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Clinical Trials

DOI: 10.1191/1740774506cn152oa 2006; 3; 259 Clin Trials

C Hendricks Brown, Peter A Wyman, Jing Guo and Juan Peña Dynamic wait-listed designs for randomized trials: new designs for prevention of youth suicide

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C:LIENICA.L Q1ClANIN¢CAi2F ='ARTICLE Clinical Trials 2006; 3: 259-271TUAL. S

Dynamic wait-listed designs forrandomized trials: new designsfor prevention of youth suicide

C Hendricks Brown%, Peter A Wymanb, Jing Guoa and Juan Pehab

Background The traditional wait-listed design, where half are randomly assignedto receive the intervention early and half are randomly assigned to receive it later,is often acceptable to communities who would not be comfortable with a no-treatment group. As such this traditional wait-listed design provides an excellentopportunity to evaluate short-term impact of an intervention. We introduce a newclass of wait-listed designs for conducting randomized experiments where all sub-jects receive the intervention, and the timing of the intervention is randomlyassigned. We use the term "dynamic wait-listed designs" to describe this new class.Purpose This paper examines a new class of statistical designs where random assign-ment to intervention condition occurs at multiple times in a trial. As an extension ofa traditional wait-listed design, this dynamic design allows all subjects to receive theintervention at a random time. Motivated by our search for increased statistical powerin an ongoing school-based trial that is testing a program of gatekeeper training toidentify suicidal youth and refer them to treatment, this new design class is especiallyuseful when the primary outcome is a count or rate of occurrence, such as suicidalbehavior, whose rate can fluctuate over time due to uncontrolled factors.Methods Statistical power is computed for various dynamic wait-listed designsunder conditions where the underlying rate of occurrence is allowed to vary non-systematically. We also present as an example a large ongoing trial to evaluate agatekeeper training suicide prevention program in 32 schools which we initiallybegan as a classic randomized wait-listed design. The primary outcome of interestin this study is the count of the number of children who are identified by the schoolsystem as having suicidal thoughts or behaviors who are then validated as beingsuicidal by mental health professionals in the community.Results A general result shows that dynamic wait-listed designs always have higherstatistical power over a traditional wait-listed design. This power increase can besubstantial. Efficiency gains of 33% are easy to obtain for situations where the inter-vention has a small effect and the variation in rate across time is quite high. Whenthe rate variation for an outcome is very low or the intervention effect is large, effi-ciency gains approach 100%. A small increase in the number of times whererandom assignment occurs from 2 -- for the standard wait-listed design, to say 4 -

can provide a large reduction in variance. Efficiency gains can also be high whenconverting standard wait-listed design to a dynamic one half-way into the study.Limitations As with all wait-listed designs, dynamic wait-listed designs can only beused to evaluate short-term impact. Since all subjects eventually receive the inter-vention, no comparison can be made after the end of the random assignmentperiod. The statistical power benefits are primarily limited to outcomes that can betreated as count or time to event data.

aDepartment of Epidemiology and Biostatistics, University of South Florida, Tampa, Florida, USA, bDepartment of

AuPatryfor coiErspiodenoe:achendrticksBr,ste,n eparktm ofESoudemlogyTan Biosistics,Univery SoPsychiatry, University of Rochester, Rochester, New York, USAAuthor for correspondence: C Hendricks Brown, Department of Epidemiology and Biostatistics, University of SouthFlorida, Tampa, Florida, USA

O Society for Clinical Trials 2006 10. 191/1 740774506cn1 52oa



260 C Hendricks Brown et al.

Conclusions A dynamic design randomly assigns units - either individuals orgroups - to start the intervention at varying times during the course of the study.This design is useful in testing interventions that screen for new or existing cases,as well as testing the scalability of interventions as they are disseminated orexpanded system wide. They can improve on the traditional wait-listed design bothin terms of statistical power and robustness in the presence of exogenous factors.This paper demonstrates that such designs yield smaller standard errors and canachieve higher statistical power than that of a standard wait-listed design. Just asimportant, dynamic designs can also help reduce the logistical challenges of imple-menting an intervention on a wide scale. When the intervention requires thatsignificant training resources be allocated throughout the study, the dynamic wait-listed design is likely to increase the rate of training and lead to a higher level ofprogram implementation. Clinical Trials 2006; 3: 259-271. www.SCTjournal.com

Introduction

In this paper we present a generalization of thewait-listed design and examline its applicability tothe evaluation of an ongoing suicide preventionprograrm. The classic wait-listed randomized trialoften provides a convenient and scientifically rigo-rous way to evaluate an intervention's short-termimpact. In such a design half of the units - whetherthey be individuals, families, classrooms, schools or

communities - are randomly chosen to receive theintervention in the first phase of the study; theother half receives the intervention in the second.

phase. During the first phase of the study, a legiti-mate comparison can be made on an outcome vari-able between intervention and control conditions,and this difference can be attributed to the trueeffect of the intervention. Data froin the secondphase cannot be used to assess initervention impactbecause there is no control group to compare over

that period of time.A wait-listed design is especially useful when a

community, school system or governmental agencyhas already decided that everyone in a specific popU-lation will eventually receive a new intervention orprogram, especially when that intervention iswidely viewed as being beneficial, even thoughthere miiay be little einpirical evidence to back upthis perception. Commnunity leaders as well as indi-viduals in thie conmunity oftein feel that the use ofa random process to determine who receives theintervention first is fair and ethical, as long aseveryone receives the intervention within a reason-able amount of time. There may also be a compen-satory advantage for receiving the intervention inthe later group, since knowledge about theprogramn's implementation in the first phase canoften lead to improved implemlentation in thesecond phase.

