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Cost -efficient design of main cohort and calibration studies where one or more exposure variables are measured with error

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Cost -efficient design of main cohort and calibration studies where one or more exposure variables are measured with error

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Content COST-EFFICIENT DESIGN OF MAIN COHORT AND CALIBRATION STUDIES WHERE ONE OR MORE EXPOSURE VARIABLES ARE MEASURED WITH ERROR by Sohee Park A Dissertation Presented to the FACULTY OF THE GRADUATE SCHOOL UNIVERSITY OF SOUTHERN CALIFORNIA In Partial Fulfillment of the Requirements for the Degree DOCTOR OF PHILOSOPHY (BIOMETRY) December 2002 Copyright 2002 Sohee Park Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. UMI Number: 3093804 Copyright 2002 by Park, Sohee All rights reserved. ® UMI UMI Microform 3093804 Copyright 2003 by ProQuest Information and Learning Company. All rights reserved. This microform edition is protected against unauthorized copying under Title 17, United States Code. ProQuest Information and Learning Company 300 North Zeeb Road P.O. Box 1346 Ann Arbor, Ml 48106-1346 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. UNIVERSITY OF SOUTHERN CALIFORNIA THE GRADUATE SCHOOL UNIVERSITY PARK LOS ANGELES, CALIFORNIA 90007 This dissertation, written by S o h ee^ P ark ................................... under the direction of h e T. Dissertation Committee, and approved by all its members, has been presented to and accepted by The Graduate School, in partial fulfillment of re quirements for the degree of DOCTOR OF PHILOSOPHY Dean of Graduate Studies D a te U^X&r.mz DISSERTATION COMMITTEE Chairperson Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Dedication To Jae-Sung and my parents with lots of love Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Acknowledgments My first acknowledgment must go to my thesis advisor, Dr. Daniel O. Stram for his intensive supervision and critical discussion during my six-years of graduate study at USC and especially throughout the writing period of this dissertation. I would like to express my sincere gratitude to my committee members, Dr. Malcolm C. Pike, Dr. Stanley P. Azen and Dr. Simon Tavare. Dr. Pike’s challenging and intellectually stimulating guidance always inspired me. Not to mention his excellent guidance on my thesis work, Dr. Azen also educated me how to better present myself as a professional researcher. I would like to thank Dr. Tavare for his critical reading and invaluable suggestions to my dissertation despite his occupied schedules. I would like to also recognize Dr. Brian Henderson for his guidance and support through the Multi-ethnic cohort study and Dr. Mimi Yu for reviewing my thesis draft. I was fortunate to have other faculty members in CHP and my office suitemates in Parkview Building with whom I could not only discuss interesting research topics but also easily hang out. My former officemate, Mark Huberman, was certainly one of them and I sincerely hope that he could share this delight in heaven. iii Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Friends outside the school deserve a significant recognition. In particular, Clara Moon- Ju Cho, and Youngah Lee who were my best friends supported me in every way during my graduate years in Los Angeles while I was far apart from my family. I also owe a huge debt of gratitude to all my family members. My sister who herself was also a graduate student shared much of her student life and gave me endless love and support. My brother, sister-in-law and brother-in-law should be acknowledged for their cheering and prayers. I am also grateful to my “new” in-laws, the “Rieh family”, for their full support and encouragement. No word could satisfactorily express my deep gratitude to my parents. Ever since I was a small child, they have educated me to open up my potential and taught me never to give up under any circumstances. I would not have been where I am now without their everlasting support, encouragement and unconditional love. My final acknowledgment goes to my husband, Jae-Sung. His love, patience, support, encouragement and companionship were my strong motivation during the late years of my graduate study. Without his support, this dissertation could not have been finished. iv Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Table of Contents Dedication ii Acknowledgments iii List of Tables vii List of Figures viii Abstract I. Introduction 1 1.1 Forword....................................................................................................... 1 1.2 Effect of Measurement Error..................................................................... 4 1.3 Methods of Correcting for Measurement Errors...................................... 9 II. Cost-efficient design in a Univariate Setting: a classical error model approach and comparison of results by Spiegelman and Gray 17 2.1 Description of Spiegelman and Gray’s approach..................................... 18 2.2 Simpler Proposed approach for the Cost-efficient Design of the Main and the Calibration studies............................................................................ 24 2.3 Calibration Study in which a “gold standard” is not available................ 46 2.4 Summary...................................................................................................... 53 III. Cost-efficient design in a univariate setting: a general error model approach 54 3.1 Formulation of the cost-efficient design.................................................. 54 3.2 Comparison of the optimal design under a general error model assumption and a classical error model assumption....................................61 3.3 Summary........................................................................................................ 64 v Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. IV. Cost-efficient design in a bivaraite setting when two covariates are correlated 66 4.1 Risk analysis when two covariates are correlated........................................66 4.2 Formulation of the cost-efficient design in a bivariate setting....................67 4.3 Examples of optimized design with two correlated covariates and comparison with a univariate setting............................................................ 74 4.4 Simulation Study............................................................................................. 92 4.5 Summary.......................................................................................................... 97 V. Conclusion 99 Bibliography 103 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. List of Tables 2.1 Simulation for Rosner’s variance formula using an exponential approximation (1000 iterations)................................................................. 32 2.2 Comparison of the total cost to detect the hypotheses of RR=1 vs. 1.5 at 95% power and 5% Type I error, when the repeated imperfect measurements are used for the calibration regression.............................. 49 4.1. Optimized number of main cohort and calibration study sizes as a function of correlations between true covariates and the strength of association between confounding v ariab le^) and outcome.................. 76 4.2a. Simulation results for Laplace approximation: To detect RR=1.5 for XI assuming a lower relative risk of confounding variable (RR-1.5 for X 2 ).......................................................................................................... 94 4.2b. Simulation results for Laplace approximation: To detect RR=1.5 for XI assuming a very strong effect of confounding variable (RR=5 for X 2 )........................................................... 95 vii Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. List of Figures 2 . 1. 2 .2 . 2.3. 2.4. 2.5. 3.1. 3.2. 4.1a. 4.1b. 4.1c. Percentage of relative external calibration study size as a function of the reliability coefficient........................................................................................ 35 Percentage of the cost spent on calibration study as a function of the reliability coefficient........................................................................................ 36 Overall cost for the entire study as a function of the reliability coefficient........................................................................................................... 37 Percentage of the cost for the external calibration study size as a function of the reliability coefficient when the replicates of the imperfect measurements are used .................................................................................... 51 Overall cost for the entire study as a function of the reliability coefficient when the replicates of the imperfect measurements are used.........................52 Graph of the integrand for computing the expected Fisher’s information (dotted line) and the normal-like function by Laplace approximation (solid line).......................................................................................................... 60 The fraction of calibration study size in the entire study as a function of correlation between true exposure and observed exposure, under a general error model ........................................................................................................63 Optimized calibration study sizes when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero................................................................79 Optimized main cohort study size when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero ................................................................80 The proportion of calibration study size in the entire study when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero ...................... 81 viii Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 4.2a. The optimized calibration study size as a function of error correlations between two observed covariates, where correlations between two true covariates are assumed to be zero ................................................................... 85 4.2b. The optimized main cohort study size as a function of error correlations between two observed covariates with a fixed correlation of true covariates........................................................................................................... 86 4.2c. The proportion of calibration study size in the entire study as a function of error correlations between two observed covariates with a fixed correlation of true covariates................................................................................................ 87 4.3 The optimized sizes of calibration study and main cohort study as a function of error correlations between two observed covariates with a fixed correlation of true covariates, when true covariates are positively correlated (pxix2 = 0.5)...................................................................................................... 88 4.4. The optimized sizes of calibration study and main cohort study as a function of error correlations between two observed covariates with a fixed correlation of true covariates, when true covariates are negatively correlated (Pxix2 = - 0 .5 )................................................................................................... 89 4.5. Optimized calibration study size to detect the relative risk of one variable that is measured with no error while it is correlated with a second variable measured with error......................................................................................... 90 4.6. Optimized main cohort study size to detect the relative risk of one variable that is measured with no error while it is correlated with a second variable measured with error.......................................................................... 91 4.7. Main cohort and calibration study sizes to detect various relative risks of the variable of interest (X i).....................................................................................96 ix Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Abstract Calibration studies are often performed on a subgroup contained within or external to large studies, for the purpose of correcting risk estimates for the effect of measurement errors. In this paper, we present a method to optimally allocate the number of subjects in the main cohort and calibration studies by minimizing the total cost while maintaining a fixed statistical power to detect a specified log relative risk. Measurement errors in the observed exposure are allowed to be subject to both random and systematic errors. It is shown that when errors in observed exposure variable contain both random and systematic errors, the optimal sizes of main and calibration studies are unaffected by the magnitude of systematic errors as long as the correlation between true exposure and observed exposure is fixed. We also deal with the case when a gold standard is not available and repeated reference measures are obtained in calibration studies. We find that non-optimal choice of the number of replicates of reference measures per calibration study subject could result in a considerable waste of resources. Furthermore, the cost-efficient design is extended to a multivariate setting where covariates in the risk model are correlated in their true values as well as in errors. As x Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. the correlation between two covariates becomes stronger, the optimal sizes for both main cohort and calibration studies increase. When the risk of the confounding variable is stronger, the optimal design requires even larger number of subjects in calibration studies to detect a non-zero relative risk for the variable of interest. However, main cohort study sizes are relatively unaffected by the strength of the association between the confounder and the outcome. When the true covariates are correlated, required main cohort study size is also influenced by the correlation between errors in two observed exposures. The stronger error correlations are, the smaller main cohort size is needed when true covariates and errors in observed exposures are correlated in the same direction. Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Chapter I Introduction 1.1 Foreword Error in measurement of exposure is an almost inevitable occurrence in much research including epidemiological studies. In nutritional epidemiology, in which the dietary intake and its association with the disease are of primary interest, the method of assessing a person’s dietary habits are often an issue of concern. The methods of food diary or 24-hour recalls have been used to assess an individual’s dietary intake. These methods are based on the items and the amounts of an individual’s actual food consumption on one or more specific days. These methods are generally expensive and subject to day-to-day variation, hence they are inappropriate for assessing past diet. Investigators have sought alternative methods for measuring long-term dietary intake (Willet 1998). Self-administered food frequency questionnaires (FFQs) were developed to assess an individual’s long-term dietary habits and have been commonly used in large studies because of their convenience and relatively low cost. 1 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Contrary to 24-hour recalls in which well-trained interviewers obtain information by asking questions to participants of what they consumed on the previous day, the FFQ method entirely relies on the self-report of participants based on their long-term memory. The FFQs consist of two components: a food list and a frequency response. As the FFQs are self-administered, they can introduce some bias in the reporting. For example, the food list in FFQs fails to produce the full coverage of food items consumed by participants, or if certain ethnic food items are not listed, then some of actual food consumption might never be reported for some participants. Further, participants may fail to report some food items because they omit some questions by mistake or they simply cannot remember all food items they consumed in the past. Measurement errors are introduced in such cases. Measurement errors in exposure can be considered of two kinds: “random” and “systematic”. We use the term “random” where values measured with error fluctuate around the truth, but the average of repeated measures eventually approaches the truth. In assessing an individual’s dietary habits, “random” errors generally arise from the daily variation of the participant’s food consumption. When random measurement errors occur in the data, disease risk estimates associated with diet are biased towards the null in a univariate exposure setting. “Systematic” errors are defined such that the average approaches some value different from the truth. This can occur, for example, when an individual intentionally or unconsciously under- or over-reports on the food consumption or an ethnic food item is missing on the food list (Willet 1998). 