Aspects of Statistical Design for the Community Intervention Trial for Smoking Cessation (COMMIT) Mitchell H. Gail, MD, PhD, David P. Byar, MD,* Terry F. Pechacek, PhD, and Donald K. Corle, MS, for the COMMIT Study Group Dwislon of Cancer Etzology, National Cancer Institute, Rockville, Maryland (M.H.G.), Diwsmn of Cancer Prevention and Control, Nattonal Cancer Instztute, Rockvtlle, Maryland (D.P.B., T F.P., D.K.C.)

ABSTRACT: We present statistical considerations for the design of the C o m m u n i t y Intervention Trial for Smoking Cessation (COMMIT). One outcome measurement, the quit rate in r a n d o m l y selected cohorts of smokers, is compared with another outcome measurement, the decrease in smoking prevalence, in terms of statistical efficiency and interpretability The COMMIT study uses both types of outcome measurements. The merits of pair-matching the communities are considered, and sample size calculations take into account heterogeneity a m o n g pair-matched communities. In addition to significance tests based on the permutational (randomization) distribution, we also describe approaches for covanate adjustment The COMMIT design includes 11 pair-matched communities, which should provide good p o w e r to detect a 10% or greater difference m quit rates between the intervention and control communities in cohorts of heavy smokers and in cohorts of light or moderate smokers. The p o w e r is only moderate to detect intervention effects on the decreases in overall smoking prevalence or in the prevalence of heavy smoking

KEY WORDS Group randomlzatlon, cluster randomlzatzon, matchmg, smokmg prevalence, commumty

studies

INTRODUCTION D u r i n g t h e p e r i o d 1965-1987, t h e a g e - a d j u s t e d p r e v a l e n c e of s m o k m g in t h e U n i t e d S t a t e s d e c r e a s e d f r o m 50.2% to 31.7% for m e n a n d f r o m 31.9% to 26.8% for w o m e n [1]. H o w e v e r , t h e p r e v a l e n c e of h e a v y s m o k i n g ( > 2 5 ciga r e t t e s p e r d a y ) r e m a i n e d c o n s t a n t at 13% for m e n a n d n e a r l y d o u b l e d f r o m 4.4% to 7.4% for w o m e n d u r i n g t h i s p e r i o d [2]. B e c a u s e h e a v y s m o k e r s acc o u n t for a b o u t o n e - h a l f of all s m o k i n g - r e l a t e d c a n c e r s , a s c a n b e c a l c u l a t e d

*deceased

Address reprmt requests to M~tchellH. Gad, MD, National Cancer Institute, 6130 Executwe Bh,d , EPN/403, Rockvtlle, MD 20892 Recewed December18, 1990, revised June 19, 1991

6 0197-2456/92/$0 00

Controlled Chmcal Trials 13 6-21 (1992) Pubhshed by ElsevierScience Pubhshmg Co , lnc 1992 655 Avenue of the Amencas, New York, Nev, York 10010

COMMIT

7

from data in the 1982 Report of the Surgeon General [3], the National Cancer Institute sought to develop an effective community-oriented approach to smoking prevention and cessation that would accelerate the overall favorable trends in smoking prevalence and would promote cessation among heavy smokers. The COMMIT study was designed to test the effectiveness of community interventions in achieving this goal. Before we describe the sample size and other statistical design calculations, which were carried out in 1985, we summarize the main elements of the design. The interventions are designed to promote smoking cessation by using a wide range of community resources to approach individual smokers and to affect community attitudes and policies toward smoking. The intervention relies heavily on the active participation of community leaders, and the interventions are managed by a local community board and at least four task forces: (a) health care, (b) worksites and organizations, (c) cessation resources, and (d) public education including media and youth. Each task force seeks to augment smoking control activities and to increase the priority of smoking prevention and control as a local public health issue. Specific health care interventions include training physicians, dentists, and their office staff in smoking cessation strategies and facilitating policies to provide a smoke-free environment in all health care facilities. Worksites and other organizations, such as churches and labor unions, are encouraged to implement smoke-free policies, sponsor innovative smoking control methods such as contests and other incentives to quit, and promote other community resources and activities. The Cessation Resources Task Force is responsible for identifying, coordinating, and building local cessation resources and services and making these resources known to the public through a "Cessation Resources Guide," a regular local newsletter, and a smokers' network. The Public Education Task Force trains local leaders to use the media more effectively and to coordinate with national smoking control campaigns. This task force also organizes two community-wide events per year to give the smoking issue high visibility and provide opportunities to quit (e.g., televised quit programs, quitting contests, local promotions of the Great American Smokeout). This task force also coordinates school prevention activities such as promotion of smoke-free schools, development of prevention curricula, and restriction of access to tobacco by school-aged youth. More detailed descriptions of intervention activities are given elsewhere [4-9]. Because the interventions were oriented toward communities rather than individuals, the community was chosen as the unit of study. Principal investigators competed for participation in the trial on the basis of being able to provide two similar communities, either one of which could receive active intervention or control surveillance. The investigators matched these communities on factors such as population size, geographic proximity, age and sex composition, degree of urbanization, and socioeconomic factors. The paired communities were geographically close enough to permit monitoring and intervention by the investigators, but not so close that educational activities in the intervention community would affect the control community. The 22 selected communities ranged in population from 52,493 to 166,824 and included sites in the northeastern, southeastern, southwestern, central, and western regions of the United States as well as one site in Canada. Following