Trhe major limitation of a wait-listed design iswell-known - it cannot be used to evaluate anything

but short-term impact since by the end of the phase2, no subjects remain in the control condition. TIhusthe long-term effects of preventive interventionscannot be assessed with such designs. Nevertheless,due to their inherent advantages, various types ofwait-listed designs have appealed to researchers aindcommunities alike.

One motivating exanmple for our work in deve-loping the new class of dynamic wait-list designs isthe Mpowerment community-based preventiveintervention. That intervention aimed to preventIJIV/AIDS by changing norms and empoweringindividuals to change their risky sexual behavior115,17, 18]. Since the Mpowerment interventionrequired intensive onsite training in a coinmunity,the study teanm could oinly traiin one community ata time. TIhe desigin stipulated that two communitiesbe randomized to either early or later intervention.With baseline measures collected on both commu-nities at the start of the study and the same datacollected on both communities after the early inter-vention community had received the intervention,an unbiased estimate of intervention effect on thispair of communities could be obtained.

'[his project actually used multiple baselines andfollow-ups on the samne two communities.However, as originally intended, this project wasdesigned to expand to additional conmmunities thatwould be randomly wait-listed at the time theyentered the study. After both of the original twocommiunities had received the intervention, amzatched pair of two new communities could thenbe randomized to the same intervention. Theprocess can then be repeated, taking a new pair ofcommunities and randomly assigning them toreceive the same intervention immediately or later.Even if the communities were not perfectlyiriatched, the random assignment would allow oneto assess intervention impact without potential biasfrom community readiness or other factors thatcould easily confound any intervention effect in a

Clinical Trials 2006; 3: 259-271 www.SCTjournal.com



Dynamic wait-listed designs for randomized trials 261

noni-randomized trial. Randomizing a number ofpairs of such communities to either iinmediateintervention or a wait-listed condition would thenover time provide unbiased data on interventioneffect. While such a continued design for evaluat-ing the Mpowerment intervention has not occurredto date, the novelty of the designi has prompted usto investigate how similar ideas can be used inpractice [4].

In this paper, we begin by describing the ration-ale for an ongoing trial where a classic wait-listeddesign has been used to evaluate a gatekeeper train-iing suicide prevention program in a large publicschool district. To date, only a handful of suicideprevenition programns have ever been evaluated withrigorous randomnized trials such as the one wedescribe here [11,13,22,28]. Epidemiologic evi-deince is provided that indicates there is currenltly alow rate of referral of suicidal youth by school staff.This provides a potential for a gatekeeper trainingprogram, such as the one being tested in the cturrenttrial, to enhance the referral of suicidal youth. Theprimary goal of this prevention program is to suc-cessfullv identify mnore children who are suiicidal sothat they can be referred to the existing mentalhealthl system for intervenltion. Like other popula-tion-based interventions, the evaluation requires usto consider that the level of suicidal behavior aswell as the rate of referral may well be influenced byuncontrolled external events - such as well-knowncontagion effects from a celebrity committingsuicide [12,21,29]. The potential influence of theseuncontrollable fluctuations makes it imperative tohave a design involving randomization that alsoblocks on time; that is, every time interval that pro-vides useful data on intervention impact must haveboth intervention and control units.

Our inew contribution is to introduce thedynamic wait-listed design. This design allows forblocking on a nuimber of smiialler timze units. VVedemnonstrate using both linear aind log-linearrandom Poisson regressioni models that this newdesign is always more efficient thain that of theclassic wait-listed design. The linear model providesan analytic expression for evaluating efficiency gainas a function of the number of time intervals. Thelog-linear model is mlore standard for the field andis used to assess the quantitative effects of changesin the number of time intervals, intervention effectand degree of variation across time. We concludethat dynamic wait-listed designs genierally providelarge gains in efficienicy. Furthermore, such designsare logistically easier to implement in settingswhere significant traininig resources are required toimplement an intervention. Finally, we return tothe gatekeeper training trial for suicide prevention.Calculations are used to project the improvementin statistical power as well as logistical training

effort provided by changing to a dynamic wait-listed design mlidway through the study.

Youth suicide and the Georgiagatekeeper project

Despite some recent information indicating thatyouth suicide in the United States has declined overthe last decade (eg, from seven to less than five per100000 aged 14-19) [5,24,361, suicide is still thethird rmost common cause of death for youth.Nationally, nearly 10% of young people reporthaving attempted to commit suicide [14]. Everydeath by suicide can be exceptionally painful tofamnily mnembers and friends. However, the loss of achild through suicide imparts a special burden to afamily and community, includiing increased risk forstressful events, family distress and relationshipproblems [3,23,33], all of which may increase thesuffering of surviving family and friends whenevera youth suicide occurs. With the latest reportedrates of suicide deaths of 9.9 per 100000 amongthose aged -15-25 1241 and rnortality rates rangingbetMeen 5-10% for mid(idle and high-school youth15,61, even m1)odest size communities are likely toconfront a youth suicide nearly every year.

Our current scientific knowledge base aboutsuicide prevention is typified by well identified epi-demiologic risk factors, developed from psycholo-gical autopsy studies, retrospective case cointrolstudies and prospective longitudinal studies [11].Several treatments are considered "promising" forreducing suicide among high-risk clinical groups126], -but there are very few population-based pre-ventive interventions that have received a scientificevaluation using randomized trials or other highquality designs [13], despite a national priority forincreased scientific rigor 1351. One of the primarydifficulties with conducting such trials is that sui-cides in the general population are, despite theenormous suffering they bring, relatively less fre-quent in occurrence compared to other targets ofprevention programs. This so-called "low base rate"condition makes it much more difficult to testpreventive interventions aimed at reducingyouth suicide.