2 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. When the variable with measurement error is studied in relation to an outcome variable, such as disease status which may itself be subject to error, measurement error can be either “differential” or “nondifferential”. If the misclassification of outcome depends upon exposure status or the misclassification of the exposure depends upon the disease status, then the errors are differential. Differential errors can occur in case- control studies. For errors to be nondifferential, it is required that the risk of disease depends only on the true exposure and given the truth, the measured exposure does not add any additional information (Thomas 1993). This paper only considers a nondifferential error setting, where the measured variable plays the role of surrogate to the true exposure and does not affect the risk of disease itself. Nutritional epidemiologic studies can be designed in various ways as ecological, case- control, cohort or intervention studies. The discrepancy in findings of the relationship between diet and disease across different studies has been controversial in nutritional epidemiology with varying views of measurement errors, either differential or nondifferential, often at the root of the controversies. For example, dietary fiber was found to be protective for colorectal cancers in numerous case-control studies (Dwyer 1993). Nevertheless, this was not observed in recent cohort and intervention studies (Giovannucci 2001; Terry 2001). This might have been caused by differential reporting in case-control studies. A similar discrepancy was also recognized in the relationship between dietary fat and breast cancer. Ecological studies, such as international correlational analyses, suggested a strong positive association between 3 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. fat consumption and breast cancer incidence. However, case-control studies have indicated a weaker association and recent cohort studies reported little evidence of an association (Willet 1992; Hunter 1996; Holmes 1999). Negative findings in cohort studies have been suspected by some to be due to measurement error. For instance, Prentice discussed the likely effects on cohort risk estimates of both random error, unrelated to true intake, and systematic underreporting by obese subjects (Prentice 1996). Beta-carotene was not found to be protective for lung cancer in intervention studies, whereas this was strongly suggested in both cohort studies and case-control studies. Residual confounding between beta-carotene intake and poorly measured smoking exposure has been argued to be a cause of the apparent protective effect among smokers who report high levels of beta-carotene (Henderson 1992; Stram, Huberman et al. 2002). 1.2 Effect of Measurement Error The effects of measurement errors have been widely recognized and studied in previous research (Cochran 1968; Kleinbaum 1982; Thomas 1993; Carroll 1995). When the exposure is measured with purely random error that is nondifferential, then the risk estimate is always attenuated in a univariate setting, that is, its expected value is smaller than the true risk. Let X denote the true exposure variable, Z denote the value of exposure measured with error, and let y be the outcome variable. Then the 4 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. measurement errors can influence the following: the mean structure, E(y\Z) compared with E(y\X), the variance structure, Var(y\Z) compared with Var(y\X). Measurement error also leads to the loss of the ability of multivariate analyses to control for confounding. Categorical exposure variables We first consider the simplest case of binary variables, as discussed by Thomas et al. (Thomas 1993), where X is the truth and Z is the observed exposure variable and y is the outcome variable. Let p t = P (X = i) be the true prevalence of exposure, r = P(y = 11 X = i) be the risk of disease in true exposure i, m: j = P{Z = j | X = i) be the misclassification probabilities, where I > , =1, and X mi } = 1. Then the observed risks classified by Z are R} =P(y = l\Z = j) = Y lP{y = i\x = i)P{x = i\z = j) 5 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Epidemiologic risk measures expressed in terms of R .’s can be shown to be biased towards the null compared with the corresponding measure expressed in terms of ’s. Continuous exposure variables Let us assume that there is a linear relationship between X and Z, E ( X \Z ) = a + b Z . (1.1) As a simple example, assume that outcome (y) and exposure variable (X) have a linear relationship, y = a + J3X + s . (1.2) If we used Z instead of X in the outcome model, then the linear regression becomes E(y\Z) = a + j3E(X\Z) = a + j3(a + bZ) = a + a/3 + bj3Z. Note that by regressing y on Z, the slope term now becomes b[3 . Under the classical error model for X and Z, i.e., Z = X + e, _ Cov(X, Z) _ Var(X) Var(Z) ~ Var(X) + Var(e)< Therefore, b(3 < (3. which implies that the risk estimate obtained from regressing y on measured exposure, Z, instead of true exposure, X, will be attenuated by factor b. In a logistic setting, logit (y) = a + (JZ, where P(y) is very small, the parameter estimates of log odds ratio, f t , will be also biased towards the null by approximately the same factor, b (Rosner 1989). 6 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Effect on sample size requirement Another considered effect of measurement error is on study power. We illustrate the effect of measurement error on sample size in a simple linear regression setting. We assume a similar relation between X and Z as in (1.1) and a linear relationship between outcome y and Was in (1.2). Let £ be the difference between X and E(X\Z). We note that is uncorrelated with E(X\Z). Then when using Z instead of X, we have the relation where R is the correlation between X and Z. Hence we see that the Var(f3) is inflated Therefore, the required sample size when the exposure is measured with error is exposure is measured without error. For example, if the correlation between true y ,= a + /3[E(Xi \Zi) + Zi] + Si = a + m X l \Zl) + f t , + £ 1 (1.3) From this, the variance of j.3 is estimated by Var{(3) = (1.4) NVar(E(X \ Z)) When (3 is small, then (1.4) is approximated as £ £ NVar(E(X \ Z)) ~ N R 2V a r(X ) ’ (1.5) by 1/R when an imperfect measurement is used instead of the true exposure. 2 approximately increased by the factor, 1/R , compared with the size needed when the 7 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. exposure (X) and measured exposure (Z) is 0.5, then the sample size required using Z would be about 4 times the sample size required using X to detect a non-zero slope. Residual confounding In a univariate setting, estimates of the effect of an exposure variable measured with purely random error is always biased towards the null. However, when two or more variables are measured with error, the bias can be in either direction. In multivariate analyses, even the effect of a variable measured without error can be biased because of the correlation with another variable measured with error, and biases can be away from the null (Greenland 1980; Walker 1985; Ahlbom 1992; Elmstahl 1997). This phenomenon is commonly known as “residual confounding”. Specifically consider a bivariate setting, where only one variable X is measured with error by Z and another variable, A, is measured with no error but is correlated with X. In this case, P(Disease \ A, X) = P(Disease | X), but P(Disease | A, Z) & P(Disease \ Z), because A picks up additional information about X, resulting in bias away from the null for A. When both variables are measured with error, further complications arise. 8 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 1.3 Methods of correcting for measurement errors Despite the effort to minimize the error when collecting exposure data, measurement errors still exist to a certain degree in most cases and the analyses results can be distorted because of these measurement errors. Various methods have been proposed for adjusting exposure-outcome relationships for measurement errors. These methods have been developed for case-control studies (Armstrong 1989), Cox proportional hazards model for failure-time survival data (Prentice 1982), and logistic regressions in cohort studies for univariate (Rosner 1989) and multivariate settings (Rosner 1990). General approaches include the calibration equation method, structural equations approach, and full likelihood approach. Structural equation approaches are applied so that the marginal relationships y\Z can be fitted directly in certain restricted situations, such as where all variables are normal and linearly related. The full likelihood method is applied by integrating over the unknown true exposure, X (Thomas 1993). The calibration method is mainly discussed here as this paper relates to the design issue of a calibration study. Regression Calibration Method The calibration method requires a reference measurement of exposure on calibration study subjects. Calibration study subjects are selected either from the main cohort members or from some other external data source. For the calibration purpose in 9 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. which we validate the exposure measurement for the main cohort members, this reference measure is ideally error-free, but the only assumption imposed on the reference measurement is that it provides an unbiased estimate of the true exposure. For simplicity, let us assume that true exposure measurements, X ’ s, are available for calibration study subjects. Let us consider a logistic relationship between the outcome, y, and the true exposure, X , such that In ' E (y \X ) ' 1 - E { y \ X ) ■a+P'X. (1.6) Assuming a linear relationship between the measured exposure, Q, and the true exposure, X, that are obtained for the calibration study subjects, the regression calibration equation is constructed as follows, X i = a' + XQt + s, where e~N(0,cr2 e) (1.7) Then the regression calibration method proceeds as follows: 1) Estimate the parameters in equation (1.7) from the calibration study population by ordinary least squares. 2) Calculate E(X\Q) for each person in the main cohort study population based on the parameter estimates obtained from step 1). 3) Substitute E(X\Q) for X in equation (1.6) for each subject in the main cohort study and estimate p and associated confidence limits. A This method would provide an unbiased estimate of (3 , however, the variance of /^’obtained from the usual logistic regression as in (1.6) is underestimated because 10 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. errors in the estimation of X from Q are ignored. Rosner et al. proposed a method to estimate the correct variance of /?’ (Rosner 1989). In addition to equations (1.6) and (1.7), define a logistic regression of y on the measured exposure, Q, such that In £ ( > ’ 1 0 A ~ a + j5Q. (1.8) ^-E(y\Q) Then Rosner’s formula for the corrected risk estimate and the variance of the corrected risk is constructed as follows: 1) Obtain an uncorrected estimate, /?, from an ordinary logistic regression of y on observed exposure, Q, in equation (1.8) in the main study population. 2) Obtain an estimate of the regression coefficient, X , from equation (1.7) in the calibration study population. 3) Estimate /?* by /? / X . 4) Estimate the variance of p as 1 B2 Var(fi*) = — Var{P) + K - Var(X). (1.9) X X Note that the variance estimate in (1.9) is based on the linearization of (31X as a function of both ft and X . Because the linearization works very poorly for large variations in X , this formula needs to be applied with care. The above methods were based on the assumption that the true exposure, X, is available for the calibration study subjects. However, it is rarely possible in practice to 11 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. know the true exposure, X, therefore even the best measurement will still contain some errors. In this case, we can replace X in the calibration study with an unbiased estimate of X, which is considered as “reference” measurement. Often a number of reference measures are obtained for each calibration study subject and the average of repeated measures is used to estimate the true exposure, assuming that the errors in these reference measures are not correlated with X. In nutritional epidemiology, the methods of food diary or 24-hour recalls are often utilized in the calibration study, in which participants keep a diary of food consumption or report to the telephone interviewer all food items and serving sizes consumed on the previous day of a randomly selected interview day. For convenience of notation, let us denote the nutrient value obtained from a self administered food frequency questionnaire (FFQ) as 0: the nutrient value obtained from an unbiased reference method, e.g., food diary or 24-hour recalls, as Z; and the true nutrient value as X. When the reference measure Z is used in place of X in the calibration study, it is assumed that the errors in Z are uncorrelated with true exposure, X and the average of repeated Z’s per subject provides an unbiased estimate of the true exposure, X. Previous studies showed that if this assumption is violated, i.e., the classical error model assumption between Z and X is no longer valid, then the measurement error correction method may result in some bias (Wacholder 1993; Wacholder 1995; Brenner 1996). Errors in Z and Q are also assumed to be independent, which could be controversial. Wacholder et al. concluded that the odds 12 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. ratio would be over-corrected when the classification errors in Z and Q are negatively correlated, independent, or weakly positively correlated conditioned on true exposure status (Wacholder 1993). Spiegelman et al. later showed that if the errors between Q and Z are uncorrelated, then regression calibration method has no bias even when the gold standard is “alloyed” (Spiegelman 1997). Spiegelman et al. also demonstrated how one can estimate the correlation between the errors in Q and Z by employing a third method of exposure assessment when it is reasonable to assume that errors in this third method are uncorrelated with the errors in the other two exposure assessment methods. Design of Calibration Study Calibration studies may be designed to meet several objectives. First, a calibration study can be used to measure the true between-subject variation in the dietary factors of interest. Second, it can be used to determine the sample size required in the main study (Carroll 1997). Third, a calibration study can be aimed to estimate the correlation between intake from the food frequency questionnaires and true measure, to serve a validation purpose. Fourth, the calibration of a dietary questionnaire against a true measure can allow for the adjustment of divergent biases in relative risk estimates resulted from heterogeneous errors in the dietary exposure assessments in subgroups of the cohorts, so that a combined analysis of multi-center cohorts can produce more reliable risk estimates (Kaaks 1995). Lastly, calibration studies can be 13 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. used to assess the exposure measurement errors and to correct the measure of association, such as relative risk, for these measurement errors (Willet 1998). Depending on the aim of a calibration study, several questions need to be answered at the design stage: 1) How many subjects will be included in the main cohort study (N)? 2) How many subjects will be required in the calibration study (n)? 3) How many repeated reference measurements per subject in the calibration study will be obtained when a gold standard is not available (m)? For the validation purpose, in order to detect the difference in correlations between FFQs and the true measures, the sample size required can be computed from the standard one-sample formula using Fisher’s Z transformation of the correlation coefficients (Snedecor 1971). In general, fewer subjects will be required for a validation study with higher degrees of validity. In most nutrient settings, about 100 to 200 subjects would be a reasonable size for a validation study (Willet 1998). It was also suggested that for a fixed total number of measurements, the most efficient allocation of measurements would usually indicate obtaining not more than two replicates per subject for any values of intraclass correlations, in order to achieve the minimal variance of the corrected correlation coefficients (Rosner 1988). 