8

M.H. Gad et al. baseline prevalence surveys, one member of each of the 11 community pairs was randomly assigned to receive active intervention (the "intervention community") and the other to receive control surveillance (the "control community") at a public ceremony in May 1988. Each member of a community pair was assigned the color red or black at random using computer-generated pseudorandom numbers. At the public ceremony, red or black was randomly assigned to "intervention" by roulette. This double-randomization technique added credibility to the. random assignment and made it difficult to tamper with the randomization because a proper random assignment is assured if either the physical roulette assignment or the computer-generated random numbers behave randomly. Interventions were to continue from October 1988 through January 1993. To evaluate the effectiveness of intervention, a baseline survey of smoking prevalence was conducted from January to May 1988 based on a telephone survey of up to 6000 randomly selected households in each community. The survey size of about 6000 households was chosen to be large enough to identify 500 randomly selected heavy smokers and 500 randomly selected light or moderate smokers w h o were willing to participate in each community. In each category, 400 of these 500 subjects were reserved for major outcome evaluations. These 400 individuals in each category were to be contacted once each year and asked about smoking status. The survey was not linked to local program activities, nor were any interventions directed specifically at these individuals. Indeed, the annual telephone interviews were conducted by a survey agency located in Rockville, Maryland, and the local investigators implementing interventions were not told who had been selected for these special cohorts. A member of these cohorts is defined as having quit smoking if he or she has not smoked for the 6 months before final evaluation in January through May 1993. The remaining 100 members in each category were to be followed for smoking status as above, but were also to be given special questionnaires. Data from these persons are not going to be used for evaluation of the main outcome measurements because their outcomes might be affected by special survey activities. A final prevalence survey is to be conducted early in 1993. On the basis of these data, four major outcome measurements will be used to evaluate these programs: (a) final smoking quit rates in the cohort of 400 heavy smokers (the primary outcome measurement), (b) final smoking quit rates in the cohort of 400 hght or moderate smokers, (c) change in community prevalence of heavy smoking from baseline to early 1993, and (d) change in the overall prevalence of smoking from baseline to early 1993. As we shall discuss, the power of the present design to detect intervention effects on cohort quit rates is high, whereas the power to detect intervention effects on changes in prevalence is only moderate. Several statistical design issues arise in connection with this trial. What are the advantages and disadvantages of using cohort quit rates versus changes in prevalence as outcome measurements? What proposed analyses and sample size calculations lead to the choice of 11 community pairs? Is matching useful or would an unmatched community randomization be preferred? What kinds of covariate adjustments are feasible? We shall deal with these issues in successive sections.

9

COMMIT COMPARISON OF COHORT QUIT RATE A N D PREVALENCE OUTCOME MEASUREMENTS

Changes in smoking prevalence have been used to evaluate other smoking intervention programs [10-13]. One concern with this outcome measurement is the possibility that migration patterns may affect smoking prevalence differentially in the paired communities. Also, the statistical power to detect differences in changes in prevalence may be less than the power to detect differences in cohort quit rates. The comparison of cohort quit rates has good statistical power and is not affected by general community migration patterns. However, if substantial numbers of cohort members are lost to follow-up over the 5 years of study, biases could be introduced if, for example, nonquitters in intervention communities tend to be lost to follow-up more than nonquitters in control communities. If the losses to follow-up are nondifferential, so that biases are not introduced, the power of the comparison would not be seriously attenuated by loss to follow-up of 150 of the 400 cohort members, because the dominant component of variability, namely, the within-pair variability in population quit rates between communities, is not affected by the final cohort size (next section). The main disadvantage of the cohort design is the possibility that contacting cohort members each year to determine smoking status and maintain follow-up may in itself act as an effective intervention, yielding higher quit rates in the cohorts than in the communities at large. However, if the effects of repeatedly contacting the cohort members are the same in the intervention and control cohorts, it may still be true that the difference in cohort quit rates provides an unbiased estimate of the corresponding difference in quit rates in the general smoking populations of the intervention and control communities. Table 1 illustrates why differences in the cohort quit rates may be easier to demonstrate than differences in prevalence. For simplicity, assume that there are no migrations or deaths during the study. In the intervention community it is assumed that 8/(24 + 8) = 25% of smokers quit, compared to 5/ (27 + 5) = 15.6% in the control community. Thus the expected difference in quit rates in a randomly selected cohort would be 25% - 15.6% = 9.4%. By contrast, the prevalence decrease in the intervention community is only 32% - 24% = 8% and in the control community only 32% - 27% -- 5%, so that the difference in prevalence decreases between treated and untreated communities is only 8% - 5% = 3%. The squared ratio (9.4/3.0) 2 = 9.8 indicates that the variances associated with the differences in prevalence decreases Table 1

Hypothetical Example to Compare Efficiencies of Cohort and Prevalence Outcome Measurements

Basehne Smoker Smoker Nonsmoker Nonsmoker

Final Evaluation Nonsmoker Smoker Smoker Nonsmoker

Intervenhon Community .08 .24 .00 .68 1.00

Control Community .05 27 .00 .68 1.00

10

M.H. Gall et al. m u s t be 9.8 times smaller t h a n the variances of the differences in paired cohort quit rates to achieve c o m p a r a b l e p o w e r . Even large p r e v a l e n c e s u r v e y s m a y not reduce the variance sufficiently, because there r e m a i n s a c o m p o n e n t of variability that c a n n o t be eliminated b y increasing the size of the p r e v a l e n c e s u r v e y (next section). A l t h o u g h the data in Table 1 are hypothetical, t h e y accurately reflect the m a g n i t u d e s of intervention effects c o n s i d e r e d in calculating s a m p l e size (next section).

SAMPLE

SIZE

Basic principles for g r o u p r a n d o m i z a t i o n are discussed b y Cornfield [14] a n d D o n n e r et al. [15]. Let X,e a n d X,c be the r e s p o n s e s in the i n t e r v e n t i o n (or experimental) a n d control c o m m u n i t i e s of m a t c h e d c o m m u n i t y pair i for i = 1, 2 . . . . . m. The quantities Xle a n d Xzc m a y c o r r e s p o n d to cohort quit rates or to p r e v a l e n c e decreases, w h i c h e v e r o u t c o m e m e a s u r e m e n t is being considered. The test for no i n t e r v e n t i o n effect will be b a s e d on the p e r m u t a t i o n a l (randomization) distribution of rn

D = ~

D,

(1)

w h e r e D , = X,e - X,c. Unless there are tied values of D,, there will be 2 ~1 = 2048 distinct values of D, c o r r e s p o n d i n g to the various h y p o t h e t i c a l reallocations of i n t e r v e n t i o n within m a t c h e d pairs, a n d a o n e - s i d e d test rejects at the .05 level if the o b s e r v e d D value falls a m o n g the largest 0.05 x 2048 = 102 values. We verify the following simple a p p r o a c h to s a m p l e size calculations by direct simulations of the p o w e r of the o n e - s i d e d p e r m u t a t i o n test, as described later in connection with Tables 2 a n d 3. The following simple a p p r o x i m a t e m e t h o d is b a s e d on the fact (Fisher [16], chapter 3) that the p e r m u t a t i o n te__st is well a p p r o x i m a t e d b y a p p l y i n g t h e t distribution to the statistic t = m ~ D / s w h e r e D = D / m a n d s 2 = X ( D , - D ) 2 / ( m - 1). The p o w e r of this statistic Table