In 2003 the present authors were invited by alarge school district in Georgia to help evaluate aschool-based gatekeeper trainiing program forsuicide prevention. Drawinig on funds provided bythe State of Georgia Legislature for suicide preven-tion, the school district had already decided to trainall its middle and high school staff members in aprogram called QPR [30], which stands for "ques-tion, persuade and refer". The QPR gatekeeperprogram is designed to enhance each adult staffmember's ability to recognize signs of youth who

Clinical Trials 2006; 3: 259-271www.SCTjournal.com




are contemplating suicide, to give them skills toapproach such children and question them-n openlyabout suicide, and to refer them to treatment usingthe centralized referral system in a school district. Itis recognized that adults who are in a youth'sformal network, eg, a teacher or informal network,eg, a cafeteria worker, can serve as either positive ornegative roles in linking a distressed youth tomental health services [34]. By training all staff in aschool regarding appropriate steps for a suicidalyouth, gatekeeper training programns aim toincrease the linkage to beneficial services. 'Ihis par-ticular school district is well-suited for a study ofgatekeeper training. h'le existing system of servicesfor youth demonstrating suicidal or other lifethreatening behavior iin this school system isbacked up by an excellent relationship with thelocal mnental health system. Free mental healthassessiments are offered to all families where a crisisresponse is needed, and these are generally com-pleted within one day.

In a collaborative stuLdy design process, theschool district agreed to implement the QPR train-ing using a randomized wait-listed design. Wereceived funding froin the National Institute ofMental Health in 2004 to begin a trial in 32 middleand high schools withl 60000 children. Currentlythe district is in the process of QPR training for the2500 staff in the first half of 16 schools assigned tothe early intervention condition.

Epidemiology of suicide and suicidalityin this school district

Over the last 16 years, this school district has exp-erienced an average of four child deaths each yearwith the number ranging from 0 to 10. With 60000school children between the ages of 11 and 18 inthis district, this rate is relatively comparable withthat of the current national average [24].l Evenwith this large size school district, the compara-tively "low" frequency of youth suicides makes itunlikely to find a statistically significant reductionin suicides in a one or two-year study. Becausesuicide is comparatively a rare event, we have

'Baseline rates of youth suicide differ substantially bylocale, level of urbanicity, race/ethnicity, age distribtu-tioIn, reporting accuracy and potential other factorssuch as school and cornmtiulity crisis response, avail-ability anid accessibility to mental health treatment,an-d potential use of antidepressive.s and other medi-cations. All of these factors make it difficult to inter-pret unadjusted rates of youth suicicle unless they varysubstantially from the national average which is niotthe case here.

chosen to study suicidal behavior and ideation asthe key target for intervention. As we show below,there is a substantial numiber of suicidal youthswho are not being identified by a school. Onegeneral prevention- strategy is to traiin all schoolstaff to identify and refer such youth. We are nowtesting in a randoimized trial whether QPR increasesthe identification and referral of suicidal youth.

For the first time this school district has begunanonymous surveys measuring suicidal behavior ineighth and tenth grade studients. Although only amodest fraction of these eighth and tenth graderwere able to schedule and complete this on-linesurvey during the 2003-2004 school year, the ratesof suicidal behavior and ideation were quite consis-tent with that in other youth surveys. Specifically,anonymous surveys in these schools revealed that3.3% of eighth graders and 2.9% of tenth gradersreported that they had attempted suicide in the lastfour weeks. The corresponding rates for attemptedsuicide in the last year were 6.7% and 6.2%, respec-tively. These rates of 12-month suicidal attempts are30% lower than thcose reported in Georgia (8.9% fortenth graders) and for the nation (9.1% for tenthgraders) in representative surveys of students in2003 [14].

A staff survey of a random 10%YO in each of the 32schools participating in the trial was conductedprior to starting training for QPR so that we couldassess the baseline level of response by staff tostudent suicidality. The vast majority of these staffmembers considered that students did talk to themabout their thoughts and feelings, but relatively fewstaff felt they could identify signs of suicidality,understood what sources were available to assistsuicidal youths, or felt they would be effective inreferring students for help. Ihose latter constructsare key targets of QI'R training. In prior implemen-tations of QPR, data from pre and post-tests haveshown that adults increase their knowledge as wellas self-efficacy with gatekeeper training [30].

The school district has had a protocol and cen-tralized system to identify and handle childrendemonstrating life threatening behavior. In thelatter half of the 2003-2004 school year, 127 chil-dren were identified in the 32 study middle andhigh schools who required iminediate crisisresponse due to suicidality, homicidal or other lifethreatening behavior. Approximately 15% of thesewere considered to be at such high risk that theyrequired inmmnediate inpatient services.

Overall, the survey data reveal that there are sig-nificant inumbers of students who are suicidal butare) not kinowin to the school district. Based on the6%Y0 prevalence of reported attempts to commitsuicide in the last year, we would anticipate that3600 students could be harboring significantthoughts and/or plans about suicide in this

Clinical Trials 2006; 3: 259-271 www.SCTiournal.com




population of 60000 middle and high schoolstudents. It is estimated that only 5% (193/3600) ofsuch suicidal children are currently identified andreferred by the school staff. Thus a gatekeepertraining program that helps identify such studentsand get them into treatment earlier would likelyhave an impact on reducing suicide attempts and,potentially, deaths through suicide.We can use these data to make a crude assess-

ment of what impact a gatekeeper training programcould have on increasing appropriate referrals. It isbelieved that most youth who go on to commllNitsuicide tell at least one other person in the week ortwo before this final act or otherwise nmanifestobservable warning signs [51. Let us define p( to bethe probability that a single staff member in theschool becomes aware that a student is suicidal andsuccessfuIlly refers that suicidal child in the schoolto appropriate crisis response, in the absence of anygatekeeper training program. It is possible to obtaina crude estimate of po based on the previous data,the number of staff in the school, which averages162, and somie sirnplifying assumptions. If all staffhappen to have the same probability of referring asuicidal child and the event of each staff memberreferring or not referring a single suicidal child isnearly independent, then the probability of a suici-dal child being successfully referred is a function ofthe individual staff probability of referral, p() andthe number of staff, NotVft,