14 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. An alternative approach to choosing the appropriate sample size in the calibration study would be to minimize the variance of corrected relative risk estimates. Stram et al. derived a formula for selecting the optimized number of calibration study subjects (n) and replicates of reference measures per subject (m), while minimizing the variance of corrected risk estimate, with the constraint of a fixed total cost on the calibration study. The optimized number of replicates per subject (m) was found to depend on two measures: the ratio of day-to-day within-person variance to the variance in true nutrient for a given FFQ value, and the relative cost of food record vs. the FFQs. They concluded that for most nutrient settings in practice, the optimal study design would rarely require more than four or five 1-day diet records per subject, and even two or three 1-day records would suffice in many cases (Stram 1995). Similar to the findings of Stram et al., other studies also suggested that only a few replicates are required for an optimized calibration study. When the main purpose of a calibration study is to adjust for divergent biases resulting from differential errors in the baseline questionnaire assessments in multi-center cohort studies, Kaaks et al. suggested that the most efficient design would include a maximum number of subjects with only a single measurement per subject (Kaaks 1995). Carroll et al. showed that when the calibration study is designed to determine the sample size for the main study, i.e., the number of required disease cases in the main study to detect a plausible effect with a reasonable statistical power, a calibration study with more subjects and fewer replicates would be more efficient (Carroll 1997). On the other hand, Greenland 15 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. suggested that the alternative of a fully validated design, i.e., the superior exposure measure is obtained on all study subjects, could provide more information per unit cost than a larger study with validation subset, especially when the nondifferential misclassification assumption is violated (Greenland 1988). In the case when both main and calibration studies are simultaneously planned and costs are allocated between them, Spiegelman and Gray proposed a cost-efficient design using a full likelihood approach, in the setting where the reference measurement in the calibration study is error-free (Spiegelman 1991). They showed that in the univariate logistic setting with a continuous exposure variable, the proportion of calibration study increases with increasing sample disease frequency, decreasing relative cost of gold standard to FFQs, increasing unit cost of outcome ascertainment, increasing distance between two alternative relative risk values. This approach, however, involves complicated calculations, and, more importantly, is based on the assumption that the true nutrient intake is known for calibration study subjects. The methods described above were constructed for a somewhat simple setting in which a single covariate is involved. The effect on calibration sample size in multivariate settings have been studied by several researchers (Elmstahl 1997; Fraser 2001). The major determinants of power with calibration were found to be the collinearity between the variables measured with error, and the correlations between crude and corresponding true variables. It was shown that the power increases with a 16 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. larger calibration study size in a multivariate setting. Fraser and Stram argued that calibration studies involving as many as a thousand subjects may be appropriate in some instances. 17 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Chapter II Cost-efficient design in a univariate setting: a classical error model approach and comparison of results by Spiegelman and Gray. Earlier work by Spiegelman and Gray (S&G) suggested a cost-efficient design for binary response data with a single continuous covariate measured with error (Spiegelman 1991). Their method, however, was complicated and only dealt with the situation where the true exposure was available for calibration study subjects. The initial work of this dissertation was motivated to develop a cost-efficient design with a relatively simpler approach than that of S&G, so that it could be easily applied not only to univariate settings but also to multivariate settings. In addition, the application was intended for more practical situations in which the “true” exposure is not available. In section 2.1, S&G’s method is reviewed. In section 2.2, our proposed method is described for a univariate setting in which the “true” exposure can be obtained and the results are compared with S&G’s approach. In the course of this work, we found errors in S&G’s report, and the univariate work in this section also provides corrections to these errors in S&G. In section 2.3, the cost-efficient design in 18 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. a univariate setting is discussed for the case when the true exposure is unavailable and replicates of a second exposure measurement with error are used instead for calibration study subjects. 2.1. Description of Spiegelman and Gray’s approach When the outcome of interest is binary, such as disease status (1 = disease present, 0 = disease absent), the logistic regression model is often utilized in epidemiologic studies. Suppose that the “true” exposure is known and is denoted by X. Then the logistic regression model is (2.i) 1 + exp(a + fiX ) where D is the observed binary outcome, coded as 0 or 1. Let Z denote the exposure measured with error. Under the assumption of a generalized Gaussian measurement error model, />(X|Z) = - r L = e x p U - L ( X ^ a ' - r Z)!}, (2.2) V2;t<7 I 2er J the classical structural measurement error model (Cochran 1968), Z = X + £ , s ~ N ( 0 , a 2 e), 19 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. cr\, can be obtained by setting a ' in (2.2) to (l-y)jux , y to -- , and a 2 to (^x + ° e) (1 - y)cr2 , when X is normally distributed with mean /jx and variance <j2 x . The usual conditional assumption was imposed as, P(D \X ,Z ) = P(D | X ) , i.e., Z contains no additional information about the exposure-disease relationship after X is taken into account. This assumption is equivalent to P (Z \X ,D ) = P { Z \X ), which is often referred to as the nondifferential misclassification or random error assumption in the epidemiologic literature. This assumption allows for the construction of a model for the observed data, *r e x p { ( a + J 3X)D\ \ f 1 , . ) p (D lz > J , V i— r ex p l - T ( x - « ' - r Z ) 2/<T, \<ix.(2.3) i 1 + e x p { ( a + /3X)D] 42t z < j2 I 2 J Main and Validation study We can distinguish two kinds of validation studies: an external validation study and an internal validation study. An external validation study is the one in which disease information is not collected for the calibration study subjects, thus the subjects in the validation study are not members of the main study. With an internal validation study, disease information is collected for calibration study subjects, and they contribute to 20 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. the disease risk estimate. In either case, subjects chosen to be in the validation study must be representative of the main cohort study subjects. The difference between internal and external studies is trivial if the disease is rare, unless the calibration study is very large. 1) External validation study When the validation study is external and exposure is prospectively ascertained, design optimization uses the log likelihood function, LA = ^ X l{ a ,P ,a \ y , a 2) + Y j i 2i{ a ', Y ^ 1), where fi,a',y,cr2) corresponds to the rth main study subject’s likelihood contribution with i x = lo g /( D |Z ) and £2j(a',y,cr2) corresponds to the rth validation study subject’s likelihood contribution with t 2 - log f ( X \ Z ) . 2) Internal validation study (doubly sampled design) When the validation study is internal, the disease information is also obtained for calibration study subjects. In this case, the design optimization uses the log likelihood function, Lb = Y j £ u (a, p,a',y,(72) + Y,£ 2. (a',y,cr2) + Y j £3 i (a, J3), i= l /= 1 r'-l where f 3 i(a ,/? ) is the likelihood contribution with f 3 = log f( D | X ) for calibration study subjects. Often t 3 will contribute little information, because the disease is rare 21 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. and n2 will be small relative to However, S&G reported large differences in optimized calibration study sizes between internal and external designs, which were perplexing results. 3) Fully validated design Rather than collecting data on a large number of subjects with imperfect exposure data, there may be circumstances under which the optimal design consists of a smaller sample of subjects whose exposure status has been “fully validated”, i.e., exposure has been assessed by the superior method only. Again, we find that the analysis of S&G seems to misidentify the situations when such a fully validated study is appropriate. Design optimality criteria S&G applied the discriminatory power criteria proposed by Greenland to compute the optimal sample sizes (Greenland 1988). For a pair of hypothesized values, /?, and Pu , the optimal design is given by the maximum of two sample sizes calculated by the usual specification of power and size, where the roles of two hypothesized values of relative risk are alternated. Let rx be the cost to obtain the “true” exposure, r? be the cost to obtain the exposure measured with error, and rD be the cost to obtain the disease information. Then, the 22 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. optimal sample sizes, nx and n2 are the maximum of the two values obtained as the solution to min \n x+n2 > x - nl ,n2:nx,n2>0 | subject to the constraints of either 1- $ Zi-g/2 ylVL (nl,n2; a L,/3L, a ’,y,cT2) - / 3 u + p L yjvu{nx,n2, a lJ,p u,a',r,o-2) or 0> Zi~a/2\lVv(nx,n2; a u , j3v ,a ',y , a 2) - ^JVL(nx,n2;a L,j3L,a',y,cr2) >K , (2.5) where VL and Vv are the variances of the estimator of (3 under the two alternative values of log relative risk being considered, to achieve the discriminatory power n and the type I error a . Based on the likelihood from the functions (2.1), (2.2) and (2.3), the optimization equation above is not analytically evaluable in a closed form. S&G utilized the numerical method developed by Crouch and Spiegelman to evaluate the expression (Crouch 1990). 23 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. In general, they concluded that the proportion allocated to validated substudy increases with increasing sample disease frequency, decreasing unit cost of the superior exposure measurement relative to the imperfect one, increasing unit cost of outcome ascertainment, increasing distance between two alternative values of the relative risk between which the study is designed to discriminate, and increasing magnitude of hypothesized values. 2.2. Simpler proposed approach for the cost-efficient design of main and calibration studies. This section describes the proposed optimal design in a univariate setting under a classical error model assumption and compares the results with S&G. Our proposed method involves additional approximations than S&G. First we assume a logistic model for the relation between D and Q as well as between D and X. In general, this approximation works well under the rare disease assumption (Rosner 1989). We also assume that the log of the odds ratio in the model using Q is attenuated such that (5 = f f X where /?* is the log of the odds ratio using X and X is the calibration regression slope, which again is a very good approximation for modest sized ft in a rare disease setting. Further we need to approximate the variance of (3 in the main study using a logistic regression. This is described below. For the purpose of 24 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. comparison, all settings were kept analogous to the work by S&G. In this section, it is also assumed that the exposure is measured without error for the calibration study subjects, i.e., the “true” exposure, X, can be obtained in the calibration study. The application to the setting in which the “true” exposure is not available, i.e., only “non gold standard” can be obtained, is discussed in a later section. Estimation for Var(p) o f the logistic regression using the exponential approximation As the variance of logistic regression cannot be obtained in a closed form, we make several approximations which we refer as the “exponential approximation”. Besides its simplicity for application, the major advantage of this approach is that we could obtain ^ * an explicit formula for the variance of corrected risk estimate, Var(f3 ). The logistic regression is set up such that e x p (a + /?£>) logit (P,) ~ a + {3Qi <=>/? = 1 + exp (a + J3Qt) We approximate this as p: = exp (a + j3Qi) under the rare disease assumption. Suppose that D ~ independent Binary(pl), where p : = exp(« + J3Q.) and Q, ~ Normal (p Q , <r*). N Then the log likelihood of D, is L = X l n P,D ' O - a ) 1 ”1 5 ’ • 25 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Assuming p. = exp(er + f3Qi), L = In{e{ a + P Q ' ]) ' ( l - e(a + P Q ‘]) \ 1 - A The Score contribution of the zth subject is • D _ e(a+m) Q (D _ e(a+m) ) ■ U £ a ,p y \ - e (a+ P Q j) \ - e ( a+ ftO j) and the contribution of the observed information is /(« ,£ ) = (c t+ fiQ i) ( \ - e ia+PQ)) Q / a+ P Q - \ l - D , ) (l„ e (a+m))2 ( l - e (a+m))2 (2.6) Our next approximation is to assume that E{Di |0 ,) = exp(a + pQ i), and ( l - exp(a + /?0 ,)) = 1. (2.7) Averaging A and integrating over the distribution of Q for the expression (2.6) gives the expected Fisher’s Information as: ,a + \/2 /3 2aQ+/3jj0 e yx + M 2 jP ’a ' o + P n 0 ? a+\/2p2 a% + fiftQ (foo+Mn) 3 ( / 3 c r l 0 + JU0 ) e ' ,a+\!2j3 <jg +Pmq (^e + {P< yl + Mo)2) The above Fisher’s information was derived from a closed-form integration of the exponentially approximated logistic likelihood function. It can be easily shown that the expectation of the observed information, (2.6), is in the form of a moment generating function for a normal random variable. The exponential approximation is 26 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. reasonable for a rare disease setting. This approximation is much more convenient than having to deal with the complicated expression that needs to be evaluated by a numerical method, although we understand its limitation as exp(a + J3Qi) increases with common diseases and high relative risks. Var{/3) is derived from the inverse of Fisher’s information, i(a,J3y c t2 q + 0 1 <t2 q + 2 f 3<j2 Q n Q + h 2 q (a+M2p1al+P^g) 2 e ( a + H l f P - O Q + P f i Q ) 2 o C T (3c72 0 + a (a+m^cr^+PnQ) 2 d" n (cc+UIP-o^+Phq) 2 £ ? C T 1 so that Var(P) + — — — ---- N a 0 exp(a + 1/2 J3 a Q + pfj,0 ) We now seek an approximation for Var(X). We assume a classical error model for X and Q such that £ = * , + £ , where S ,~ N { 0,rx?) (2.8) Then from the bivariate normality of X and Q, the relation between X and Q can be re expressed as a calibration equation 27 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. X, = a ' + AQt + e. , where e, ~ N ( 0, a 2 e) (2.9) by setting a' = ju,, y - *— 7 , and 0 ^ = 0 ^ <yx + c r i 2 2 . o-^. + o-; . V • * * y From the linear regression equation (2.9), Var(X )-Var(e ) R 2 = -----^ (2.10) Var(X) Also from (2.8), we have R 2 = C orr{X,Q f C ov(X ,Q f _ C ov(X ,X + g)2 ~ Var(X)Var(Q) ~ Var(X)Var(X + £) Var(X)2 ~ Var(X)Var(X + % ) Var(X) ~V ar(X + g) = A Hence we get, Var(e,) = Var(Xi) - R1Var(Xi) = ( l - R 2)Var(Xi) = (1 -A)Var(X ), where A is the reliability coefficient. 28 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Therefore Far (A) can be approximated as Var(i) = , ^ £ ( q - o f i= . 1 nVar(Q) (l-A)Far(X,) ~ n(Var(X,) + Var( £ )) _ 1(1 - A ) n Var(X.) Also note that Var(Q.) = — -----— under the classical measurement error model. A Using Rosner’s fomula (Rosner 1989) for the variance of the corrected risk estimate, f? , we obtain Var(f! ' ) = ~ Var(p) + A Var(X) A A 1 1 + J32 A (l-A ) A2 Ncr2 exp(a +1 / 'lp1< J2 0 + pfa0) A4 n We can simplify this formula further by assuming that X is distributed as a standard 2 1 normal random variable so that ju0 = 0 and orQ= — . Then the variance formula is A simplified as 29 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. AN exp a + The optimal allocation of the number of subjects in the main cohort study (T V ) and in the calibration study (n) is derived by minimizing the cost function, where rx is the cost to obtain the “true” exposure in the calibration study and rz is the cost to obtain the exposure measured with error in both main and calibration studies and rD is the cost to obtain the disease information only for main study subjects, with the constraint of discriminatory power criteria given in (2.4) and (2.5). The solution to this minimization problem can be attained by the Lagrange Multiplier’s method. For comparison with the example given by S&G, we set the power to be 95% and type I error at 5%. Then from the first discriminatory power criteria (2.4), we get C(rX’rZ’rD) = N (rD + rz) + n(rX +rZ)» (2.11) l J 1 .9 6 V L - lo g ( 4 ) + l° g (A ) I N >0.95 = > 1 .9 6 ^ -lo g (A ,) + log(A ), , <-1.645. (2 .12) 30 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. And from the second discriminatory power criteria (2.5), we get 1 - 0 1 .9 6 7 fr -lo g (A ,) + log (pL) & >0.95 => 1 . 9 6 ^ -log(/?