2

N u m b e r of Rejections of the Null H y p o t h e s i s of N o I n t e r v e n t i o n Effect on C o h o r t Quit Rates b y the O n e - S i d e d .05 Level P e r m u t a t i o n Test in 1000 Simulations Number of pairs

Case

n

p,

0 .2

A B C D E F G H I J

250 250 250 250 250 250 250 250 250 500

0.15 0.15 0 15 0.15 0.15 0.15 0.15 0.15 0.25 0.25

00318 .00318 .00318 .00318 .00800 .00800 .00800 .00800 .00318 00318

m

8 9 10 11 8 9 10 11 11 11

0

05

1

15

44 47 64 46 55 52 63 51 51 41

418 506 522 531 232 266 284 303 517 569

894 924 955 976 613 662 717 792 963 985

955 1000 1000 1000 895 930 943 973 1000 1000

11

COMMIT Table 3

Estimated N u m b e r of C o m m u n i t y Pairs m Required to Detect Differences in Prevalence Decreases Annual % of Smokers Who Quit

All smokers (initial prevalence .32)

Heavy smokers (initial prevalence .087)

Control Community

Intervention Community

4

Required m n

Power 0.9

Power 0.5

7.5

6000 3000

27 28

10 10

3

9

4

7.5

3

9

6000 3000 6000 3000 6000 3000

11 11 24 29 10 12

5 5 9 11 4 5

d e p e n d s o n the m e a n s and variances of the {D,}. Let 3 = m-IF,E(D,) and ,.£2 = m-lY.Var(D,). A l t h o u g h required sample sizes u n d e r n o r m a l t h e o r y could be based on the noncentral F distribution [17], we u s e d the simpler approximate m e t h o d given on page 113 of Snedecor and Cochran [18]. We c o m p u t e the required n u m b e r of c o m m u n i t y pairs m by first c o m p u t i n g m' = (Z~ + Z~)2T2/~2

(2)

w h e r e Z~ = 1.645 a n d Z , = 1.282 c o r r e s p o n d to a one-sided c~ = .05 level test with p o w e r 1 - ~ = 0.9. T h e n we set m = m'{int(m') + 2}/int(m')

(3)

w h e r e int(m') is the smallest integer greater than or equal to m'. To a p p l y these ideas to cohort quit rates, a s s u m e that n individuals are followed in each cohort and that the expected difference in quit rates E(D,) is constant at ~ for all c o m m u n i t y pairs. From the r a n d o m effects m o d e l described in the Appendix, Var(D,) = 2o~,(1 - n-') 2 + n-l{(p~ + ~)(1 - p, - ~) + p,(1 - p,)}

(4)

w h e r e p, = E(X,c) and ¢2 is the variance of the u n d e r l y i n g p o p u l a t i o n quit rates in c o m m u n i t i e s with matching characteristics hke those in c o m m u n i t y pair I. If matching were completely effective, the first term w o u l d vanish. To be conservative, w e a s s u m e matching is completely ineffective a n d equivalent to r a n d o m l y pairing communities from the general p o p u l a t i o n of c o m m u m ties. H e n c e we substitute ~2 for o~, in (4), w h e r e 0.2 is the variance of u n d e r l y i n g p o p u l a t i o n quit rates in the general u n m a t c h e d p o p u l a t i o n of communities. The binomial c o m p o n e n t of variation in (4) can be r e d u c e d by using larger cohort sizes, but the b e t w e e n - c o m m u n i t y c o m p o n e n t , o~ = 0-2, w o u l d not be r e d u c e d by increasing n. The only ways to control b e t w e e n - c o m m u n i t y variation are to improve matching or to increase the n u m b e r s of c o m m u n i t y pairs m.

Unfortunately, data are not available from c o m m u n i t y studies to gauge the variance of quit rates oa. H o w e v e r , some data are available for assessing the variability of quit rates in 22 clinics from the Multiple Risk Factor Intervention

12

M.H. Gall et al Trial (MRFIT) [19]. The between-clinic c o m p o n e n t of variance in these chmcs w a s e s t i m a t e d to be 0-2 = 31.8 x 10~, as described in Ref. 20. Using this estimate w e find for n = 500, p, = . 15, a n d 8 = . 1 that the b i n o m i a l c o m p o n e n t of variation in (4) is only 6.3 x 10 4, or a b o u t 10% of the b e t w e e n - c o m m u n i t y variahon. To s t u d y the effects of loss to follow-up, w e c o n s i d e r e d n = 250. Reducing n f r o m 500 to 250 only c h a n g e s the variance (4) f r o m (63.6 + 6.3) x 10 4 = 69.9 x 10 4 to (63.6 + 2 x 6.3) x I(Y4 = 76.2 x l(Y 4, an increase of only 9.0%. To detect a &fference in quit rates 8 = .1 a m o n g h e a v y s m o k e r s , w i t h n = 250, p~ = .15 for all l, a n d 0-2 = .00318, w e calculate f r o m (2) that m' = (1.645 + 1.282) 2 x (76.2 x 10-4)/(0.1) 2 = 6.52 a n d f r o m ( 3 ) t h a t ,1 = 6.52 x (9/7) = 8.4, so that nine city pairs should yield p o w e r 0.9 or greater if our estimate of 0.2 is a p p r o p r i a t e . The value ~ = . 1 w a s c h o s e n b e c a u s e it w a s large e n o u g h to be medically i m p o r t a n t a n d yet s e e m e d plausible, b a s e d on p r e l i m i n a r y data f r o m other c o m m u n i t y i n t e r v e n t i o n studies [21,22]. Because these calculations d e p e n d e d on a p p r o x i m a t i n g the p o w e r of the paired t test, w h i c h itself w a s u s e d to a p p r o x i m a t e the p o w e r of the perm u t a h o n test, w e verified the p o w e r calculations a n d studied the effects of v a r y i n g n, p,, 8, a n d 0-2 b y simulating the p o w e r of the o n e - s i d e d p e r m u tation test (Table 2). For each case studied, 1000 h y p o t h e t i c a l trials w e r e s i m u l a t e d u s i n g the r a n d o m effects m o d e l in the A p p e n d i x , a n d the n u m ber of times the null h y p o t h e s i s test w a s rejected b y the p e r m u t a t i o n test w a s recorded. These simulations confirm that for 8 = 0 the size of the perm u t a t i o n test is n e a r the n o m i n a l .05 level a n d falls within two s t a n d a r d deviations (36, 64) in each case. For the p r o p o s e d effect, ~ = .1, the p o w e r is e s t i m a t e d at 0.894 or m o r e w i t h m = 8, 9, 10, or 11 city pairs, e v e n with n = 250. Because 0-2 e s t i m a t e d f r o m clinics m i g h t not a d e q u a t e l y reflect variation a m o n g c o m m u n i t i e s , w e also c o n s i d e r e d 0-2 = 0 . 0 0 8 0 0 , w h i c h is a b o u t 2.5 times the original estimate. The p o w e r d r o p s noticeably (Table 2), but with m = 11 city pairs the p o w e r is still 0.792 (case H). C h a n g i n g the quit rate in the control c o m m u n i t y p~ or increasing n to 500 has little effect on p o w e r , as can be s e e n b y c o m p a r i n g case I w i t h case D a n d case J with case I. Because p o w e r is insensitive to p , these calculations also a p p l y to detecting a difference in q m t rate 8 = .1 in the cohorts of light a n d m o d erate s m o k e r s . Thus, the p l a n with m = 11 pairs has g o o d p o w e r to detect ~ = .1, e v e n if 0-2 is 2.5 times greater t h a n indicated f r o m clinic data in MRFIT. If the m a t c h i n g has b e e n effective in r e d u c i n g 0-2, the p o w e r is e v e n greater t h a n indicated (see next section). U n r e p o r t e d simulations verify that h e t e r o g e n e i t y of i n t e r v e n t i o n effect 8 across city pairs has a negligible effect on p o w e r , p r o v i d e d the m e a n i n t e r v e n t i o n effect is held c o n s t a n t at .1. The results in Table 2 indicate that n = 250 w o u l d s u f f i c e in these cohorts, b u t u s i n g n = 400 allows for the possibility of loss to follow-up. Similar calculations w e r e carried out for assessing the feasibility of detecting larger decreases in p r e v a l e n c e a m o n g i n t e r v e n t i o n c o m m u n i t i e s t h a n a m o n g control c o m m u n i t i e s . In this case, X,e is the e s t i m a t e d decrease in p r e v a l e n c e in the i n t e r v e n t i o n c o m m u n i t y a n d X,c is the e s t i m a t e d decrease in p r e v a l e n c e in the control c o m m u n i t y . Equation (4) b e c o m e s

