The Healthy Weigh Study

Analysis Plan 11.1 Statistical Considerations Descriptive analyses We will produce data summaries regularly using frequencies for categorical variables and means, medians, and ranges for continuous variables. We will assess data quality and examine distributional assumptions with graphical methods. To evaluate balance among groups achieved by randomization, we will compare baseline values of all variables across the 4 arms using appropriate tests. General procedures All primary analyses will be on an intent-to-treat basis including each participant in the group to which s/he was randomized, regardless of adherence to the assigned strategy. Given the high rates of missing data typical of weight loss studies, handling of missing data is an important issue. Primary analyses will use multiple imputation for the missing in-person weight outcome at 18 months, using the randomization strata (sex, employer, initial BMI), study arm and other baseline variables as predictors in the imputation model. Baseline variables will include age, race, income, education, marital status, household size, physical activities, eating behavior index, stages of change, SF-36 General Health, and baseline weight. Sensitivity analyses will be performed with imputation models that also use post-baseline data, , and recent weight loss trend before drop out, as well as an analysis that assumes that any participants for whom follow-up weight loss data are unavailable have had their weight return to baseline (weight at beginning of Pre Phase). Within each arm, this last assumption is likely to be conservative but this may not be the case in inter-arm comparisons, depending on the dropout rates in the different arms and true follow-up weights of the dropouts. Thus, a key secondary analysis will consider the effect of differential dropout among the treatment arms. For this analysis, methods that address potential patterns of MNAR may be considered in the missing data imputation, such as pattern mixture models as appropriate. Finally, we will also consider a per-protocol type analysis, which examines the difference in the intervention arms in the complete case data. Efficacy Analyses All hypotheses will be tested using two-sided, 0.05-level tests unless otherwise specified (notably the Holm testing approach will be used for the five primary hypotheses in Specific Aims 1-4). The primary analyses will be an unadjusted intent-to-treat analyses, using a t-test for differences in weight change from baseline to 18 months, as measured by the in-person weight, between each intervention group and the control group, and the combined compared to each single intervention, applying the Holm p-value correction for multiple comparisons testing. If weight change appears to be non-normally distributed in the blinded data, we will find an appropriate. Missing data will be handled as described above. Weight change between baseline and 18 months, with 95% confidence intervals (CIs), will be estimated for comparison with adjusted analyses. We will estimate regression models adjusted for the stratification variables (sex, employer, initial BMI) and other participant characteristics factors including age, race, income, and education. We will evaluate the evidence of confounding for other baseline variables (baseline weight, marital status, household size, physical activities- i.e total minutes of MVPA+walking/week, eating behavior index, stages of change, SF-36 General Health) using change in estimate criterion (10%). We will fit exploratory models of the repeated weight measurements that incorporate time as a polynomial function or using visit-specific indicator variables to determine the most parsimonious model that adequately describes the observed patterns, as necessary. Models will be built separately for the in-person and at home weight data. Models using the at-home weight data would be considered only as potential exploratory analyses comparing the 3 intervention arms, since at-home weights are not available for the control arm. We will investigate random-effects models that allow for baseline individual variability as well as variability in the changes in weights over time; an example is the following: E(weightij) = ß0 +ß1Timej + ß2Groupi+ ß3Xi + b0i + b1i Timej, where i indicates subject, j indicates assessment times, the parameters are fixed effects linking time, a treatment group vector, and a vector of other demographic or clinical covariates Xi to the outcomes, and b0i and b1i are random intercept and slope effects. Tests for significance of random effects will use likelihood ratio tests for nested models; we will compare models with different random effects structures using the maximized log-likelihoods and the Akaike Information Criterion (AIC). We will apply standard diagnostic techniques to assess model adequacy. We will use treatment by time interactions to assess whether the rate of change in weight differs by intervention arm. We hypothesize that incentives may be more effective among lower income individuals and will evaluate this using interaction terms of income with treatment group. We will explore differential effects by race and education and baseline levels of intrinsic motivation and stages of change. We will also consider other potential mediators, such as the home food and activity environment. To assess the sensitivity of treatment effect estimates to missing data, we mayfit hierarchical or mixed effects models with and without accounting for informative missing data. For Specific Aim 5, we will consider appropriate methods for cost effective analysis such as the models proposed below. We will assess the costs of each of the intervention arms from both the employer and social perspective and compare the cost differences between each arm relative to the effectiveness measured by incremental weight loss