SSB Attachment 1 Data Collection Background

Supporting Statement B
Attachment 1

Data Collection Background
Analysis

OS Objectives, Hypotheses, and
Biomarkers

7.3

Data Analysis

Analyses of longer term intervention effects will employ the weighted (2-sided) log rank
statistic as originally described (The Women’s Health Initiative Study Group, 1998). Such a
statistic can be written
T = Σ wi ( Oi - E i)
where wi is the value of the weight function evaluated at the ith largest time from
randomization to clinical outcome event among women in both groups, Oi is one or zero
depending on whether the outcome occurred in a woman in the treated group or not, and Ei is
the conditional expected value of Oi. If Vi represents the conditional variance of Oi, then it
follows that the variance (σ2) of T is estimated by σ2 = Σ wi2Vi and the test for differences
between groups is then made by referring T2/σ2 to the 95th percentile of a chi-square
distribution on one degree of freedom.
The weighting was intended to enhance test power under the expectation that intervention
versus control disease incidence ratios increase in absolute value approximately linearly as a
function of time since randomization. The weights wi were chosen to equal time from
randomization up to a disease-specific maximum (three years for cardiovascular disease and
fracture occurrence, 10 years for cancer occurrence and total mortality) and to be constant
thereafter. Because this assumption was supported in some instances in the hormone trials and
not in others, both weighted and unweighted statistics will be used, with unweighted statistics
as the default test statistics unless a prior evidence had suggested otherwise (e.g., for effects on
cancer incidence).
To examine post-intervention effects, weighted and unweighted time to event analyses will be
conducted, typically using date of the close-out visit (or date of official notification of study
closure for the HT trials) as the “time zero” for these analyses. Weights for post-intervention
analyses will be defined to account for changing exposure to the interventions, lag-time and
carry-over effects.
Analyses of intervention effects will typically be stratified on baseline age (50-54, 55-59, 6069, 70-79), and self-reported prevalent disease (if applicable) for that outcome, and the
categories of the other interventions. The primary HT comparisons will be examined
separately based on baseline WHI hysterectomy status.
To assess potential selection bias among Extension Study participants relative to the initial trial
cohort, comparisons of demographics, health history, adherence to intervention and key
outcome event rates will be made between Extension Study enrollees and non-enrollees using
data from the initial WHI database. Methods to account for non-representative enrollment
using probability weighted tests may be employed if there is evidence of noteworthy selection
in Extension Study enrollment.

All analyses of clinical trial results will be reported as two sided tests with acknowledgement
of multiple testing issues, either by appropriate adjustment of p-values and confidence intervals
or by an acknowledgement of the number of tests performed.
More detailed explanatory analyses will include tests for group differences with concomitant
adjustment for covariates, as well as explanatory analyses that examine the extent to which an
intervention benefit can be explained by changes in intermediate variables and outcomes (e.g.,
nutritional and biochemical measurements). These analyses will be conducted using relative
risk regression methods, with appropriate account of measurement error in the intermediate
variable measurements, using data obtained in a reliability substudy. Nested case-control and
case-cohort sampling procedures (see next subsection) will be used in most such analyses since
stored materials used to determine immediate variable values will not be routinely analyzed for
the entire CT cohort.
Simple graphical displays and standard statistical methods will be used to present biochemical,
bone density, and nutritional results by treatment group, clinic, and time since randomization
during the course of the CT. Similar displays will describe the frequency and severity of
adverse effects.
Observational Study
The ability to estimate relative risks reliably for the outcomes of interest in the OS as a
function of baseline characteristics (exposures, behaviors or biologic measurements), or as a
function of changes in such characteristics between baseline and three years is dependent on
the accurate measurement of the characteristics (and outcomes) under study, and the accurate
ascertainment and proper accommodation of all pertinent confounding factors. Even
measurement error that is nondifferential in the sense that it is unrelated to disease risk given
the 'true' characteristic values, can severely attenuate or otherwise distort relative risk
estimates. Since many of the characteristics to be ascertained in the OS (e.g., nutrient intakes,
blood cholesterol) are subject to noteworthy measurement error, a stratified 1% random
subsample of the OS women had repeat baseline information and specimens obtained at
between one and three months following their OS enrollment, and again at between one and
three months following their three year clinic visit. This reliability subsample provides
information of the reproducibility of the measurements taken (Langer et al, 2003), and can be
used, under classical measurement error assumptions, to correct relative risk estimates for nondifferential error in predictor and confounding variables. The 1% reliability sample was
stratified on age, racial/ethnic group, and socioeconomic group. The size of the OS cohort, and
the comprehensive set of measurements obtained allow a particularly thorough accommodation
of confounding, by means of individual matching, stratification or regression modeling.
Relative risk regression methods (e.g., Cox, 1972) will also provide the primary data analytic
tool for the OS. These methods, which can be thought of as an extension of classical personyear methods that avoids the assumption of constant disease risk for a study subject across the
follow-up period, allow flexible modeling of the risks associated with the characteristics under
study, as well as flexible accommodation of potential confounding factors, by means of
stratification, matching, or regression modeling. Though less well developed they can also
accommodate the types of reliability sample alluded to above (e.g., Pepe et al, 1989; Espeland
et al, 1989; Lin et al, 1992), in order to produce 'deattenuated' relative risk estimates. Finally,