COMMIT

13 Var(D,) = 2o'~, + (K/n){~r,o(1 - ~r,o) + ~r,r(1 - -rr,~) + ~r,o(1 - ~r,o)

(5)

+ (~,r - 8)(I - ~r,f + 8) - 2 ~ - 8(1 - 2Tr,f)} where o~, now corresponds to heterogeneity of the underlying prevalence decreases among communities with matching characteristics like those in pair i, n is now the size of the prevalence survey sample, K is a design effect to account for the fact that telephone surveys of prevalences are based on cluster sampling (see chapter 2 in Ref. 23), ~r,0 is the expected baseline prevalence, "rr,f is the expected final prevalence in the control community, and ~,t - ~ is the expected final prevalence in the study community. D. R. Jacobs and P. J. Hannan kindly provided data from the Minnesota Heart Health Program [12] on four control and two intervention cities, from which 0-2 was estimated as 19.4 x I(Y 4 for decreases in the prevalence of smoking and as 1.03 x 10~ for decreases in the p r e v a l e n c e of h e a v y s m o k i n g . T h e y also calculated that the d e s i g n effect K in (5) w a s unlikely to exceed 1.2, the value w e used. To carry out the p o w e r calculations for p r e v a l e n c e studies (Table 3), w e a s s u m e d an initial p r e v a l e n c e of ~,0 = .32 for all s m o k e r s , an a n n u a l quit rate of 7.5% p e r y e a r a m o n g i n t e r v e n t i o n c o m m u n i t i e s , a n d a n a n n u a l quit rate of 4.0% p e r y e a r a m o n g control c o m m u n i t i e s . After 4 y e a r s of intervention, these quit rates w o u l d yield a final p r e v a l e n c e of Tr,f - 8 = .32 x (.925) 4 = .2343 in i n t e r v e n t i o n c o m m u n i t i e s , a final p r e v a l e n c e of ~,f = .32 x (.96) 4 = .2718 in control c o m m u n i t i e s , a n d 8 = .0375. If 9% of s m o k e r s quit each y e a r in i n t e r v e n t i o n c o m m u n i t i e s , c o m p a r e d to 3% in control c o m m u n i t i e s , the c o r r e s p o n d i n g figures are "rr,r - 8 = .32 x (.91) 4 = .2194, "rr,f = .32 x (.97) 4 = .2833, a n d 8 = .0639. For h e a v y s m o k e r s , with initial p r e v a l e n c e ~r,0 = .087, c o r r e s p o n d i n g calculations yield "rr,f - ~ = .0637, "rr,f = .0739 a n d = .0102 for a n n u a l quit rates of 7.5% a n d 4% in i n t e r v e n t i o n a n d control c o m m u n i t i e s , a n d "rr,f - ~ = .0597, ~,r = .0770, a n d ~ = .0174 for a n n u a l quit rates of 9% a n d 3% in i n t e r v e n t i o n a n d control c o m m u n i t i e s . Using these values of 8 a n d either n = 3000 or 6000 in the p r e v a l e n c e s u r v e y s , w e calculated the required n u m b e r s of city pairs to p r o d u c e p o w e r 0.9 or 0.5 w i t h o n e - s i d e d .05 level p e r m u t a t i o n tests f r o m f o r m u l a s (2), (3), a n d (5). It is seen (Table 3) that m = 11 city pairs are sufficient to detect the m o r e e x t r e m e e s t i m a t e s of the effectiveness of i n t e r v e n t i o n (annual quit rates of 3% vs. 9%) w i t h p o w e r 0.9 for n = 6000, b o t h for all s m o k i n g a n d for h e a v y s m o k i n g . H o w e v e r , the p o w e r to detect m o r e m o d e s t i n t e r v e n t i o n effects (annual quit rates of 4% vs. 7.5%) is o n l y a little g r e a t e r t h a n .5. T h e s e calculations are subject to large u n c e r t a i n t y b e c a u s e e s t i m a t e s of 0 -2 , a l t h o u g h derived f r o m a v e r y similar e x p e r i m e n t , are b a s e d o n only 4 d e g r e e s of freed o m (df). To s u m m a r i z e , these calculations indicate that 11 city pairs will yield g o o d p o w e r to detect r e a s o n a b l e decreases in cohort quit rates b u t m a y n o t h a v e sufficient p o w e r to detect i m p o r t a n t differences in the rates at w h i c h p r e v a lence decreases. O N THE USEFULNESS OF M A T C H I N G If m a t c h i n g is e q u i v a l e n t to r a n d o m pairing of c o m m u n i t i e s , s o m e efficiency is lost b y m a t c h i n g b e c a u s e the paired t test, b a s e d on m - 1 = 10 df, will