„) + log(/?1) _ -----------==----------------- <-1.645 (2.13) First, we considered the external calibration study with the equivalent settings to the examples given by S&G. The baseline disease rates were set to either 0.005 or 0.05. The cost to obtain the error-prone measurement, rz , was set as $1. In nutritional epidemiology, this would be the cost to obtain the exposure information from self administered questionnaires. The cost to obtain the disease information, rD, was set as $1. The cost to obtain the true exposure, rx , was set as either $50 or $500, which resulted in the ratio of 50 (or 500) for the cost of error-free exposure and error-prone exposure. Four pairs of relative risks were considered for the hypotheses: 1 vs. 1.5; 1 vs. 5; 2 vs. 5; 2 vs. 10. These relative risks were for one standard deviation increase of the true exposure, X, where the X ’ s were assumed to follow a standard normal distribution. Simulation for Rosner’ s Variance Formula with the exponential approximation Table 2.1 presents the results from the simulation to study how well the Rosner’s formula using all our approximations estimates the variance of the corrected risk 31 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. estimate for various underlying relative risks and baseline disease rates. Baseline disease rate was set to either 0.005 or 0.05. The hypothesized relative risks varied from 1.2 to 5 per one standard deviation increase of the exposure measure. In each simulation run, the number of subjects in the main and calibration studies was chosen to achieve the discriminatory power of 95%. One thousand iterations were performed. Empirical mean of the Rosner’s variance formula using our approximations described /v /v /v /v earlier, Var(fi / A) , was compared with the sample variance of the values of /? / A . The Gauss software program was utilized to perform the simulations. Table 2.1. Simulation for Rosner’s variance formula using an exponential approximation (1000 iterations) RR* RR** b/w 1st and 4th quartile P N n Expected # of cases 0 ' (1) Sample variance of P' (2) Mean of Rosner’s Var(f3*) Ratio (2)/(l) Power 1.2 1.5 0.18232 160977 213 P(D)=0.005 804.89 0.18525 0.00251 0.00268 1.07 96.5% 1.5 2.5 0.40547 33296 99 166.48 0.40658 0.01343 0.01369 1.02 96.1% 2 4.9 0.69315 11516 60 57.58 0.70816 0.04080 0.04186 1.03 98.2% 3 12.5 1.09861 4521 39 22.61 1.14006 0.10127 0.11152 1.10 99.6% 5 40.5 1.60944 2062 25 10.31 1.58895 0.22617 0.26656 1.18 99.1% 1.2 1.5 0.18232 17245 71 P(D)=0.05 862.25 0.18274 0.00323 0.00326 1.01 94.8% 1.5 2.5 0.40547 3844 35 192.20 0.41871 0.01838 0.02054 1.12 95.7% 2 4.9 0.69315 1450 22 72.50 0.70897 0.06163 0.07655 1.24 94.3% 3 12.5 1.09861 637 16 31.85 1.10558 0.91264 15.44632 16.92 88.5% 5 40.5 1.60944 323 12 16.15 1.83004 36.56785 118116.48 3230.06 78.1% * Relative risk for one standard deviation increase of the true exposure. ** Relative risk between the last and the first quartile. The reliability coefficient o f 0.5 was used in all simulations. 32 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. We observed that the Rosner’s formula performs very well for the rare disease with baseline rate of 0.005 and with the relative risk of up to 3 per one standard deviation increases in X. When the relative risk is very high (RR=5), the Rosner’s formula overestimates the variance of the corrected risk estimate. When the baseline disease rate increases to 0.05, the Rosner’s formula performs reasonably well in the low range of relative risks such as 1.2 or 1.5 and it fails to estimate the variance of the corrected relative risk for higher relative risks based on our optimal design sample size. We acknowledge the limitation of this design for large relative risks because it estimates the sample size for the calibration study to be too small in the optimization problem. However, one should also note that the relative risks in this simulation are for one standard deviation increase in the true exposure, thus some of these hypothesized relative risks are in fact exceedingly high for usual epidemiologic settings. For example, the relative risk of 1.5 indicates that there is a 3.5 times higher risk in the last quartile relative to the first quartile, and the relative risk of 5 indicates that there is a 40 times higher risk in the last relative to the first quartile, as shown in Table 2.1. We claim that the Rosner’s variance formula with our approximations for Var(j3) and Var(X) work well for the reasonable range of relative risks for the last vs. the first quartile in typical epidemiologic settings where the underlying disease of interest has low incidence. 33 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Results and comparison with Spiegelman and Gray’ s report Figure 2.1 presents the fraction of the external calibration study size relative to the entire study size as a function of the reliability coefficient (2) of the exposure measured with error in four settings: (A) P(D) - 0.005, RX = $50, RZ = $1, RD = $1 (B) P(D) = 0.005, RX = $500, RZ = $1, RD = $1 (C) P(D) = 0.05, RX = $50, RZ = $1, RD = $1 (D) P(D) = 0.05, RX = $500, RZ = $1, RD - $1 When the baseline disease rate is very low as in (A) or (B), no greater than 2.5% of the entire study subjects are allocated to the calibration study, both when rx = $50 and rx = $500. For all pairs of relative risks, there is a general trend of increasing proportion of the external calibration study size with increasing measurement error. When baseline disease rate is 0.005, relative cost ratio of obtaining true exposure to error- prone exposure is 50, and the hypothesized relative risks of 1 vs. 1.5 (Figure 2.1-(A)), the optimal cost-efficient design is attained by allocating only 0.35% of the entire study subjects to an external calibration study where the reliability coefficient for the exposure measured with error is low (A— 0.3). With the moderate measurement error (A,=0.5), the optimal design would assign 0.30% of the entire study subjects in the calibration study. When there is almost no measurement error, i.e., the reliability 34 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 2.1. Percentage of relative external calibration study size as a function of the reliability coefficient (A) P(D)=0.005, RZ=$1, RX=S50, RD=$1 (B) P(D)=0.005, RZ=$1, RX=$500, RD=$1 3.00 2.50 2.00 50 1.00 0.50 0.00 0.3 0.4 0.5 0.6 0.7 0.8 0.9 0.99 R eliability C o effic ie n t 3.00 2.50 2.00 £ c T + z c 1.00 0.50 - 0.00 0.3 0.4 0.5 0,6 0.7 0.8 0.9 0.99 R eliability C o effic ie n t (C) P(D)=0.05, RZ=$1, RX=S50, RD=$1 (D) P(D)=0.05, RZ=$1, RX=$500, RD=S1 7.00 6.00 5.00 4.00 - 3.00 2.00 1.00 0.00 0.3 0.4 0.5 0.6 0.7 0.8 0.9 0.99 R eliability C o efficien t 7.00 6.00 5.00 s l 4.00 c + z 1 3.00 2.00 0.00 0.3 0.4 0.5 0.6 0.7 0.8 0.9 0.99 R eliability C o effic ie n t — 1 V S 1.5 Ht-lvsS - a - 2 vs. 5 -* - 2 v s 10 35 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 2.2. Percentage of the cost spent on calibration study as a function of the reliability coefficient (A) P(D)=0.005, RZ=$1, RX=$50, RD=S1 (B) P(D)=0.005, RZ=$1, RX=$500, RD=$1 100 80 70 r a 50 > £ 40 0.3 0.4 0.5 0.6 0.7 0.8 0,9 0.99 R eliability C o effic ie n t 100 £ o ■ > a w o o o ' * 0.3 0.4 0.5 0.6 0.7 0.8 0,9 0.99 R eliability C o effic ie n t (C) P(D)=0.05, RZ=$1, RX=$50, RD=$1 (D) P(D)=0.05, RZ-Sl, RX-S500, RD-Sl 100 - •w W c .2 * 3 * D r e > 0.3 0.4 0.5 0.6 0.7 0.8 0.9 0.99 > * T 3 3 to C . 2 3 r e * o 1 ( 0 o o 1 0 0 90 80 70 60 50 40 30 20 10 0 0.3 0.4 0.5 0.6 0.7 0.8 0.9 0.99 R eliability C o effic ie n t R eliability C o effic ie n t .1 vs 1.5 H i— 1 VS 5 -2vs 5 -2vs 10 36 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 2.3. Overall cost for the entire study as a function of the reliability coefficient (A) P(D)=0.005, RZ=$1, RX=$50, RD=$1 (B) P(D)=0.005, RZ=S1, RX=S500, RD=$1 $ 180,000 $ 160,000 $ 140,000 $120,000 $ 100,000 $80,000 1,000 $40,000 $20,000 0.8 0.3 0.4 0.5 0.6 0.7 0.9 0.99 R eliability C o effic ie n t $ 180,000 $160,000 $ 140,000 $ 120,000 $100,000 $80,000 $60,000 $40,000 $20,000 $ - 0.3 0.4 0.5 0.6 0.7 0.8 0.8 0.99 R eliability C o effic ie n t (C) P(D)=0.05, RZ=$1, RX=$50, RD=S1 $18,000 $16,000 $14,000 $12,000 $10,000 $8,000 ;,ooo $4,000 $2,000 $ - 0.7 0.8 0.9 0.99 0.3 0.4 0.5 0.6 R eliability C o effic ie n t (D) P(D)=0.05, RZ=$1, RX=$500, RD=$1 $45,000 $40,000 $35,000 $30,000 $25,000 $20,000 $15,000 $10,000 $5,000 ----- 0.8 0.9 0.99 0.3 0.4 0.5 0.6 0.7 R eliability C o effic ie n t -1 va 1.5 —1 vs 5 ■ 2vs 5 ■ 2vs 10 37 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. coefficient is very high (k=0.99), only 0.04% of the entire study subjects are allocated to the calibration study in the optimal design. This observation fits the expectation that one wouldn’t need to perform a calibration study if the exposure is perfectly measured with no error. When the hypothesized relative risks and the distance between two relative risks increase, the percentage of the number of calibration study subjects increase. For example, in Figure 2.1-(A), when the observed exposure contains moderate measurement errors (k=0.5), the percentage of calibration study size relative to the entire study size was 0.3% for RR=1 vs. 1.5; 1.2% for RR=1 vs. 5; 1.4% for RR=2 vs. 5; and 2.1% for RR=2 vs. 10. The difference in the fraction of calibration studies among different relative risks appears to be more distinct when measurement errors are large. As seen in all graphs in Figure 2.1, when there is almost no measurement error (X-Q.99), the percentage of calibration study size converges to zero and there are smaller differences in the percentage of calibration study size across different pairs of hypothesized relative risks. When the cost of obtaining the true exposure increases to $500 (Figure 2.1-(B)), even smaller number of subjects are allocated to the calibration study. With the moderate reliability coefficient (k=0.5), only 0.1% of the entire study size is allocated to the calibration study for RR-1 vs. 1.5; 0.4% for RR-1 vs. 5; 0.5% for RR=2 vs. 5; and 0.7% for RR=2 vs. 10. 38 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. If the baseline disease rate increases, then more subjects are allocated in the calibration study. For example, in Figure 2.1-(C), we observe that when the background disease rate is common (5%) and the measurement error is moderate (a=0.5), 0.9% of entire study subjects are allocated to the calibration study for RR=T vs. 1.5; 3.6% for RR=1 vs. 5; 4.4% for RR=2 vs. 5; and 6.1% for RR=2 vs. 10, compared with the smaller percentages in Figure 2.1-(A) under the rare baseline disease rate (0.5%). From the comparison of four situations in Figure 2.1 (A)-(D), the cost-efficient design appears to require a larger calibration study size when the baseline disease rate is low, hypothesized relative risks are low, the cost ratio of obtaining the true exposure relative to the error-prone exposure is high and the reliability coefficient of observed exposure is low. Figure 2.2 presents the fraction of the cost spent on the calibration study as a function of the reliability coefficient. The y-axis values were computed by ( ■ rz + rx ) n — xlOO, (rz +rD)N + (rz +rx )n where n is the optimized number of the subjects in the calibration study and N is the optimized number of the subjects in the main study, and again where rx is the cost for the “true” exposure in the calibration study and rz is the cost for the exposure measured with error in both main and calibration study and rD is the cost for the disease information only for main study subjects. The required fraction of the total 39 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. cost to be spent for the calibration study decreases as the reliability coefficient increases. It is also observed that if the distance between two hypothesized log-relative risks are high, e.g., RR=1 vs. 5, then about half of the resources are allocated for the calibration study in the optimal design. Figure 2.3 shows the overall cost for the entire study as a function of the reliability coefficient. There is a distinctive trend of decreasing overall cost with increasing reliability coefficient in order to achieve the 95% power and 5% type I error. Furthermore, with a smaller distance between the two hypothesized relative risks, the overall total cost is larger. Figure 2.3 illustrates the overall trend of the total cost that reflects the sample size by several factors such as the reliability coefficient, baseline disease rate, hypothesized relative risk pairs, and the ratio of the true and error-prone exposure measurements, hence we acknowledge the magnitude of the absolute total cost itself in y-axis depends on the arbitrary choice of the unit costs of rx , r2 and rD. A major peculiarity with S&G’s results is that the reported numbers in the figures seem to be barely reasonable. The reported percentages of calibration study subjects are strangely high in the original manuscript. For example, their method suggests to allocate approximately 60% of the entire study subjects into the calibration study when the hypothesized relative risks are 1 vs. 5 and rx = $50, rz- $1, rD= $1 and P(D) = 0.005. This inflated proportion had been noticed by Dr. Malcolm Pike and the authors published an erratum in the later issue of the journal to describe the y-axis unit 40 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. in the graph should be divided by one hundred (Spiegelman 1991). However, the numbers with the corrected units seem to be too low and the other figures appear to be still perplexing. In S&G, the percentage of the calibration study subjects does not decrease monotonically as the reliability coefficient increases. For instance, when rx = $50, rz - $1, rD r ;; $ 1 and P(D) = 0.005, the reported proportion of the calibration study subjects increases up until the reliability coefficient is 0.7 and decreases afterwards, counter to the monotonic decreasing trend that we observed as shown in Figure 2.1. Under a classical error model, with all other parameters to be fixed the same, the required calibration study size is expected to decrease as the measurement errors in the observed exposure reduce, i.e., the reliability coefficients increase. The overall main and external calibration study costs in Figure 2 of S&G are much higher than what our method suggests. When rx = $50, rz = $1, rD= $1, P(D) = 0.005, the relative risks are 1 vs. 1.5 and the reliability coefficient is 0.5, S&G reported that the overall cost is approximately $205,000,000, whereas our method suggests that the overall cost would be about $72,000 for the equivalent setting. When the reliability coefficient is 0.3 and all other settings are the same, the overall cost for the optimized main and external calibration studies would be about 1.1 billion dollars in S&G. The actual numbers of the optimized sample size in the main and the external calibration studies were not reported in S&G. However, with their reporting of 0.025% for the optimized calibration study proportion and the overall required cost of 1.1 billion dollars from Figures, the sample sizes can be induced as N = 546,515,094 and n = 41 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 136,663, which are exceedingly high. Even with the correction of the units in the published erratum, these numbers hardly seem to be reasonable. Internal Calibration Study The internal calibration study is a randomly selected sub-sample from the main cohort study. Unlike an external calibration study, the disease information is also collected for the internal calibration study subjects and this information is used for estimating the relative risk. For a rare disease, the two study designs wouldn’t differ very much in terms of the optimization, especially when the cost of obtaining the disease information is relatively low. Consider the logistic regression model on the internal calibration study subjects, f ( D \ X ) = exp{(a + f3i„lX )D }/{l + exp(a + /Si^X )} , (2.14) where p C a H b denotes the estimated log relative risk from the calibration study subjects. The corrected log relative risk f3 can be estimated by where oj, = 1 and 1 VarCPcam) 42 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Then the variance of the corrected risk estimate is Var(j3’) = Var / a h P a* A t Cl y ( © , + © 2 ) X (a>i + © 2 ) Calib ^ cox + ©2 j Var + Var (Plant) ^ ©j + © 2 y ■ + ©, © , ©j + © , 2 J ©, © j + © 2 In the above derivation, we assumed that /? / A and p C a !ib are independent. Previous study showed that these two values are asymptotically uncorrelated as the calibration sample size becomes large (Spiegelman 2001). With the constraint of the discriminatory power criteria as in the external calibration study setting given in (2.4) and (2.5), our goal for the optimized study design is to minimize the cost function, C(rx ,rz ,rD) = N(rD+rz ) + n(rD+rx +rz ), in which the cost of the disease information is now added for the internal calibration study subjects as well. Under the assumption of an internal calibration study, the optimized sample sizes are not much different from those of the external calibration study. The difference becomes quite trivial, especially when the underlying disease rate is low and the cost to obtain the disease information is low. For example, if the underlying disease rate is 0.005, the cost for the disease information is $1, the cost for the error-prone exposure measurement is $1, the cost for the true exposure measurement for the calibration 43 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. study subjects is $50, and the reliability coefficient is 0.5, then the optimized number of the internal calibration study is n=106 and the optimized number of the main study is N=32,592, which indicates that 0.32% should be allocated to the calibration study. This result is very similar to what we observe for the external calibration study design in the same setting: the optimized calibration study size is n=99 and the optimized number of main study is N=33,296, which indicates that 0.30% should be allocated to the calibration study. In contrast to our results, S&G reported that there was a “marked” difference in the total overall cost between the external and internal calibration study. When the cost for the disease information is relatively low compared with the cost for the true exposure ($1 vs. $50) in their examples, it is quite puzzling how their results were so dramatically different. For example, their reported total cost for the external calibration study of approximately $205,000,000 was reduced to $2,000,000 for the internal calibration study with the same setting under a rare disease assumption. These results with their comments about fully validated studies imply that the errors in S&G are more significant than just simple transcription or arithmetic errors. 