relative risk regression methods are also readily adapted to accommodate nested case-control
(Liddell et al, 1977; Prentice and Breslow, 1978) and case-cohort (Prentice, 1986) sampling
schemes.
Nested case-control sampling proceeds by selecting for each 'case' of a study outcome one or
more 'control' women who have not developed the disease in question by the follow-up time at
which the corresponding case was ascertained. Additional matching criteria in the OS will
typically include baseline age, clinic, and date of enrollment, and depending on the analysis
may also include racial/ethnic or socioeconomic group, or other factors. Nested case-control or
case-cohort sampling provides the only practical approach to reducing the number of OS
women whose blood specimens need be analyzed and processed, if the measurements of
interest cannot be assumed to be stable over time. For example, certain of the antioxidant
concentrations to be measured in blood specimens are known to substantially degrade over the
course of a few months or years of storage, in which case the follow-up-time-matched aspect
of the nested case-control approach is essential to valid relative risk estimation. For
measurements that are stable over time, however, case-cohort sampling could provide an
alternative that has some decided advantages. Case-cohort sampling involves the selection of a
random, or a stratified random, sample of the cohort to serve as a comparison (control) group
for the cases of all the outcomes under study.
Analyses that relate change in risk factors to disease risk have particular potential for gaining
insight into disease mechanisms. For example, the OS provides a valuable forum for
addressing the issue of whether or not the association between low blood cholesterol (e.g.,
<160 mg/dl) and excess non-cardiovascular mortality derives primarily from persons who have
experienced major reductions in blood cholesterol over the preceding three years. In fact the
OS is large enough that such analysis could be restricted to women with relatively low baseline
blood cholesterol (e.g., lowest two quintiles) in order to avoid a complicated interpretation if
the effect of interest happened to 'interact' with baseline cholesterol measurement.
Furthermore the OS, by virtue of ascertaining a range on non-specific markers of debility or
disease (e.g., serum albumin, hemoglobin; cancer biomarkers; baseline and follow-up disease
prevalence by questionnaire and physical exam) may be able to examine whether the excess
mortality associated with reduced blood cholesterol can be explained by the presence of
recognized or latent disease. The careful accommodation of measurement error in predictor
and confounding variables is particularly important in such risk-factor-change analyses.
Appendix 3 of the original WHI protocol provides power calculations for OS analyses as a
function of disease rate, exposure frequency, relative risk, follow-up duration and, importantly,
as a function of subsample sizes corresponding to racial/ethnic, age, and other important OS
subgroups.
Clinical Trial and Observational Study
Separate analyses in both the CT and OS will be conducted according to self-reported baseline
prevalence of the clinical outcome being analyzed. In fact, whenever applicable, relative risk
analyses based on randomized CT comparisons will be accompanied by corresponding OS
relative risk analyses. The comparability of these analyses is enhanced by the common aspects
of baseline data collection procedures and outcome determination procedures in the CT and
OS. Estimated relative risk functions from the two sources will take suitable account of prior

"exposure" histories and of measurement error in exposure assessment. Under circumstances
in which careful analyses of this type lead to substantial agreement between CT and OS results,
analyses will be conducted to extrapolate the relative risk results beyond those examined in the
CT, using the OS. For many observational analyses, joint analyses of the CT/OS cohorts with
stratification on cohort will also be a useful strategy for examining possible explanations for
differences between relative risks in the CT and OS.

Outcome Ascertainment Process

Statistical Power/Data Analysis