14

M.H. Gail et a|. have less p o w e r than an u n p a i r e d t test, based on 2m - 2 = 20 dr. H o w e v e r , the relative efficiency of these two procedures, based o n a formula that takes into account the degrees of f r e e d o m for estimating variances [24], is approximately {(20 + 3)/(20 + 1)}{(10 + 3)/(10 + 1)}-1 = 0.93, so that the paired p r o c e d u r e retains good efficiency e v e n if matching is ineffective. If matching is completely effective, so that intrinsic parameters are identical a m o n g communities with the same matching factors, t h e n the first terms in Eqs. (4) and (5) vanish. This p r o d u c e s potentially v e r y great gains in efficiency because the first terms are the largest variance c o m p o n e n t s . The first terms in (4) and (5) are r e d u c e d by the factor 1 -

2 Cov(X~,,X,c){Var(X,e)

+ Var(X,c)}-1

(6)

by matching. Equation (6) v e r y nearly equals (1 - p), w h e r e p is the "intrad a s s " correlation b e t w e e n X,e and X,¢, and equality holds if Var(X,e) = Var(X,~). Here the "classes" r e p r e s e n t m a t c h e d c o m m u n i t y pairs. F r e e d m a n et al. [25], using data from the baseline survey, estimated the percentage of smokers w h o had quit over the previous 5 years in each of the 22 selected communities and estimated an intraclass correlation p = . 78. T h e y used a regression model to take into account the fact that these previous quit rates m a y not have the same correlation as the o u t c o m e m e a s u r e m e n t s of current interest. H o w e v e r , we will simply s u p p o s e for example that the intraclass correlation for prevalence decreases is only .5 instead of .78. T h e n the first term in Eq. (5) is r e d u c e d by a factor of about 1 - p = 0.5. Using the m e t h o d s in the previous section, we calculate that only m = 15 pairs w o u l d be required to achieve p o w e r 0.9 to detect a decrease in prevalence of smoking c o m p a r e d to m = 27 pairs in the first row of Table 3. For h e a v y smokers, m = 16 pairs w o u l d be required c o m p a r e d to 24 pairs m row 5 of Table 3. Thus matching has induced correlations a m o n g estimates of previous cohort quit rates obtained from the baseline s u r v e y and promises to i m p r o v e the p o w e r of the design considerably, c o m p a r e d to the conservative assumption of completely ineffective matching used in the previous section.

DISCUSSION The interventions in COMMIT rely on media and educational campaigns, training of health professionals, approaches to worksites, and other comm u m t y resources that have the potential to affect most inhabitants of the c o m m u n i t y [4-9]. This fact necessitates the choice of the c o m m u n i t y as the unit of r a n d o m assignment and treatment. In other contexts w h e r e treatments are confined to individuals, one can sometimes choose b e t w e e n selecting the individual as the unit of r a n d o m assignment or selecting g r o u p s of individuals as the unit of assignment. In a study of the impact of vitamin A s u p p l e m e n tation [26], it was decided "for political and administrative reasons" to rand o m l y allocate 450 villages in n o r t h e r n Sumatra either to serve for 1 year as a control village or to serve as a site of vitamin A distribution for preschool children. In a n o t h e r trial, 24 factories were c h o s e n as the units of r a n d o m assignment in a s t u d y comparing workers in factories w h e r e advice was given on m e t h o d s to p r e v e n t heart disease with workers in factories w h e r e no such special advice was given [27]. Schools or classrooms have also b e e n u s e d as

COMMIT

15

units of random assignment and treatment in lifestyle intervention studies [28]. Although one usually obtains more information per patient studied by using individuals as the unit of assignment, there can be logistical and economic advantages to selecting groups of individuals as the unit of treatment and assignment, as illustrated by these examples and as discussed by Cornfield [14]. One can similarly apply these ideas to assigning all patients in a given medical practice or clinical ward to one or another treatment modality [29], but such a design only satisfies the assumptions required for an analysis based on the randomization distribution if the physicians and patients in each ward or practice are willing to implement whichever treatment is randomly assigned. This requirement is not satisfied in settings where inquisitive patients are allowed select physicians whose practices have already been randomly assigned to treatments. The major problem in designing community intervention trials such as COMMIT is obtaining reliable estimates of the between-community component of variation, o~, in Eqs. (4) and (5). Cornfield [14] and Donner [30] stressed the need to obtain and publish empirical data on this quantity in various areas of application to facilitate the planning of such trials. Although the variability of quit rates in clinics of the MRFIT study may not be the same as the variability in quit rates among communities in COMMIT, we have tried to be conservative by ignoring the potential improvements in efficiency from effective matching and by considering estimates of o~, that are 2.5 times greater than that observed in MRFIT. These considerations suggest that m -- 11 pairs will have good power to detect differences in cohort quit rates of .10 or more, in cohorts of both heavy and light or moderate smokers. Although the power to detect differences in decreases in prevalence is less satisfactory (Table 3), these calculations are based on a very small sample for estimating (r2. Therefore, it is possible that the power for detecting differences in decreases in prevalence is larger than indicated in Table 3, especially if the matching is as effective for decreases in prevalence as for previous cohort quit rates. It seemed advantageous to try to study both types of outcome measurements, not only because they address somewhat different questions (see section "Comparison of Cohort Quit Rate and Prevalence Outcome Measurements"), but also because the required screening sample needed to recruit a random sample of 500 heavy smokers in each community was large enough to yield good baseline prevalence estimates. Thus changes in prevalences could be estimated for the moderate additional cost of a final prevalence survey. These prevalence surveys should also yield improved estimates of quantities hke ~r2 in Eq. (5), which are needed to design future prevalence surveys. An interesting statistical aspect that we have not described is what telephone survey techniques were used to estimate prevalence and obtain randomly selected cohorts of heavy and light or moderate smokers. This work will be described in a separate publication. We have stressed simple permutation tests in designing this trial. Donner and Donald [31] discussed tests based on weighted sums of pairwise differences {D,}. Permutational tests that incorporate covariates can be constructed as described in Gail et al. [32]. For example, suppose a null logistic model is fit to all the cohort data to predict each individual's chance of quitting. The model can contain covariates describing the community and the individual,