44 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 2.3. Calibration study in which the “true” exposure is not available. Estimation of X by the average of repeated second measurements of the exposure In most calibration studies in practice, the “true” exposure, also referred to as the “gold standard” in the literature, is not known. Instead, multiple records of a second measurement of the exposure are obtained and these are often referred to as the “alloyed gold standard”. The average of these multiple records for each individual is used to provide an unbiased estimate of true exposure, X, under the assumption that the errors in the alloyed gold standard are uncorrelated with the true exposure. Although the validity of this assumption is highly controversial in nutritional epidemiology, we do not deal with this issue here. In nutritional studies, multiple 24- hour recalls or food records are used as reference measurements to provide an unbiased estimate of the individual’s true food consumption. Now we consider Z/; as a reference exposure measurement on the yth day for the zth subject in the calibration study and denote Q. as the first exposure measurement that is obtained for the entire cohort and X f as the “true” exposure for the zth subject. We consider several relationships among Q., Z and X fs. We assume Z = X\ +StJ, where StJ denotes the daily variation from the true long-term exposure for the zth 45 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. subject on the jth day. Instead of regressing X on Q as in (2.9), the calibration equation of Z on Q is constructed such that 1 m Z = a' + AQ + e ', where e '= e -i — ■ (2.15) J We also assume a classical measurement error model for Q and X in (2.8). It can be easily shown that if Z is an unbiased estimator of X, i.e., E(Z) = X , then the A expectation of the least squares estimate of A obtained from (2.15) would be the same as the expectation of the slope estimate from regressing X on Q as in (2.9). In this case, however, Var (A) would become larger in (2.15) as shown below. Var ( A ) ■ a], nVar(Qi) 2^- 2 m nVar(Xi +%) (1 -A) A , assuming a constant variance for S , n mn(Var{Xj) + Var(c,)) (I-A) A < j~ cr; n mn(Var(Xj) + Var(g.)) cr] (I-A) A n (1- 1)1 m cr n K 1 + v mj , where K = 46 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Here K is the ratio of the within-person variance to the conditional variance of X given Q. Since m is the number of repeated measurements that takes a positive value and K is the ratio of the variances, the value of K /m should be always positive. Hence the Var ( A) from the calibration equation using repeated imperfect measurements is increased by a factor of 1 - i — - , compared with when the true exposure is available. V m ) We can also see that if m — > co . i.e., we have a very large number of replicates for the reference measurement of which the average can be considered as “true” exposure, or if K — > 0, i.e., the within-person variance relative to the conditional variance of X given Q is really small, then the Var(l) would be equal to the usual form where the true exposure, X, is used in the calibration regression. In usual nutritional epidemiological settings, the estimated variance ratio, K, appears to range from 1 to 10 (Stram 1995). The cost to get the replicates of the reference measurements such as repeated 24-hour recalls for the calibration study is often much higher than the cost to obtain the usual exposure measurement from self-administered questionnaires. We define rzl to be the cost for the initial contact and collecting the exposure measurement on the first day of 24-hour recalls and rZ 2to be the cost to collect the subsequent 24-hour recalls. Then the optimal design is obtained by minimizing the cost function, C(rzl, rZ2,rQ,rD) - N{r0 + r^ ) + w-ifo + + {pi ~ l)?y2) ’ 47 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. with the constraint of the discriminatory power criteria given in (2.4) and (2.5) using the variance formula for the corrected log risk estimate, Var(j3*) = 1 AN exp 2 a + P 2A + r A3 n K \ 1 + — m j In the optimization process, the choice of m is only dependent upon the value of K and the ratio of rzl and rZ2, which was also shown by Stram et al. (Stram 1995). When the optimized solution of m is a non-integer value, we took the closest integer that is greater than or equal to the optimized solution and then solved for N and n with the selected value of m. Selected Results Figure 2.4 and 2.5 are the selected results for the optimized design when the hypothesized relative risks are 1 vs. 1.5 for one standard deviation increase, the cost for the questionnaire is $1, the cost for the initial 24-hour recalls is $30, the cost for the following 24-hour recalls is $20, and K, the ratio of the within-person variance to the between-person variance conditioned on Q, is 3. The baseline disease rates considered are again 0.005 and 0.05. In this example, the optimized choice of m is 2. We also studied the difference in the optimal design if we forced m = 28, which was 48 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. used by the Nurses’ Health Study as being equivalent to having a “true” exposure measurement (Willet 1985). Table 2.2. Comparison of the total cost to detect the hypotheses of RR=1 vs. 1.5 at 95% power and 5% Type I error, when the repeated imperfect measurements are used for the calibration regression. Reliability Coefficient P(D)=0.005 P(D)=0.05 m=2 (optimal) m=28* Cost Ratio m=2 (optimal) m=28* Cost Ratio 0.3 $135,307 $178,204 1.32 $21,381 $39,272 1.84 0.4 $99,262 $128,575 1.30 $15,314 $27,095 1.77 0.5 $77,561 $98,563 1.27 $11,624 $20,095 1.73 0.6 $62,967 $78,608 1.25 $9,146 $15,383 1.68 0.7 $52,365 $63,865 1.22 $7,322 $11,886 1.62 0.8 $44,211 $52,151 1.18 $5,872 $8,761 1.49 0.9 $37,552 $42,458 1.13 $4,625 $6,399 1.38 0.99 $31,788 $33,022 1.04 $3,387 $4,003 1.18 * m=28 was chosen to represent the number o f replicates that is considered as sufficient to provide almost the “true” exposure measurement. This number of replicates was used in a classic paper from the N urses’ Health Study (Willet 1985). Figure 2.4 presents the proportion of the entire resource that is allocated to the calibration study cost. When the disease rate is higher, the optimized design allows for spending more resources on the calibration study. When m=28, the proportion of the cost for the calibration study is higher than when the optimal choice of m~2 is used. Figure 2.5 shows the overall cost for the entire study to detect the hypothesis pair of RR=1 vs. 1.5 at 95% power and 5% Type I error. The general trend is in the 49 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. agreement with our previous results for the case when the true exposure is available. As the disease rate increases, the overall cost required for the optimal design decreases. Within the same disease rate, it is obvious that we would require more cost when we used the non-optimal choice of m, in this example, when m=28, compared to the optimal choice of m=2 is used. Table 2.2 illustrates the detailed numbers that correspond to Figure 2.5. As seen in the “Cost Ratio” column, non-optimal choice of m could result in a considerable waste of our resources without gaining any power to detect the difference in the log relative risks. For example, when the disease rate is 0.05 and the measurement error is moderate (A =0.5), then the study design with the non-optimal choice of m - 28 would require the 73% exceeding cost compared to the study design with the optimal choice of m=2, in order to detect the same relative risk at the same power and Type I error. 50 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. % Cost t o Validation S tu d y Figure 2.4. Percentage of the cost for the external calibration study size as a function of the reliability coefficient when the replicates of the imperfect measurements are used (RD = $1, RQ = $1, RZ1 = $30, RZ2 = $20) 10 0 0.4 0.5 0.6 0.7 0.8 0.9 0.99 0.3 R elia b ility C o e ffic ie n t Z^p(D)=oTo057m=2loplimal) :^ l 3(D)=0^057m=28 —A— P(D)=0.05, m=2 (optimal) P(D)=0.05, m=28 51 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 2.5. Overall cost for the entire study as a function of the reliability coefficient when the replicates of the imperfect measurements are used (RD = $1, RQ = $1, RZ1 = $30, RZ2 = $20) $200,000 $180,000 $160,000 $140,000 $120,000 $100,000 $80,000 $60,000 1,000 $20,000 0.5 0.7 0.8 0.99 0.3 0.4 0.6 0.9 R eliability C o effic ie n t P(D)=0.005, m=2 (optimal) - * - P ( D ) = 0 .0 0 5 , m =28 — A— P(D)=0.05, m=2 (optimal) — x — P(D)=0.05, m =28 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 2.4 S u m m a ry In this chapter, we conclude that the Rosner’s formula for the corrected variance using an exponential approximation performs reasonably well in ordinary epidemiologic settings within the range of low disease rate and modest relative risks. The optimized sizes in internal and external calibration studies were observed to be similar when the disease rate is low and the cost ratio of the reference measurement to the imperfect measurement is not high. When the replicates of reference measurements are obtained for calibration study subjects, designing the study with optimized selection of the number of replicates is essential in order to avoid the misusage of resources. Calibration studies appear to be costly in general. Up to fifty percent of the entire resources may be allocated to the calibration study in the settings we examined. 53 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Chapter III Cost-efficient design in a univariate setting: a general error model approach In this chapter, we generalize the cost-efficient design in a univariate setting by allowing for both random and systematic errors in observed exposure measures. In section 3.1, we describe the general error model structure and formulate the optimal design of main cohort and calibration studies. In section 3.2, we present the results of optimal design under a general error model assumption and compare them with the case under a classical error model assumption. 3.1. Formulation of the cost-efficient design For observed FFQ values (Q), we allow both random and systematic errors so that their relation with the true exposure (X) can be classified as the following: Qt =a + bX, + £ , where N {0 ,a : ) (3.1) 54 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Here we assume the true exposure, X ’s are normally distributed with mean,p x , and variance, a 2 . Then the observed exposures, 0 ’ s, are normally distributed with mean, a + bpx , and variance, b2<j2 x + ct2 £. Note that when a- 0 and b=l, the general error model (3.1) represents the usual classical error model. From the bivariate normality of X and Q, the conditional expectation and the variance of X given Q are expressed as the following where p is the correlation between X and Q. o \ E ( X \Q = q) = p x + p (q~/u0) c r, / 7 \ ®X ®X = p x - (a + bpx )p — + p- cr, o cr, o 1,2 _ 2 b ci x b W x + a l j abal b2cr2 \ r + bal J r 2 2 . 2 Kb a x + a € j q , and V ar(X \Q = q) = a 2 x ( l - p 2) = a b2c b2crl + c r Thus we can construct a calibration regression equation to predict the true exposure (T) conditioned on an individual’s observed exposure ( 0 such that X . = a ' + XQi + st , where si ~ N ( 0, a ] ) , 55 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. by setting a ' = p x b2 a \ b2(Tx +(Tl j ab<y2 x b < 7 x + a 2 Z-- bcrl b2 < y2 x + a 2 and / 2 2 b cr b2a \ a $ y Again we assume a logistic relation between the outcome, D, and the true exposure, X, such that logit (pi) = a +fi*Xj . We also assume a logistic relation between the outcome, D, and observed exposure, Q, such that logit {pi) = a + pQ i . Note that we denote the risk estimate that is associated with the true exposure, X, by P*, to distinguish it from the crude risk estimate, P , that is associated with the observed exposure. Similar to the case under a classical error model assumption in Chapter 2, the cost- efficient design is constructed by minimizing the total cost while maintaining a given fixed statistical power and type I error to detect a hypothesized log relative risk. When the true exposure, X, is assumed to be known, the cost function is constructed such that c ( r x X Q X D ) = N(rD +rQ) + n(rx + rQ) (3.2) 56 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. where rx is the cost to obtain the “true” exposure in the calibration study and rQ is the cost to obtain the observed exposure that contains errors in both main and calibration studies and rD is the cost to obtain the disease information only for main study subjects, subject to the statistical power, 1-t c , at Type I error, a to detect a non-zero log relative risk, Pa , when the null hypothesis is p = 0: where V0 is the variance of risk estimate under the null hypothesis, P0, and VA is the variance of the risk estimate under the alternative hypothesis, PA . Statistical power is based on detecting the risk of exposure variable that is corrected for measurement error using calibration regression method. Rosner’s variance formula for corrected risk estimate in a univariate setting was applied (Rosner 1989). Under an exponential approximation with rare disease assumption, i.e., 1 + exp(a + P X ) « 1, the variance of the corrected relative risk is formulated as: V m i V ) V 57 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. b2 1 p* N(b2a 2 + < r2) 1 exp d + ft ~~(a + bpx ) + /?2 /7, {b2< J x + a 2) + ft~-~(a + bpx ) Px 2 Zr + - np 1 r ~ i ~ ^ A p V ^ e x p a + ftpx + ~ ft2p 2cr2 v 2 y + l 2( l - p 2) n p 2 (3-3) In the above expression (3.3), ft is the hypothesized log relative risk for one standard deviation increase in the “true” exposure, a is the disease rate at X = 0, and p = C o rr# 0 , Laplace approximation for estimating Var {ft) Besides using an exponential approximation, the variance of the crude risk estimate, Var{ft), can be estimated from a Laplace approximation. Assuming that the outcome, Dt s follow a Binary distribution with success probability, exp {a + ftQft P, 1 + exp (a + ftQft 58 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. the log likelihood is L=Xin/>,fl( i - A ; r = 2 > / = ] 1 * 1 exp(a + PQ,) 'I A f 1 1 1 -D , [ l + expia + PQ;)) [ 1 + exp(a + PQ.) J In order to compute the expected Fisher’s information, we need to integrate the following expressions over the distribution of Q: exp(a + p Q ) Q, expja + fJQ ) (1 + exp(a + pQ. ))2 (1 + exp(a + P Q ))2 Qi Qxp(a + PQ:) Qf exp(a + fJQ! ) (1 + exp(« + p Q i ))2 (1 + exp(a + pQ i ))2 These are not evaluable in a closed form. Consider the approximation to the first integral, exp (a + PQ,) 1 I (1 + exp(a + P Q )) J I t u c t rexp 2< t3 dQ , (3-4) The Laplace approximation estimates the integrand of (3.4) as h f t exp (0 - / 0 ^ xcr, 2cr, o J (3.5) where /^maximizes the integrand of (3.4) as a function of Q ,, a] is equal to -1 times the second derivative of the log of the integrand in (3.4) evaluated at Qi=jU0 and h is the maximum value of the function (3.4). Then note that the integrand of (3.4) greatly resembles a Gaussian distribution as shown in Figure 3.1. 59 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 3.1. Graph of the integrand for computing the expected Fisher’s information (dotted line) and the normal-like function by Laplace approximation (solid line). 0 .1 2 “ i 0.08 - 0.06 - 0.04 0.02 * 1 -0.5 0 0.5 1 1.5 2 2.5 3 3.5 4 Q - - - - Integrand for expected Fisher's information Laplace approximation * Baseline disease rate is very high (5%) and the relative risk of true exposure is RR=5. The observed exposure variable, Q, is assumed to follow a general error model, Q = 1.42 + 0.62X + e, where X ~ N(0,1) and e follows a normal distribution with zero mean and a constant variance. We can see that the Laplace approximation identifies the function very well as the two curves in the graph are almost identical. This example represents an extreme case when the baseline disease rate is very high (5%) and the relative risk of the true exposure is assumed to be very strong (RR=5 per one standard deviation increase). In less extreme examples with lower baseline disease rates and moderate relative risks, the integrand of (3.4) is estimated even more precisely by the Laplace approximation (graphs not shown). The integration of (3.4) is approximated from dividing the 60 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. maximum height of the function (3.4) by the height of the normal density evaluated at Q, = ju0, i.e., h^2n:al . We can estimate other components in the expected Fisher’s information from multiplying h-sjlTicrl by the mean and expected value of Qj from the normal distribution in (3.5). When all the components are estimated for the variance, Var(P') = ^ 7 Var(p) + £ - V a r ( i) , X 2 X' the optimal number of subjects in main cohort (N) and calibration studies (n) can be obtained from the solution of N and n by minimizing the total cost function (3.2) with constraints of statistical power criteria. This minimization problem is solved by Lagrange Multiplier’s method. 