Pr(Referredl) l - (1 PO)Nal (1)!Solving for po and setting Pr(Referred) to ourestimate of 5%, a straightforward estim-ate of theindividual's probability of successfully identifyingand referring a suicidal stubject is

Po - 1 (1 _- 0.05)1/102 = 0.00032 (2)This minute number suggests there is large room forimprovement, and a gatekeeper trainiing program isdesigned specifically to improve such rate. Definingy as the increase in odds of a single trained personbeing able to effectively refer a suicidal child, andf as the fraction of staff at a school being trained,the probability of having a suicidal child referred isthen

Pr(Referred) = 1 -- (1 -- Po)' f)lNstaft (1 -- Pi)tNst,a (3)

where p, is the probability of a single staff membertrained in the gatekeeper trainiing program success-fully referring a suicidal child,

P1 P (4)1-p 1-p(o

Figure 1 uses these formulae to determine the pre-dicted effect on the probability of referring a suici-dal child as a function of the level of trainingsaturation at each of the schools (abscissa) and dif-ferent hypothesized effectiveness of the gatekeeper

10

- ,-.---- 0

10

--I T -- I---

0.0 0.2 0.4 06. 0.0 1.0

Proporton Tranled

Figure 1 Probability of someone referring a suicidal child asa function of proportion of staff trained and training effec-tiveness scaled from one to 10 times the individual levelpretraining referral rate y

training, measured by the factor that measurestraining effectiveness. Note from the topmost curvethat if the individual level odds of referring a childi s increased tenfold by training (thusPi = 10 x 0.00032 = 0.0032), and 90% of the staffare trained, then the potential for identifying a sui-cidal youth can increase from 5% to 400/o. Ihisshows that even a small increase in everyone'sability to detect and refer suicidal individuals due toa successful gatekeeper training program can have avery large effect in identifying those who would Inotnormally be detected.

In January of 2004, we implemented a wait-listedrandomized trial to evaluate the QPR gatekeepertraining mnodel in this school district. The 32 eligi-ble middle and high schools, which had neverreceived QPR training, were stratified based onmiddle or high school and level of crisis referrals inthe previous year (split at the median). Within eachof these four strata, half of the schools were ran-domly selected to receive training in the first phaseof the study. Thus staff in one-half (16) of allschools were designated to receive QPR trainingduring the 2003-2004 school year. These schoolsare called "early intervention" schools. Ihe otherone-half of the schools were placed on a "wait list"and served as a control group during this firstschool year. During the next school year, thesewait-listed schools will receive Q1'R training. Wealso took steps to ensure that Ino school or childever receives less support than nlow provided bythe school district. In our analyses, we will examinethe effectiveness of the gatekeeper training inimproving surveillance of stuLdents at risk forsuicide and timely referral of these students formental health service. TIhe primary outcome of thisprevention trial is the rate of detection of childrenwho have been identified by the school as suicidal





and then verified by immediate assessment by a

mental health professional.

Training demand in a wait-listed design

For a typical wait-listed design, half of the urnits are

immediately assigned to intervention after baselinedata are collected. hus, half of all training beginsat the same time. It can be burdensomne for schoolsystems and other organizations to manage all thistraining at once, and it normnally takes some timefor such training to be scheduled and begin at all.In the Georgia gatekeeper trial, one can see that notraining occurred until approximately 40 days intothe study (see Figure 2). Even though it may takesome time to begin training and to provide all thetraining to half the units, we would typically treatthe date of randomization.or date of first trainiing asthe beginrning of the trial.

This tradition, inherent in the "iintent to treat"approach to randomiiized trials [10,7,9,'16], canhave the effect of attenuating differences betweenintervention and control conditions since little orno differences exist until training is actually pro-vided. During the first 125 days of training, theschool district was able to train 1387 out of 2498(56%) staff in the 16 early interventioin schools. Thelevel of training over time for all these schools was

not uniforin as shown in Figure 3. Virtually alltraining occurred within schools within a few days,so that no additional traininrg occturred over timeonce training began. Also, schools that began train-ing earlier had higher completioni rates thanschools starting later, as shown in Figure 4. 'lhesefigures indicate that training continued to occur

throughout most of this time; for single schoolsmost of the training occuLrred over a short period oftime, and these start times for the differentschools were dramatically different. This level of

iOs

'r

O 20 40 60 no 14444 120

Figure 2 Proportion of school staff trained since trial beganin 16 early training school by time

Tf .~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~'-T ' 7

l) 4) 44 64 K00 " io o

I..\Wtky

Figure 3 Variation in proportion and time trained in the 16different schools

0

0 O

0

t:

40 60 80 100 120

First Day Tyaimsl

Figure 4 Relation between time training began and propor-tion trained in first 125 days

incompleteness in training has persuaded us thatwe need to extend training in these early interven-tion schools over a longer period of time throughthe current school year, to provide booster trainingfor those staff trained in the previous year, and torevise the system of training for the wait-listedschools. T'he major irnplication of these data is thatinefficiencies appear to exist regarding the tiimingof training. In the dynamic wait-listed designdescribed below, the training schedule is likely tobetter match the logistical challenges inherent in a

large school system or other community settingwith multiple sites for training.