16

M H. Gaff et al. but not intervention indicators. For each c o m m u n i t y the difference between the observed quit rate and the expected quit rate based on the null model can be calculated by s u m m i n g expectations over individuals in the community. These differences (residuals) are exchangeable within c o m m u n i t y pairs u n d e r the null hypothesis. Thus one can perform a permutation test on these residuals to test the null hypothesis of no intervention effect while adjusting for imbalances on c o m m u n i t y a n d individual level covariates. Donner [33] proposed alternative rdethods for taking c o m m u n i t y level covariates into account, and Prentice [34] described alternative m e t h o d s to take c o m m u n i t y and individual level covariates into account. The pair-matched group randomization design has been used in a large s t u d y to prevent heart disease [27] and, as suggested in the previous section, pair matching has the potential to increase efficiency substantially. Two recent papers [35,36] describe sample size calculations for pair-matched studies similar to those in the section "Sample Size." General considerations motivating cancer prevention trials [37] a n d a discussion of general statistical aspects of cancer prevention trials [38] have also been published. Other aspects of the evaluation plan for the COMMIT study have been described [39], including special surveys to evaluate changes in attitudes toward smoking, assessments of the degree to which planned interventions were in fact implemented, and measures of cost effectiveness.

APPENDIX: RANDOM EFFECTS MODELS LEADING TO EQS. (4) AND (5) AND TO SIMULATION RESULTS (TABLE 2). First consider cohort quit rates. Let al, a n d a2z be the u n d e r l y i n g true quit rates in the intervention and control communities, respectfully, in c o m m u n i t y pair I. Because the communities in pair z are regarded as a sample from a population of communities with like matching characteristics, we consider al, and a2z to be i n d e p e n d e n t r a n d o m variables each with m e a n pr and variance o~,, for i = 1, 2 . . . . . m. Conditional on al, and a21, the n u m b e r of quitters is binomial with m e a n n(8 + al,) a n d na2, respectively in the cohorts within the intervention and control communities in pair I. The corresponding unconditional means of the proportions quitting are (8 + p,) and p~. The corresponding variances of the proportion quitting are ~ + E(8 + al,)(1 - 8 a l , ) / n = o-~,(1 - n -~) + (p, + 8)(1 - pr - 8 ) / n and o~,(1 - n -1) + p,(1 - p 3 / n , which lead to Eq. (4). In the simulations for Table 2 we a s s u m e d the same value p, in each stratum a n d the same o~,, which corresponds to ineffective matching, in each stratum. We a s s u m e d a~, a n d a2~ were normally distributed, and if either air or a2, was negative in simulations, it was set to .01. A similar r a n d o m effects model applies to prevalence decreases. Let ~/,o~ and "Y,t,- be the initial a n d final population prevalence rates in the control community, and let ~,o~ and ~/,~e be corresponding prevalences that would have been seen in the intervention c o m m u n i t y had there been no intervention. Assume ~/ro~and %0~ each have m e a n "a',0 and variance 02. Likewise assume ~/,te and "Y,~ceach have m e a n ~r,f and variance ~q2. Finally assume ~/,0c, %0~, ~/,te, and ~/rf~are mutually independent. The conditional expectation of the difference in prevalence decreases given these ~/values is -

COMMIT

17 {y,0~ - (yce - 8)} - (y,o~ - yet),

(A1)

a n d the c o r r e s p o n d i n g unconditional expectation is 8, the a s s u m e d fixed effect of treatment. The conditional variance of the estimated difference in prevalence decreases is (K/n){y,0~(1 - ~/,o~) + y,0e(1 - y,o~) + y,fc(1 - Y,lc) + (Y,re - 8)(1

-

Y,fe

(A2)

q- 8)},

w h e r e n is the size of each prevalence s u r v e y and K is the s u r v e y design effect (we take K = 1.2). The first term in Eq. (5) is the variance of (A1), w h e r e o~, in (5) equals 2"q2. The expectation of (A2) equals the second term m (5). For example, the expectation of ( K / n ) ( y , l e - 8)(1 - Y,re + 8) is (K/n)[E{(y,re)(1 - "/,re)} - E{8(1- 2y,re)}], which equals (K/n){'rr,r(1 - "a'¢) + ,q2 _ 8(1 2~r,f)}. A d d i n g the three other similar expectations yields the second term in Eq. (5). We thank Mrs Jennifer Donaldson for typmg the manuscript and the Editor and reviewers for helpful clanficahons.

REFERENCES

1. United States Department of Health and Human Services: Reducing the Health Consequences of Smoking: 25 Years of Progress. A Report of the Surgeon General. Washington, D.C., U.S. Government Pnnting Office, 1989. DHHS (CDC) 89-8411, p 269 2. United States Department of Health and Human Services: The Health Consequences of Smoking: Nicotine Addiction. A Report of the Surgeon General. Washmgton, D.C., U.S. Government Printing Office, 1988, p 579 3. Umted States Department of Health and Human Services. The Health Consequences of Smoking: Cancer. Washington, D.C., U.S. Government Pnnting Office, 1982. DHHS (PHS) 82-50179 4. Llchtenstein E, Wallack L, Pechacek TF: Introduction to the community mtervention trial for smoking cessation (COMMIT). Int Quart Commun Health Educ 11: 173-185, 1990-1991 5. Ockene JK, Lmdsay EL, Berger L, Hymovltz N: Health care providers as key change agents in the community intervention trial for smoking cessation (COMMIT). Int Quart Commun Health Educ 11:223-237, 1990-1991 6. Pomrehn P, Sciandra R, Shlpley R, Lynn W, Lando H: Enhancing resources for smoking cessation through community intervention: COMMIT as prototype. Int Quart Commun Health Educ 11:259-269, 1990-1991 7. Sorensen G, Glasgow RE, Corbett K: Promoting smokmg control through worksRes in the community intervention trial for smoking cessation (COMMIT). Int Quart Commun Health Educ 11:239-257, 1990-1991 8. Thompson B, Wallack L, Lichtenstein E, Pechacek T: Pnnciples of community organization and partnership for smoking cessation in the community mtervention trial for smokmg cessation (COMMIT). Int Quart Commun Health Educ 11.187203, 1990-1991