3.2. Comparison of optimal designs under a general error model assumption and a classical error model assumption. In the variance formula (3.3) under a general error model derived using the “exponential approximation”, we find that the systematic error terms, a and b, are not involved in this variance formula as long as the correlation between the true and observed exposure (p) is fixed. The variance term seems to be complicated by the 61 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. presence of and <j\ . Let us consider when fix ^ 0 . In order to keep the same baseline disease rate, a + needs to remain the same. Therefore, with a non-zero mean of X, the optimal study design is not affected while keeping the same baseline disease rate. Next let us consider the case when <j2 x 1. From the power criteria, s e a(P‘) in order to keep the log relative risk scaled to a one standard deviation change of X, we divide 0 A and j 3 { ) by c r x. Since every factor in the expression (3.6) involves 1 / c r x , that can be cancelled out, the power criteria is unchanged. Therefore we observe an important finding that introducing systematic errors in the observed exposure has no effect on the optimal study design as long as the correlation between the true exposure and the observed exposure remains unchanged. When the Laplace approximation was used to numerically estimate the expected Fisher’s information in the computation of the variance, we also observe that the optimal design is unaffected by the magnitude of systematic errors. Hence the optimal study design suggests the same number of main and calibration studies under a classical error model assumption and a general error model assumption. Figure 3.2 shows the fraction of calibration study size in the entire study as a function of the correlation between the true and observed exposures when a general error model is 62 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 3.2. The fraction of calibration study size in the entire study as a function of correlation between true exposure and observed exposure, under a general error model RQ=$1, RX=$50, RD=$1, Baseline disease rate = 0.5%, power=90% and Type 1 error = 0.05. 1.40 1.20 1.00 0.80 0.60 0.40 0.20 0.00 0 0.1 0.2 0 .3 0.4 0 .5 0.6 0.7 0.8 0.9 1 Correlation between X and Q RR=1 vs. 1.5 RR=1 vs. 2 A RR=1 vs. 3 - X — RR=1 vs. 5 assumed for the observed exposure, Q. The optimal design is identical regardless of the magnitude of systematic error factors, a and b in the general error model (3.1) as long as the correlation between X and O is unchanged. The percentage of the calibration study size in the entire study monotonically decreases as the correlation between X and Q increases. As the non-zero log relative risk becomes larger, the optimal study allocates a larger proportion of subjects to the calibration study. 63 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 3 .3 . S u m m a ry When systematic errors are introduced in the observed exposure and a general error model is assumed, the optimal design is identical to that under a classical error model assumption as long as the correlation between true exposure and observed exposure is unchanged. Therefore, we find that the more important determinant of the optimal design is the correlation between the true and observed exposure, rather than the magnitude of systematic errors. We can consider the observed exposure that contains systematic errors as simply “rescaled” values and from this we expect the optimal study design would be unaffected by introducing the systematic errors. 64 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Chapter IV Cost-efficient design in a bivariate setting when two covariates are correlated. 4.1. Risk analysis when two covariates are correlated. Multivariate analyses are often applied in epidemiologic studies, when confounding is believed to exist and the adjustment for confounding variables is pursued. In a univariate setting, when the exposure variable is measured with nondifferential error that follows a classical error model, the bias in risk estimate is always towards the null. In a multivariate setting where one or more covariates are measured with error, the risk estimate of these covariates may be biased either towards or away from the null. The classical example where biases are away from the null is often described as “residual confounding” (Greenland 1988; Armstrong 1989; Kipnis 1997). In this case, one variable is correlated with a causal variable that is measured with error. For example, suppose that we are interested in the association between dietary fiber and risk of breast cancer. If dietary fiber consumption is negatively correlated with fat consumption and there is an elevated risk of breast cancer with increased fat 65 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. consumption, then a protective effect of dietary fiber for breast cancer will result even if there is no effect of dietary fiber on the risk of breast cancer. In this case, it is important to control for fat consumption when studying the effect of dietary fiber on the risk of breast cancer. However, since fat consumption is measured with error, it is not sufficient to simply include the questionnaire estimate of fat in the risk model to control for true fat intake. To correct the risk estimates in this multivariate setting where covariates are measured with error, a multivariate calibration technique described by Rosner et al. is required (Rosner 1990). Little previous research has addressed the design of calibration studies with multivariate models. One paper that does directly discuss this issue is Fraser and Stram (Fraser 2001). Within a calibration setting, Fraser and Stram illustrated the effect of the calibration study size on power when two nutrients of interest are correlated. They demonstrated by a simulation experiment that increasing calibration study size to a very large number of subjects sometimes 1000 or more, continues to achieve a useful gain in power when an important collinearity is present. The issue of determining the optimal allocation to achieve a cost-efficient design was not addressed. It is certain that the power continuously increases with increasing calibration study size. However, would it be the most effective way of improving study power to solely increase the calibration study size? At a certain point, the study design would become more efficient when the resources are spent in accruing more subjects in the main study than in including further subjects in the calibration study. 66 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. In a bivariate analysis, we should be able to detect the independent effect of the covariates under the fairly strong confounding between covariates. The regression slopes in multivariate calibration equations given the confounder are a function of several different aspects of the problem. This includes the strength of the relation between confounder and outcome variable, the level of correlation between the two true covariates, and correlation between the errors in two measured covariates. In this chapter, we study the cost-efficient design when there are two covariates in the risk model where one variable of interest is correlated with another variable that is considered as a confounder. Simultaneous consideration of the optimized sample sizes of main cohort and calibration studies in a bivariate setting has never been dealt with in previous studies. We show how the correlation between two covariates as well as error correlations in observed covariates influences the optimization in the cost- efficient design of main cohort and calibration studies. 4.2. Formulation of cost-efficient design in a bivariate setting Formulation o f error model, risk model and calibration models First we consider two true covariates, X, and X 2, that are bivariately normally distributed with X, ~ N(juX i ,cr2 X {) andX 2 ~ N(juX i , ct2 Xi ) with Corr(X,,X2) = px^ . 67 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. We suppose that the observed exposure variables, Qx and Q2, both follow general error models such that Qm — a\ + b\Xu + , where < % u ~ N (0 ,a ^ ) and and X u are independent, and Qn ~ a2 b2X 2 1 + E ,2j, where E ,2 i ~ W(0,cr| ), and £2 j and X 2 i are independent. From the multivariate normality between X and Q, we can re-express the relation as following multivariate regression calibration equations: X u = «> + KxQu + KiQn + eu >w h ere eu ~ N (°> ) and X v =a'2+ XnQh + Xn Qv + e2i, where e2 , ~ N ( 0, ). (4.1) We continue to assume a logistic model for the data with a binary outcome variable and two exposure variables that are measured with errors such that logit (p.) = a + f3x Qu + j32Q2t. (4.2) Again we denote /fs to be risk estimates associated with observed exposures, whereas / f ’s are risk estimates associated with unknown true exposures as in logit (P;) = a + f i x h+/3;x2, (4.3) 68 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Optimized design criteria To optimize the design of main cohort and calibration studies in a bivariate setting, we aim to minimize the total cost function, assuming that rx is the cost to obtain the “true” exposure for both X x and X 2 in the calibration study and rQ is the cost to obtain the observed exposures, Qx and Q2, that contain errors in both main and calibration study and rD is the cost to obtain the disease information only for main study subjects, while maintaining the usual statistical power criteria, Here the statistical power is computed to detect the risk estimate of one variable of interest by treating the other variable as a confounder. c ( rx ,rQ,rD) = N(rD+rQ) + n(rx +rQ\ (4.4) >7t. 69 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Estimation o f risk estimates and variance that are corrected for measurement errors Calibration regression equations in (4.1) can be expressed as a matrix form such that X X "1 Qn Qu ' r _ ^ 2 1 " a . x * X 2 2 = 1 Qn e 22 1 A i 2 A i + ^12 ^22 ■ A i X X _ 1 Qu t 5 O l __ U2 22 _ l R From the design matrix, V= "1 Qn 02,' x u ~ 1 Qn q 2 2 and X = x » x 2 2 1 Qu 1 R _ fN Ol X t R , we estimate a { a 2 x = A i A i b y i = ( v Tv y ' v Tx _ A 2 A 2 _ Using the multivariate calibration technique suggested by Rosner et al. (Rosner 1989), the corrected risk estimates for two covariates, /?* = (/?* are estimated by A A A A A A P = P?C , where P = /?, p. and X = A i A . A A A 2 A2 2 and the variance-covariance matrix of the corrected estimates, X , is estimated PXP) from Cov(P]J]PHA'Z^A)Mi +PTA J iJJ \ , (4.5) 70 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. where A = X 1 and A h is the variance-covariance matrix relating the elements in the 7/th and72th columns of A. As we are interested in detecting the effect on the risk of one variable (arbitrarily X, is chosen) in computing the statistical power, we compute X . Here to obtain the covariance matrix within the 1st column of the F P i > A matrix A, X^ x j, the following approximation was used as described in Rosner et al., ^!\ r ^ I ^'( 5 i 5 r = l .y=l r= l w-1 where z j and z 2 are the row numbers of A. To compute the elements in the variance-covariance matrix of corrected risk estimate, X ,, , in (4.5), we need to obtain the uncorrected risk estimate’s variance- PU P) covariance structure. When estimating X - , we make several approximations. First, we assume that two exposure variables Qx and Q2 follow a bivariate normal distribution with a joint density function, f(Q ,Q 2)= 2 -2.r ~ exP 2nox a 2 aJI - p (g , - / o ! . p ( q - A ) < a - f t ) . ( a - f t ) 1 N 2 2 ° ~ i________ ° ~ 2 2(1- p 2) (4.6) where E(Ql) = p {, E(Q2) - ju2, Var(Ql) = cr,2, Var(Q2) = cr2 2 and p - correlation between Ql and Q2. Under general error models, the correlation between Qx and 71 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Q2 are expressed as p = blb2p x]x2 + p ^ 2 . We compute the variance-covariance matrix of /3 from the inverse of the expected Fisher’s information. Computation o f expected Fisher’ s Information We again assume a logistic relation between the outcome and observed covariates such that, logit (p.) = a + + f 2Q2i. - revisited (4.2) Suppose that the outcome variable, D, ’ s follow a Binary distribution with probability, exp (a + P&U+ PiQu) p t, where p. = 1 + exp (a + p x Qu +J32Q2i) and (Qu,Q2i)~ BVN(pl,p 2,cr,,cr2,p ) . Then the log likelihood of Dj is L = Y \ n p , D ' { \ - PiT D ‘ 7 = 1 The Score contribution of the rth subject is D +(D - i y “ + ^a, ^a, ) j _ l_ g(a+AQi +fh.Qu) Qi(Di +{Di -\)e{a+m’+ lh & ')) j _ l_ g(“+ A £ii +P iQ ii) 0 2 ; (/)+(£>- I g(a + A S < + A & 1 ) and the Fisher’s expected Information involves the integration of the following expression over the distribution of Q: 72 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. g (< * + A £ ? li+ A0 2 f) Q + ^2 2 2 > ) ^ J _ |_ g(a+P\Q \i +faQli) ^2 _ l _ g(a+ fliQ ii+ PiQu) ^2 1 ^ 1 + Q ( 'C C + ^1 -ll+ ^2 -2 i^ q 1 q- 01+ P\Q u + PiQii) Q Q g(a + fliQ ii + fhQ zi) (l + e(a+A eii+/32ft,))2 _ j_ g(a+PlQli+ P 2Qli) ^ j _ l _ g(a+fiiQii + P iQ h ) ^2 Q Q s< 'a+A~1 '+ ^2 ® 2 1 ^ Q2 g (a+PlQ\i + P 2Q 2:) r ( i + g{a+fl\0\j +^2Qn) f (>+ g(a+fhQ ii The above expression is again not evaluable in a closed form. We apply the Laplace approximation technique to estimate the integral of the above expressions over the distribution of Q. The performance of this Laplace approximation is further discussed in the section, 4.4. Then the variance-covariance of uncorrected risk estimates, 2 ^ , is obtained from the inverse of this expected Fisher’s information estimated from Laplace approximation. When a gold standard is not available in a bivariate setting The problem of optimizing the number of replicates per subject when a gold standard is not available can also be incorporated into the optimal design for bivariate cases. In a univariate case as described in Chapter 3, the number of replicates only depends upon two quantities associated with calibration study: the cost ratio of reference measurement to a conventional method and the ratio of within-person day-to-day variation in reference measurement to the conditional variance of unknown true 73 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. exposure given the measured exposure (Var(X\Q)). However, the formulation would be more complicated in a bivariate case because the number of multiple records per subject now depends upon additional factors such as the error covariance structure of two observed exposures and also the risk estimates, /?s. We emphasize correlated exposure variables and its influence on the cost-efficient design in this chapter, hence we do not deal with replicates issue here. Instead, dealing with replicates in a bivariate case will be discussed in the future work. 4.3. Examples of optimized design with two correlated covariates and comparison with a univariate setting In this section, we illustrate how correlations between true covariates and error correlations affect the optimal sizes of main cohort and calibration studies in the cost- efficient design of a bivariate setting by selected examples. In all examples, we assume the cost to obtain true exposure for both Xj and X 2 are $50, the cost to obtain conventional measurements are much lower at $1, the cost to obtain the disease information is $1, and Type I error of 0.05 and statistical power criteria of 90% are used. Baseline disease rates range from 0.5% to 5% and relative risks range in values of RR= 0.5, 1, 1.5 and 5 per one standard deviation increase in the true exposure. 