing; item missing). Where < 10% of data were missing, we treated them as if they were missing completely at random (MCAR).108_{If > 10% of data were missing, we explored the missing}

data and tabulated them by the stratification variables both as reported at randomisation and as validated after quality assurance; by participant demographics; and by other important covariates. Rather than exclude participants missing some data, we chose to impute these data (seeAppendix 5).

Missing items within a subscale

For missing items within a subscale we took account of methodological publications about the instrument. To impute missing items we used the principle that, if < 25% of the items within a subscale were missing for a participant at a time point, one should impute them by the weighted mean of the completed items, but if > 50% of the items within a subscale were missing for a participant at a time point, one should treat that subscale as wholly missing and impute it accordingly.

Missing subscales

Where between 25% and 50% of the items within a subscale were missing, we proceeded thus: if < 40% of the subscales for a participant at a time point were missing, we imputed all missing subscales by a single application of the general regression model for missing data imputation used in SPSS (Statistical Product and Service Solutions, SPSS Inc., Chicago, IL, USA),109_{taking account of all validated stratification}

variables. If > 40% of the subscales for a participant at a time point were missing, but < 20% of participants experienced that problem, we imputed all missing subscales by a single multivariate

imputation across all time points that also took account of all validated stratification variables. Fortunately these rules covered the whole of FolATED.

Missing time points

If one of the four time points for a participant was missing, we imputed all subscales within that time point byfive iterations of the repeated-measures model for missing data imputation used in SPSS using all other subscales at all time points together with age, gender, centre and group.107

Data description and transformation

Initially we summarised data by allocated treatment and centre. Rather than test for statistical differences between allocated groups at baseline, we adjusted for any imbalance by analysis of covariance. Our analysis plan assumed that residual variation from our statistical models follows Normal distributions. This is a robust assumption in the sense that only a substantial deviation would invalidate each analysis. So we plotted and reviewed residual distributions. As none of these was substantial, we did not need to transform data to improve consistency with the assumption of Normality. Hence we present all data as collected.

Methods for analysing outcomes

All of our statistical tests were two-sided with a significance level of 5%.

Continuous outcomes with baseline and more than one follow-up

We used the AUC average, not only to summarise treatment outcome across the whole of the 25 weeks of data collection, but also to take account of the correlation between successive measurements for the same participant. We calculated the AUC average by using the trapezium rule89,110_{to weight the outcome scores}

at baseline and the three actual follow-up points. From the imputed data set we estimated the average score for each participant over his or her total follow-up period as the area under the EQ-5D utility curve divided by the duration of follow-up, using the trapezoidal rule specified by the formula:

Uav¼∑ 2 j¼0 ðUjþUjþ1Þ 2 ðtjþ1tjÞ T ð1Þ whereUjis the utility attributed to thejth measurement,Tis the duration in days of the participant’s study

period,tjis the time in days at which thejth measurement takes place for that participant,111and

valuesj= 0, 1, 2 and 3 correspond to the baseline and three subsequent follow-ups respectively. We used similar formulae to calculate AUC averages for BDI-II, MADRS and SF-12 physical and mental

component scores.

As covariates in these analyses we used the validated stratification variables–centre, sex, new or continuing case, type of antidepressant and previous counselling. For the individual time points, which contribute to and illustrate the AUC, we used analysis of covariance to adjust for the corresponding baseline score.

Continuous outcome with no baseline and only one follow-up (Morisky scale)

We used analysis of covariance with baseline depression scores and validated stratification variables as covariates, to test whether medication adherence, measured on the Morisky scale, differs significantly

between the two treatment arms. If so, we would have added the Morisky score and ADMs recorded by GPs to the usual covariates.

Dichotomous outcomes (serious adverse events and adverse events)

We used logistic regression of (S)AE compared with no (S)AE over each participant’s time in the trial to test whether the proportion of (S)AEs differs between treatment arms, using baseline scores and validated stratification variables as covariates. We transformed all estimatedfixed effects back from their logistic form and summarised them by OR, standard error, 95% CI, and significance level.

Covariates to be adjusted within the statistical model

We kept baseline depression scores and validated stratification variables as covariates throughout. We also explored covariates of potential scientific relevance, including demographic (notably age, ethnicity, marital status, number of dependants and employment status, coded in accordance with usual demographic practice) and clinical (e.g. referral source, smoking, alcohol consumption and medication adherence, measured by both Morisky scale and recorded prescriptions). Wefitted and retained these if they showed evidence of an effect at a significance level of 10%.

Interactions to be tested

Within each analysis we tested for interaction between treatment and centre, not least because of substantial differences in psychiatric practice and recruitment policy. Onfinding no evidence of interaction we estimated the treatment effect for each centre. We also tested for interactions between treatment and significant covariates.

Deviations from protocol

During the trial there were two protocol deviations that resulted in systematic missing data–one within a centre at one time point, the other within a single instrument early in the trial. First, early in the trial 13 participants in one centre did not receive appointments for visits at 4 weeks as the centre was under pressure from a large number of referrals; fortunately preventive action prevented any recurrence. Second, early in the trial 83 participants completed an incorrect version of the MADRS instrument: 40 at screening; 29 at randomisation; eight at 4 weeks; and six at 12 weeks. As both were administrative errors balanced between treatment groups, however, sensitivity analysis suggested that neither resulted in systematic bias. We therefore invoked our standard missing data procedures (seeImputation of missing data for ‘analysis by treatment allocated’, above).

Sensitivity analyses

We applied three main sensitivity analyses–to the BDI-II as primary outcome in thefirst instance, with the intention of applying them to other outcome measures if the BDI-II proved sensitive to alternative

assumptions. First we used‘complete case’analysis to test the sensitivity offindings to the absence of missing data; and the methods we used to impute those missing data. Secondly we used multi-level modelling with the same covariates, also known as repeated measures analysis of variance, to test the sensitivity offindings to our choice of AUC as main method of analysis; we estimated parameters for three

fixed factors–the three time points (4, 12 and 25 weeks), centre and treatment group. Finally we

reweighted the‘analysed population’to match the characteristics of the‘randomised population’, and test the sensitivity offindings to non-response. To do so, we matched the participants completely lost to follow-up to participants from the analysed population. First we linked them by allocated treatment, centre and gender. Then we used a hierarchical cluster analysis to identify the best set of variables to match the non-responders to members of the responding trial population–age, marital status, reported alcohol intake, and BDI-II at screening and at baseline. We conducted this procedure both on raw data and on imputed data.

Biochemical analyses

Thefirst of our secondary objectives was to explore whether baseline folate and homocysteine predict response to treatment–the difference between baseline and follow-up. We followed participants at

12 weeks, as they completed the trial medication, and at 25 weeks, the usual endpoint of antidepressant trials. Though many of our analyses of effectiveness use simple linear regression, this is less well suited to analyse topics where multicollinearity, that is multiple correlation, plays a major role. Instead we use repeated measures analysis of variance, which examines all four time points (i.e. baseline and 4, 12 and 25 weeks) simultaneously byfitting all four measures and adjusting for stratification variables, baseline measurements, biochemistry, demography and other covariates.