Dynamic wait-listed designs

We introduce a generalization of the wait-listed ran-

domniized desigin that is well suited to examiningintervention inmpact when intervenition condition

Clinical Trials 2006; 3: 259-271

C

.11

f,

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is assigned at either the group (eg, school) or indi-vidual level. In this new design, all units begin in,the control condition and at specified time inter-vals are switched to active intervention. If thenumber of total units to be assigned is N and thenuLmber of time intervals in the design is T, then atthe beginning of each new time interval, an addi-tional m = N/i units are randomlv selected fromthose still in the control condition and are assignedto start the intervention at that time. This processcontinues until all units are assigned to intervern-tion. TIable 1 corrmpares a standard wait-listeddesign, where r is two, with one where T is eight.Both of these designs take place over the same totaltime interval, which we have set to two years. I}heprimary difference, however, is that a wait-listeddesigin can compare intervention versuLs controlonly in the first year whereas the dyinamic wait-listed design continues to allow comparisons ofintervention versus control for all time unlits butthe last time interval when all units are finally inthe active intervention condition.

Variance in intervention impact estimate andpower for a dynamic wait-listed design

By dividing the total time of the study into X timeintervals, the dynamic wait-listed design permits acomparison of intervention and control conditionsat every time interval except the last, since only inthis last time interval are all units allocated to thesame active intervention condition. this providesan advantage over the classic wait-listed designwhich provides a legitimate comparison only in thefirst half of the stuLdy as seen in Table 1. Oni theother hand, it may appear that the statistical powerof a dyniamic wait-listed design is adversely affectedby an imbalance in the number of intervention andcontrol units at each time period as well as theshortened time blocks for assigning new units toactive intervention. As we show below, however, forvirtually all cases, the dynamnic wait-listed designactually increases statistical power despite these lasttwo countervailing factors.

We now consider power calculations for examin-ing intervention impact whein the outcome variableis based on a rate, such as the number of referredsuicidal children per fixed unit of time. Ourdevelopmen-t below begins with a linear randomeffects Poisson model since in that case we canobtain an exact expression for the general leastsquares solution. We then provide similar results forthe more traditional log-linear random effectsPoisson model.

Let 7' be the total time in the entire study andpartition the timne interval from 0 to T into T equaltime intervals. At each time interval [(t -- 1)T/,t7-i/.) indexed by t, t = ', ..., T- 1, let Xt representthe timne adjusted rate of referred suicidal childrenin those units who have been assigned to the inter-vention by time j and Yt be the same time adjustedrate of referred suicidal children in those units thathave not yet been assigned to iintervention by timej. Note that each of these rates are comprised of thesums of reported rates for each unit in the twointervention conditions over that particular timeinterval. Specifically, let Stk be the randoin numberof referred suicidal children in time interval t fromthe kth unit (here school), k = 1, ... , N. Also let Akbe the randomn assignment tinme for the kth unit,k= 1 ..,N.A simple model we consider first is one of a con-

stant intervention effect over all units along withain additive random Poisson time effect to allow fortime variations in referrals. It turns out that a closedform solution exists for the additive Poisson modelbut not for the more traditional multiplicativePoisson model. Thus we begin with the additivelPoisson model where we show that the variance ofthe intervention effect estimated by generalizedleast square quickly decreases with I.In this addi-tive Poisson model let y1 be the randoom effect attimne t, with a meain of zero, and let the Poisson rateparameter Ao refer to the control condition and Alrefer to the intervention condition

Szk- ![k()iSSorn((Ao + y7)IT) ifAk > t (5)

IIOissotl((A1 + yt)/T) if AA -: t (6)

Table 1 Unit assignment for standard wait-listed and dynamic wait-listed designs

Wait-listed design Dynamic wait-listed design

Year Time block Intervention Control Intervention Control

1 1 N/2 N/2 m N- m2 N12 N12 2m N-2m3 N12 N12 3m N- 3m4 N/2 N/2 4m-- N/2 N- 4m = N/2

2 5 N 0 Sm N- 5m6 N 0 6m N- 6m7 N 0 7m N im8 N 0 8m= N N---- 8m=0





with -y, being independent at each time interval andhaving zero mean and variance given by (Tr. Thismodel is equivalent to treating time as a blockingfactor. Then the observed average rates per time T ofsuicidal referrals in the intervention and controlconditions at time t are given respectively by

Xk.A <t StfX= v x (7)mt

k. Ai >t Stk

Yt= (8)

Using the independence assumption,

XtrT"lit X PoisFfln(nit(A1 + Yt1/T) (9)

and similarly

Yt -/N - nit) \ P'oisson((N - rnt)(A() + yt)T) (10)

rhese have conditional expectation A1 -+ y, andAO +yt respectively, and their conditional variancesare given by Var(Xtlyt) = ('r/mt)(A1 + yt) andVar(yt-ylt) = (Tl/(N - mt))(A0 + -yt) respectively. In thismodel we have assumed that -yt has zero mean sothe unconditional variance of the difference Xt - YtuLnder the null model of no intervention effect(Ako = A1 = A) is then

Va(r(Xt - Y') (1l/nit + 1/(N - Mnt)) x Ar

= (l/t-l1/( --- t)) X Ar/m (11)

To obtain an efficient combined estimate of thedifference between intervention anid control con-ditions over all the r - 1 time blocks, one shouldobtain a linear estimate where the weights areinversely proportioinal to each variance, that is,letting wt = (1/t + 1/(r - t)) 1, the best uinbiasedweighting for A1 - AO is

0 Etw1 t(Xt-Yt) (12)Y-t=l Wt

Ihe variance of 0 under the null model of nointervention effect is then

Var(o)= fwt Ar /m (1 3)t=1

This can be simplified by noting thatT-l T-1

wt (1/ t + 1 / (T - t))-ft=1 t=1

_ t(r-t)T- Tt=l

T-1 T-1

I t-E t2 ITt=1 t=1

=(r- 1)/2 - (2T - 1)(r -1)/6

=(T2- 1)/6 (14)