74 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Table 4.1 presents the optimized sizes of main cohort and calibration studies proposed by the cost-efficient design, as a function of the correlations between two true covariates ranging from 0 to 0.9. We assume no error correlation in this example to emphasize the effect of correlations between true covariates on sample sizes. In addition, we studied the impact of the strength of confounding variable’s association with outcome on the cost-efficient design by considering three cases: 1) detect RR=1.5 for X; when X 2 has no effect, 2) detect RR=T.5 for Xj when X 2 has moderate effect (RR=1.5), 3) detect RR=1.5 for Xj when X 2 has strong effect (RR=5). For both observed exposure variables, we assumed the reliability coefficients to be 0.5. Several interesting aspects of the results are described here. First of all, larger main cohort and calibration studies are required once a non-zero correlation between two covariates is introduced and the study sizes continue to increase as the correlation between true covariates increases. This is true even when we assume that there is no confounding effect. For example, when there is no effect of confounding variable on the risk of disease, the optimal design requires 67 subjects in the calibration study if no correlation between two true covariates exists. However, when two covariates are correlated ( p xlX2- 0.6), about twice as many subjects (n=T55) are required. This increased size in a calibration study becomes more dramatic as the confounder has a stronger association with the outcome. As shown in the example of Table 4.1, 75 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Table 4.1. Optimized number of main cohort and calibration study sizes as a function of correlations between true covariates and the strength of association between confounding variable(X2) and outcome. To detect RR-1.5for the variable of interest (Xj) Correlation RR=1 for X2 RR==1.5 for X2 Between Two covariates N N Expected # o f Cases** N n Expected # o f Cases** 0 27,065 67 140 27,357 96 148 0.1 27,611 68 143 27,849 101 152 0.2 29,353 73 152 29,540 109 163 0.3 32,647 80 169 32,781 124 184 0.4 38,281 93 199 38,354 148 218 0.5 47,962 115 249 47,953 188 276 0.6 65,764 155 342 65,628 262 383 0.7 103,359 239 538 102,983 417 609 0.8 206,917 465 1,080 205,926 846 1,234 0.9 740,481 1,599 3,874 736,521 3,067 4,477 Correlation RR=5 for X2 Between Two covariates N N Expected # o f Cases** 0 27,256 303 263 0.1 27,599 312 279 0.2 29,107 335 309 0.3 32,102 375 358 0.4 37,314 442 439 0.5 46,330 555 576 0.6 62,943 761 828 0.7 97,998 1,194 1,368 0.8 194,308 2,378 2,882 0.9 688,554 8,438 10,874 *Error correlations were assumed to be zero and reliability coefficients for Q1 and Q2 are both set as 0.5. ** Expected number o f cases were computed by N*p, where p=average disease rate under the alternative hypothesis. when the correlation between two covariates is 0.5 and the confounding variable has the relative risk of 1.5, the required calibration study size is n=188, which is about 3 times many subjects compared to the case with no correlation and no confounder’s 76 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. effect. When the confounding variable has a stronger relative risk (RR=5), then the design requires 555 subjects in the calibration study that is more than 8 times many subjects. The size of the main cohort study is relatively unaffected by the strength of the association between confounder and outcome. However, as is also seen in the table, the expected number of cases occurring in the cohort will be much larger when the confounder gives very high risk. We computed the expected number of cases that by N*p, where p is the average disease rate was estimated from = I ^ - / m . f ( Q g d Q e J l + exp(a + A a + A 02) where f (Qx , Q2) is the bivariate density function in (4.6). We note that although the cohort size is slightly smaller when the confounder is strong, the number of cases required is far larger than when the confounder is moderately associated with risk. A case can occur when one covariate is negatively correlated with the other, for example, dietary fiber and fat intake in nutritional epidemiology. We studied how negative correlations between two covariates influence the cost-efficient design. Figure 4.1a illustrates that the optimal design requires more subjects when the correlations between two true covariates becomes stronger regardless of the sign. In this example, to clearly see the influence of the correlation between true covariates on calibration study size, we again assumed that the error correlations are zero. However a similar trend of increasing calibration study size is observed when error correlations are non-zero values (not shown). Comparing across different relative risks for the 77 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. second variable (confounder, Xj), we see that the largest calibration study size is required at the highest relative risk of X?. Again, the lowest calibration study size is required when there is no effect of the confounding variable (RR=1 for JG). When the effect of the confounding variable is protective (RR=0.5), the optimal design also requires a larger calibration size than when no effect exists. Also note that the U-shape of the graph is not perfectly symmetric at zero correlation except when the confounding variable’s risk strength is also zero. Somewhat larger calibration studies are required when RR> 1 for X? and correlations are positive compared to when correlations are negative. Similarly, when X 2 is protective (RR<1), somewhat larger calibration studies are required when correlations are negative than when they are positive. Figure 4.1b shows the required main cohort study size as a function of correlation between true covariates. First we observe U-shape graph of main cohort study sizes as correlation between two true covariates ranges from -0.9 to 0.9, hence conclude that the main cohort size increases dramatically as the correlation between true covariates is high in its absolute value. From overlapped four graphs, it is obvious that main cohort study sizes are hardly affected by the strength of association between the confounder and outcome, although there are many more cases in the cohort when the confounding is a strong positive risk factor. 78 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Optimized calibration study size (n) Figure 4.1a. Optimized calibration study sizes when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero. 2,600 2,400 2,200 2,000 1,800 1,600 1,400 1,200 1,000 800 600 400 200 0 -0.9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Correlation between two covariates (X1 and X2) RR=1.5 for X1 and R R = 5forX 2 -HH— RR=1.5 forX1 and R R = 1.5forX 2 RR=1.5 for X1 and RR=1 for X2 —X— RR=1.5 for X1 and RR=0.5 for X2 * RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Optimized main cohort study size (N) Figure 4.1b. Optimized main cohort study size when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero. 240,000 220,000 200,000 180,000 160,000 140,000 120,000 100,000 80,000 60,000 40,000 20,000 0 ■0,9 -0 .8 -0 .7 -0 .6 -0 .5 -0 .4 -0 ,3-0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Correlation between two covariates (X1 and X2) — RR=1.5 for X1 and RR=5 for X2 RR=1.5 for X1 and RR=1.5 for X2 RR=1.5 for X1 and RR=1 for X2 ~ ¥ r ~ RR=1.5 for X1 and RR=0.5 for X2 * RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 80 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.1c. The proportion of calibration study size in the entire study when negative correlations exist between two observed covariates, compared with positive correlations, when error correlations are assumed to be zero. £ * 3 C © G > 0 > N W > * Ig | $ £ J D , 1 5 o o £ 2 a. 1.30 1.20 1.10 1.00 0.90 0.80 0.70 0.60 x- 0.50 0.40 0.30 0.20 0.10 0.00 ■0.9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Correlation between two covariates (X1 and X2) - RR=1.5 for X1 and RR=5 for X2 RR=1.5 for X1 and RR=1 for X2 • RR=1.5 for X1 and RR=1.5 for X2 RR=1.5 for X1 and RR=0.5 for X2 * RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.1c presents another interesting feature in the proportion of calibration study size in the entire study as a function of correlation between true covariates, as well as the strength of confounder’s effect on the outcome. We observe that the proportion of calibration study size has different trends as a function of correlations between true covariates, depending on the direction of confounder’s effect. When there is no effect of confounder, there is almost no change in the proportion as the correlation between true covariates, p xxxl, changes. When there is a protective effect of confounder (RR=0.5), the proportion monotonically decreases as a function of p XXX2- On the other hand, when a risk effect of confounder is positive, the proportion of calibration study monotonically increases as a function of p XXX2 ■ With a fixed correlation between two true covariates, changing the correlations between errors in observed covariates also influences main and calibration study sizes. We first look at the simple case when correlations between true covariates do not exist and only allow for error correlations to vary from -0.9 to 0.9. Figure 4.2a shows that as error correlation increases, the required calibration study size also increases when the confounding variable has a risk effect on outcome (RR-1.5 or RR=5 for X2), and the relation is reversed when the confounding variable has a protective effect on outcome (RR=0.5 for X2 ). This implies that when the directions of risks in two covariates are the same, strongly negative error correlations are more beneficial. However, when the directions are opposite (one variable has a protective effect and another variable has a risk effect), strongly positive error correlations could be 82 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. beneficial in correctly estimate the risk in the variable of interest. Figure 4.2b shows that the main cohort study size is not much affected by error correlations. There seems to be a slight monotonic trend while the direction and slope are determined by the concordance of the sign of log relative risks in two covariates as well as the strength of confounding variable’s effect. Figure 4.2c shows the proportion of calibration study in the entire study. The general trend is very similar to the case observed in the absolute calibration study sizes in Figure 4.2a. How would the trend discussed above be changed when the correlations between true covariates are non-zero values? We further looked at two cases: when pxlX2 = 0.5 and when p xlx2= -0.5. Figure 4.3 (pxix2~ 0.5) and Figure 4.4 {pxlX2~~ 0-5) show that the calibration study size is no longer a simple monotonic function of error correlations when the correlation between two true covariates is non-zero. When the true correlation is positive (pXXX2 = 0.5), optimal design requires smallest calibration study size when there is a strong positive error correlation. Similarly, when the true correlation is negative (pXXX2~ -0.5), strong negative error correlations appear to be more beneficial in the optimal study. This trend is more obvious in required main cohort study sizes. There is a clear monotonic trend in decreasing main cohort size when the error correlations are strong at the same direction of the correlations between true covariates. 83 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. In a residual confounding problem, we would be also interested in the case when the variable of interest is measured perfectly without any error but the confounding variable is measured with error. Our proposed method in a bivariate setting shows that even when the variable of interest is error-free, we would still need a reasonable size of the calibration study if a second variable is measured with error and is correlated with the variable of interest. Figure 4.5 presents the optimized calibration study size when the variable of interest has no error and the confounding variable has the reliability coefficient of 0.5. When there is no effect of the confounding variable (RR=1 for Xi), we observe the usual U-shape graph for the calibration study sizes as a function of correlation between two true covariates. However, when the error-prone confounding variable has an association with the outcome, we have more complicated results. Generally when the correlation between two true covariates are moderate or smaller (-0.5 < p xix2 ^ 0.5), we need a relatively larger number of subjects in the calibration study when there is any significant effect of the confounding variable that is measured with errors. When there is a strong correlation between two true covariates, this trend is not necessarily true as shown in Figure 4.5. However, for the main cohort study, there seems to be a more stable pattern as seen in Figure 4.6. In general, a larger number of subjects are required when there is a strong correlation between two true covariates, except when the confounding variable has a very high relative risk (RR=5). 84 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.2a. The optimized calibration study size as a function of error correlations between two observed covariates, where correlations between two true covariates are assumed to be zero. 0 ) N > “ O 3 C o + 3 2 fi 15 o s N E 33 a O 340 320 300 280 260 240 220 200 180 160 140 120 100 80 60 40 20 0 “ O r 1 - 0.9 - 0.8 - 0.7 - 0.6 - 0.5 - 0.4 - 0.3 - 0.2 - 0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1 Error c o rre la tio n s betw een m e a su re d e x p o s u re s RR=1.5 for X1 and RR=0.5 for X2 H I— RR=1.5 forX1 and RR=1 forX2 -. 4 — RR=1.5 for X1 and RR=1.5 for X2 RR= 1.5 for X1 and RR=5 for X2 * Correlation between the two true covariates are fixed to be 0 (C orr(X l, X2)=0). * R Q = $1, R D = $1, R X = $50, baseline disease rate= 0 .5 % ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 85 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Optimized M ain Cohort study size (N) Figure 4.2b. The optimized main cohort study size as a function of error correlations between two observed covariates with a fixed correlation of true covariates. 30,000 25,000 20,000 15,000 10,000 5,000 0 1 - 0.9 - 0.8 - 0.7 - 0.6 - 0.5 - 0.4 - 0.3 - 0.2 - 0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1 Error correlations betw een m easu red e x p o su re s - RR=1.5 for X1 and RR=0.5 for X2 -R R =1.5forX 1 and RR=1 forX2 • RR=1.5 for X1 and RR=1.5 for X2 - RR=1.5 for X1 and RR=5 for X2 * Correlation between the two true covariates are fixed to be 0 (Corr(Xl, X2)=0). * R Q = $1, RD=$ 1. RX = $50, b aseline disease rate= 0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 86 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.2c. The proportion of calibration study size in the entire study as a function of error correlations between two observed covariates with a fixed correlation of true covariates. O t N £ 3 Vi c o £3 2 £ o H — o c o • ■ E a 2 a. 1.20 1.10 1.00 0.90 0.80 0.70 0.60 0.50 0.40 0.30 0.20 0.10 0.00 -1 - 0.9 - 0.8 - 0.7 - 0.6 - 0.5 - 0.4 - 0.3 - 0.2 - 0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1 Error correlations between m easured exposures - RR=1.5 for X1 and R R =0.5forX 2 ■ RR=1.5 for X1 and RR=1 for X2 RR=1.5 for X1 and RR=1.5 for X2 - RR=1.5 for X1 and RR=5 for X2 * Correlation between the two true covariates are fixed to be 0 (Corr(Xl, X2)=0). * R Q = $1, R D = $1, R X = $50, b aseline disease rate= 0 .5 % ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.3. The optimized sizes of calibration study and main cohort study as a function of error correlations between two observed covariates with a fixed correlation of true covariates, when true covariates are positively correlated (Pxix2 ~ 0.5) 650 S 600 - o 550 - N 500 - $ 3 450 - 400 - £ O £3 350 - 2 300 - •Q 250 - ■ 8 200 - N 150 E *3 100 - a O 50 - < D N * » 3 % r . o sz o o e '5 E 73 0 ) N 80,000 70.000 60.000 50.000 40.000 30.000 20.000 '5 10,000 Q. o - 0.8 - 0.7 - 0.6 - 0.4 - 0.3 - 0.2 - 0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 E rro r c o r r e la tio n s b e tw e e n tw o o b s e r v e d c o v a r ia te s - 0.8 - 0.7 - 0.6 - 0.4 - 0 . 3 - 0.2 - 0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 E rro r c o r r e la tio n s b e tw e e n tw o o b s e r v e d c o v a r ia te s ~ & -R R = 1 .5 fo rX 1 and RR=1 forX 2 — RR=1.5forX1 and R R =1.5forX 2 -HH— RR=1.5 forX1 and R R =5forX 2 — RR=1.5 for X1 and RR=0.5 for X2 * R Q = $1, R D = $1, R X = $50, b aseline disease rate= 0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 88 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.4. The optimized sizes of calibration study and main cohort study as a function of error correlations between two observed covariates with a fixed correlation of true covariates, when true covariates are negatively correlated (pxix2 = - 0.5) 650 _ 600 £ 550 500 450 400 350 300 250 ■ o 200 o ■| 150 1. 1 0 0 ■0.9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Error co r r e la tio n s b e tw e e n m e a su r e d e x p o s u r e s 80,000 £ 70,000 © N ‘ 5 5 60,000 * D * 5 5 50,000 tL O ■§ 40,000 0 '< 5 30,000 s *o 8 20,000 1 10,000 0 -0,9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Error c o r r e la tio n s b e tw e e n m e a su r e d e x p o s u r e s —•#— R R =1.5forX 1 and RR=0.5 for X2 —■ — RR=1.5 for X1 and RR=1 for X2 RR=1.5 for X1 and RR=1.5 for X2 —X - RR=1.5 for X1 and RR=5 for X2 RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 89 ] Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Optimized calibration study size (n) Figure 4.5. Optimized calibration study size to detect the relative risk of one variable that is measured with no error while it is correlated with a second variable measured with error. 180 160 140 120 100 80 60 40 20 0 ■0.9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Correlation between two covariates (X1 and X2) - RR=1.5 for X1 and RR=5 for X2 - - it RR=1.5 for X1 and RR=1.5 for X2 - RR=1.5 for X1 and RR=1 for X2 ~~x-~ RR=1.5 for X1 and RR=0.5 for X2 * RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for the second observed variable, Q2 is assumed to be 0.5. 90 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. O ptim ized main cohort study size (N) Figure 4.6. Optimized main cohort study size to detect the relative risk of one variable that is measured with no error while it is correlated with a second variable measured with error. 27,000 24,000 21,000 18,000 15,000 12,000 9,000 6,000 3,000 0 •0.9 -0.8 -0.7 -0.6 -0.5 -0.4 -0.3 -0.2 -0.1 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Correlation between two covariates (X1 and X2) —♦ — RR=1.5 for X1 and RR=5 for X2 - a - RR=1.5 for X1 and RR=1.5 for X2 RR=1.5 for X1 and RR=1 for X2 -~X~- RR=1.5 for X1 and RR=0.5 for X2 * RQ=$1, RD=$1, RX = $50, baseline disease rate=0.5% ** Reliability coefficients for the second observed variable, Q2 is assumed to be 0.5. 