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9. Wallack L, Sciandra R- Media advocacy and public education in the commumty intervention trial for smoking cessation (COMMIT). Int Quart Commun Health Educ 11.205-222, 1990-1991 10 Egger G, Fitzgerald W, Frape G, Monaem A, Rubinstein P, Tyler C, McKay B Results of large scale media anti-smoking campaign in Australia North coast "Quit for Life" programme Br Med J 287.1125-1128, 1983 11 Dwyer T, Pierce JP, Hannan CD: Evaluation of the Sydney "Quit for Life" antismoking campaign Part 2 Changes in smoking prevalence. Med J Aust 144 344347, 1986 12. Jacobs DR, Luepker RV, Mlttelmark MB, Folsom AR, Pirle PL, Mascloh SR, Hannan PJ, Pechacek TF, Bracht NF, Carlaw RW, Kline FG, Blackburn H. Communitywide prevention strategies. Evaluation design of the Minnesota Heart Health Program J Chron Dis 39 775-788, 1986 13 Farquhar JW, Fortmann SP, Flora JA, Taylor B, Haskell WL, Williams PT, Maccoby N, Wood PD Effects of communitywide education on cardiovascular disease risk factors The Stanford five-city project J Am Med Assoc 264 359-365, 1990 14. Cornfield J. Randomizahon by group a formal analysis Am J Epldemlol 108 100102, 1978 15. Donner A, Blrkett N, Buck C" Randomization by cluster sample size requirements and analysis. Am J Epidemlol 114-906-914, 1981 16 Fisher RA The Design of Experiments, 8th Edition. New York, Hafner, 1966 17 Pearson ES, Hartley HO: Charts of the power function of the analysis of variance tests, derived from the non-central F-distribution Blometrika 38:112-130, 1951 18 Snedecor GW, Cochran WG. Stahstical Methods (6th Ed) Ames, Iowa State University Press, 1967 19 Neaton JD, Broste S, Cohen L, Fishman EL, Klelsberg MO, Schoenberger J Multiple Risk Factor Intervention Trial (MRFIT): VII. A companson of risk factor changes between the two study groups. Prev Med 10 519-543, 1981 20. Byar DP: The design of cancer prevention trials. In Recent Results in Cancer Research, Kay R, Scheurlen H, Eds Heidelberg, Spnnger-Verlag, 1988 21. Farquhar JW, Maccoby N, Wood PD, Alexander JK, Breitrose H, Brown BW Jr, Haskell WL, McAhster AL, Meyer AJ, Nash JD, Stern MP Community education for cardiovascular health Lai,cet 1:1192-1195, 1977 22. Blackburn H, Luepker RV, Khne FG, Bracht N, Carlaw R, Jacobs D, Mlttelmark M, Stauffer L, Taylor HL. The Minnesota Heart Health Program: a research and demonstration project In cardiovascular disease prevention. In Behavioral Health. A Handbook of Health Enhancement and Disease Prevention. Matarazzo JD, Weiss SM, Herd JA, Miller NE, Weiss SM (Eds). New York, John Wiley and Sons, 1984 23. Klsh L: Statistical Design for Research. New York, John Wiley and Sons, 1987 24. Cox DR- The use of a concomitant variable in selecting an experimental design Biometrika 44:150-158, 1957 25 Freedman LS, Green SB and Byar DP: Assessing the gain in efficiency due to matching in a community intervention study. Stat Med 9:943-952, 1990 26 Sommer A, Dlunaedl E, Loeden AA, Tarwotjo I, West KP Jr, Tilden R: Impact of vitamin A supplementation on childhood mortality. A randomized clinical trial Lancet 1-1169-1173, 1986 27. Rose G, Tunstall-Pedoe HD, Heller RF: UK Disease Prevention Project: incidence and mortality results. Lancet 1:1062-1065, 1983 28. Murray DM, Hannan PJ, Zucker DM. Analysis issues In school-based health promotion studies. Health Educ Q 16:315-320, 1989

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29. Simon R: Composite randomization designs for chnical trials. Biometrics 37.723731, 1981 30. Donner A: An empIncal study of cluster randomization. Int J Epidemlol 11:283286, 1982 31. Donner A, Donald A: Analysis of data arising from a stratified design with the cluster as unit of randomtzation. Stat Med 6:43-52, 1987 32. Gall MH, Tan WY, PmantadosiS: Tests for no treatment effect in randomized clinical trials. Biometrika 75:57-64, 1988 33. Donner A: Statistical methodology for paired cluster randomization Am J Epldemiol 126:972-979, 1987 34. Prentice R: Correlated binary covariates specific to each binary observation. Biometrics 44:1033-1048, 1988 35. Hsieh FY: Sample size formulae for intervention studies with the cluster as unit of randomization. Star Med 8"1195-1201, 1988 36. Shipley MJ, Smith PG and Dramalx M: Calculation of power for matched pair studies when randomization is by group. Int J Epidemiol 18:457-461, 1989 37. National Cancer Institute: Cancer Control Objectives for the Nation: 1985-2000. Greenwald P, Sondik EJ (Eds). NCI monographs, 1986 38. Byar DP: Some statistical considerations for design of cancer prevention trials Prey Med 18:688-699, 1989 39. Mattson ME, Cummings KM, Lynn WR, Giffen C, Corle D and Pechacek T: Evaluation plan for the community intervention trial for smoking cessation. Int Quart Commun Health Educ 11:271-290, 1990-1991

APPENDIX: THE COMMIT RESEARCH GROUP National Cancer Institute (NCI) Dwision of Cancer Prevention and Control; Cancer Control Sciences Program; Smoking, Tobacco, and Cancer Branch (Bethesda, Maryland). Cancer Control Sciences Program Director: Claudia R. Baquet, M.D., M.P.H.; Smoking, Tobacco, and Cancer Program Coordinator (1982-1989): Joseph W. Cullen, Ph.D.; Project Officers: Terry F. Pechacek, Ph.D.; William R. Lynn, B.S.; Medical Officer: Marc Manley, M.D., M.P.H.; Public Health Advisors: Lamar F. Neville, M.S.W.; Joanne C. Odenkirchen, B.S.; Other staff contributors: Thomas J. Glynn, Ph.D., Donald R. Shopland, Jesse C. Gruman, Ph.D., Gayle M. Boyd, Ph.D.

Divzsion of Cancer Prevention and Control; Biometry Branch (Bethesda, Maryland). Chief: David P. Byar, M.D.; Section Head, Clinical and Diagnostic Trials Section: Sylvan Green, M.D.; Computer Systems Analyst: Donald K. Corle, M.S.; Expert: Lawrence S. Freedman. Division of Cancer Etiology; Biostatistics Branch (Bethesda, Maryland). Head, Epidemiologic Methods Section: Mitchell Gail, M.D., Ph.D.