Irnsertirig this last expression into Equation (13),we obtain,

Var(O)= 6( 1M(T2 _ 1)6X2 A

(T2 _ 1) N(15)

witlh the last expression resuLlting from the rela-tionship mn = N17. Since only the first factordepends on r, this factor r 2/(r2 - 1) determines therelationship between the number of time intervalsand the variance of the resulting estimate. Thisfactor is decreasing in T when T= 2, 3, ... I N,implying that the variance of the estimatordecreases with increasing number of time intervals.'the relative reduction in variance is most pro-nouniced for small ., for r= 3 the improvement inprecision is 1 8%, for 7 = 4 the gaini is 25%IX, and thelimiting value is 33% gaini in efficiency whenl T = Naind each unit is raindomly assigned to interventionindividually.

Results for marginal maxiMLum likelihood esti-mation of intervention impact under a gammamixture of Poissons shows an even more pro-nounced gain in efficiency, especially with increas-ing intervention effect. Specifically, if we assumethat the count for eaclh time point and each unithas a Poisson distribution depending on interven-tion status and a random factor at each time point,

5tk - PIoivSw(lp)idf 'k -t

- IPoisson(lQit) ifAk t

(16)

(17)with

(18)

ILOt = ytA/T (19)where the random factors yt are centered around 1and lhave independent and identically distributedgamma distributions, Yt 1-'(a, P), t= 1,..., T -

with mean alp = 1 and variance a/p2In Figure 5 we present an examination of the effi-

ciency or ratio of asymptotic variances of marginalmaximum likelihood estimates interventionimpact, A,/AO for the dynamic wait-listed designcompared to the standard wait-listed design.Plotted on the abscissa is the nunmber of time inter-vals, with 2 corresponding to the classic wait-listeddesign. This figure demnonstrates the efficiency gainwhen there is both small and large variation in ratesover time, as well as the impact of differing levels ofintervention effectiveness. Beginning at the bottommost curve for no intervention impact and highvariability in rates across time, this shows the rapidincreasing efficiency to an upper limit of 1.3 just aswe presented for the general weighted least squaresresult in the previous section. Next note that in this


Il t =~-YIA /T

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V 32

All Intervention Effects wI Low Vanance ;n Rates over Time- IntervenTion Effect ofi8w High Variance in Rates over Tirne-Itervennon Effect of 4 wi Htig Variance in Rates over Tlane

nIwerventiorn Effect of 2 wi Hie Variantce ii Rates over TiirieIntervention Effect of 1 wl Higri Variance in Rates rver T ire

2 3 4 5 6 7 8

Tinrrinci

Figure 5 Efficiency of estimating intervention effect A1/A2for dynamic wait-listed designs (T -> 2) relative to a standardwait-listed design (T- 2) for different effects of intervention

case of high variability in rates across time, the effi-ciency increases substantially with increasing effectsize, from 2, to 4, to 8. The topmost curve indicatesthe efficiency gain at the other extreme when thereis low variation in the rates across time. Note thatefficiency increases to a maximum of 2, and there isno difference in efficiency as a function of effectsize. We can thus conclude that efficiency gains canvary from 1.3 to 2.0, with larger efficiencies withstronger intervention impact and smaller variationin these rates across time.

Use of a dynamic wait-listed design in theongoing Georgia gatekeeper project

The previous findings of gains in efficiency haveimplications for our current designl of the Georgiagatekeeper project eveen though we are already inphase I of a classic randominzed wait-listed design.Traditionally, the second phase of a wait-listeddesign, during which staff in the wait-listed schoolswould become trained, is not used for evaluatingintervention impact. Hlowever, it is still possible torandomly assign these remaining wait-listedschools to start at different time intervals in thesecond half of the study. That is, all the wait-listedschools are randomly assigned to two or more starttimes during the last half of the study. We presentthe effects on statistical power afforded by thisdesign chainge in Figure 6. In this figure the abscissacorresponds to the efficiency, in terms of the overallschool rate, of the interventioin to identify suicidalyouth relative to control. Note that with the tradi-tional wait-listed design (r = 2), there is 80% powerto detect a 32% increase in referral rates in theintervention condition compared to controls. Forthe planned modification where schools continue

04I1<.

- _

1.0

// __'_

/,

32 Time Blocks16l ine Blocks

- 8 Tiene BNcks6 Time Blocks

- "4 Trino Siocks- Standard Wait LUst

r./

Ar#R

11 12 1 3 14 1.S

Fffect = Interventtion Rate Cointrol Rate

Figure 6 Statistical power for estimating intervention effecton increasing referrals for suicidality with a dynamic wait-listed design begun in the second phase of the Georgia gate-keeper project

to be raindomized to intervention at different timesin the second phase, there is 80% power to detect a23% increase in referral rates. This gain would cor-respond to adding six schools to the current design.We plan to continue to randomize at the group

(ie, school) level to immediate or delayed interven-tion. -lowever, unlike a wait-listed design, whichwe used at the start of the Georgia gatekeeper trial,we do not require that half of the groups wait afixed amiouInt of time, ie, until the second year. Thischange will allow the schiool district to handle thescheduling of training and supervision necessaryfor a new intervention; it will also increase statisti-cal power over the wait-listed group yet provide thesame amount of protection in random assignmentas does the original wait-listed design. To carry outthis design, a blinded, randomized list of schools isgenerated; this determines the sequence of trainingof each school. At a specified advance time, thenext block of schools in this random sequence isnotified of its upcoming training so that schedulingcan occur. Once this training in a particular schoolis complete, the next school on the list begins theirtraining. This dynamic assignment of the sequenceof schools or other groups continues until allschools are completely trained.