91 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 4.4. Simulation study When computing the variance of risk estimate for the variable of interest that are adjusted for measurement errors in the optimization problem, we computed the “uncorrected” variance-covariance of risk estimate, , using several approximations as described in section 4.2. We performed simulation studies to study how well the variances of the risk estimates were estimated using these approximation methods. Using the main cohort study size (TV) that was suggested from the proposed cost- efficient design, we generated N observations with X, Q and outcome D. First vectors of X = (Xi, X 2) was generated from a bivariate normal density with a pre-assigned variance-covariance structure in the true exposures, X/ and X2. Then the measured covariate vector, Q = (Qi, Q2), were generated by assuming a reliability coefficient of 0.5 and the assigned error covariance structure (Cov(sj, 82)). Outcome variable, D ’s, were generated from a binary distribution with the success probability exp(a + fi* xX u + P * 2 X 2i) Pl 1 + exp(a + /? ,X + p [ X v ) ‘ For calibration subjects, n observations were generated for a set of X and Q. Then a logisitic regression was fit for D on Q on main cohort study members, and estimates of /?s were obtained. Corrected risk estimate /? was computed from/? = , where /V A f3 ’s were obtained from logistic regressions and X ’s are slopes obtained from fitting 92 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. calibration regressions. Gauss software program was utilized to perform this simulation and 1000 iterations were performed in each case. After 1000 iterations, ^ ^ * empirical variances of (3 and (3 were computed and compared to the estimated values in our proposed cost-efficient design. Table 4.2a and 4.2b shows the comparison between estimated values in the proposed cost-efficient design and the simulation results in the estimates and variances for both uncorrected and corrected relative risks. Table 4.2a represents the case where the confounding variable gives a lower relative risk (RR=T.5) and Table 4.2b represents the case with a higher relative risk (RR=5) of the confounding variable. The Laplace approximation seems to work very well under a lower relative risk setting as shown in the ratio column for uncorrected variance of f3 in Table 4.2a. When the confounder’s relative risk is very high (RR=5), the Laplace approximation performed less efficiently as seen in Table 4.2b. In this case, we also observe that the uncorrected a values (baseline disease rate) obtained from simulation are quite different from the approximated a values that were used in the optimal design. This is suspected to be due to the non-linearity of the logistic function when relative risks are high, which results in the imprecision of estimating the uncorrected relative risks by /v /y ^ /\ f3 — (3 X . Overall the simulation study supports the use of the Rosner variance formulae combined with the Laplace approximation indicating that the results of this are reasonably reliable and that the general trends described are valid. 93 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Table 4.2a. Simulation results for Laplace approximation: To detect RR=1.5 for XI assuming a lower relative risk of confounding variable (RR=T.5 for X2) Number of iteration = 1000 Proposed Cost-efficient design Method Simulation (1000 iteration) Rho=0.5, psi=-0.5, Main cohort study size (N) 58034 Calibration study Size (n) 184 True risk estimate for XI Ln(1.5)=0.405465 0.4027425 True risk estimate for X2 Ln(1.5)=0.405465 0.4101119 V a r ( f i ) Rosner’s Variance 0.0159387 Empirical Variance 0.0175533 a -5.298700 -5.238767 Uncorrected risk estimate for xi (A) 0.303042 0.303042 Uncorrected risk estimate for X 2 ( A ) 0.304664 0.304664 Ratio Far(A ) 0.0014611 0.0013840 0.947 Far(A) 0.0014611 0.0013579 0.929 Rho=0.5, psi=0.9 Main cohort study size (N) 27179 Calibration study Size (n) 124 True risk estimate for X 1 Ln(1.5)=0.405465 0.411183 True risk estimate for X2 Ln(1.5)=0.405465 0.403043 Var(fi\ ) Rosner’s Variance 0.017449913 Empirical Variance 0.014285218 a -5.298700 -5.1720609 Uncorrected risk estimate for X I (A ) 0.1788817 0.1812861 Uncorrected risk estimate for X2 ( A ) 0.1788817 0.1743660 Ratio V a r ifi, ) 0.0065650 0.0057128 0.870 V a r (f i2 ) 0.0065650 0.0059315 0.903 * Optimal study sizes are based on RQ=$1, RD=$1, RX = $50 and baseline disease rate=0.5%, and the reliability coefficients for both Q1 and Q2 are assumed to be 0.5. 94 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Table 4.2b. Simulation results for Laplace approximation: To detect RR=1.5 for XI assuming a very strong effect of confounding variable (RR=5 for X2) Number of iteration = 1000 Proposed Cost-efficient design Method Simulation (1000 iteration) Rho=0.5, psi=-0.5, Main cohort study size (N) 53720 Calibration study Size (n) 572 True risk estimate for XI 0.405465 0.376357 True risk estimate for X2 1.609438 1.511824 V a r ( K ) R osner’s Variance 0.0141035 Empirical Variance 0.0103707 a -5.298700 -4.772489 Uncorrected risk estimate for x i ( A ) 0.605092 0.565910 Uncorrected risk estimate for X 2 ( A ) 0.906085 0.849644 Ratio V a r { fix) 0.0007219 0.0005211 0.722 V a r ( A ) 0.0007719 0.0005789 0.750 Rho=0.5, psi=0.9 M ain cohort study size (N) 26824 Calibration study Size (n) 340 True risk estimate for XI 0.405465 0.369021 True risk estimate for X2 1.609438 1.460818 V a r ( P l ) 0.0171399 0.0131605 a -5.298700 -4.452688 Uncorrected risk estimate for x i ( A ) -0.057191 -0.053032 Uncorreeted risk estimate for X2 ( A ) 0.946119 0.857185 Ratio Kar(A ) 0.0034994 0.0018334 0.524 V a r ( X ) 0.0036450 0.0018378 0.504 * O ptim al study sizes are b ased on R Q = $1, R D = $1, R X = $50 and b aseline disease rate= 0 .5 % , and the reliability coefficients for both Q1 and Q 2 are assum ed to be 0.5. 95 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Figure 4.7. Main cohort and calibration study sizes to detect various relative risks of the variable of interest (Xj) a) High cost ratio: RX=$50, RQ=$1, RD=$1 C ost ratio=50, RR=1.5 for X2 f f l N » >. ■ o 3 W ^ « Z o ■ c o o re £ 1 , 000,000 900.000 800.000 700.000 600.000 500.000 400.000 300.000 200.000 100,000 0 2,500 2,000 1,500 0 1.000 1.1 1.2 1.3 1.4 1.5 1.6 1.7 1.8 1.9 2 R e la tiv e risk fo r v a r ia b le o f in te r e s t (X1) Main cohort study size (N) — •— Calibration study size (n) f f l N ' 5 5 > . T J 3 W — t z o JC o o r a £ b) Low cost ratio: RX=$10, RQ=$1, RD=$1 C o st ratio=10, RR=1.5 for X2 900.000 800.000 700.000 600.000 500.000 4 00.000 300.000 200.000 100,000 0 4,000 3,000 2,000 1.000 1.1 1.2 1.3 1.4 1.5 1.6 1.7 1.8 1.9 2 R e la tiv e risk fo r v a r ia b le o f in te r e s t (X1) Main cohort study size (N) — •—Calibration study size (n) * True covariates were assumed to be moderately correlated (pxm = 0.5) and no error correlation in observed measures was assumed. 96 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. 4.5. S u m m ary In the optimization problem in a bivariate setting, the required main cohort and calibration study sizes are determined by many factors: 1. Baseline disease rate 2. Cost ratio of obtaining reference measures to conventional measures 3. Correlation between true covariates 4. Error correlation between measured covariates 5. Hypothesized risk estimate of the variable of interest 6. Strength of the association of confounding variable with outcome variable Generally, the number of subjects in the main cohort and calibration studies increases as the correlation between the two true covariates increases. As the risk associated with the confounder increases, the optimal calibration study size increases. However, main cohort study sizes are relatively unaffected by the strength of the association of the confounder with the outcome. When the true covariates are correlated, required main cohort study size is influenced by the correlation between errors in observed exposure. The strong error correlations are, the smaller main cohort size is needed when true covariates and errors in observed exposures are correlated in the same direction. General trends for calibration study size in our bivariate results also agree with Fraser and Stram (Fraser 2001) that argued useful gains in power accrue with calibration study size up to 1,000 subjects when there is important collinearity between covariates. As seen in Figure 4.7, when the cost ratio of reference measurement to conventional measurement is not very high, proposed cost-efficient 97 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. method requires more than 1,000 subjects in the calibration study to detect a small relative risk of the variable of interest when two covariates are well correlated. 98 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Chapter V Conclusion In this paper, we proposed a cost-efficient design of large cohort and calibration studies when they are simultaneously considered at the planning stage. The proposed method is extended from Spiegelman and Gray’s approach in many aspects. First, our approach is simpler in its application. Second, we studied the case when the observed exposure contains both random and systematic errors. Third, it deals with the case when a gold standard is not available and the average of repeated reference measurements is used. In such a case, the optimal number of replicates is also computed simultaneously in the cost-efficient design. Lastly, and more importantly, the cost-efficient design is expanded to a bivariate setting where two covariates are correlated in their true values as well as in errors. Generally, in a univariate setting, a larger calibration study is required when the observed covariate contains larger errors. The proportion of calibration study size in the entire study is also dependent upon the magnitude of relative risk that we wish to 99 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. detect in the risk model. The larger the relative risk is, the larger fraction of calibration study size is allocated in the entire study. When the baseline disease rate is higher, the optimal study design allocates a larger fraction of subjects to the calibration study. The proportion of calibration study in the entire study is also dependent upon the cost ratio of obtaining exposure from reference measurements vs. conventional method. When errors in observed exposure variable contain both random and systematic errors, the optimal sizes of main and calibration studies are unaffected by the magnitude of systematic errors as long as the correlation between true exposure and observed exposure is fixed. Therefore the major determinant in the cost-efficient design of main and calibration studies in a univariate setting is found to be the correlation between true and observed exposure. It was also shown that the optimized sizes in internal and external calibration studies are similar when the disease rate is low and the cost ratio of the reference measurement to the imperfect measurement is not high. When the replicates of imperfect reference measurements are obtained for calibration study subjects, designing the study with optimized number of replicates is essential in order to avoid the inefficient usage of resources. Calibration studies appear to be costly in general. Up to fifty percent of the entire resources may be allocated to the calibration study in the settings we examined. If the covariates in the risk models are correlated, it is important to control for the confounding effect when we are interested in the risk of one variable of interest. To 100 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. correct for the measurement error in such a case, bivariate calibration regression method is used. The proposed study design shows that required main cohort and calibration study sizes are determined by many factors such as baseline disease rate; cost ratio of obtaining reference measures to conventional measures; correlation between true covariates; error correlation between measured covariates; hypothesized risk estimate of the variable of interest; and the strength of the association of confounding variable with outcome variable. In general, the optimal design allocates more subjects in both main and calibration studies as the correlation between two true covariates increases. When the risk of the confounder is stronger, the optimal design requires even larger number of subjects in calibration studies. However, main cohort study sizes are relatively unaffected by the strength of the association between the confounder and the outcome. When the true covariates are correlated, required main cohort study size is influenced by the correlation between errors in two observed exposures. The stronger error correlations are, the smaller main cohort size is needed when true covariates and errors in observed exposures are correlated in the same direction. We also observed that a reasonable size of calibration study is needed even when the variable of interest is measured without error but is correlated with another variable that is measured with error. The optimal design in a bivariate setting is rather complicated because there are many determinants that influence the allocation of subjects to the main and calibration studies in complex ways. Although we only 101 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. reported the bivariate case for a classical error model and assumed the true exposure is known for calibration study subjects in this paper, we discussed many important findings in the optimal design for a bivariate setting where covariates are correlated in their true values as well as errors. As a future work, we can further discuss the optimal design in a bivariate setting where reference measurements are imperfect in calibration study subjects. Simultaneous consideration of the optimal number of replicates and the size of calibration and main cohort studies in a bivariate setting would be more complicated because the number of multiple records per subject now depends upon additional factors such as the error covariance structure of two observed exposures and the risk estimates, f f s. However, we anticipate that this work is feasible. We also have made a number of approximations in our cost-efficient design such as the normality of all covariates and errors. One could certainly envision simulation studies that would clarify whether these results are robust to the assumptions we made of the normality. We’ve shown that even for the non-linear cases with strong relative risks, our approximation performs relatively well. A computer program is under the development for the cost-efficient designs of both univariate and bivariate settings that deals with the case when a gold standard is not available. 102 Reproduced with permission of the copyright owner. Further reproduction prohibited without permission. Bibliography Ahlbom, A., Steinbeck, G. (1992). "Aspects of misclassification of confounding factors." American Journal of Ind. Medicine 21: 107-112. Armstrong, B. G., Whittemore, A.S., Howe, G.R. (1989). "Analysis of case-control data with covariate measurement error; application to diet and colon cancer." Statistics in Medicine 8: 1151-1163. Brenner, H. (1996). "Correcting for exposure misclassification using an alloyed gold standard." Epidemiology 7(4); 406-410. Carroll, R. J., Pee, D., Freedman LS., et al. (1997). "Statistical design of calibration studies." American Journal of Clinical Nutrition 65(4 Suppl): 1187S-1189S. Carroll, R. J., Ruppert, D., Stefanski, L.A. (1995). 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(1995). "Sample size requirements for calibration studies of dietary intake measurements in prospective cohort investigators." American Journal of Epidemiology 142(5): 557-565. Kipnis, V., Freedman, LS., Brown, CC., et al. (1997). "Effect of measurement error on energy-adjustment models in nutritional epidemiology." American Journal of Epidemiology 146: 842-855. Kleinbaum, D. G., Kupper, L.L. (1982). Epidemiologic Research. Belmont, CA, Lifetime Learning. Prentice, R. L. (1982). "Covariate measurement errors and parameter estimation in a failure time regression model." Biometrika 69(2): 331-342. Prentice, R. L. (1996). "Measurement error and results from analytic epidemiology: dietary fat and breast cancer." Journal of the National Cancer Institute 88(23): 1738- 1747. Rosner, B., Spiegelman, D., Willet, W.C. (1990). "Correctioin of logistic regression relative risk estimates and confidence intervals for measurement error: the case of multiple covariates measured with error." 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"Dietary fat and fiber in relation to risk of breast cancer." JAMA 268(15): 2037-2044. Willet, W. C., Sampson, L., Stampfer, M.J., et al. (1985). "Reproducibility and validity of a semiquantitative food frequency questionnaire." American Journal of Epidemiology 122: 51-65. Reproduced with permission of the copyright owner. Further reproduction prohibited without permission.

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Creator Park, Sohee (author)

Core Title Cost -efficient design of main cohort and calibration studies where one or more exposure variables are measured with error

School Graduate School

Degree Doctor of Philosophy

Degree Program Biometry

Publisher University of Southern California (original), University of Southern California. Libraries (digital)

Tag health sciences, nutrition,health sciences, public health,OAI-PMH Harvest,statistics

Language English

Contributor Digitized by ProQuest (provenance)

Advisor Stram, Daniel O. (committee chair), Azen, Stanley (committee member), Pike, Malcolm (committee member), Tavare, Simon (committee member)

Permanent Link (DOI) https://doi.org/10.25549/usctheses-c16-257724

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