Natzonal Institute on Alcohol Abuse and Alcohohsm, D:vision of Clinical and Prevention Research (Rockville, Maryland). Staff Collaborator: Margaret E. Mattson, Ph.D.

Chair, Steering Committee Erwin Bettinghaus, M.A., Ph.D., Michigan State University.

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Research Institutions

American Health Foundation (New York, New York). Principal Investigator: Mario A. Orlandi, Ph.D., M.P.H.; Co-Principal Investigator: Alfred McAlister, Ph.D.; Co-Investigator: Jacqueline Royce, Ph.D.; Project Director: Lesa T. Dalton, B.A.; Field Director: Carolyn Weiner; Community Analyst: Bonnie Edelman, B.S. Fred Hutchinson Cancer Research Center (Seattle, Washington). Principal Investigator: Maureen Henderson, M.D., Dr. P.H.; Project Director: Beti Thompson, Ph.D.; Co-Investigator: Deborah Bowen, Ph.D.; Community Analyst: K. Mark Leek, M.A.; Field Director: Juliet Thompson, B.A. Kaiser Permanente Medical Care Program, Northern California Region, Divlszon of Research (Berkeley, California). Principal Investigator: Lawrence Wallack, Dr. P.H.; (Principal Investigator until 12/86: Thomas Coates, Ph.D.); Co-Principal Investigator: Kitty Corbett, Ph.D.; Co-Investigators: Enid Hunkeler, M.A., Nancy Gordon, Sc.D.; Project Coordinator: Robert McGranaghan, M.P.H.; Analyst: Dorothy Snow, M.P.H. LovelaceMedical Foundation (Albuquerque, New Mexico). Principal Investigator: Neill F. Piland, Dr.P.H.; Project Director: Lawrence R. Berger, M.D., M.P.H.; Community Analyst: Annette M. Phillipp, M.P.H.; Field Director: Aile Shebar, R.N. Oregon Research Institute (Eugene, Oregon). Principal Investigator: Edward Lichtenstein, Ph.D.; Co-Principal Investigator: Russell E. Glasgow, Ph.D.; Project Coordinator: Linda Nettekoven, M.A.; Field Director: Carolyn Johnson, B.S.; Community Analyst: Shari Reyna, M.A. Research Triangle Instztute (Research Triangle Park, North Carolina). Principal Investigator: Tyler D. Hartwell, Ph.D.; Co-Principal Investigator: Robert H. Shipley, Ph.D.; Project Director: David Austin, M.S., M.P.H.; Project Director (until 9/89): Elizabeth T. Walker, B.S.; Field Director: Len Stanley, M.P.H.; Community Analyst (until 9/90): Sheri E. Fehnel, B.A. Roswell Park Memorial Institute (Buffalo, New York). Principal Investigator: K. Michael Cummings, Ph.D., M.P.H.; Project Director: Russell C. Sciandra, M.A.; Community Analyst: Eva Anderson Sciandra, B.S. University of Iowa (Iowa City, Iowa). Principal Investigator: Paul R. Pomrehn, M.D., M.S.; Project Director: John E. Ferguson, Ph.D.; Co-Investigators: Kristi J. Ferguson, Ph.D.; Robert B. Wallace, M.D., M.S.; Samuel L. Becker, Ph.D.; Harry A. Lando, Ph.D. (University of Minnesota); Community Analyst: Kelly O'Berry, B.S.; Field Director: Aleena Erickson, B.A. University of Massachusetts Medical School (Worcester, Massachusetts). Principal Investigator: Judith K. Ockene, Ph.D.; Co-Principal Investigator: Glorian Sorensen, Ph.D.; Project Coordinator: Linda C. Yackel, B.S.; Field Director: Barbara Silva; Community Organizers: Philip Merriam, M.S.P.H.; Gary Donnelly, M.P.H.; Community Analyst: Edward Purcell, B.S.; Community Analyst (until 7/89): Krisfine Sanden, B.S. University of Medicine and Dentistry of New Jersey (Newark, New Jersey). Principal Investigator: Norman Hymowitz, Ph.D.; Co-Principal Investigators: Lawrence Meinert, M.D.; Lee B. Reichman, M.D.; Norman L. Lasser, M.D., Ph.D.; Eugene Lewit, Ph.D.; John Slade, M.D.; Project Director: Karel Campbell, B.A.; Co-Project Director: Janice Marshall, R.N., M.S.N.; Field Director:

COMMIT

21

Sharon Jones Rudolph, B.S.; Community Analyst: Connie Strickland Farrakhan, M.A. University of Waterloo and McMaster University (Waterloo, Ontario). Principal Investigator: J. Allan Best, Ph.D.; Co-Investigators: A.J. Roy Cameron, Ph.D.; V.T. Farewell, Ph.D. (until 12/88); Charles H. Goldsmith, Ph.D.; K.L. Liaw, Ph.D. (until 4/87); Elizabeth A. Lindsay, M.S., Ph.D.; A.G. Logan, M.D. (until 12/87); David Nostbakken, Ph.D. (until 12/88); Ronald P. Schlegel, Ph.D.; Edward Smith, Dr.P.H. (until 6/89); G.L. Stoddart, Ph.D. (until 5/87); S. Martin Taylor, Ph.D.; Leslie van Dover, Ph.D.; Norman F. White, M.D.C.M., D. Psych.; Douglas M.C. Wilson, M.D.; Mark P. Zanna, Ph.D.; Project Director: Rosemary L. Walker, M.Sc.; Community Analyst: Terri Finch, B.A.; Field Director: Dianne Ferster.

Coordinating Center Information Management Services, Inc. (Silver Spring, Maryland). Principal Investigator: Janis A. Beach, A.A.; Co-Principal Investigator: Carol A. Giffen, D. V. M.; Project Director: Marie A. Topor, B.S.; Senior Information Specialists: Jerome L. Felix, M.A.; Lauren E. Rich, B.S.; Systems Analysts: Julie D. Buckland, B.A.; Senior Analyst/Programmer: Andrew A. St. John, B.S.; Biostatistician: David Pee, M.Phil.

Policy Advisory Committee (PAC) Chair: Virginia L. Ernster, Ph.D.; Karl Bauman, Ph.D.; David M. Bums, M.D.; Richard Carleton, M.D.; William T. Friedewald, M.D.; Kenneth E. Warner, Ph.D.; Donald Iverson, Ph.D. also served as Chair (1987-1988).