Discussion

The dynamic wait-listed design is a new variant ofthe classic randomized wait-listed design. We notethree advantages, statistical efficiency, trainingefficiency and ability to improve statisticalmodeling.We have concludeed that nearly every dynamic

wait-listed design is much more efficient than thatused in the traditional wait-listed design. Gains in

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I T I

0.; "i -I

i: 11i-0 . J'sI

.i U):.9 -. --i0

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-

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268 C Hendricks Brown et al,

efficiency are subtantial and range fro{:m 33% to100%/v for mnost situations. The corresponding gainsin statistical power due to this gain in efficiency canalso be substantial. In our current trial, the switchto a dynamic wait-listed design in the second phaseis equivalent to adding another six schools to thestudy. The power calculations in this paper are allbased on a Poisson model, but this is not a require-ment. As long as the variance in the counts isinversely proportional to the length of the timeinterval, the same results hold. If the variance inthe outcome is not a function of the time interval,say a single follow-up self-report measure of suici-dality or timne to a suicide attempt, then the powerfor this wait-listed design is expected to do nobetter or Ino worse than that of a classic wait-listeddesign.

In many instances where training resources arelimited, a dynamic wait-listed design is expected tospeed up the training process and result in morecomplete training. A dynamic wait-listed designrequires that finite training resources be allocatedrepetitively to a small nutmber of units. In our par-ticular trial that is testing the QPR gatekeeperprogram, this concentration on the training of staffin a few schools at a tinme would make it easier toapproach full saturation in each school sooni afterbeing assigned to active intervention status.Complete saturation of training should also trans-late into higher levels of referral of suicidal chil-dren, as shown in FiguLre 1.A third advantage to using a dynamic wait-listed

design is that it allows for more general statisticalmodeling of intervention impact that is likely toreflect the realities of any intervention.

For example, we have omnitted any discussiorl ofvariation in intervention effectiveness, includingthe potential for the effects of training to wear offover timle. In the classic wait-listed design there isno way to unconfound the actual time of trainiingwith that of selection factors such as readiiness fortraining or organizational climnate. We have seein inour trial evidence that sclhools that train their staffearly are more successful in achieving nearlycomplete training. By allowing the actual time oftraining to vary in a dynamic wait-listed design,however, we can model whether referrals dropoff as a function of length of timne since trairningoccurred. Such information would be useful indetermining if and when booster training isneeded.

In a sufficiently large trial, it would also bepossible using a dynamic wait listed design todeterminie if an intervention had differentialeffectiveness at specific periods duriing the year. Forexample, rates of suicide tend to be higher in thewinter and spring [19,27,311. By allowing time oftraining to vary in a dynamic wait-listed design, it

wouli be possible to test if the effectiveness of gate-keeper training was miore effective at certain phasesof the year (eg, several months before elevated sui-cidal behaviors). Such information could enablecommunities and schools to use finite trainingresources more effectively by focusing trainingduring periods of maximal impact.

One could ask which of the dynamic wait-listeddesigns is most efficient. The solution to this israther straightforward. Simply conduct a standardwait-listed design with half of the units immedi-ately assigned to intervention and the remainingunits assigned to intervention at the last possibletime. Thus the most efficient dynamic wait-listeddesign approaches that of a standard wait-listeddesign that lasts twvice as long, hence the upperboLund of 100%/ efficiency gain. However, this is nota particularly useful design. It is unlikely that com-munities which are interested in having all units ina study receive the intervention would favorwaiting twice as long for any in the second half toreceive the intervention. The design change that wehave proposed in the Georgia gatekeeper project,which converts from a standard wait-listed designto that of a dynamic wait-listed design in thesecond phase is imore appealing aind still increasespower substantially.

While most randoinized trials still involveassigniment of individuals to condition, grouLp-based or place-based ran-domized trials haverecently become popular [1,32]. This new dynamicwait-listed design adds a third dimension for ran-domization, that of time. There is symmetry in thisrespect with the epidemiologic complex of person,place, and time. Now all three, or combinations ofthese three, can be used in random assignment tocreate an efficient design. In our trial we have ran-domlized at the school (place) level and are nowrandomizing across multiple time periods in adynamic wait-listed design. Similarly, randomiza-tion of individuals can take place at different timesas well. The traditional RCT that stratifies subjects,say on age and gender, and blocks on the sequentialorder of subjects is just one example of a design thatrandomizes individuals across time. We suggest thatcombinations of these three factors of person,place, and time can also be useful in evaluatinginterventions thought to have different impactacross both subject characteristics and contextualcharacteristics. This could be useful in testing theeffect of timiing of an interventioin on a disorderthat is affected by gene by environment interac-tions.

Being a true randomized trial, the dynamnic wait-listed design has clear advantages over interruptedtime series designs. The first of these designs,introduced by Cook and Campbell [37], did notspecifically involve randomization, but such





opportunities were soon recognized [38]. 'lIhere are,however, somewhat related multiple baselinedesigns that do involve randomization simlilar tothat presented here 18,391. Such multiple baselinedesigns are often used in education witlh a smallnumber of subjects (typically four or so) and a largenumber of times for testing (typically more than15). The scores of each person prior to their randomtransition time to the intervention is consideredbaseline and is compared to those scores after thetransition time. While the multiple baseline designis generally used for assigniment of a small numnberof individuals who are measured on a continuousoutcome, this sanme strategy of randomly assigningof time of intervention, is applicable to group ran-domnization, to larger studies, and the nmodeling oflow frequency counts with individual level as wellas group level covariates as in the examnple pre-sented in this paper.