achieved. The principal incremental cost-effectiveness ratios between intervention and control arms will be from the employer's perspective and we will compare costs during the intervention from baseline to 18 months per unit change in weight. Secondary analyses may also 1) evaluate this same ratio but use either 6 months post- intervention data (24 month visit) or 12 months of intervention data (12 month visit) and 2) evaluate these 2 ratios using a limited social perspective. Cost models will use a generalized linear model with a log link and gamma family. Missing data strategies will parallel those described above. We will assess sampling uncertainty for the comparison of costs and effects by calculating parametric 95% CIs for the cost per kg lost and acceptability curves. Standard errors and correlation of the difference in cost and effect will be derived using a bootstrap procedure. 11.2 Power and Sample Size Considerations We have designed the study with adequate power to detect differences in weight loss over an 18-month period. Our intervention should achieve its maximal impact in maintaining initial weight loss at the end of Phase II (month 18), when the incentive payments cease. To maintain the experiment-wide Type I error and guard against false conclusions of effectiveness, we will use the Holm multiple comparisons adjustment for test the 5 primary comparisons in Specific Aims 1-4 . If the interventions are as effective as hypothesized, the proposed sample size maintains greater than 90% power to show significance for each of the three intervention arms compared to control and greater than 80% power to show significance for the combined intervention group compared to each of the two interventions alone. It is important to note that while we originally planned to recruit 328 participants, a small subset was unable to successfully set up their Withings scales post randomization due to Wi-Fi connectivity issues. Therefore, we increased our target sample size by the number of people who were unable to connect their Withings scales to the Way To Health platform (16 additional subjects), bringing our recruitment total to 344 participants. The final statistical analysis is adjusted for the stratification factors to account for any imbalances that may have occurred. We have previously communicated this information to the IRB and the members of the Data Safety and Monitoring Board (DSMB), who approved this approach. The following information outlines our original power calculations and sample size considerations. We plan to recruit approximately one third of the participants required for the start of Phase I from each of our participating employers (IBC, SEPTA, and City of Philadelphia). Given the large number of potentially eligible employees, we can, if needed, easily increase the proportion of participants from any of these employers to meet recruitment targets. Participants will be randomized to our 3 intervention groups and the control group using a 1:1 ratio for the intervention arms. We built in a margin of 20% of our original target sample size of 328 for potential attrition before the 18-month assessment, resulting in an expected 260 participants (65 per arm) who are available for analysis at the end of Phase II. This sample size will provide us with greater than 90% power to detect a difference in weight change between baseline and the 18-month weigh-in of 5 kg between each single intervention group and the control group (primary outcomes for Specific Aims 1-3) and 87% power to detect a 3 kg difference between the combined group and either the incentive or environmental strategies groups (Specific Aim 4). Namely, we will have greater than 85% power for the 5 primary comparisons of interest for an expected weight change between months 0-18 of -8 kg, -5 kg and 0 kg in the combined, intervention and control groups, respectively (a net difference between single intervention and control groups of 5 kg, combined intervention and control groups of 8 kg, and 3kg between the single interventions and combined group) and assuming a standard deviation (S.D.) of weight loss of 5 kg. We will also have greater than 80% power to detect a difference of 4.6 kg in weight change between single intervention and control groups and 7.3 kg between the combined and control groups (primary outcomes for Specific Aims 1-3), while maintaining approximately 80% power for a 2.7 kg difference between the combined and each single intervention (Specific Aim 4). For our secondary outcomes (Specific Aim 5), we wish to compare the cost differences between each arm relative to the effectiveness measured by incremental weight loss achieved. We will calculate a point estimate of cost per kg of weight loss based on estimated inter-arm differences in weight loss and the incremental cost of the interventions, as described in C.3.d.ii.c. For weight loss at 18 months, given an expected incremental cost of $810 (incentives) and incremental weight loss of 5 kg, 328 participants provide 80% power to detect a cost per kg lost of $430 and greater than 90% power to detect a cost per kg lost of $575. This study is primarily a test of the efficacy of these interventions. Due to resource constraints and because we do not yet know about intervention effectiveness, we did not power this study based on cost effectiveness analyses. Estimated detectable costs per kg are a function of wide confidence intervals due to sample size. 11.3 Measurement of effect: The goal of this analysis will be to assess relative weight loss in the intervention arms relative to control. For the principal cost-effectiveness analysis, measurement of incremental weight loss will be based on differences in weight between baseline and the 18 month visit; in secondary analyses it will be based on weight differences between baseline and 24 months and baseline and 12 months.