Designs that randomize intervention time maybe quite valuable in evaluating the effectiveness ofprograms as they are expanded or "scaled Up" ina community. It is one thing to demoonstrateeffectiveness of an inter-vention with a randomizedtrial using 12 schools, for example; it is anotherthing to implemenit this intervention system:i-wide.Scalability is of fundamental importance for dis-semination and implemenitation research since thisis the final step in implemzenting evidence-based orempirically supported prevention programs in drugabuse, mental health and social services, and educa-tion. To date few scalability studies have consideredrandomly assigning the time that classes, schools,families or agencies begin intervention. We believethat randomization has an important role in thedesign of such studies, and such designs can beinformed by the results described here.

l"hese dynamic wait-listed designs are also appro-priate for testing early detection screeningapproachles for cancer, [lIV and other medical con-ditions as well. For example, to test the effective-ness of identifying lunlg cancer, one couLldrandomize the time at which inidividual clinicsswitch from the usual practice where chest X-raysare occasionally ordered by physicians, comparedto routine use of helical CL. At each interval oftime, all eligible patients who visit the clinic can betested with the new screening procedure. Rates ofidentification of lung cancer by cancer stage canthen be compared, along with false positive ratesand cost effectiveness evaluations. Such a designwould work whether or not the screening protocolrequires retesting at specified intervals or only asingle test. In the latter case, as long as there arepatients who continue to come for their first visitafter a clinic begins the new screening procedure,the results of these screening tests can be used toassess intervention impact. Modeling over time

would of course need to take into account patientcharacteristics anid length-biased sampling sincepatients who attend more frequently are likely todiffer fromi those coming to the clinic less fre-quently. Similar ideas were suggested by Braver andBraver [39].

There are situations where this dynamic wait-listed design should not be used. In particular, inthose instances where it is not possible to varytraining schedules, such as training in a newreading curriculum where all teachers need to beprepared at the beginning of the year, random starttimes throughout the year would be inappropriate.However, a dynaimic wait-listed design could poten-tially be used over multiple years to accomplish arolling-in of a new curriculum. In this way supervi-sion or coaching during the year, rather than initialtraining, could be concentrated on a limitednumber of newly trained teachers each year. Asecond set of circuimstances that would make thisnew design inappropriate is under a conditionwhere those randomized to wait may end up with-drawing frorm the study before they are assigned toactive intervention. For example, in clinical trials ofinterventions to reduce suicide amnong individualswith prior histories of suicide attempts [26], it maybe inappropriate to extend waiting periods for soineindividuals givein the high-risk status of all trialparticipants. A classic wait-listed design that trainseveryone eligible soon after assignment would havea smaller average wait-time to intervention com-pared to the dynamic wait-listed design. Also, in adynamic wait-listed design the variance in time tobeginning the intervention increases with thenumber of time intervals, so those towards the endof the line mnay be inore likely to withdraw or findarn alternative active intervention. Of course, thesedifferences in time to training of a standard versusdynamic wait-listed design diminish if much of thetraining cannot be accomplished until towards theend of the study.

Acknowledgements

Work on this paper was supported by the NationalInstitute of Mental I-lealth, the National Instituteon Drug Abuse and the Centers for Disease Controland Prevention under the main grant and supple-mnents of RO1 MH40859, as well as from theNational Institute of Mental Health under grantsR34 MH071 189 and P20 MH07 1897. We thankour colleagues in the Prevention Science andMethodology Group (PSMG), especially Dr WeiWang, for their comments, for support from ouLrcolleagues at the University of Rochester Centerfor Public I-lealth and Population Interventions forthe Prevention of Suicide, as well as Drs Kevin





Cain, Elaine Thompson and other members of ourData Safety and Monitoriing Committee for initialdiscussions that led to the development of thisdesign. We also want to thank Jerry and ElsieWeyrauch without whom the Georgia Gatekeeperproject would never have taken place. They haveworked tirelessly for the development of rigorouLsscientific studies in the prevention of suicide.Special thanks go to our colleagues in the schooldistrict, who remain anonymous for reasons ofschool policy, for their dedication to their studentsas well as to this evaluation.

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Appendix. Derivation of designefficiency for dynamic wait-listeddesigns based on a 1 mixture ofPoisson counts

X (p + bt) XtNt x A1NItA0NOt

Tohe log likelihood is thenT-1

log L(A1, A2) = const +± - (a + Nt)log(p+ bt)t=l

+ Nit logAl +Not logA0

The score equations are

alogL TE _ (a+N) l+ 1DA, t=l (a+bt) r Al

alogL T-1 (a+Nt)m0t NotaAA t-l (a+bt) T AO

Tlhe informiationi matrix is then given by

In this appendix we present the general formulaefor the variance for mnaximum likelihood estimatorsof two Poisson rate parameters when differentnumbers of units are assigrned to intervention or

control conditionis over time. For timae t, t = 1, ....- 1, let m1t be the number of units assigned to

the intervention condition aind mot be the num-

ber assigned to the control condition. DefineN tEk St, as the total

number of observed counts in intervention unitsand control units respectively at time t. LetNt = Nit + Not, Also define bt = (m1tA1 + mt.tk)/,the expected number of reported events in intervalt when yt = 1. The joint density of the counIts attime t is then given by

f(Stl, ... I SIN)°- r( ) 7- e-l'yF(a)x e-y -stn0l,+i .k,)/TyN' d NA N~ (20)

The expected information is obtained by notingthat

E(NIt) = Eyt E( Y, Sk IYt)k:A t

= initAIE(Yr)

in tAk1,C/p

E(N,t) --- mnotAoalp

(26)

(27)

(28)

(29)

'l'he final step is to calculate the variance of theMLE for A1/Ao (or its logarithm). TIhis can beobtained through an application of the multivariateDelta method.


(21)

(22)

(23)

(24)

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